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46
AN EVALUATIVE REPORT ON THE CURRENT STATUS OF PARAPSYCHOLOGY
BY
JOHN PALMER, PH.D.
PRINCIPAL INVESTIGATOR
PARAPSYCHOLOGY LABORATORY
UNIVERSITY OF UTRECHT
UTRECHT, THE NETHERLANDS
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ARI SCIENCE COORDINATION OFFICE, EUROPE
EUROPEAN RESEARCH OFFICE, U.S. ARMY, LONDON, ENGLAND
(SCIENTIFIC COORDINATION OFFICER: DR. MICHAEL KAPLAN)
DECEMBER 1985
PREPARED UNDER CONTRACT NUMBER DAJA 45-84-M-0405
U.S. ARMY RESEARCH INSTITUTE FOR THE BEHAVIORAL AND SOCIAL SCIENCES
5001 EISENHOWER AVENUE
ALEXANDRIA, VIRGINIA 22333
USA
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AN EVALUATIVE REPORT ON THE CURRENT STATUS
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John Palmer, Ph.D.
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Parapsychology Laboratory
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Parapsychology, anomalies, extrasensory perception, psychokinesis, psi.
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This report constitutes a critical review of eight major research
areas in the field of parapsychology over the past twenty years. The
report begins with a philosophical analysis of the way research questions
in parapsychology are formulated. It is concluded that the claim to
have established psi in the sense of paranormality can be.rejected
a priori because of the generally conceded absence of a confirmed para-
normal theory. Given this fact, the important question becomes whether
the observations reported by parapsychologists have adequate conventional
explanations or whether they are true anomalies.
The methods and results of each research project are summarized,
along with whatever criticisms of these projects have been published.
This material is then critically evaluated from the point of view of
assessing what conventional mechanisms could conceivably account for
these findings and the adequacy of these mechanisms as explanations.
In general, it is concluded that despite some methodological
shortcomings and inadequate reporting, parapsychologists have succeeded
in documenting genuine anomalies worthy of scientific interest. Reliable
application of whatever paranormal process these anomalies might repre-
sent is unlikely until this process (if it exists) is better understood.
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The research reported in this document has been made possible by
Contract number DAJA 45-84-M-0405 from the U. S. Army Research Institute for
the Behavioral and Social Sciences through its European Science Coordination
Office at the European Research Office of the U. S. Army, London, England.
As stated above, the opinions expressed are those of the author; they do not
necessarily represent the opinions of the U. S. Army.
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TABLE OF CONTENTS
Note:
The pages in parentheses refer to the pages in Chapter 10 where the
summary of the chapter in question begins.
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Chapter 1: Introduction.
1 (202)
Chapter 2: The Maimonides Dream Experiments
22 (203)
Chapter 3: Remote Viewing
41 (205)
Chapter 4: The Ganzfeld Debate.
66 (207)
Chapter 5: Random-Event-Generator Research.
97 (209)
Chapter 6: The Delmore Experiments
125 (212)
Chapter 7: Correlational Studies
138 (214)
Chapter 8: Psi-Mediated Instrumental Response.
.162 (216)
Chapter 9: Metal Bending
178 (218)
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Chapter 10:
Summary and Conclusions
.202
References.
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FINAL REPORT
AN EVALUATIVE REPORT ON THE CURRENT STATUS OF PARAPSYCHOLOGY
by John Palmer, Ph.D.
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ACKNOWLEDGMENTS
1
I wish to introduce and gratefully acknowledge the important
contributions made to this report by the following three individuals, all of
whom were supported by the grant.
My Research Assistant, Debra H. Weiner, has been involved in the field
of parapsychology for 9 years and has contributed numerous articles to
parapsychological publications. In addition to typing and editing the
manuscript, her critical comments on the content have been very useful.
I have employed two technical consultants. I chose these particular
individuals because (a) they are knowledgable in the areas where I needed
technical expertise, (b) they are familiar with parapsychology, (c) they
have a level-headed and detached attitude toward parapsychology, and (d) I
know them personally and know I can communicate with them effectively.
My statistical consultant was Dr. Donald S. Burdick, Associate
Professor of Mathematics and Biomedical Engineering at Duke University. Dr.
Burdick has been a consulting editor to the Journal of Parapsychology and is
a co-author of a chapter on statistical methods in the Handbook of
Parapsychology.
My engineering consultant, whose advice was sought primarily for
Chapter 9, was Ronald S. Hawke. Mr. Hawke is a research physicist at
Lawrence Livermore National Laboratory. He has a long-standing interest in
psychokinesis and is a contributor to The Geller Papers, an edited series of
reports on research with Uri Geller.
Whereas the above individuals have given me valuable assistance, all of
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Chapter 1
INTRODUCTION
The purpose of this report is to critically review experimental research
in the field of parapsychology. This introductory chapter has two purposes.
The first is to familiarize the reader with the basic terms, methods, and
strategies used by parapsychologists in their research, as well as the classes
of criticisms leveled against this research by outside commentators. The
second purpose, which will require that I indulge in some philosophical
analysis, is to propose a reconceptualization of the basic question one must
ask in evaluating parapsychological research. The chapter will conclude with
a brief discussion of the approach I will take in succeeding chapters to
address this basic question.
An Overview of Parapsychology
Parapsychology can be defined as the scientific study of interactions
between living organisms and their environment which seem to transcend the
currently accepted laws of physics or, more precisely, the so-called "basic
limiting principles" of nature, such as those defined by philosopher
C. D. Broad (1953) :
(1) General Principles of Causation. It is self-evidently impossible that
an event should begin to have any effects before it has happened ...
(2) Limitations on the Action of Mind on Matter. It is impossible for an
event in a person's mind to produce directly any change in the material world
except certain changes in his own brain ...
(3) Dependence of Mind on Brain. A necessary, even if not a sufficient,
immediate condition of any mental event is an event in the brain of a living
body ...
(4) Limitations on Ways of Acquiring Knowledge. It is impossible for a
person to perceive a physical event or a material thing except by means of
sensations which that event or thing produces in his mind ...
(pp. 9-12)
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term psi.
Psi is traditionally subdivided into two major categories:
extrasensory
perception (ESP) and psychokinesis (PK). ESP is taken to mean acquisition of
information not available to the recognized physical senses or through logical
inference. Because of the roots of parapsychology in Cartesian dualism, a
further metaphysical distinction is made between telepathy (where the source
of the information is assumed to be another mind) and clairvoyance (where the
source of the information is assumed to be a material object, event, or
process). In those cases where the source of information as such exists in the
future rather than in the present, the process is called precognition.
PK refers to the influence of physical objects or events by an organism
in ways that cannot be attributed exclusively to known physical forces. During
the last decade an analog to precognition has been introduced which postulates
PK influence of an event backwards in time; i.e., the effect precedes the
cause. This process is referred to as retroactive PK, or retro-PK.
Basic Methodology
ESP. In a test of ESP, the subject is asked to guess a randomly selected
target or sequence of targets without access to pertinent sensory information.
If another person, called the agent, is attempting to "send" the identity of
the targets to the subject, the test is defined operationally as a test of
telepathy or of general extrasensory perception (GESP). The latter term is
preferred because it takes account of the possibility that the source of
information could either be the physical representation of the target or its
registration in the mind of the agent. Tests in which there is no agent are
referred to as clairvoyance tests. If the targets are not generated until
after the guesses are made, it is called a precognition test.
Each attempt to ascertain a target is called a trial, and an
uninterrupted series of $x
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The number of hits can be summed over the run or other unit to provide a total
score.
If the score is higher than the number expected on the basis of chance
(called mean chance expectation or MCE), it is called psi-hitting.
A
below-chance score is called psi-missing. Scores are also sometimes
conceptualized in terms of the deviation from MCE irrespective of direction.
If the scores deviate widely from MCE the result is called high variance. An
overly compressed distribution of scores is called low or tight variance.
Methods for testing ESP can be broken down into restricted-choice (RC)
and free-response
(FR) categories. In RC tests, the subject is asked to guess
a concealed sequence of target items arranged in a random order. The procedure
is called restricted-choice because the number of target alternatives and thus
the number of scorable responses is fixed and finite.
The traditional targets for RC tests are a deck of cards consisting of
five geometric symbols: star, circle, cross, square, wavy lines. A wide
variety of standardized test procedures has been developed using these cards
(Rhine & Pratt, 1957) and they still see occasional use. A more common
procedure, however, is to utilize a device called a random event generator
(REG). A random sequence of events is produced through the sampling of an
electronic noise source which in some machines is further mediated by the
randomly timed emission of beta particles from a decaying radioactive source
(Schmidt, 1970b). These decisions are then registered on counters inside the
machine or in the memory of a computer to which the device is attached. The
subject's task is to identify a symbolic representation of the target state,
generally presented to the subject through some sort of display, which the REG
has selected (or will select) for each trial. The number of target
alternatives generally ranges from two to ten and, much more commonly than
with card tests, subjects are given feedback of the identity of the target
after each trial. The advantages of REGs over more traditional methods include
the more reliable method of randomization and the automated recording of
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In all RC tests, standard statistical techniques are used to determine
whether the number of hits or the variance of the scores exceed the
theoretically expected value to a significant degree. If this is the case, and
to the extent sources of artifact have been eliminated, ESP is claimed to have
been demonstrated.
Free-response (FR) tests have become increasingly popular because they
are generally more interesting to the subject and more closely approximate the
way ESP operates in the "real world." The targets used in FR tests are
generally more complex than those used in RC tests. Examples of FR targets are
prints of paintings (Ullman, Krippner, & Vaughan, 1973) and View-Master slide
reels (Honorton & Harper, 1974). In the highly publicized remote viewing
procedure (Targ & Puthoff, 1977), the targets are most commonly geographical
sites.
The subject in an FR test is encouraged to free-associate, i.e., to
report anything and everything that comes into his mind with the intent that
this mentation will pertain to the unknown target. The response period can
last anywhere from 5 to 45 minutes, and there is normally just one trial per
session. Later, the subject or an outside judge is asked to select on a blind
basis from among a set of pictures, sites, etc. (including the target), the
one which corresponds most closely to the subject's imagery or mentation
report; alternatively, the pictures may be ranked or rated for correspondence
on a scale.
These methods ultimately allow the results to be evaluated statistically
in ways comparable to those used for RC tests. However, this is accomplished
at the price of a great loss in power such that statistical significance can
rarely be demonstrated for a single session. Some more powerful techniques
which involve breaking down the targets and/or responses into discrete
information units have occasionally been applied (e.g., Jahn, Dunne, & Jahn,
1980).
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The subject is often prepared for a FR test through induction of a
hypnagogic-like state of consciousness designed to break down linear thought
processes, encourage inward focusing of attention, facilitate the flow of
mental imagery, and eliminate distracting external stimulation. The most
popular of such techniques is the ganzfeld, a procedure in which the subject
looks through halves of ping-pong balls covering the eyes into a white or red
light while listening to white or pink noise being played through headphones
(Bertini, Lewis, & Witkin, 1969). This procedure often produces effects
somewhat similar to longer-term perceptual deprivation, but without the
adverse side effects.
PK. The traditional method of PK testing utilizes mechanically thrown
dice, the subject's task being either to make one face appear uppermost or to
cause the dice to fall on one side or the other of a divided surface (Rhine &
Pratt, 1957). However, dice tests have not been used for many years. By far
the most common method of contemporary PK testing is to have the subject
attempt to bias the output of an REG by influencing the electronic noise or
radioactive decay processes. If desired, trials can be generated at very rapid
rates (hundreds per second), which allows for the application of powerful
statistical analyses. Ongoing analog or digital feedback can be provided to
subjects in innumerable ways in either the visual or auditory mode, and the
feedback display itself is often presented to the subject as the target (e.g.,
"Keep the red line above the center of the screen"). Methods of statistical
analysis are comparable to those employed in ESP tests.
A wide variety of other techniques involving an equally wide range of
physical processes have seen limited use. Those which seem most likely to
evolve into standardized experimental paradigms involve the subject attempting
to produce localized changes in temperature as measured by thermistors
(Schmeidler, 1973) or stress in metalic objects as measured by strain gauges
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metal-bending procedures in which the subject is allowed physical contact with
the target specimen are notoriously difficult to control and generally not of
scientific interest unless anomalous molecular transformations in the
structure of the specimen can be demonstrated.
One finds even less standardization in the study of PK effects on
biological systems. Examples of target systems in past research range from
digestive enzymes in vitro (Smith, 1972) to bacteria (Rauscher & Rubik, 1980)
to skin lesions in mice (Grad, Cadoret, & Paul, 1961). Serious "healing"
research with humans is virtually non-existent, but some attempts have been
made to remotely influence psychophysiological responses such as GSR (e.g.,
Braud, 1978).
Research Strategies
There are two major research strategies which parapsychologists have
adopted. Proof-oriented experiments, which to the extent they are limited to
this strategy could more properly be called demonstrations, involve attempts
to demonstrate psi effects in such a way that all reasonable "normal" or
conventional explanations have been ruled out. Almost all psi experiments
which are widely known outside of parapsychological circles are primarily or
exclusively proof-oriented.
The majority of psi experiments, however, are primarily process-oriented.
In its pure form, this approach avoids tackling the ontological status of psi
directly and attempts instead to identify its psychological and physical
correlates as a basis for the development of explanatory theories or
models. Psi scores are treated as dependent variables to be related to such
things as scores on psychological tests and manipulations of physical or
psychological conditions as independent variables. Because of the need to
improve the reliability of psi effects, particular interest has been directed
toward identifying test conditions that
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develop networks of reliable correlates of psi effects that differ from what
might be predicted on the basis of conventional counterexplanations of these
effects.
Most process-oriented research is guided by implicit theory and sometimes
by more fully developed models from which testable hypotheses are
derived. Most theorizing in parapsychology is psychologically oriented and
addresses such issues as how ESP "information" is processed, blocked, or
distorted after it reaches the mind of the subject. The most fully articulated
and comprehensive of these psychological models is that of Psi-Mediated
Instrumental Response (PMIR), which links both ESP and PK to principles of
learning theory and dynamic psychology (Stanford, 1977).
Theorizing about how information gets from the source to the receiver in
ESP, or how the subject affects the target system in PK, draws more heavily on
physics. The most fully developed specimens here are the so-called
Observational Theories (OTs), especially the version of Walker (1975). These
theories represent extensions or radical interpretations of quantum mechanics,
their main premise being that observation of the data of a psi experiment
serves a function analogous to measurement in quantum mechanics. The notion of
retro-PK is a direct consequence of these theories. The OTs have generated
some testable predictions as well as much controversy.
Most process-oriented psi experiments are also proof-oriented in the
sense that attempts are made to incorporate the kinds of controls demanded of
proof-oriented experiments. Nonetheless, the objectives of the two kinds of
experiments are clearly different.
Criticisms
External critics of parapsychology generally have not acknowledged the
existence of the process-oriented approach in psi experimentation, so their
criticisms are directly relevant only to the proof-oriented approach. The
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Fraud. Because of the origins of parapsychology in Spiritualism and the
fact that a high percentage of its external critics are either amateur or
professional stage magicians, suggestions of fraud by high-scoring subjects
have become commonplace. Some critics also consider it appropriate to
speculate about fraud on the part of experimenters. Isolated cases of
experimenter fraud have in fact been uncovered in parapsychology (e.g., Rhine,
1974), but the extent to which such transgressions can be generalized to the
field as a whole is debatable.
Sensory Cues. In ESP experiments, the subject should have no access to
sensory information about the target. Critics are not always satisfied that
such cues have been eliminated. Hyman (1985), for example, has noted that in
some .FR experiments the target picture handled by the agent is included in the
set of pictures later given to the judges for scoring and could contain
identifying fingerprints, etc.
Randomization. It is generally considered to be important that the
target sequences in ESP experiments be satisfactorily random. This is
particularly crucial in those experiments where subjects are given
trial-by-trial feedback of targets and could learn to identify patterns in the
sequence during the course of the test. Likewise, in REG PK experiments it is
·
considered important that the output of the REG be satisfactorily random in
the absence of attempted PK influence. Whether adequate procedures have been
used both to generate and to verify randomness has been a major focus of
criticism of psi research.
An alternative to establishing randomness, which is necessary in those PK
procedures where theoretical chance baselines cannot be defined, is to compare
psi test results to empirically defined baselines established in control
conditions.
Statistics. Statistical criticisms of psi experiments are difficult to
compartmentalize,
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test employed or failure to adjust significance levels for multiple analyses.
Data Selection. It is sometimes suggested that parapsychologists
withhold nonsignificant results from their reports or classify them as
exploratory on a post-hoc basis, thereby making the reported results seem more
significant than they really are. A related criticism is labeled optional
stopping, which refers to aborting an experiment or series of trials at a
randomly occurring apex in the scoring level. It is generally agreed that it
is permissible to apply optional stopping to subunits of trials (e.g., the
number of trials contributed by a particular subject in a multi-subject
experiment) so long as the total number of trials in the experiment is
specified in advance.
:
Replicability. Although replicability by itself cannot establish the
paranormal nature of psi anomalies, most parapsychologists and their critics
agree that it is a necessary prerequisite for establishing the reality status
of psi. No one claims that psi effects are reproducible on demand, but many
parapsychologists claim that certain psi effects are replicable to a degree
that significantly exceeds chance expectancy, i.e., statistical
replicability. Various attempts have been made to demonstrate this claim
through a technique that has come to be called meta-analysis (Glass, McGaw, &
Smith, 1981), in which groups of experiments are treated statistically in much
the same way as are groups of subjects in individual experiments.
A closely related problem is that successful psi experiments are not
randomly distributed among the investigators who conduct them. In other words,
while some experimenters in parapsychology seem to consistently obtain
significant evidence of psi in their experiments irrespective of the
particular type of experiment undertaken, others just as consistently do not.
This so-called experimenter effect looms as a major problem in the field and
has obvious implications for the replicability issue. The fact that successful
experimenters tend to be those favorably inclined to the reality of psi has
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Introduction
Page 10
their "belief" in psi causes them to overlook potential
artifacts. Parapsychologists, on the other hand, have suggested that
successful experimenters either are better at motivating their subjects or are
the sources of the psi themselves. Some empirical evidence has been offered
in support of both of these hypotheses.
Asking the Right Question
In Search of the Conclusive Experiment
We have now come to the point where it is necessary to examine how
parapsychologists have formulated their basic research objectives.
Parapsychological inquiry has traditionally organized itself around the
question, "Does psi exist?" The term psi, as noted in the preceding section,
is defined negatively as some process that transcends currently accepted
1
physical principles. It is not surprising, therefore, that the approach to
its verification or validation has also been negative. Again as previously
noted, psi is considered to have been demonstrated if, and only if, all
conventional processes, i.e., processes subsumed under the basic limiting
principles, have been eliminated. Both parapsychologists and their critics
have agreed on this requirement. Indeed, the controversy around the
pioneering experiments of J.B. Rhine in the 1930s focused on just this
question: Did any of Rhine's experiments in fact eliminate all such
possibilities?
Rhine, perhaps influenced by the simplistic behaviorism which reigned in
psychology at the time, overestimated the ease with which this requirement
could be met. In Extrasensory Perception After Sixty Years (Rhine, Pratt,
Stuart, Smith, & Greenwood, 1940) he and his colleagues painstakingly analyzed
all the experimental work up to that time with reference to 35 conventional
mechanisms proposed by critics, which included faulty statistics, data
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experiments were found to be immune to all 35 criticisms, of which the two
most prominent ones were the Pearce-Pratt Series and the Pratt-Woodruff
Series. However, critics, most notably C. E. M. Hansel (1966), had little
difficulty in pointing out ways in which the statistically significant results
of these two experiments could be explained by conventional processes: in the
case of the Pearce-Pratt experiment, it was by cheating on the part of the
subject; in the case of the Pratt-Woodruff experiment it was by cheating on
the part of the junior experimenter. Rather indignant exchanges about both
experiments raged in the literature into the 1970s, with no clear resolution.
With the benefit of 20/20 hindsight, it is nonetheless fair to say that
both experiments could have been better designed to take account of the
possibilities raised by the critics. It is equally clear that no other psi
experiment has been shown to be immune to all conceivable counterexplanations.
In fact, parapsychologists no longer claim such an experiment. The approach
nowadays is to argue either that the "flaws" cited by critics in response to
the better experiments are trivial and speculative (i.e., the
counterexplanations are implausible) or that the collective weight of the
experiments is compelling even though no single experiment by itself is
conclusive.
.
On the other hand, parapsychologists have been reluctant to repudiate
explicitly the proposition that an evidential psi experiment must eliminate
all conventional alternatives, probably out of the quite reasonable fear that
to do so would expose them to charges of sloppiness, lowering methodological
standards, etc. This reluctance has allowed critics to argue persuasively
that parapsychologists have failed to establish the existence of psi by their
own (parapsychologists") criteria.
However, the fact remains that the standard of the conclusive experiment
is encumbered by logical difficulties which are both real and fatal.
Criticisms such as experimenter fraud, if carried to their logical conclusion,
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(e.g., Hyman, 1981). Although Hansel replies that sufficient independent
replication of psi experiments would suffice to overcome such criticisms, this
conclusion does not follow logically from his premises. The replicability of
an effect, however consistent that might be, tells us nothing about its causal
mechanism. Even collusion or fraud on the part of all the experimenters,
although a rather implausible scenario, would be a preferable explanation to
psi, according to the logic of Hansel's position. In fact, Hansel is rather
explicit in stating that the implausibility of a conventional hypothesis
should not be held against it: "A possible explanation other than
extrasensory perception, provided it involves only well-established processes,
should not be rejected on the grounds of its complexity." (Hansel, 1980,
p. 21)
But even if a critic were to concede the honesty of the experimenter (or,
for that matter, the subjects) and no other counterhypothesis could be put
forth, it still would not follow that all such counterhypotheses have been
ruled out. The reason is simply that one cannot be sure that all
counterhypotheses have been thought of at a given point in time.
It is
therefore legitimate, as Hyman (1981) has in fact done in relation to the
successful PK experiments of Helmut Schmidt, to ask that we suspend judgment
for an unspecified period of time, banking on the idea that an acceptable
counterexplanation will eventually emerge. The problem, however, is that the
possibility of conventional counterexplanations can never be ruled out because
the population of such counterexplanations can never be defined in a way that
is known to be adequate. In other words, since one can never know if all
possible counterexplanations have been thought of, one must suspend judgment
indefinitely.
The implication of the preceding analysis is simply that the presence or
absence of a "conclusive" experiment, even a repeatable one, is not an
adequate standard by which to evaluate the claim "psi exists," because it is
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Inherently unfalsifiable.
So what is an adequate standard?

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Conflation in the Use of "Psi"
Before answering this question, it is necessary to consider a curious
characteristic of the way the term "psi" is used both by parapsychologists and
their critics. According to the official definition, "psi" refers to a
paranormal principle or cause; i.e., it is intended to be a theoretical or at
least a quasi-theoretical construct that serves to explain certain natural
events. However, the term "psi" is often used as well to label the events
themselves, as in the more complex term, "psi phenomena." The point here is
that with respect to actual usage, no clear distinction is made between the
phenomena under study and the quasi-theoretical principle proposed to account
for them, between the explanandum and the explanans.
One illustration of this conflation is the accepted definition of
parapsychology: "the scientific study of paranormal phenomena" (Thalbourne,
1982, p. 51), which can be translated as "the scientific study of psi." Note
that the definition assumes that the paranormality of the phenomena under
investigation is granted a priori. This of course does not adequately
describe most parapsychological research, which does not assume paranormality
a priori but rather is undertaken to verify paranormality a posteriori,
empirically. The definition, however, defines the subject matter of
parapsychology in terms of parapsychologists" preferred explanatory framework.
The same conflation can be detected in the writings of critics when they
claim that parapsychology lacks "facts" or a subject matter. What they really
mean is that parapsychologists have failed to establish the "existence of
psi." However, what parapsychologists have failed to establish is psi the
theoretical principle, i.e., psi the explanans. But a theoretical principle
is not a subject matter. The subject matter of parapsychology is its
phenomena, the explanandum. Only if we conflate the explanandum and the
explanans does the statement that parapsychology lacks a subject matter seem
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The way out of the conflation is simply to define the phenomena
parapsychologists study in a theoretically neutral way, that is, independently
of whether the phenomena are in fact paranormal. In a previous paper (Palmer,
1985) I have suggested that the term psi be retained to label the phenomena
and proposed the term omega to label the theoretical or quasi-theoretical
principle proposed by parapsychologists to account for them. Only omega
implies paranormality. While we await the adoption of this or some comparable
scheme, I have suggested that "psi phenomena" be labeled as "ostensible
psychic events" (OPEs).
Rephrasing the Question
-
Appreciation of this conflation encourages a critical examination of how
the fundamental research problem in parapsychology is phrased. The
existential phrasing of the question "Does psi (i.e., paranormality) exist?"
both reflects and reinforces the conflation of explanandum and explanans
because "existence" is more naturally attributed to the former than to the
latter. Indeed, reification of a theoretical construct is often considered
objectionable in the philosophy of science. In any event, the preceding
analysis suggests a better phrasing of parapsychology's fundamental research
question: "How can ostensible psychic events (OPEs) be best explained?"
This new question has several important implications which bear upon our
original question of what is the appropriate standard for evaluating evidence
for psi. One is that parapsychologists can only "demonstrate" paranormality
by confirming a theory that adequately explains OPEs by appeal to some
"paranormal" theoretical principle, i.e., a theoretical principle that
transcends Broad's basic limiting principles. This means that paranormality
would not be established even if a conclusive experiment were both possible
and replicable on demand. "Paranormality" can only be legitimately claimed in
the context of a theory that
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Introduction
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eliminating competing alternatives is logically flawed and can be rejected
prior to analysis of their success in actually eliminating the alternatives
considered.
Have parapsychologists succeeded in establishing paranormality by the
more proper route, i.e., by confirming a paranormal principle or theory? Even
the great majority of parapsychologists would concede that this has not yet
been accomplished. Although the Observational Theories represent a serious
attempt in this direction, these theories have not yet been sufficiently
tested to be considered established.
On the other hand, and this is a key point, the failure of the
parapsychologists to provide an adequately verified paranormal explanation of
OPEs does not imply the existence of adequate conventional explanations.
Another of the unfortunate consequences of the question "Does psi exist?" is
that it has caused parapsychologists and critics alike to assert that the
burden of proof in parapsychology falls exclusively on the claim of
paranormality, i.e., the claim that "psi exists." The main rationale for this
conclusion is that it is unreasonable to demand verification of the opposite
conclusion, "Psi does not exist," because it is a universal (and existential)
negative. But this is no longer the case when the question becomes "How can
OPEs be best explained?" Here the canons of scientific method clearly state
that the burden of proof falls upon anyone who proposes to explain OPEs,
whether the appeal be to paranormal or conventional explanations.
OPEs for which no adequate explanations have yet been found can be
construed as anomalies with respect to the basic limiting principles, because
when taken at face value they are inconsistent with them (Palmer, 1985).
Calling them anomalies is in no way meant to imply that the explanations of
OPEs are necessarily paranormal, or that an adequate conventional explanation
of OPEs may not someday be found. However, the fact that such events are
paranormal when taken at face value is considered reasonable grounds for
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Introduction
Page 16
potential explanations of OPEs that need to be considered.
Although parapsychology experiments are routinely construed both by
parapsychologists and their critics as tests of the "psi hypothesis," the
present analysis suggests that in most cases they could more profitably be
construed as tests of certain specific conventional hypotheses which purport
to explain OPEs. Only rarely do such experiments test a paranormal theory or
mechanism. Thus, the real issue in most experiments is not whether OPEs are
paranormal but whether they are anomalous. The results of such experiments
are anomalous to the extent it can be shown that no conventional explanation
of the results is scientifically adequate.
Redefining the Standards of Evidence
The most difficult question confronting this analysis is what criteria
should be set for an adequate scientific explanation of OPEs. Some would
argue on philosophical grounds that one such criterion is that the explanation
must be conventional, based on appeal to the so-called "coherence" principle.
This principle states that the currently accepted laws of nature, which
preclude paranormal processes, are universal in scope. Although the coherence
principle has not always been a reliable guide in science, Newtonian mechanics
being its most notorious failure, it is nonetheless positively valued in the
scientific community and I cannot logically compel its abandonment. On the
other hand, no empirical evaluation of parapsychological research, such as
will be attempted in this review, would make sense if the coherence principle
were to be accepted in its strongest form. It is worth noting that a
moderately strong form of the coherence principle plays a prominent role in
the approach of most critics of parapsychology, especially those like Hansel
who argue that all conventional hypotheses must be ruled out before paranormal
hypotheses can be entertained.
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explanation of OPEs,
apart from logical ( internal) coherence and the like are the como omnifinal
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criteria we see in the rest of science. Whereas these are hard to define on
paper and disagreements abound as to how well they are met in specific
instances, at least the problem we are dealing with is a familiar one.
It is perhaps worth mentioning in passing that many scientists (including
some parapsychologists) who accept a weak form of the coherence principle
would argue that a greater degree of empirical evidence is necessary to
support a paranormal theory than a conventional one, that "exceptional claims
require exceptional proof." I admit to being somewhat of a maverick in
rejecting this proposition. Briefly, my reasons are the following: (1)
applying such a principle leads to selective rejection of research findings
and a bias in the research literature that would artifactually favor a
conventional theory; (2) a conventional theory that really works should not
need such a crutch; and (3) in the case of OPEs, confirmation of a paranormal
theory would not logically require abandonment of any conventional theory but
simply a redefinition of its boundaries. My own position is that standards of
evidence should be uniform (and rigorous) throughout science. However, this
issue is not, strictly speaking, relevant to the present review since
paranormal and conventional theories are not being contrasted; for the most
part conventional hypotheses are being examined in isolation.
The history of parapsychological criticism clearly shows that it is easy
to devise ad hoc conventional explanations of the OPEs that appear in
laboratory experiments. However, a possible explanation is not the same as a
scientifically adequate explanation. But how is it possible in practice to
assess the scientific adequacy of conventional explanations of the results of
particular psi experiments?
I will propose the following three guidelines:
(1) Internal empirical evidence within the experiment itself. Sometimes
the conventional hypothesis leads to predictions that can be tested by new
analyses of the data from the experiment under consideration.
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(2) Empirical support for the hypothesis in related contexts. This might
include confirmation of the hypothesis in related experiments or experiments
explicitly designed to test the hypothesis.
(3) Plausibility. This is a hard term to define and is admittedly
subjective. In a nutshell, it is simply a commonsense judgment of the
likelihood that a conventional process would take place. It might include such
things as the difficulty or complexity of the process, the apparent motivation
of a subject to undertake it (as in the case of fraud), etc.
Perhaps the best summary guideline might be the following: Would we be
willing to accept a particular conventional hypothesis if the experiment were
an "ordinary" one and the controversial question of paranormality were not
involved? Often there is a temptation to accept a conventional hypothesis
simply because the alternative (paranormality) is seen as intolerable. The
preceding question helps us to avoid this temptation.
General Approach
In the remainder of this report, I will explore the question of whether
experimental data exist which can be properly classified as anomalous, data
for which the available conventional explanations are inadequate (even if
possible) and the possibility of paranormal causes must, therefore, be
seriously considered. A great deal of research relevant to this question has
been published in parapsychological journals over the last century. Two
approaches can be taken to reviewing this material. The first is to provide
an overview of the entire literature, and the second is to provide a more
in-depth review of the most potentially evidential subsections of this
literature. I have chosen the second approach for two reasons. Although the
first approach can serve useful functions, particularly for those sympathetic
to the concept of paranormality who are looking for promising hypotheses for
process-oriented research
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analysis of specific research programs is simply not possible within the
framework of a broadly based review. My second, more pragmatic reason for
choosing the second approach is that I and others have already written
relatively current reviews of the first type (see Krippner, 1977, 1978, 1982,
1984; Wolman, 1977).
Commitment to the second approach raises the question of which research
programs should be selected for review. For the most part, I have avoided
trying to apply some objective formula but have relied instead upon my own
professional judgment, based on 15 years of experience in the field of
parapsychology, in making my selections. Nonetheless, there are certain
general principles which guided my thinking. These include the following:
(1) The research must represent an integrated body of experiments using a
similar methodology. "One-shot" studies, however impressive, were not
considered unless they could be related to similar studies by other
investigators.
(2) On the surface, the research program must have yielded statistically
significant results with at least moderate consistency.
(3) The research program must be considered important and evidential by a
significant proportion of contemporary parapsychologists and, preferably,
achieved sufficient notoriety to evoke responses by outside critics. (An
exception was made on this point for the research on metal bending. Even
though this research is not highly regarded by most parapsychologists, it
represents an important new research direction with potentially far-reaching
implications.)
I have chosen to evaluate eight classes of parapsychological research
programs which have been conducted since 1970. Each of the following chapters
(2-9) is devoted to one of these classes, and several of the chapters review
more than one program. Eight major research programs conducted by a
particular parapsychological investigator or research team are reviewed. The
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conducted are as follows: John Bisaha and Brenda Dunne (Mundelein College);
Charles Crussard (Pechiney-Ugine-Kuhlmann Aluminum Company, Paris); John
Hasted (University of London); Robert Jahn (Princeton University);
B. K. Kanthamani and Edward Kelly (Institute for Parapsychology, Durham, NC);
Harold Puthoff and Russell Targ (SRI International); Rex Stanford (St. John's
University);
and Montague Ullman and Stanley Krippner (Maimonides Medical
Center). In addition to the above, two chapters (4 and 7) are devoted to
groups of experiments on common themes conducted by a wider range of
investigators. Summaries of each of these chapters are presented in Chapter
10.
The reader may find it helpful to peruse the summary of a given chapter
before turning to the chapter itself.
Each of the chapters 2 through 9 is organized in more or less the
following manner:
(1) A description of the methodology employed in the experiments;
(2) A description of the results obtained and their interpretation by the
investigators;
(3) A description of published criticisms of the research;
(4) My own evaluation of the research and the criticisms.
A few additional comments on the last component are in order at this
point. First, the reader has a right to know something about my own
background and involvement with the field of parapsychology. My training is
as an experimental psychologist, with my specialty in the area of
personality/social psychology. As noted previously, I have been involved in
parapsychological research for 15 years, and I thus could be considered an
"insider." Parapsychologists are an extraordinarily close-knit group, and I am
thus on a first-name basis with the great majority of the parapsychologists
(as well as several of the critics) whose work I will be reviewing. I do not
feel that this fact has compromised by objectivity, and in at least two cases
I have introduced novel criticisms of research conducted by investigators whom
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My involvement in the field has obviously conditioned the attitudes I
have brought to this task. On this score, I view myself, and I think I am
viewed by most of my colleagues, as a moderate. On the one hand, I would not
have remained in parapsychology this long if I did not feel that there was
"something to it," that the field is potentially very important. On the other
hand, I am impressed with how little we know about the causes which underlie
the effects we study in parapsychology, and I tend to react negatively to
"extremists" on both sides who make claims or draw conclusions that in my
opinion outstrip the evidence.
Given the above, the reader should not be surprised to discover that I
will not be drawing definitive conclusions about the evidence reviewed in this
report. How one evaluates the evidence inevitably comes down to the
plausibility one attaches to the "normal" explanations which can be attached,
just as inevitably, to any piece of psi research. The question the reader
must constantly ask himself or herself in the following pages is how far the
researchers have succeeded in pushing these "normal" explanations in the
direction of absurdity. These judgments will inevitably involve a subjective
component, and reasonable people can be expected to differ in the judgments
they make. The best I can do as a reviewer is to point out what the known
"normal" explanations are and what must be taken into account in assessing
their plausibility. Although I feel responsibility as a reviewer to express
my own opinions about their plausibility, I also encourage readers to feel
free to draw their own conclusions.
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Chapter 2
THE MAIMONIDES DREAM EXPERIMENTS
The first major ESP research project in the modern era to use
free-response methodology was a series of experiments conducted at
Maimonides Medical Center in Brooklyn, New York, exploring telepathy in
dreams. The principal investigators were psychiatrist Montague Ullman and
psychologist Stanley Krippner, with major contributions also being made by
Charles Honorton.
The basic method was to have an agent attempt to influence the dreams
of a percipient by concentrating on a randomly selected art print. Later
the percipient(s) and/or outside judges would attempt to match up the
targets for the series with the dream protocols on a blind basis, using
standard methodologies for judging free-response ESP materials. Generally,
only one trial was collected per night.
The Maimonides experiments can be divided into three categories:
(1) Formal Experiments: One Trial per Subject. This category includes two
screening experiments in each of which twelve paid volunteers participated
as subjects (Ullman, Krippner, & Feldstein, 1969; Ullman & Krippner, 1970).
I have also included in this category one other experiment in which
selection criteria were somewhat more rigid, i.e., subjects were to have
reported spontaneous telepathic experiences or to be acquainted with the
agent (Krippner, Honorton, Ullman, Masters, & Houston, 1971).
(2) Formal Experiments:
Multiple Trials per Subject. In these experiments,
subjects selected either on the basis of promising results in the screening
experiments or because for other reasons they were expected to perform well
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in this type of task participated in four to eight sessions each. Two

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William Erwin, was the subject in two experiments consisting of seven and
eight trials, respectively (Ullman et al., 1969; Ullman & Krippner, 1970),
and a secretary, Theresa Grayeb, who completed one eight-session experiment
(Ullman & Krippner, 1970). One graduate from the second screening
experiment, a psychologist named Robyn Posin, completed an eight-session
experiment (Ullman & Krippner, 1970). The remaining subjects, who had not .
participated in the screenings, were psychologist and parapsychologist
Robert Van de Castle and a psychic named Malcolm Bessent. Van de Castle was
the subject for one eight-night series (Krippner & Ullman, 1970). Bessent
was the subject for two eight-night series using a precognition procedure
(Krippner, Ullman, & Honorton, 1971; Krippner, Honorton, & Ullman, 1972),
and one four-trial telepathy series in which the agents were the audience of
a rock concert (Krippner, Honorton, & Ullman, 1973). Another psychic,
Felicia Parise, served as a control percipient in this experiment; i.e.,
the audience was unaware of her involvement. This group of experiments was"
obviously the most important in the project because it was restricted to
subjects who were expected to succeed.
(3) Informal Pilot Sessions. Several hundred pilot sessions were conducted
during the course of the research project and reported in unpublished
manuscripts. The methodology was the same as that of the formal experiments
with respect to basic controls.
Methodology
Targets and Target Selection.
The targets for the Maimonides
experiments were usually postcard-sized prints of famous paintings selected
for simplicity and distinctiveness of detail and, in later series, emotional
evocativeness. Also in later series, the prints (or slides) were
supplemented with multi-sensory materials to increase the salience of the
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tartets.
These varied from tov obiects in the second Erwin experiment to
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Maimonides Dream Experiments
Page 24
appropriate recorded music in one of the group experiments. This latter
experiment will subsequently be labeled as the "sensory bombardment"
experiment (Krippner, et al., 1971).
Sets of targets were assembled for each experiment, each set generally
equal to the number of trials in the experiment. The prints in each set
were selected to be maximally diverse in content. In the early experiments
the target pools were selected by the agent and experimenter but later on
this task was performed by a third party not involved with the actual
conduct of the sessions.
The agent selected the target (without replacement) from the prints
remaining in the pool. Procedures varied somewhat from experiment to
experiment, but in all cases except possibly one (Krippner, et al., 1973)
the target was determined by a digit from a random number table, the
designation of the digit in turn being determined by a complex quasi-random
procedure. Some of these selection methods are problematic and will be
discussed further in the evaluation section.
Test Procedure. Again, the procedures for the test sessions varied
slightly from experiment to experiment, but the following account is
representative.
When the percipient arrived for the session, he or she was allowed to
meet with the agent to establish rapport. The agent was a member of the lab
staff and in some studies the percipient was given some choice in
determining the agent for a given session. The percipient then got ready
for bed and electrodes which measure EEG and eye movements were applied.
During the course of the night the pattern of brainwaves and eye movements
were monitored by the experimenter, located in an adjacent room, to
determine those times at which the percipient was likely to be having a
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mentation).
These
norinds are called "-a
"rapid eve movement" or REM Derinds and near about three
Samt about
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to six times per night.
Once the subject was in bed, the agent went to a room at the other end
of the building and selected the target picture. Periodically during the
night the agent attempted to "send" the contents of the target to the
percipient. In later studies, the experimenter signaled the agent by a
buzzer, indicating the onset of a REM period, so that the sending could be
yoked to the percipient's dreams. Toward the estimated end of each REM
period, the experimenter awakened the subject and elicited a dream report,
which was taped.
In the morning, the experimenter played back the tapes of the dream
reports and asked the percipient to add any associations he or she might
have had to the dream mentation and to venture a guess as to the identity of
the target. These associations were also taped. Collectively, this
material constituted the dream protocol for the session.
The intercom set-up allowed no communication from the agent's room to
either the percipient's room or the experimenter's room. The agent had no
contact with the percipient until after the session and percipient judging
(if this was done) was finished.
The possibility of sensory cues was further minimized in the two
precognition experiments with Bessent. In these experiments the "agent"
selected the target for the night and displayed it to the percipient in the
morning after the dream protocol had been completed.
Judging.
In most cases judging was undertaken both by the subject and
by outside judges (usually three) who worked independently of each other.
(In several cases, one or more other judges conducted supplementary
judgings. ) At the end of an experiment, which consisted of from four to
twelve sessions, each judge was asked to rate each possible
target-transcript pair on a 100-point scale indicating confidence in it
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rankings. Judges also evaluated the dream protocols both with and without
the morning-after associations. In some cases, ratings were also based on
the subject's "guess for the night," an assessment based upon his dream
reports and associations.
Most of the reports contain no information about the order in which the
targets and protocols were given to the judges. However, in three of the
experiments (the second Erwin experiment and the two precognition
experiments) rankings were not used and the judges were asked to rate all
possible target-protocol pairs in random order.
In the experiments in which subjects completed only one trial, the
subject ranked and rated his or her protocol against each of the potential
targets in the experiment at the end of the session. This only applied to
the screening sessions. In the experiments with multiple trials per
subject, the subject performed the same judging task as the independent
judges after all sessions had been completed. However, subject judging was
not used in the "sensory bombardment" experiment, the second Erwin
experiment, or the precognition experiments.
Judging by both subjects and independent judges was always done blind
and duplicate target sets were always used; i.e., the print handled by the
agent was never included in the judging material.
Statistical Analysis. A variety of methods of analysis were employed
.. . ........ .
and multiple methods were frequently used in the same experiment. Regarding
the ranks, hits were defined either as a rank of one (direct hit) or, more
commonly, as a rank in the lower half of possible ranks (binary hit).
Significance was then determined by a simple binomial or exact probability
test .
Ratings were evaluated by comparing the mean rating (averaged over
the outside judges) assigned to the correct target-transcript pairs to the
mean rating assigned to the incorrect pairs using one of a variety of
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methods varying from Scheffe analysis of variance (Scheffé, 1959, Ch. 10)
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to a latin square ANOVA to a Mann-Whitney U test.
In summary, the analysis options were distributed along the following
three dimensions:
1) Independent judging and subject judging;
2) Dream protocols with and without morning-after associations,
and "guess for the night;"
3) Rankings and ratings.
Thus, several tests of the hypotheses were customarily included in the
reports.
·
Results
It is sometimes but by no means always clear which analysis or analyses
had been designated in advance to be the primary test of the hypothesis.
Fortunately, in most cases the analyses converged on a common conclusion.
Formal Experiments: One Trial per Subject. The two screening
experiments both yielded nonsignificant results. However, in the first
screening experiment, post-hoc analysis revealed that the results of those
subjects tested when the male research assistant served as agent and the
female as experimenter were significantly positive and significantly better
than those when the roles were reversed. Results from the Krippner et
al. (1971) study were significantly positive for independent judging but not
for subject judging.
Combined, these three experiments produced 21 binary hits from 32
trials (66%) based on the rankings (or converted ratings) of the independent
judges as applied to the total transcripts (dreams plus associations). This.
is associated with a corrected Z (Z ) of 1.59, which is not significant.
Formal Experiments: Multiple Trials per Subject. The two experiments
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with Erwin, the one with Van de Castle, and the three with Bessent all
1.
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Maimonide's Dream Experiments
yielded significant positive results. The single experiment with Grayeb and
the single experiment with Posin yielded chance results. The results of
Parise, the control subject in one of the Bessent experiments, were also
close to chance.
Combined, these experiments produced 49 binary hits from 67 trials
(73%) based on the rankings (or converted ratings) of the independent
judges. This is associated with a 2 of 3.67, which is significant at
P <. 001.1 (The Parise results are included since it can be argued that
agents" focus of attention on the percipient may not be necessary for psi to
occur in this paradigm.)
Pilot Experiments. Of the 280 pilot trials evaluated by independent
judges, 165 were binary hits (59%). This is a smaller percentage than was
found with the other single-trial-per-subject experiments, but due to the
larger sample size it is significant (Z=2.99, p <. 01).
The probability values reported above do not take into account the
multiple analyses employed by the authors or possible dependencies in the
judgings and thus should be considered approximate. Additional analyses
will be presented in the evaluation section. Nonetheless, these analyses,
along with the fact that seven of the eleven formal experiments were
significant (six of eight with selected subjects), suggests that, taken at
face value, the research project as a whole yielded results exceeding chance
expectancy.
Wyoming Replications
Single replications of two of the successful Maimonides experiments,
the Van de Castle experiment and the "sensory bombardment" experiment, were
undertaken by dream researcher David Foulkes and colleagues at the
University of Wyoming (Belvedere
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Van de Castle served as the subject in the first replication, and subjects
in the second replication were selected on the basis of the same criteria
(spontaneous telepathic experiences and rapport with the agent) as in the
original experiment. In the sensory bombardment replication, a main
difference was that, in contrast to the original experiment, the agent (in
New York) was several thousand miles away from the percipient (in Wyoming).
However, since distance does not appear to be a critical limitation to ESP,
this modification was considered acceptable by all parties concerned.
The experimental procedures of the replications closely followed those
of the original studies. The most notable differences were that the targets
for each night were selected by an additional experimenter in the Wyoming
V
experiments whereas they had been selected by the agent in the Maimonides
experiments. Also, the agent could not leave his or her room in the Wyoming
replication of the Van de Castle study .. (The door and windows were sealed
shut. ) Such elaborate precautions were not taken in the Maimonides
experiment.
Judging was performed by both the subject and two independent judges in
the Van de Castle replication and by three independent judges in the
"sensory bombardment" replication. Only rankings were used. The results
were nonsignificant for both experiments.
Criticisms
The most extensive criticism of the Maimonides experiments has been
offered by the British psychologist C.E.M. Hansel (1980) who for many years
has been the most prolific critic of major psi experiments. His critique of
the Maimonides experiments dwelled exclusively on the possibility of sensory
leakage in the Van de Castle experiment, which he compared unfavorably to
the replication attempt by Foulkes in this respect. His main specific point
was that in the experimental report which he used, the description of the
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method implies that an experimenter appears to have been with the agent
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when he opened his target envelope" (p. 246). This of course would mean
that the experimenter, who elicited the dream reports from the subject, was
not blind to the target.
Another criticism, made primarily by psychologist James Alcock (1981),
is that there was no control judging to provide an empirical baseline. This
would require that the targets in the control judging be assigned in a
random order. He acknowledged that the Maimonides team did perform such a
control judging for one of the successful experiments (the second Erwin
experiment) but he considered this inadequate.
Psychologists Leonard Zusne and Warren Jones (1982) suggested that in
some of the experiments the percipient was shown the target prior to
collection of the dream reports. This is a misunderstanding of the
procedure which perhaps reflects the fact that they used as their source a
brief description of the second Bessent precognition experiment. which
appeared in a popular book (Ullman & Krippner, 1978). In this particular
experiment, sessions designed to test for precognition were alternated with
other sessions designed to determine whether the experience of observing the
precognition target for the night before would affect dream mentation during
the night following. This brief description of the procedure apparently
left Zusne and Jones with the impression that these latter sessions were
meant to be the precognition sessions.
Finally, psychologist Irvin Child (in press) pointed out that in most
of the series in which a subject completed multiple trials it cannot be
assumed that the judgings were independent as required by the statistical
tests
employed. Although judges were instructed to assess the trials
independently, it cannot be assumed that this independence was achieved in
practice. The only experiment of this type to which this criticism is'
inapplicable is the Van de Castle experiment where a separate target pool
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1
Child, however, attempted to show that this criticism is not fatal by
demonstrating that the results of judgings to which the criticism does not
apply (including some judgings in the single-trial-per-subject experiments
and all judgings from the pilot sessions) were collectively significant.
This was accomplished by taking the most sensitive analysis available from
the reports, converting the result to a Z, and combining the Zs by the
Stouffer method (Mosteller & Bush, 1954). The resulting p-values were less
than .002 for subject judging and less than 10-6
for independent judging.
Evaluation
.
Statistical Independence
Child's criticism of the statistical methods employed by the Maimonides
researchers is appropriate. Moreover, he is right in recognizing that a
uniform definition of the dependent variable must be decided upon if the
significance of the Maimonides studies collectively is to be determined.
Although Child's own analysis, described above, is sound, it has the
disadvantage of not including all the studies in the data base. An
alternate approach can be taken by recalculating the delinquent Zs using an
error term that assumes "worst-case" dependence of judgings. I decided to
undertake such an analysis, which thus included all the formal series. I
also decided to use a uniform method of scoring (ranks) rather than the most
sensitive method given in the report.
My statistical consultant developed a revised Z formula as follows:
Z=(T-N(N+1)/2[±.5])/(N2(N+1)/12).5
where T is the sum of ranks assigned to the target and N is the total number
of trials. As the number of trials in these studies varies from 7 to 12,
the assumption of normality is unlikely to be grossly violated, although
marginal outcomes should be interpreted cautiously.
Separate analyses were performed for subject judging and independent
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means of the judges" ranks were introduced into the equation, a slightly
conservative procedure. In the later studies, which employed ratings, the
sums
of the ratings of the multiple judges were converted to ranks for the
analysis. Finally, in a handful of cases the only information available was
whether the target was a hit or a miss, i.e., above or below the theoretical
median rank. In these cases, all hits were assigned the theoretical median
of the possible "hit" ranks and the misses the theoretical median of the
possible "miss" ranks. (E.g., in an eight-trial series, the hits would all
be assigned a rank of 2.5 and the misses 6.5.) This procedure is also
conservative.
The Zs computed by the above methods are presented in"Table 1. When
these Zs are combined by the Stouffer method over all 11 studies, the
cumulative Z for independent judging was 5.41. The corresponding Z for
subject judging, cumulated over the eight studies which employed subject
judging, was 3.09, p <. 005. Thus, even when one includes the screening
studies, the cumulative results of the formal Maimonides dream experiments
are clearly significant statistically. As Child's analysis indicates, the
pilot sessions (not included in my analysis) do not detract from this trend.
Given that the collective outcome of the Maimonides experiments cannot
be attributed to chance, what can be said about the likelihood of these
results being attributable to nonparanormal factors?
Sensory Leakage
The most serious allegation here is Hansel's contention that the
experimenter in the Van de Castle study appears to have been present with
the agent when the latter opened the target envelope. The following is the
paragraph.upon which Hansel based this inference. I have underscored those
phrases which Hansel himself emphasized in his critique and which led him to
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Table 1
Z STATISTICS OF RANKS CORRECTED (WHEN NECESSARY)
FOR POSSIBLE DEPENDENCE OF JUDGINGS*
Zs
Indep. Js
Subj Js
I.
Single Trial per Subject
A.
Screening I
0.62
1.24
B. Screening II
-0.21
1.08
c.
Sensory Bombardment
3.25
0.00
II.
Multiple Trials per Subject
A. Erwin I
-
1.64
1.05
B. Erwin II
3.54
c .. Grayeb
-0.51
0.51
D.
Posin
1.08
1.08
E.
Van de Castle
2.61
2.86
F.
Bessent. I
2.53
G.
Bessent II
2.96
H.
Rock Concert
0.44
0.92
TOTAL (Stouffer Z)
5.41
3.09
*
Underscoring means that judgings were truly independent and the uncorrected
sum-of-ranks Z formula was applied.
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Upon arriving in his room, A opened the envelope containing the target
picture. He was encouraged to write down his associations, to visualize the
picture, to concentrate upon it, and to treat. it in any other manner which
would make its contents a dynamic part of his conscious processes. Once
this was done, there was no way the A could communicate with E or with S
without leaving his room and breaching the conditions of the experiment.
(Ullman & Krippner, 1970; pp. 99-100).
First of all, nowhere is it stated that E accompanied A to his
room. "He was encouraged" could be taken to imply this, but it could also be
read as implying that the "encouragement" had been part of the general
instructions given to A before the experiment began. "Once this was done"
could be taken to mean, as Hansel believes, that only after the target had
been opened (in E's presence) was A to E communication impossible, but, if
the more generous interpretation of the preceding phrase is correct, it
could mean that as soon as A entered the room such communication was
impossible.
There is no question that the paragraph is ambiguous and poorly worded.
However, by no stretch of the imagination is the implication that E
accompanied A to his room clear enough to justify Hansel all but concluding
that this is what happened. Further, certain aspects of the procedure seem
to argue against Hansel's interpretation. Doesn't it seem odd, for example,
that E would need to remind A before each trial how to do the sending?
Fortunately, the procedure is stated more clearly in one of the other
reports of the experiment, where it is affirmed that the experimenter only
stayed with the agent until the latter went to his room to open the target
envelope (Ullman & Krippner, 1968).
The other possibility alluded to by Hansel concerns cheating on the
part of one or more of the participants. The unsuccessful Foulkes
experiment with Van de Castle was indeed somewhat more secure in this regard
than the Maimonides experiments. In particular, the latter, unlike the
former, did not preclude the possibility that the agent might leave his or
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Maimonides, Dream Experiments
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target to the percipient without the experimenter knowing it. Indeed, the
reports of the first screening and first Erwin experiments refer to the
agent occasionally relieving the experimenter during the night, although
never talking to the subject. However, there is no evidence that an agent
ever compromised a session and several agents would have to be implicated if
all the significant Maimonides experiments are to be accounted for as fraud.
Since the agents in all the Maimonides experiments were lab staff, this
specific criticism falls into the category of experimenter fraud, which can
be offered as a possible alternative explanation of all the experiments
considered in this review.
However, the fact remains that two experiments with different outcomes
(i.e., both the Maimonides and the Wyoming experiments with Van de Castle)
did differ procedurally in terms of the opportunities they provided for
fraud by the agent. However, they differed in other respects as well. Van
de Castle (1977) notes, for example, that he was disturbed by the skepticism
of the Wyoming team and that this created a bad psychological climate for
the Wyoming experiment. The Wyoming investigators' indeed reported evidence
of negative feelings toward the experimenters in Van de Castle's dreams
during the experiment. Critics often complain bitterly that
parapsychologists use this kind of argument as an alibi to explain away
failures after the fact. It certainly would be premature to conclude that
Van de Castle's explanation is the correct one, but the fact remains that
the psychological state of the subject differed in the two experiments and
that this was as real a difference as the procedural differences stressed by
Hansel. Also, if a "psi" process does exist, it is not unreasonable to
suppose that it is influenced by the psychological state of the percipient.
Other differences, such as a higher concentration of sessions in the Wyoming
experiments, could also have been factors. In short, as long as multiple
differences in conditions exist, one cannot confidently attribute
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by other internal evidence in the data.
Lack of Baseline Judgings
The artifact which baseline judgings are supposed to control for, as is
clear from reading Alcock's (1981) critique, is the possibility that a
target-dream correspondence will be considered evidential because of chance
correspondences or because the dream protocols contain highly general
statements which could apply to many pictures. The Maimonides judging and
analysis procedures in fact control for this artifact because the rank or
rating the dream protocol receives depends on how closely it corresponds to
the target picture relative to how well it corresponds to the other pictures
in the judging pool or set. To put this another way, the mean ratings or
rankings assigned to the incorrect pairings serve as the baseline against
which ratings and rankings assigned to the correct pairings are assessed.
Another way to address this issue is to ask what the interpretation
would be if control judgings in which the correct pairings were assigned
randomly or arbitrarily consistently yielded significant results. Such an
outcome would be every bit as anomalous as that of the real Maimonides
experiments and would fit many definitions of psi, including the one used
for this review. If the outcome, on the other hand, were nonsignificant,
its deviation from the theoretical "chance" value is properly construed as
error and thus should not be incorporated into the baseline estimate.
In
other words, for this type of research problem, the best external baseline
is the theoretical estimate built into the Maimonides procedure.
Many psi experiments other than the Maimonides dream experiments
compare obtained results to theoretically defined baselines. The same basic
arguments apply in those cases. For a further discussion, see
Palmer (1982).
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Randomization
A potential source of bias not addressed by previous reviewers of the
Maimonides experiments is the inadequacy of the randomization procedure used
to select targets in some of the experiments. For example, in the second
Erwin experiment, a random digit was used to select which of the ten art
prints in the pool would be the target for the first trial. The same
procedure was used for subsequent trials, except that if the random digit
exceeded the number of prints remaining in the pool, the selector would go
back to the first print and continue counting until the random number was
reached. A moment's reflection will reveal that this procedure does not
lead to each print having an equal opportunity of being selected for each
trial. For example, for the second trial, selection of a random digit "1"
or "0" ("0" being equivalent to "10") leads to the first print being
selected, whereas each of the remaining prints are associated with only one
digit; i.e., the first print has twice as much chance of being selected for
this trial as any of the others. A proper procedure would have been to
select a new random digit each time a digit exceeded the number of prints in
the pool.
To determine the extent of the bias, I performed a computer simulation
of the above selection procedure. The random numbers were determined by a
random event generator, and 1000 mock "experiments" were run, each
consisting of eight trials with an initial pool of ten prints as in the
second Erwin experiment.
The resulting matrix is reproduced as Table 2. The figures inside the
table refer to the number of times each print was selected for each trial.
Eight chi-squares were also computed, one for each trial, to indicate the
extent to which the distribution of selections for that trial departed from
the ideal of each print being selected an equal number of times.
The chi-square for the first trial was not significant. This is to be

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Table 2
RESULTS OF COMPUTER SIMULATION
TESTING FOR BIASED TARGET SELECTION
TRIAL
1
2
3
4
5
6
7
.
8
-
A
82
205
142
101
91
78
96
79
B
97
90
150
144
113
83
97
96
T
H
C
91
101
145
121
119
86
87
109
A
D
102
.84
86
135
98
83
111
105
E
87
84
83
120
126
101
108
98
R
F
108
87
95
88
111
96
108
101
G
G
102
92
72
79
111
106
101
109
E
H
115
84
75
69
104
103
81
109
T
I
116
85
72
71
65
125
112
104
J
100
88
80
72
62
139
99
90
,2
X
11.36
124.96
93.92
71.74
42.18
34.66
9.50
8.46
Numbers indicate the number of times in 1000 "experiments" that target
was selected for that trial; underscored numbers show the maximum fre-
quency for the target
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the chi-squares for Trials 2 through 6 are highly significant (p <. 001). The
bias is strongest in Trial 2 and steadily declines until by Trial 7 it is no
longer detectable for the sample size employed.
-.
-
..
!
The most important feature of the bias is that within Trials 2 through
6 there is a tendency for earlier members of the target pool to be favored
on the earlier trials and later members on the later trials. This can be
seen by observing in Table 2 for which trial (in the range of Trials 2
through 6) each print receives its maximum number of selections. These
figures are underscored in the table and form a virtual diagonal from the
upper left to lower right. For instance, Print A receives its maximum
number of selections on Trial 2, whereas Print J receives its maximum number
of selections on Trial 6.
This bias is serious to the extent that the judge has a tendency to
assign early targets in the pool to early trials, either as a natural
tendency or because of knowledge that such a bias exists in the
randomization procedure. Fortunately, in the second Erwin experiment the
judges were all asked to evaluate the possible target-transcript pairings in
random order. If this means that they had no knowledge of the original
ordering of the targets (i.e., the order of the envelopes before the first
trial), then the bias can be considered irrelevant, unless one entertains
the rather implausible assumption that the order of the subject's dreams was
somehow naturally correlated with the order of the targets in the pool.
Even if the judges did know the target order, the fact that they judged the
pairs in random order might tend to neutralize any natural judging biases
toward selecting one of the first targets seen for early trials, and so on.
Randomization of targets given to the judges was not discussed in the
reports of the first Erwin experiment. However, Krippner (personal
communication) claims that in all the experiments targets were given to each
·
judge in a different random order. How this randomization was accomplished
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The biased selection procedure poses a slightly different problem in
the Van de Castle study than in the Erwin studies, because a separate target
pool was used for each trial.
Since each pool contained eight prints, this
meant that for each trial the first two members of the pool had twice as
great a chance of being selected as the others. Precise details of how the
pools were constructed were not given in the report, but if there had been
any tendency to put the "best" art prints early in the pool -- an unverified
but not implausible assumption -- an effective bias could have resulted.
It is not clear what target selection procedure was used in the
"sensory bombardment" experiment. If the faulty method was used, the bias
would be comparable to that which applies to the Van de Castle experiment,
since there again a single target pool was used for each trial. It also is
not reported what randomization procedure was used in the replications of
the Van de Castle and "sensory bombardment" experiments conducted by the
Wyoming team. Finally, it should be noted that the faulty target selection
procedure was not used in the two successful precognition experiments with
Bessent. The procedures used in the second of these experiments, although
complicated, seem adequate.
Another form of biased target selection occurred in the first of the
precognition studies with Bessent (Krippner et al., 1971), however. In this
experiment, a word was randomly selected from a dictionary of common dream
themes and one of the experimenters created a multi-sensory experience (like
a mini-drama) which Bessent experienced the morning after the test night.
It thus served as the precognitive target. Descriptions of these
experiences were given to the judges for matching with the dream
transcripts.
!
The problem with this procedure is that even though the topic was
selected randomly, the actual material in the description was not.
For
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about Bessent's activities or thoughts during the previous day, or by
newsworthy happenings that day totally unrelated to Bessent. If such
activities or events had come to be reflected in Bessent's dreams,
artifactual correspondences could have been produced.
None of the biases discussed in this section seem particularly likely
as explanations even of the experiments to which they apply, because they
require the acceptance of rather implausible ad hoc assumptions.
Nonetheless, they must be treated as possible explanations of the results.
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NOTE
1
Unless noted otherwise, p-values cited in this report are two-tailed. In
general, I have cited the p-value given by the authors when referring to
tests they computed. I have generally cited two-tailed probabilities for my
own analyses. Z-scores which exceed 4.0 are generally considered
sufficiently astronomical to not require the citation of the exact p-value
alongside them.
.....
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Chapter 3
REMOTE VIEWING
A great deal of public attention has accrued to experiments using a
free-response ESP procedure called "remote viewing (RV)." The main
distinguishing characteristic of this procedure is that the targets tend to
be "real" objects or geographical sites as opposed to photographs, slides,
etc. However, it is also likely that the term was adopted to avoid the
"occult" connotations which, despite the efforts and wishes of conservatives
like Rhine, have become attached to the term "ESP."
The remote viewing procedure is most closely identified with two
physicists, Harold Puthoff and Russell Targ, who at the time of their
.
initial RV experiments were both employed at SRI International in
California. This background and affiliation is part of the reason that
their research has attained such notoriety in scientific circles.
I will begin by critically reviewing the primary RV experiments of
Puthoff and Targ and the controversy about these experiments initiated by
psychologists David Marks and Richard Kammann. I will then critically
discuss the major replication attempts by Bisaha and Dunne, Schlitz and
Gruber, Karnes, and Marks and Kammann. I will not consider various minor
experiments, especially those using the "group remote viewing" procedure in
which multiple subjects attempt to reproduce a single target.
Puthoff and Targ Experiments
The experiments to be considered used a total of nine subjects, three
of whom were labeled as "experienced" (i.e., having participated and
succeeded in previous psi experiments), three as "learners" and three as
"visitors." The most extensive testing and the most successful (and
controversial) results were associated with a former police commissioner
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named Pat Price and a professional photographer named Hella Hammid
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Remote Viewing
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(Puthoff & Targ, 1979).
Main
Series
A pool of over 100 target locations within a short driving distance
from SRI was assembled by a person not otherwise involved with the
experiments. This person randomly selected one location from this pool to
be the target for each trial. The method of randomization was not specified
nor is it clear whether targets were placed back in the pool after they had
been used (i.e., sampling with replacement).
For each trial, a group of two to four "outbound experimenters"
ascertained the target location and drove to it. They then observed the
location for 15 minutes, during which time the subject (who was located at
SRI with the "inbound experimenter") attempted to receive impressions of the
site. These impressions were recorded on tape and the subject also drew
sketches of the presumed target. The inbound experimenter, who was himself
blind to the target location as well as to the contents of the pool, asked
the subject questions in an effort to achieve further clarification and
elaboration of the impressions. Following the trial, the subject was taken
to the site for feedback.
The total of 39 trials was divided into five groups of five to nine
trials, each group consisting of the attempts of one or two subjects.
For
each trial, an unedited transcript of the subject's tape-recorded
impressions was attached to the subject's sketches. (Hereafter, the term
"transcript" will be defined as including these sketches.) The transcripts
for each group of trials were assembled and given to one outside judge who
was asked to visit each of the target sites for that group and rank the
transcripts in the order of the degree of perceived correspondence to the
site. The ranks assigned to the correct transcripts for all trials in the
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group were then summed and the sum was evaluated for statistical

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Morris (1972).
Results. Four of the five groups of trials yielded one-tailed
probabilities of less than .05 in the psi-hitting direction. The most
significant groups were the nine trials of Price (p = 2.9x10->) and the nine
trials of Hammid (p = 1.8x10-6).
*
Technology Series
The target pool for this series, which was designed to assess the
resolution capacity of RV, consisted of seven pieces of equipment: drill
press, photocopy machine, video terminal, chart recorder, random event
generator, machine shop, and typewriter. It was specified that sampling
from the pool occurred with replacement. Otherwise, the randomization
procedure was the same as in the geographical series. The test and judging
procedures were also the same as those previously employed, except that only
the subjects" sketches were used for judging.
Twelve trials were completed by five subjects, all but one of whom had
participated in the geographical series. Multiple responses to a given
target were combined for judging, thereby reducing the number of trials for
judging from twelve to seven. The sum of ranks given to the correct targets
was again evaluated for significance by Morris" tables.
Results. The total sum of ranks was 18 (p <. 05, one-tailed) in the psi
hitting direction.
The Marks-Kammann Critique
Sensory Cues. In their book Psychology of the Psychic, Marks and
Kammann (1980) leveled a harsh critique at the Puthoff-Targ RV experiments.
Their most important argument concerned the availability to judges of
sensory cues from the unedited transcripts of the subjects" impressions.
Marks and Kammann were able to gain access to the raw records of the Price
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and Hammid series. In each case they noticed that the transcripts contained

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i
information that could help the judge match them correctly to the target
list, provided (in most cases) that the target list was not randomized, thus
allowing the judge knowledge of the correct target order. For example, the
fourth transcript in the Price series contained the statement from the
inbound experimenter: "Nothing like having three successes behind you."
This statement could cue the judges that the trial was the fourth one in the
series, or that it certainly did not occur earlier than that.
Marks and Kammann then cited a letter written by the judge (who was
their source for both the raw data and the letter) to the effect that for
both the Price and Hammid series he had received the list of target
locations in the order that they had been used, i.e., unrandomized. The
lack of target randomization for the Price series was acknowledged by
Puthoff and Targ (1981) but was challenged both by them and by Morris (1980)
with respect to the Hammid series. Morris, who had requested and received a
copy of the judge's letter, noted that the judge explicitly stated that he
did not know whether the target list had been randomized or not and thus
decided to (re)randomize it himself. While observing that the experimenters
should have told the judge explicitly that the list had been randomized;
Morris concluded that the judge's letter refuted the assertion that Marks
and Kamman had made about the Hammid series.
In rebuttal, Marks (1981a) did not directly challenge Morris"
assertion. However, he did provide additional evidence in support of his
basic argument. The judge's letter revealed that in addition to the target
list itself, he had received two other sources of information about the
targets for the Hammid series. One of these was pages of notes each
containing information about the target site for that trial. He had
discovered after judging that the order of these pages correlated .83
(p <. 01) with the order of target usage. This "almost perfect" (p. 199)
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The other was a map of the area designating the target sites.
In a
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subsequent paper, Marks (1982) reported that a judge of his choosing was
able to use information provided by the map plus cues in the transcripts to
obtain a more significant score than the original judge on six transcripts
from the Hammid series. (For some reason, Marks was not permitted access to
the other three.)
With respect to the Price series (for which the availability of sensory
cues was conceded), Marks and Kammann (1980) sought to demonstrate
empirically that the cues could account for the significant results of this
series. First, eight judges were given a list of the targets in the correct
order, as well as a randomized set of transcripts containing only the
biasing statements from the corresponding real transcripts" On the basis of
this information alone, and without actually visiting the target sites, each
of the eight judges was able to match the targets and transcripts to a
highly significant degree. Thus, the cues indeed had the potential to bias
the judging.
However, the crucial point is whether the matching could be performed
successfully with the biasing cues removed. To determine this, two
additional judges, described only as "research psychologists" (p. 30), were
asked to rank the list of targets in random order against randomized
transcripts identical to the originals except that the biasing cues had been
removed.
These judges actually visited the sites. Since four of the trials
had been published and the judges might have seen the pertinent information,
this analysis was restricted to the remaining five trials. The matchings of
each judge were nonsignificant and close to chance expectation. The authors
thus concluded that " ... the successful identification of target sites by
judges is impossible unless multiple extraneous cues ... available in the
original unedited transcripts are utilized" (Marks & Kammann, 1978).
Charles Tart (Tart, Puthoff, & Targ, 1980) attempted to counter this
criticism by editing all nine transcripts, "removing all phrases suggested
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which even the most remote post hoc cue argument could be made," and having
them matched against the nine randomized target locations by "a new
independent qualified judge (having previously shown competence
in ... analysis of similar materials) who was unfamiliar with the Price
series." This judge achieved a high level of significance comparable to that
obtained in the original analysis.
..
Marks (1981b) objected that the transcripts had been edited by Tart,
who knew the correct matches and who could have been biased in his editing.
Second, he questioned whether it could be established that the "blind" judge
really lacked access to information about the four published trials.
Puthoff and Targ (1981) then countered by briefly describing a second
reanalysis for which the probability of a hit for each trial was adjusted to
account for the biasing effect of cues and the revised p-value remained
highly significant. I was unable to find details of this analysis either in
this report or in a supposedly more detailed paper referred to therein.
Marks and Kammann were unable to gain access to raw data from the other
RV series; thus, they had to resort to speculations about how possible
breaches of protocol (e.g., informal contacts between the experimenter and
the judges) could have biased the series even if cues had been removed
and/or the data sheets properly randomized.
Data Selection. The second major criticism in Psychology of the
Psychic referred to data selection. Although Puthoff and Targ claimed in
their popular book Mind Reach (Targ & Puthoff, 1977) that they had not
:
selected only their best results for publication, Marks and Kammann claimed
to find circumstantial evidence to the contrary. They noted, for example,
that in Mind . Reach Targ and Puthoff referred to "more than one hundred
experiments of [remote viewing]" (pp. 9-10) whereas only 55 had been
published,
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Concrete examples of indirect evidence that some trials were omitted were
provided in the case of the Hammid and technology series. These will be
discussed below.
Evaluation of the Marks-Kammann Critique
Sensory Cues. The biasing information uncovered by Marks and Kammann in
the unedited transcripts of the Price and Hammid series clearly render the
results of the original judging of these series invalid. Fortunately, the
experiments were designed in such a way that a proper rejudging could easily
be conducted. No such rejudging has been attempted for the Hammid series.
Two attempts were made for the Price series, one yielding significant
evidence of RV and the other yielding chance results. Unfortunately,
neither rejudging completely excluded the possibility of bias.
Two major problems beset the Marks and Kamman rejudging. First, by
eliminating the four published trials, they drastically reduced the power of
their statistical test, thereby making it more difficult to reject the null
hypothesis. Moreover, since the best matches tended to be the ones selected
for publication, those trials retained for analysis were not truly
representative of the whole data set. This problem is illustrated by the
results of Tart et al.'s rejudging; the p-value they obtained based on
judging all nine transcripts was 10"", whereas that based on just the five
transcripts selected by Marks and Kammann was only .025. Surely it would
have been possible for Marks and Kammann to find a judge or set of judges
for whom familiarity with the RV experiments could have been reasonably
excluded; in fact, the judges would not even have needed to be informed
that the transcripts pertained to an ESP experiment at all, and they could
have been asked afterwards if the material looked familiar.
A potentially more serious problem, however, involves the selection of
judges by Marks and Kammann. An obvious and important qualification for
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achieve correct matches.
Otherwise, they may give the task short shrift or
be less observant.
When the judges are selected by persons favorably
disposed to the experimental hypothesis, it is reasonable to assume that
this qualification is met. That is not the case when the person selecting
the judges is a skeptic. Under such circumstances the reader requires
additional assurances about the judge's motivation. Suspicion is
particularly justified in the present case because the judges were "research
psychologists," a population that is notoriously hostile to parapsychology.
The burden is on Marks and Kammann to provide the necessary assurances on
this point.
The two problems with the Tart rejudging noted by Marks and Kammann are
not as serious as those affecting their own rejudging, but they are
troublesome nonetheless. It is indeed possible that Tart, who knew the
correct matchings and was motivated to see the RV hypothesis confirmed,
might unwittingly have been biased to more readily excise statements from
the transcripts unrelated to the target than statements related to the
target, especially since a liberal exclusion rule was employed. (It is not
reported who edited the transcripts in the Marks and Kammann rejudging, so
this problem might apply in their case as well.) Second, further assurances
about the blindness of Tart's judge would be desirable.
Finally, some comments are in order about the extent of potential bias
in the original judging of the Hammid series. Here it seems that the main
target list was randomized, but questions were raised about the accompanying
information pages and the map of the area.
The close correspondence between the ordering of the information pages
and the order of target usage, although problematic, is not quite as
damaging as Marks and Kammann imply. While a .83 correlation seems high, it
in fact represents only about 70% of the variance. For example, I had no
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locations. However, if the judge had been sensitive to the possibility of
the pages being in the correct order, he could have inferred rather reliably
whether a target had been visited during the first or second half of the
experiment, which would have been useful information. Finally, it should be
stressed that the .83 correlation does not suggest that the experimenters
failed to randomize the pages, only that the randomization was done poorly.
The more damaging criticism derives from the success of Marks" judge in
performing a significant matching of transcripts and targets with the aid of
cues from the map. A curious feature of this analysis is that the judge's
success seemed attributable in part to the apparent validity of an
assumption he made that targets close together on the map were visited by
the outbound experimenter on successive trials on the same day. But if the
targets for each trial were selected randomly, as stated in the published
protocols, the locations of successive trials should have been independent
of their physical proximity to each other. Does this mean that the judge
was "lucky" enough to a gear his judging to a freak correspondence, or does
it mean that the published protocol was not really followed?
In conclusion, although the RV researchers have succeeded somewhat in
neutralizing the Marks and Kammann critique pertaining to sensory cues,
legitimate grounds for doubt remain about the evidentiality of the data.
Fortunately, the validity of the sensory-cue criticism could still be
resolved by means of a further rejudging of all the series in the experiment
which had the following characteristics: (1) editing of the transcripts by
an impartial person blind to the correct matchings; (2) adequate
randomization of all judging materials; (3) inclusion of all trials; and
(4) judging of the edited transcripts by one (preferably more) judge(s) who
are (a) highly motivated to achieve correct matches, (b) demonstratably
unlikely to have information about the RV experiments, and (c) uninformed
about the identity of the data they are to evaluate.
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....
Data Selection. Marks and Kammann strongly suggest that Puthoff and
Targ selectively published only positive results, thereby misrepresenting
their actual rate of success. Consider two examples from the Hammid series
discussed in Psychology of the Psychic (pp. 34-35). Although Marks (1982)
later retracted their charge as it pertains to this series (based upon"
further information received from Puthoff), an analysis of it may
nonetheless be useful in revealing the kinds of ambiguities and gratuitous
interpretations of these ambiguities that have beset the remote-viewing
controversy from its inception.
.
First, Marks and Kammann cited a statement made by the inbound
experimenter from the transcript of Trial 4: (Targ): "Hella [Hammid] has
made a drawing of Hal's [Puthoff] first location. And we'll see where he is
for the next fifteen minutes." According to Marks and Kammann, "This [Hal's
first location] is clearly [italics mine] a reference to the preceding
experiment ... in which Hal Puthoff had visited the target site." But since
Targ had been the outbound experimenter for Trial 3, Marks and Kammann
concluded that there must have been an unreported trial between 3 and 4 for
which Puthoff was the outbound experimenter.
In my judgment, it is anything but clear, at least based on the Marks
and Kammann account, that the quotation refers to any preceding trial. It
seems much more plausible that the statement refers to the current trial
(for which Puthoff must have been the outbound experimenter, since Targ was
the inbound experimenter) and that Hammid had made her sketch for that trial
before recording her verbal impressions. If there is something else in the
transcript that made it "clear" to Marks and Kammann that this was not the
case, they have done a disservice to their position by not stating it.
In the next paragraph, Marks and Kammann quote the following statement
from the last trial in the series: "Hal has gone off to the first of three
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Hammid series. The problem here is that Puthoff and Targ consistently use
the term "experiment" -- not in the sense of a series -- but as a synonym for
what most parapsychologists call a trial. Thus, Targ was most likely saying
that Puthoff visited three sites in the same trial, not that there were
three trials. Marks and Kammann should be aware of this usage, because in
their book they frequently quote statements by Puthoff and Targ which adopt
it.
Even if we assume that Targ was using the term "experiment" as a
synonym for series, the Marks and Kammann interpretation makes no sense.
Taken that way, the statement says that the Hammid series consisted of three
trials, when according to the Marks and Kammann rendition it consisted of at
least nine and probably 13 trials.
None of this is meant to take away from the fact that the statement is
puzzling and ambiguous. Why, indeed, should the outbound experimenter visit
three locations on the same trial? Could it refer to the fact that the
outbound experimenter positioned himself at three different locations at the
same (broadly defined) site? The statement could eventually prove
troublesome and Puthoff and Targ owe us an explanation. The point, however,
is that Marks and Kammann had no grounds for jumping to the conclusion that
the statement is evidence of data selection.
A final example of Marks and Kammann's jumping to unwarranted
conclusions occurs in their discussion of a trial from the technology
series. They imply that data selection was the reason that in a secondary
analysis (not the primary analysis described in a previous section) a judge
was shown only the better of the two responses to the drill press target.
They fail to appreciate that the objective of the analysis was not to
evaluate the significance of the trial per se but to demonstrate that the
better response was so accurate that the judge could not only match the
target but, based upon the drawing, correctly name it. This intent is
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it to emerge as a likely possibility.
The above discussion is not meant to imply that there are not questions
pertinent to the possibility of data selection that need to be answered.
For example, it would be desirable to have a complete list of the "more than
one hundred [RV] experiments" (p. 9) to which Targ and Puthoff refer in Mind
Reach. On the other hand, the conclusion reached by Marks and Kammann in
Psychology of the Psychic that "there is clear evidence that [data]
selection has occurred" (p. 41) is unwarranted and, especially given the
severity of the charge (which amounts to an accusation of experimenter
--
fraud), unfair.
Other Criticisms
Logical Inference. It has been suggested by Hyman (1979) that since
the subjects in most cases received feedback of the correct target after
each trial, the subject could have gained some advantage by avoiding to
mention characteristics of targets in earlier trials in their responses in
later trials. As noted by Targ, Puthoff, and May (1979), the target pool
for the geographical-site experiments was sufficiently large and contained
sufficient redundancy that this is unlikely to be a significant biasing
factor. However, more precise information on this point would have been
desirable. This criticism does not apply to the technology series, where
sampling occurred with replacement.
Statistics.
The Morris tables used by Puthoff and Targ assume
statistical independence of trials. The important point is not the
independence of the actual trials as they occur but instead whether the
judge treats the trials as independent during judging. For example, the
assumption of independence would be violated if the judge were reluctant to
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tempted to do this, especially if he knows that the target pool was sampled
without replacement. In any event, there are no indications that the judge
was admonished to make his ratings independently.
As a result, it is likely that the original published significance
levels are biased. However, the point is moot because the data were later
reanalyzed using a direct-count-of-permutation method suggested by Scott
(1972) in which the p-value corresponds to the number of possible
permutations of the matrix of ranks that would yield a lower sum of ranks
than that actually obtained. This method takes into account the possible
nonindependence of rankings. The p-values obtained by this method closely
approximated those obtained by the earlier method, with five of the six
series continuing to be significant by a one-tailed test (Puthoff, Targ, &
May, 1979).
Attempted Replications
In this section I will critically review the research of the four major
replicators of the Puthoff and Targ remote viewing studies. John Bisaha and
Marilyn Schlitz have consistently obtained positive results; Edward Karnes
and Marks and Kammann have consistently obtained negative results. Although
each has undertaken multiple experimental series, I will focus primarily on
the most prominent single experiment of each investigator. With the
possible exception of Karnes, the methodology has been fairly uniform within
experimenter. In discussing methodology, I will focus on those aspects in
which the procedures differed from those adopted by Puthoff and Targ.
Bisaha and Dunne
In collaboration with Brenda Dunne, Bisaha obtained statistically
significant evidence of RV in three experiments (Bisaha & Dunne, 1979;
Dunne & Bisaha, 1979). The most prominent of these experiments (Dunne &
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Bisaha. 1979) used a precognition procedure in which the subiect was asked
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to describe a location to be selected by the outbound experimenter five
minutes after the response period was terminated. The target pool consisted
of 100 sealed envelopes, each containing the name of a location in the
Chicago area. For each trial, a sub-pool of 10 of these envelopes was
chosen by an unspecified random method. The actual target was selected by
the outbound experimenter from among these ten by reaching into a container
and picking out one of ten equally sized folded sheets of paper. The
appropriate envelope was then opened and the target location revealed. The
outbound experimenter was given 15 minutes to get to the target site, where
she remained for 15 minutes, taking a photograph of the site as well as
making notes about it. The subject received an unspecified form of feedback
about the identity of the target site after each trial.
Two inexperienced subjects completed a total of eight trials. A single
judge was assigned to. each of the eight target locations. The judge was
given a photograph or photographs of the target site along with its name and
the outbounder's notes made at that site, and then was asked to rank the
eight unedited transcripts in order of their perceived similarity to the
target. Judges did not actually visit the target sites. The sum of ranks
assigned to the correct transcripts was evaluated by an expanded version of
Morris" tables and found to be significant (p <. 008, one-tailed).
Criticisms. Marks (1982) made three critical points about the Bisaha
experiments. The first point was that results from only seven of ten trials
were reported. The implication seems to be that the results of the omitted
trials were dropped because they were poor; in other words, data selection.
The second criticism concerned the editing of the transcripts. Marks
obtained the transcripts from Bisaha and found that they did obtain some
biasing cues, such as the name of the percipient and the date. The third
criticism was that not all the photographs taken of a given site were
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presented to the judges;
if the person who made these selections was not
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blind to the transcripts, he might have selected the photograph(s) which
gave the best match, thereby biasing the results.
Evaluation. The use of a separate judge for each trial was an
important improvement over the method employed by Puthoff and Targ.
Not
only did it assure independence of the trials in judging, thus allowing
proper use of the tables, but it precluded the kinds of intra-judge
comparisons across trials that provided the raw material for the sensory-cue
criticism of Marks and Kammann (that is, if one can assume that the judges
had no way of inferring to which trial in the sequence they had been
assigned). However, their choice of the outbounder's photographs as target
material for the judges, as opposed to having the judges visit the sites
themselves, provided a compensating opportunity for sensory cues. As noted
by Stokes (1978), factors such as the weather could be indicated both in the
subject's transcripts and either in the notes of the outbound experimenter
or the photograph of the site, thereby providing the judge with biasing
information. Dunne and Bisaha noted this objection in their report (Dunne &
Bisaha, 1979) and said that they had examined the transcripts and
photographs for cues and had found none. (No mention was made of the notes.)
An independent evaluation excluding the notes would be desirable, however.
The authors refuted the suggestion of logical inference based upon
.
feedback (see p. 52 above) by noting that their target pool was not sampled
in a "closed-deck" manner. However, if I understand the sampling procedure
correctly, it was not possible for a target to be selected for more than one
trial, thus rendering the interpretation possible in principle. However,
the size of the overall pool and the fact that no effort was made to force
diversification of the sites suggests that this was unlikely to have been a
serious source of bias.
Another weakness in the authors" report is a failure to document fully
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the judging materials. The fact that the judging materials were randomized
at all is mentioned only in a preliminary report of the experiment (Bisaha &
Dunne, 1977).
The Marks (1982) critique raises some novel and important points, but
again it suffers from gratuitous interpretations of the Dunne and Bisaha
report. One complicating factor is that the protocol he describes is not
that of the main experiment he cites as his reference and the one I have
chosen for review (Dunne & Bisaha, 1979), but that of an earlier study
(Bisaha & Dunne, 1979). For example, the number of trials in the Dunne and
Bisaha experiment is eight, whereas Marks cites it as seven, the number in
the earlier experiment. However, the basic arguments apply to both
experiments and so the discrepency does not present a serious problem.
I
will base my evaluation on the later experiment, however.
Nowhere do the authors state or imply in their report of the experiment
that there were unreported trials. It is true that each target pool
contained ten targets, but this does not necessarily mean that ten trials
were
planned. For instance, target pools where the number of targets
exceeded the number of trials were also employed in the Maimonides dream
experiments, where it was clearly stated that the number of preplanned
trials was less than ten. However, the authors can be criticized for not
reporting whether eight was the number of preplanned trials; thus, optional
stopping is a logical possibility.
Mark's final criticism, concerning editing of the transcripts,
resembles that of Stokes discussed above. The only examples of biasing
information which Marks reported concerned the name of the subject and the
date.
This kind of information would only be helpful, however, if
corresponding information appeared on the target photographs or in the
notes.
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as gross incompetence for which there is no independent evidence.
It is not clear from the report whether Marks" assertion that not all
the photos of each site were given to the judges is valid. The procedure is
described by Dunne and Bisaha (1979) as follows:
Each judge was given one transcript of a percipient's description to
read and was then presented with a set of eight photographs with
accompanying agent's notes, one of which was the correct target. The number
of photographs for each target varied, depending on the agent's judgment of
the complexity and size of the target as well as her own observational
perspective at the time of the trial. The judges were given these
photographs taped to a sheet of paper with the name of the target and the
agent's descriptive notes typed below the photographs. (pp.20-21; my
emphasis)
The first underlined phrase supports Marks" interpretation. The second
underlined phrase could be taken as referring to the sentence immediately
preceding it, in which case it would be more consistent with the opposite
interpretation, i.e., that all pictures were included. This would require
the additional assumption, however, that "eight photographs" in the first
sentence really means "eight sets of photographs." If Marks" interpretation
is correct, and selection of the photos was made by a person not blind to
the transcripts, a bias could have occurred. Although I think his
interpretation is the most likely, some doubt remains.
Additional Trials. Dunne, Jahn, and Nelson (1983) subsequently
reported the results of 300 separate remote viewing trials, which included
the trials just discussed. As procedural details of the subsequent trials
are not included in the report, a methodological critique cannot be
undertaken. The principal objective of the report was to illustrate the use
of a method of analysis for RV data in which both the transcript and the
target site are coded on 30 descriptive characteristics (e.g., indoors
vs. outdoors). Various scoring schemes based on how well the codings of
transcript and site match up on a given trial were assessed statistically
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The composite Z-scores derived from this method for the total sample ranged
from 5.45 to 7.71, depending upon the particular scoring scheme employed.
Results did not seem to be affected by the distance between the viewer and
outbound experimenter, nor the time interval between sending and receiving.
Twenty-one percipients and nine agents contributed to the formal data base
of 168 trials. The fact that only four percipients (19%) and one agent
(11%) contributed net negative Z-scores (three or more negative out of the
five scoring schemes) suggests that the effect is distributed fairly
uniformly across the sample.
Schlitz
Marilyn Schlitz has reported two successful remote viewing experiments
using herself as subject (Schlitz & Gruber, 1980, 1981; Schlitz & Haight,
1984). The most prominent of these two was an experiment conducted with
.
Elmar Gruber in which Schlitz was located in Detroit and Gruber (the
outbound experimenter) in Rome. A target pool of 40 geographical sites in
Rome was intentionally constructed so as to contain several targets of a
given type (e.g., fountains, churches). Gruber selected by means of a
random number generator one of these 40 sites (without replacement) as the
target for each of the ten trials. Gruber visited each site at the time
Schlitz was making her response, tape-recording his impressions of the site.
Schlitz, who received no feedback about the target sites until the
experiment had been completed, mailed her written impressions and sketches
for each trial to Gruber at the end of the experiment. Gruber and another
person, who was not aware of the target sequence, translated the subject's
transcripts into Italian. They also looked for biasing cues of the type
indicated by Marks and Kammann but found none. The translations were then
checked for accuracy by a third person who was blind to the target sequence.
Photocopies of the ten transcripts were given 1.
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wished. They also had access to Gruber's notes about each site. Not only
did they rank the transcripts at each site but they also rated each possible
transcript-site pairing for correspondence on a 0-100 scale. The resulting
10x10 matrices of ranks and ratings were each evaluated by the
direct-count-of-permutations method and both were found to be significant at
approximately 5x10-6, one-tailed.
Concerned about the possibility that the notes might have provided
sensory cues of the type referred to in the discussion of the Bisaha
experiments, the experimenters later asked two new judges to complete the
rankings and ratings without the notes (Schlitz & Gruber, 1981). The
results in both cases remained significant, but at a more modest level
(p <. 002).
Evaluation. Although it is not customary for experimenters to serve as
their own subjects in psychological research, there does not seem to be
concrete objections that can be raised against this procedure in this case.
At the same time, some precautions which could easily have been taken either
were not taken or not reported. For instance, no mention was made of
whether Schlitz sent Gruber the transcripts in random order. Why did
Gruber, who knew the target order, allow himself to participate in the
translation and editing of the transcripts when two other persons who were
blind to the target order were available for the task? Was the order in
which the target sites were presented to the judges randomized? Were the
judges given the notes in random order?
These problems were eliminated in an otherwise strict replication of
the above procedure by Schlitz and Haight (1984). Ten trials were conducted
with Schlitz in Durham, North Carolina, and the sender (Haight) in Cocoa
Beach, Florida. The response transcripts were edited by a third party who
was blind to the correct matchings, both the transcripts and target list
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were randomized before judging, and there were no notes by the sender. The
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results were significant (p <. 05, one-tailed) for both rankings and ratings.
This study is the best controlled and most fully reported of those
considered in this chapter.
Karnes
Edward Karnes and associates have reported three nonsignificant RV
experiments (Karnes & Susman, 1979; Karnes, Ballou, Susman, & Swaroff,
1979; Karnes, Susman, Klusman, & Turcotte, 1980), although I do not think
the Karnes and Susman study should be classified as an RV experiment. Of
the remaining two, the 1980 study most closely approximated the SRI
procedure and I will focus on it.
.
The subjects for this experiment were eight self-proclaimed psychics,
divided into four sender/receiver pairs according to their own preferences.
The four subject pairs completed a total of 16 trials. The target pool
consisted of 16 "distinctly different" outdoor and indoor geographical
sites, the order of which was randomized by means of a random number table.
During each trial, Karnes and the sender went to the target site, the sender
taking a movie of the site and recording his or her impressions on tape.
Receivers tape-recorded their impressions and drew sketches. The period for
both sending and receiving was 15 minutes. Subjects received feedback after
each
trial.
.
The sender and receiver mentation reports were transcribed, edited to
remove biasing cues, and randomized. Four judges were assigned to each site
and asked (1) to indicate the eight transcripts which best described the
site and (2) to rank these eight "best" transcripts. In addition to
visiting the site, the judge had access to the senders" edited notes and the
movie as part of the protocol.
In selecting the eight "best" transcripts, the 64 judges obtained 25
approached but did not reach significance (p <. 10). The mean of the ranks

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assigned to the correct transcripts was 4.36 compared to MCE of 4.5, which
was a nonsignificant difference (t[24] -. 48).
Evaluation. Although the results of this experiment were
nonsignificant, I will nonetheless offer a methodological critique for
purposes of comparison with the other studies being considered.
(1)Logical Inference. Since the 16 target sites were selected as distinctly
different and subjects received post-trial feedback, the Hyman criticism
(regarding the advantage of avoiding characteristics of previous targets on
subsequent responses) applies. This bias is somewhat ameliorated by the use
of multiple subjects, although two of the subjects each completed six
trials. Also, randomization methods were not fully documented.
(2) Sensory Cues. These are unlikely, given the randomization of both sender
and receiver transcripts and the editing of both. However, it is not
indicated whether the person who edited the transcripts was blind to the
correct matches. Another possible source of sensory cues, noted by Tart
(1980), is that Karnes, who knew the target for each trial, had sensory
contact with the receiver during the administration of the instructions
prior to the trial. The nonsignificance of results is not an adequate
rebuttal to this criticism, since the cues could bias the subject toward
incorrect impressions as well as correct ones. On the other hand, it is
difficult to see how meaningful cues could be transmitted to the subject
during a rather standardized administration of instructions unless one
assumes gross negligence by Karnes.
(3) Statistics. The statistical analysis of hits is, strictly speaking,
improper, since the judgments of the members of each group of four judges
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seem to apply as well to the analysis of the ranks.
However, it is
extremely unlikely that these statistical errors affected the authors"
conclusions, since they would more likely tend to inflate rather than reduce
significance levels. The analysis of ranks was rather insensitive in that
it was restricted to only .the best transcripts (i.e., restricted range), but
this analysis was secondary.
..
Marks and Kammann
Marks and Kammann (1980) completed five RV series, totalling 35 trials,
in an attempt to replicate the SRI results. One subject participated in
each series. The target pool consisted of 100 geographical sites, one of
which was selected for each trial, without replacement, by an unspecified
random method. The test procedure seemed essentially identical to that used
by Puthoff and Targ, and subjects received feedback after each trial. The
response transcripts were edited for biasing cues and randomized. There
were five judges in each of the first four series and one judge in the
fifth. The judges went to each site and ranked the transcripts for that
site. There was no statement that the order of sites given to the judges
was randomized. The method of statistical analysis was not specified, but
the results of each series were reported as nonsignificant.
Evaluation. In criticizing the methodology of the experiment, it is
important to keep in mind that Marks and Kammann made a conscious effort to
duplicate the SRI method as closely as possible, except for the editing of
the transcripts. The one point that should be noted in this connection is
that nowhere do the authors state whether the person who edited the
transcripts was blind to the correct matchings. In other respects, the same
methodological criticisms that applied to the SRI research apply to the
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General Evaluation
Why have some investigators consistently obtained positive results in
RV experiments and others just as consistently obtained negative ones? The
traditional skeptical answer to this question is that the experiments which
obtain negative results are superior methodologically. However, when we
consider the final judgings, the methodological quality of the positive and
negative studies reviewed in this report appear to be about equal, at least
insofar as quality can be inferred from the experimental reports.
The actual test procedures seem quite uniform, so it is unlikely that
the key resides here. Since inexperienced as well as experienced subjects
produced positive results in the successful experiments and amateur psychics
were used in some of the unsuccessful experiments, subject characteristics
also seem to be a poor bet.
The identity of the judges is perhaps a more promising option.
Although most of the controversy has focused on the skill of the judges, the
motivation of the judges may be a more important variable. Unfortunately,
the judges are rarely described in the experimental reports. However, all
else being equal, it is reasonable to assume that "pro-psi" experimenters
(the ones who achieved the positive results) are more likely to select
highly motivated judges than are skeptical experimenters. This is not to
suggest that many of the judges used by Karnes and by Marks and Kammann (in
their experiment) were skeptics, and the lone judge in their final series
was identified as being a "sheep"; yet they might still not have been as
highly motivated as the more "successful" judges. Unfortunately, since we
lack sufficient data, this interpretation can only be considered an educated
guess, at best. The only variable that I can discern which is known to
distinguish reliably the results of these experiments is the identity (and
the theoretical orientation) of the principle investigators. Why this makes
a difference is, of course, the crucial unanswered question.
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Some mention should be made of the generally poor level of
methodological detail in the experimental reports. This is true of the
reports of the skeptics as well as those of the proponents. For example, in
only one case (Schlitz & Haight, 1984) was the method of randomizing targets
and judging materials described in detail. Often the method was not
described at all, and in several key instances it was not mentioned whether
any kind of randomization took place. This deficiency of reporting is one
of the major reasons why so much controversy has arisen about the RV work
and why a proper evaluation of the current status of the evidence is so
difficult. However, it would be unfair to single out the remote viewing
research in this connection; we will repeatedly confront the problem
throughout this report.
Finally, one factor of a more ad hominem nature must be briefly
considered in evaluating the SRI research program.
I refer to the
reluctance of Puthoff and Targ to share their raw data with critical
investigators. Marks and Kammann complained bitterly about this in their
book and another critic, Christopher Scott, has also had considerable
difficulty obtaining the data he needs (e.g., Scott, 1982).
Such recalcitrance inevitably creates the impression that the
investigators have something to hide and thus damages the credibility of the
research. More importantly, if Marks and Kammann had not been able to
obtain the raw data of the Price and Hammid series from the judge, the fatal
flaws in the initial judging of the Price series may never have come to
light.
On the other hand, one can sympathize with the reluctance of
investigators to share data with antagonists who may misrepresent it in
print to promote their own viewpoint or ideology or to make public
insinuations of fraud based upon inadequate evidence. Regrettably, there is
precedence for this type of behavior on the part of critics in the history
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of parapsychology (e.g., Hansel, 1966, 1980). The nature of some of the
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criticisms of Marks and Kammann, as discussed earlier, seems to justify such
concerns in the case of these particular commentators.
Nonetheless, given the importance and controversial nature of the SRI
research, it is my opinion that the SRI researchers have not been as
forthcoming as they could have been in addressing the concerns of critics
and, in particular, in seeking independent evaluation of their data and
procedures under circumstances that protect their legitimate interests. It
is unclear to what extent, if any, external pressures might be responsible
for this behavior.
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Chapter 4
THE GANZFELD DEBATE
A major preoccupation of parapsychologists since the 1970s has been the
exploration of techniques that might be used to increase the manifestation
of ESP and PK in experimental settings through the induction of altered
states of consciousness (ASCs). One technique that has enjoyed widespread
use is the ganzfeld. Originally introduced by Bertini, Lewis, and Witkin
(1969), the ganzfeld is a sensory deprivation procedure that encourages
inward focusing of attention and a hypnagogic or hypnagogic-like state of
consciousness. The principal rationales for its use in parapsychology are
that the inward focusing of attention and the reduction of meaningful
sensory input facilitate detection of subtle psi-laden mental impressions
(Honorton, 1977) and that it reduces "linear constraints on mentation"
(Stanford, 1979).
The ganzfeld procedure eliminates patterned stimulation in the visual
and auditory modes. Visual isolation is provided by taping acetate
hemispheres (halves of ping-pong balls) over the eyes, stuffing small pieces
of cotton around the edges, and shining a light through them from a short
distance. Many investigators prefer a red to a white visual field, which
can be achieved by using either a red light or red-dyed ping-pong balls.
Auditory isolation is provided by playing white or pink noise (or a similar
stimulus, such as waterfall sounds) to the subject through headphones at
moderately loud volume. Specific parameters for the strength of
illumination, loudness of sound, etc., have not been standardized and often
are not reported. Frequently, subjects are allowed some latitude in
adjusting these parameters themselves.
The percipient is left in the ganzfeld for 20 to 45 minutes, although
the longer durations are PrefeEr
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give ongoing mentation reports, although in some studies the reports are
postponed until just after the ganzfeld period.
The ganzfeld is used in conjunction with standard free-response ESP
test procedures. Targets for ganzfeld sessions consist of relatively
complex and often emotionally evocative pictures, usually in the form of
photographs or slides. One of these is randomly selected from a large pool
to serve as the target for each session (or trial). In most experiments, an
agent attempts to send the content of the target picture to the percipient
during the ganzfeld period. After the session, either the subject or an
outside judge (or judges) assesses the correspondence between the subject's
mentation (or a transcript of the mentation report) and each of a set of
pictures, one of which is the target, on a double-blind basis.
.
THE CONTROVERSY
!
The ganzfeld studies entered into the psi controversy when critic Ray
Hyman chose to treat them as a representative sample of state-of-the-art psi
research in evaluating experimental parapsychology generally. His choice
was conditioned by the fact that strong claims had been made by some
parapsychologists (e.g., Honorton, 1978) for the repeatability of the
results using this procedure. His interest in this data base evolved into a
protracted debate with Charles Honorton (Honorton, 1983; Hyman, 1983). The
culmination of this debate was a lengthy exchange which has recently
appeared in the Journal of Parapsychology (Honorton, 1985; Hyman, 1985).
In the remainder of this chapter, I will first summarize and then critically
evaluate this exchange. Two central issues have defined the debate and I
will treat them separately. The first issue is the true level of
replicability reflected in the data base; the second issue is whether
procedural flaws are sufficiently serious to undermine the experiments as
evidence for psi.
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Issue 1: Replicability
Hyman's Critique
Several published literature reviews have estimated that in the
neighborhood of 55% of published ganzfeld experiments have provided
significant evidence of ESP (Blackmore, 1980; Honorton, 1978). Hyman chose
to base his analysis on an unpublished evaluation by Honorton in which 23 of
42 separate experiments (55%) "achieved overall significance on the primary
measure of psi at the .05 level" (Hyman, 1985, p. 5).
In attacking this claim, Hyman set two broad objectives for himself:
first, to show that the claimed success rate of .55 was too high and,
second, to show that the claimed error rate of .05 was too low.
Success Rate.
Regarding the first objective, Hyman made the following
points:
(1) Ten experiments in the data base had multiple cells (i.e.,
experimental conditions), each of which he felt should be treated as a
separate experiment. With one exception (to be discussed below), Honorton
had pooled cells to arrive at a decision regarding significance for each
experiment. Hyman was particularly critical of Honorton's strategy in
relation to a very complicated experiment by Braud and Wood (1977) in which
the objective was to determine if immediate, trial-by-trial feedback of
results could enhance scoring within the ganzfeld paradigm. Among other
things, Hyman noted that the baseline condition of this study, which closely
approximated a standard ganzfeld experiment, produced nonsignificant results
and should be counted as a failed experiment.
The one case where Honorton did not pool cells was an experiment by
Raburn (1975) in which the presence of a sender and the percipient's
knowledge of whether he was taking a psi test were manipulated in a 2x2
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Factorial design.
Significance was restricted to the one cell in which a
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not to include the two cells in which subjects were not aware that they were
taking a psi test on the grounds that the conditions were grossly atypical
of ganzfeld research, and treated the other two cells as separate
experiments. Hyman objected to the exclusion as arbitrary, noting that
other atypical conditions in other ganzfeld studies were not excluded and
that in other ESP studies (but not ganzfeld studies) ESP had been
demonstrated when subjects were unaware of being tested for it. He also
objected to Honorton's inconsistency in not adhering to his own pooling
criteria, which would have resulted in the experiment being classified as a
failure even with the exclusion of the two disputed cells.
Hyman concluded that if the cell had been used as the unit of analysis,
as he preferred, there would have been 25 "successes" out of 80, thus
reducing the percentage of success from 55% to 31%.
Details of how this
figure was arrived at were not provided.
(2) Hyman claimed circumstantial evidence that a number of mostly
unpublished experiments not included in the data base had a lower success
rate than those which were included. He first cited studies alluded to in
reviews by Blackmore (1980) and Parker and Wiklund (1982) which, if added
in, would reduce the success rate from 55% to 43%. Again, no details were
provided.
His primary piece of circumstantial evidence was the observation that
the rate of successes did not increase as the sample size (and thus the
statistical power) increased, as one would expect from statistical theory.
He demonstrated his point through an analysis in which he divided the data
base into four subgroups of increasing sample size. Estimating the
percentage of hits for the entire sample to be 38%, he computed the number
of significant experiments expected for the median N of each subgroup and
compared it to the observed number of significant experiments in each
subsample by a chi-square test. The overall chi-square was highly
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attributable to an excess of significant studies in the smallest class
(N<20 trials). As an explanation, he speculated that small studies which
were nonsignificant were dismissed as having inadequate power and thus were
not reported, whereas larger nonsignificant studies were reported. Also,
studies showing poor results on early trials might have been aborted and
thus not reported.
Finally, Hyman noted six "retrospective" experiments which he suggested
were not originally scheduled for publication but were only published when
the results proved significant. One was a compilation of trials conducted
when film crews visited the laboratory (Honorton, 1976), one was a classroom
demonstration (Child & Levi, 1979), one was not published until three years
after it was conducted (Braud, Wood, & Braud, 1975), and the other three
were defined as exploratory.
Hyman did not attempt to provide a numerical estimate of how much these
factors would reduce the claimed success rate but he concluded this first
section of his critique by stating that "the apparent rate of successful
replications must be well below 30%" (p. 16).
Error Rate. Regarding the second objective, Hyman focused on the fact
that
there was no uniform definition of the dependent variable, i.e., the
ESP score. In particular, he noted that any of five separate indices (e.g.,
direct hits, sum of ranks assigned to the targets) were used by the
reviewers in classifying experiments as significant. He argued that since
the reviewers would accept any of these measures, the ostensible .05 error
rate should be adjusted to take account of this fact. To determine the
appropriate error rate, he performed two simulations, each consisting of
1000 computer-generated "experiments" with random assignment of scores.
Taking into account the observed intercorrelations among the five indices,
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He then performed a more conservative simulation in which he determined
the error rate for each experiment based upon the number of indices actually
reported and came up with an average error rate of approximately .10.
However, he provided circumstantial evidence and one concrete example
suggesting that not all indices actually used were reported, which, if taken
into account, would of course raise the error rate somewhat. He implied
that the .22 error rate is the more appropriate, because it is the one that
defines the operating assumption of the reviewers. In neither case did
Hyman provide enough details about how he arrived at his estimates to allow
a proper evaluation.
Hyman concluded by listing five other sources of multiple testing, that
each applied to between 7% and 64% of the data base. He felt these should
also be taken into account in determining the true error rate. They are:
(1) alternative significance tests on the same scores; (2) empirical as
well as theoretical baselines; (3) multiple types of ESP scores (other than
the indices discussed above); (4) multiple experimental conditions; and
(5) use of both subjects and outsiders as judges.
Hyman concluded from his analysis that "the arguments I have
made ... make a strong case that the overall effective error rate per study
could easily be [.25] or higher" (p. 25). Since he had previously concluded
that the real success rate "must be well below 30%," his ultimate conclusion
that "this rate of 'successful" replication is probably very close to what
should be expected by chance given the various options for multiple testing
exhibited in this data base" (p. 25) follows naturally.
Honorton's Rebuttal
Success rate. Honorton treated his disagreements with Hyman regarding
the appropriate unit of analysis (cell or experiment) and whether two of the
four cells of the Raburn experiment should have been disqualified as
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readers to "examine the original study descriptions and draw their own
conclusions" (Honorton, 1985, p. 54).
Honorton did not dispute Hyman's claim that the success rate of studies
with small sample sizes is disproportionately high but he did dispute
Hyman's conclusion that this can be attributed to nonpublication of
nonsignificant studies with small numbers of subjects. He argued that:
(1) free-response ESP experiments quite often are originally designed
for small sample sizes and nonsignificant as well as significant studies of
this type are frequently reported;
(2) Hyman's six examples of "retrospective" experiments do not fit his
criteria (e.g., two actually had large sample sizes and a third was
nonsignificant);
(3) Blackmore's (1980) survey of unpublished ganzfeld studies revealed
that none of these studies were aborted solely because of nonsignificant
results; and
(4) Hyman has no right to assume that studies with small and large
sample sizes are equivalent in other important respects. For example, in two
of the larger experiments it was noted that scoring level was inversely
related to the number of sessions conducted per day. (However, it should be
noted that this is not the same as sample size, although bunching of trials
on a single day is more tempting in large studies than in small ones.)
Referring to an analysis to be described below which he claimed
corrects for the inflated error rate, Honorton argued that the rate of
success of the published experiments is sufficient to compensate for the
effects of some unpublished failures. First, he noted that the success rate
is not diminished by eliminating the studies with small sample sizes.
Second, he cited application of a statistic suggested by Rosenthal (1979) to
estimate the number of nonsignificant experiments that it would take to
reduce a data base to nonsignificance,
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unlikely that publication bias, if it exists at all, is anywhere near that
extreme.
Error rate. Honorton conceded the existence of a multiple analysis
problem, but he argued that for the purposes of the meta-analysis, it should
be restricted to multiple indices or analyses of the overall effect.
Analyses which refer to comparisons between conditions or subsamples of the
overall study are irrelevant. He then adjusted the significance levels of
all 42 studies, based upon the number of indices each employed to test for
overall significance, using the Bonferroni inequality (Rosenthal & Rubin,
1984). This reduced the number of significant studies from 23 to 19, or
from 55% to 45%.
However, his main rebuttal was to perform a new analysis using as a
single, uniform index the number of direct hits. This information was
provided for 28 of the 42 experiments. Specifically, he converted the exact
probability values of the direct-hit rates to Z-scores and cumulated them
according to a method developed by Stouffer (Mosteller & Bush, 1954). The
resulting Z was a highly significant 6.60. If one assumes the remaining
studies in the data base had an average Z of 0 (chance), the Stouffer Z is
slightly reduced to 5.67. He also calculated that 43% of these experiments
were significant at the .05 level and that 82% were in the positive
direction. Finally, he demonstrated that the Stouffer Z was still
significant (Z=3.67, p =. 0001, one-tailed) if the results of experiments from
the two most successful laboratories (out of the ten reporting ganzfeld
experiments) were eliminated.
Evaluation
Success rate. There is disagreement between the protagonists as to
whether the experiment (Honorton) or the experimental condition (Hyman) is
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ganzfeld, although both acknowledge that a case might be made for either
alternative. Not surprisingly, each reviewer chose the alternative that
provided the outcome most consistent with his favored conclusion.
Only Hyman really addressed the issue. He offered two reasons why the
experiment might be considered the appropriate unit and rejected both.
First, he noted that using the condition creates interdependence among the
units because the same subjects were often used in different conditions, but
he rejected this as a problem because the interdependence exists regardless
of how the pie is divided. In other words, the interdependencies are
shifted from within the units to between the units. I agree with Hyman that
interdependence is not an adequate reason for rejecting the condition as a
unit, but neither is it an adequate reason for preferring it.
Second, Hyman conceded that his approach reduced statistical power by
reducing the mean unit sample size, but he says this is not a problem
because there is no relation between sample size and proportion of
significant outcomes in the data base. Here I must disagree with Hyman's
reasoning in that I fail to see the relevance of his point to the issue at
hand. Whatever the relation between sample size and outcome, dividing a
unit into subunits reduces the capacity to detect significance in the
subunits compared to that capacity for the whole unit. While some of the
power might be recovered by the increase in the number of units analyzed,
the issue being debated is not the significance of the overall percentage of
successful studies with respect to some total number of studies but the
percentage itself: 31% (Hyman) or 55% (Honorton). In my judgment, the
difference between these percentages is primarily if not wholly attributable
to the relative lack of power of Hyman's procedure compared to Honorton's.
Thus, Honorton's procedure is preferable.
I am not persuaded that the "file drawer" problem (lack of publication
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providing the 423 such studies needed to reduce the data base to
nonsignificance. In particular, I think Hyman has gone way beyond the data
in attributing the relatively high success rate of small-sample experiments
to selective reporting.
Error rate. The adequacy of Honorton's rebuttal to Hyman's charge of an
inflated error rate now depends upon the adequacy of Honorton's analysis of
the direct-hit studies using the single index of number of direct hits.
There seems to be a priori justification for adopting this measure, both
because it was the one most frequently used in the data base and also
because it was the method adopted in the first published report (Honorton &
Harper, 1974). However, it was also an advantageous choice for Honorton.
For unknown reasons, the mean Z-score of these 28 studies (+1.31) was
significantly higher than the mean Z-score of the other 14 studies (+0.01)
for which direct-hit scores were not available and other scores were used to
compute the Zs (t[34]=2.06, p <. 05). Honorton did not mention this fact in
his report, but he did compute a revised cumulative Z-score under the
assumption that the 14 omitted experiments had an average direct-hit Z-score
of 0, which seems a realistic estimate of the true state of affairs. The
cumulative Z was only reduced slightly, from 6.60 to 5.67.
By applying the same reasoning outlined in his discussion of the
multiple indices problem, Hyman could challenge Honorton's revised analysis
on the ground that many of the individual Z-scores should be reduced to
allow for the fact that other indices either were used or could have been
used. However, this reasoning is invalid, both in the critique of multiple
indices and (if it were to be so applied) in the present case. The kinds of
corrections Hyman advocated are appropriate, indeed necessary, if one wishes
to draw conclusions from single studies (i.e., does Experiment X, by itself,
provide significant support for the hypothesis?). However, in the present
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supports the hypothesis. In this circumstance, the corrections are not
appropriate because the p-value one wants from each study is how many times
as extreme a score would be achieved in X number of replications (the
uncorrected value).
Consider, for example, a sample of 1000 such studies, each of which was
analyzed in two ways such that one of these ways always yielded a
significant outcome at the .05 level and the other always yielded a
nonsignificant outcome. If each of the significant p-values were multiplied
by two, as suggested by Hyman, all 1000 of the significant outcomes would be
reduced to nonsignificance. Not only would this lead to the absurd
conclusion that the effect was a statistical artifact, but the number of
truly significant outcomes would actually be significantly lower than the 50
predicted by the null hypothesis (Z =- 7.25) ! This is because the number of
significant outcomes expected by chance would not be achieved. Although the
example is idealized, the conclusion is obviously absurd.
The Z-score method employed by both Honorton and Hyman in the latter
stages of their controversy is much more sensitive than the arbitrary
classification of experiments as significant or nonsignificant. An
important feature of the data which only the Z-score analysis reflects is
the fact that 82% of the direct-hit studies (Z-3.21, p <. 01) and 76% of all
studies (2-3.24, p <. 01) yielded Z-scores in the positive direction. This
fact is mentioned only briefly by Honorton and not at all by Hyman, yet it
is the most powerful single argument for the non-chance character of the
data base. Although it may be quite reasonable to expect publication bias
to favor significant over nonsignificant outcomes, it is less reasonable to
expect such bias merely with respect to the direction of outcomes.
In conclusion, although the true success rate of all the ganzfeld
experiments actually conducted by the time of the controversy is almost
than the 55%
agipally claimed by Honorton,
it is clearly
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higher than the rate to be expected by chance. Thus, there is something

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here to explain. The question remains as to how to explain it.
Issue 2: Procedural Flaws
Hyman's Critique
Hyman began his critique by listing six major categories of procedural
flaws that applied to 24%-74% of the experiments in the data base. They can
be summarized as follows:
(1) Single Targets: Cases in which the target handled by the agent was
included in the set of pictures subsequently judged by the percipient, thus
allowing for the possible transmission of sensory cues.
(2) Randomization: Cases in which no randomization or an inadequate
method of randomization, such as shuffling cards or tossing coins, was
employed to select the order of targets, or cases in which the method was
not sufficiently described. Procedures specifying the use of REGs or random
number tables (RNTs) were considered acceptable.
(3) Feedback: Cases in which single targets were employed and the
order of pictures in the judging set was not properly randomized. Also,
cases in which inadequate precautions were taken against the percipient
communicating with the agent at the time of feedback.
(4) Documentation: Primarily cases in which it was not reported how
frequently the agent was a friend of the percipient or whether this variable
affected the results.
(5) Security: Cases where inadequate security was taken against
threats to the "validity" of the experiment, particularly cases which
employed a single experimenter such that the agent and percipient were not
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both monitored.
(6) Statistics: Cases in which the statistical tests were improperly
applied.
Hyman next responded to the argument of some parapsychologists that
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difference in study outcome. Conceding, for example, that studies using
single target sets did not produce significantly better results than studies
using duplicate target sets, he argued that a cause-effect relationship may
still exist if this flaw interacts in certain ways with some other flaw that
is also causally related to study outcome. Finally, he argued that "such
flaws are signs that the study was probably not carefully planned or
properly carried out" (p. 31).
Hyman then reported an "exploratory data analysis" in order to "suggest
hypotheses about what may be going on" (p. 32). Up to seven measures of psi
(e.g., significance, effect size) as dependent variables, along with nine
flaws (the six listed in this section plus three reflections of multiple
analysis discussed in the previous section) as independent variables, were
incorporated in both a cluster analysis and a factor analysis. Each
analysis yielded three overlapping clusters (or factors), which Hyman
labeled as "general security," "statistics," and "controls." Only the
controls factor, which included as the most strongly weighted components the
flaws of randomization, feedback, and documentation, correlated
significantly with the measures of study outcome. These three component
flaws, as well as the statistics flaw, also correlated significantly by
themselves with the measures of significance of study outcome.
Hyman then reported a second factor analysis, which included as
predictors the five experimenters who contributed the most experiments to
the data base as well as the scores in the three clusters derived from the
earlier analysis, and a few other predictors. Four factors were extracted,
of which Hyman found the fourth the most interesting. It included a high
loading on the "controls" cluster (which had previously been a significant
predictor of study outcome), plus a high positive loading from one of the
experimenters who habitually obtains significant results in ganzfeld
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supporting the conclusion that "experimenters who pay the most attention to
such controls also report the smallest effects" (p. 36), thus providing
evidence as well that the "experimenter effect" in parapsychology can be
attributed to differences in the care different experimenters put into
designing and executing their experiments.
As a final coup de grace, Hyman computed two multiple regression
equations using the previously identified significant flaws of
randomization, feedback, and documentation as predictors of the statistical
significance (Z-scores) and effect size (respectively) of studies in the
data base. Both multiple correlations were significant, and the equations
predicted that for studies eliminating all three of these flaws, the
expected Z-score would be zero and the expected hit rate 27% (assuming a
chance hit rate of 25%).
Hyman's final conclusion was that "the current data base has too many
problems to be seriously put before outsiders as evidence for psi" (p. 42).
Honorton's Rebuttal
Honorton began by quoting Glass et al. (1981), authors of a seminal
book on meta-analysis, in defense of the opinion that the influence of study
quality on study outcome is an empirical question that should not be
determined a priori. He then proceeded to his main line of defense which
was (1) to challenge Hyman's assignments of flaws and (2) to show by his own
codings and meta-analysis that when flaws are properly assigned and coded
there are in fact no significant relationships between presence of the flaws
and study outcome. In order to control for the confounding effects of
multiple analysis, Honorton restricted these analyses to the 28 experiments
where a direct-hit analysis was possible, using significance levels of this
analysis (converted to Z-scores) as his dependent variable.
Honorton agreed with Hyman's codings on two of the six procedural
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complaint was that Hyman failed to follow his own stated criteria in several
instances. With respect to the security, documentation, and feedback flaws,
he complained about ambiguity in Hyman's definition of the flaw or
inconsistency in his application of it to the studies under consideration.
He also questioned the seriousness of some of the "flaws". Specifically, he
questioned whether card shuffling is really an inadequate method of
randomization in studies where the randomization is performed separately for
each trial. Regarding security, he quoted an example showing that a
procedure was in fact secure despite the fact that it met Hyman's formal
"flaw" criterion of having only one experimenter present.
Second, Honorton computed separate correlations between presence of the
flaws single target, randomization, feedback, and documentation with his
revised codings, showing in each case that the correlations were not
significant. (Hyman had claimed significant correlations for these latter
three plus statistics). Finally, for single target and randomization,
i
Honorton demonstrated in each case that the direct-hit experiments which
Hyman regarded as adequate with respect to the flaw in question were
collectively significant by the Stouffer method. For single target, ten
adequate experiments produced a highly significant Stouffer Z of 4.35. For
randomization, 16 adequate studies yielded a Stouffer 2 of 4.14.
Finally, Hyman's multivariate analyses were dismissed by David Saunders
(1985), Honorton's statistical consultant. He noted, first, that the sample
of 42 studies was simply too small for factor analysis to be meaningfully
employed. Second, the factor analysis was compromised by certain
dependencies among the variables entered into them; e.g., each experimenter
was treated as a separate variable, guaranteeing that the intercorrelations
among these variables must be strongly negative. Finally, the significance
of Hyman's final multiple correlations predicting study outcome from flaws
are meaningless because the predictors were selected post hoc from at least
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Evaluation
There is no question that Hyman has uncovered flaws in the methodology
of a large percentage of the ganzfeld experiments which could conceivably
serve as the basis for conventional interpretations of the results of these
experiments, singly as well as collectively. What remains for evaluation is
the likelihood that these flaws do indeed account for the results.
Honorton and Hyman disagree about the necessity of empirical support
for the conventional interpretation. However, Hyman went to considerable
pains to provide such empirical evidence, despite his denial of its
necessity. Therefore, it would seem appropriate to begin by evaluating his
success at this endeavor.
My statistical consultant and I agree that Saunders" critique of
Hyman's factor analyses is appropriate. Although Hyman has labeled his
analyses as "exploratory," they were nonetheless used as an important part
of his argument and thus demand critical attention. Strictly speaking, the
analyses do not support Hyman's conclusion, culminating in his regression
analyses, that a linear combination of three flaws-randomization, feedback,
and documentation -- can account for the significance of the results.
However, there is reason to qualify somewhat this harsh assessment.
In
particular, Hyman noted -- regrettably, without providing supporting
statistics -- that four of the six procedural flaws (including those related
to multiple analysis) were independently and significantly correlated with
the primary (or, at least, the most sensitive) measure of statistical
significance, the Z-score. Even allowing for multiple indices -- a criticism
which Hyman was quick to level at the parapsychologists but to ignore in his
own work -- I find this outcome noteworthy. The three most pervasive of these
flaws are incorporated in the "Cluster III" (the "controls" cluster) of his
first factor analysis, which, irrespective of the validity of the factor
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Because of the questionable nature of the factor analysis, I have
chosen to proceed by treating the components of Cluster III separately and
to explore in each case the validity of the claim that the flaw is
significantly related to the Z-scores. If these prove not to hold up, the
factor analyses are invalid in any case. I have chosen Hyman's Z-scores as
the dependent variable rather than Honorton's, because they are provided for
more of the studies than the more conservative exact-probability Z-scores
supplied by Honorton and are highly correlated with the latter (r =. 99). I
have chosen to express the relationships between the flaws and these
Z-scores as biserial correlations, which provide an index of the magnitude
of relationship as well as the significance. On average, these tend to give
slightly higher correlation values (favoring Hyman) than the point-biserial
correlation, which might also be justified. My criterion for significance
will be a generous p <. 05, one-tailed.
For each of the flaws to be considered, Honorton provided correlations
with Z-scores which are nonsignificant, thus contradicting Hyman. There are
two major differences in procedure that must be considered in evaluating
these discrepencies:
(1) Honorton and Hyman differed in their flaw codings
of several studies and (2) Honorton restricted his correlations to the
. .
"direct-hits" experiments which comprised 28 of the 36 studies for which
Z-scores were available (78%). Not only does this mean that Honorton's
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correlations were less powerful than Hyman's but, given the sizable mean
difference of Z-scores between the direct-hit experiments and other
experiments, Honorton's correlations may have been attenuated due to a
restriction of range on the dependent variable.
Randomization. Hyman used three categories of randomization codings:
(1) appropriate, (2) inappropriate, and (3) inadequately described.
He
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(3)
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most powerful analysis and appeared to be Hymans" primary method, I began
using this approach. The resulting biserial correlation, based on the full
sample of 36 cases, was +.372 (Z=1.65, p =. 05), thus confirming (barely)
Hyman's conclusion from his factor analyses.
There were 11 cases of randomization which Honorton coded as
appropriate which Hyman coded as either inadequate or inadequately
described. In 10 of the 11 cases I was able to find unequivocal evidence
from the experimental report consulted by both reviewers that Hyman's
minimal criterion of adequacy, "using a table of random numbers or a random
number generator to select the specific target from a pool" (p. 27) was met.
Recoding of these cases reduced the biserial r to +.02 (Z-+.08, n.s.).
Thus, using this breakdown, Hyman's significant result can be entirely
accounted for by improper coding of ten of the experiments.
However, this negative conclusion must be qualified on the basis of the
analysis in which the experiments in Hyman's third category (inadequate
description) are eliminated. Removal of these seven experiments causes the
biserial r to rise substantially to +.385 (Z-1.87, p <. 05). The result is
essentially the same when the analysis is confined to the direct-hit studies
(three of which fit in the third category, leaving N=25): r=+. 407
(2-1.84, p <. 05). Thus, even with corrected codings there is a marginally
significant difference between studies clearly using "adequate" and
"inadequate" randomization procedures, the latter category yielding the
higher mean Z-score.
This result was not reflected in Honorton's analyses because most of
the studies judged inadequate by Hyman used a shuffling procedure, to which
studies Honorton assigned the intermediate coding on his three-point scale.
Without commenting at this point on the reviewers" disagreement about the
absolute merit of the shuffling technique, I must disagree with Honorton's
coding of these studies as higher than those where the method was not
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Feedback. Only the first of Hyman's feedback criteria (i.e.,
randomization of the judging sets) can be evaluated. 1 Since the feedback
flaw so defined applied only to the 21 experiments which employed single
target sets, the remaining cases are eliminated from the following biserial
correlations. The correlation for the surviving 21 cases, using Hyman's
codings, was +.565 (Z=2.76, p <. 01).
Honorton noted two cases assigned the feedback flaw by Hyman in which
it was indicated in the report that the members of the target set were
rearranged in an order independent of the original target locations,
descriptions comparable to those in other studies to which Hyman did not
assign the flaw. (In one of these two cases [ Sondow, 1979], the method of
reordering was only specified for one of the two experimental conditions,
but this was the condition responsible for the significance of the study and
it is reasonable to infer that the same method of reordering was used in the
other condition. ) Honorton also cited two cases where Hyman did not assign a
flaw but should have done so. My own inspection of the reports confirms
Honorton in all these cases. Moreover, I uncovered two cases among the
eight "non-direct-hit" studies excluded from Honorton's analysis in which
the flaw was not assigned by Hyman but should have been (Habel, 1976;
Parker, 1975). When the coding errors are eliminated, the biserial
correlation is reduced to +.141 (Z-0.42, n.s.).
In conclusion, there is no significant relation between presence of the
feedback flaw (first criterion) and significance of outcome in this data
base.
Documentation. Hyman defined this flaw in such a way that makes
independent evaluation of its coding extremely difficult. The one criterion
he specified, which is the major one but apparently not the only one,
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"the number
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provide data on whether this made a difference ... " (p. 28). First, it is
never stated (to my knowledge) in any of the reports that all the
percipients were unknown to the agents, even in those cases (generally not
assigned this flaw by Hyman) in which the agent was one of the experimenters
and the percipients were college students. Second, failure to evaluate this
variable does not by itself constitute a flaw any more than failure to
evaluate the sex, race, or hair color of the subjects constitutes a flaw.
It is only a flaw if one specifies why this particular variable should have
been evaluated, and Hyman was silent on this point.
Reading between the lines, one can make a highly plausible inference
about what is going on here. Throughout his paper Hyman scrupulously
avoided any mention of possible fraud by either subjects or experimenters,
although we know that critics traditionally are obsessed with this problem.
If one assumes that some subjects were motivated to cheat and. (sensory)
communication between agent and percipient is one of the most obvious ways
that such cheating might occur, then cheating is a more likely possibility
on those trials where agent and percipient were friends and relatively
likely to be in collusion. Indeed, communication from percipient and agent,
allowing the agent (in some cases) to reselect the target to bring it more
in line with the percipient's mentation report, was the second criterion for
the feedback flaw, which Hyman seems to have abandoned.
Concerp with possible fraud by the agent might also have influenced
Hyman's selection of the first feedback criterion (randomization of the
judging set). In this case, I suspect he had in mind the first of the
ganzfeld experiments (Honorton & Harper, 1974), in which the agent, who was
sometimes a friend brought by the percipient, was responsible for reordering
the judging set prior to judging by the percipient. If agent and percipient
had been in collusion and knew something of the procedure beforehand, it
would have been a fairly simple matter for them to have agreed that the real
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this would have been risky if the percipient's mentation obviously favored
one of the other targets.) Assuming the experimenters were honest, this
possibility only existed for those trials where the percipient brought a
friend to be the agent, and it could be tested by reporting those trials
separately. This was not done, hence assignment of the "documentation"
flaw. This particular scenario -- final reordering of the judging set by a
subject -- does not appear to have been possible in any of the other
experiments in the data base.
In other words, Hyman's documentation flaw seems to be an indirect way
of criticizing parapsychologists for a lack of sensitivity to the
possibility of subject fraud in their experiments. However, if this is the
case, it seems unfair to condemn an experiment on these grounds without
considering what precautions were actually taken to prevent agent-percipient
communication by sensory means.
Honorton seemed to have had the same hypothesis in mind when he
attempted to operationally define the flaw by assigning it to studies, and
only to studies, where (1) there was an agent, (2) the agent was not always
the experimenter, and (3) when the second criterion was not met, there was
no analysis of the effect of agent-percipient relationship on scoring. If
one is willing to assume honesty on the part of the experimenters (which
both Honorton and Hyman seemed to be doing), Honorton's criteria seem
reasonable.
According to Hyman's codings of all 36 cases, the biserial correlation
with the Z-scores was +.473 (2-2.71, p <. 01), confirming the result of his
factor analysis. Restricting himself to the "direct-hit" experiments,
Honorton, using his criteria, uncovered ten cases in which Hyman assigned
the flaw but should not have. My own survey of the reports caused me to
concur with Honorton in all cases. Also, among the remaining experiments, I
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might justify his codings by his criteria.) Incorporating all the coding
changes in line with Honorton's criteria reduces the biserial correlation to
+.008 (Z=0.04, n.s.). Retaining all Hyman's codings for the non-direct-hit
studies raises this correlation only slightly to +. 178 (Z=+0.60, n.s.).
In conclusion, to the extent that Hyman's documentation flaw can be
objectively defined by an independent analyst it is not significantly
related to study outcome. To the extent that it cannot be so defined, the
reader should not be asked to take it seriously.
Statistics. Using Hyman's codings, which were not disputed by Honorton,
the biserial correlation with Z-scores was +.183 (Z=+0.82, n.s.), which
fails to support the significance relationship reported by Hyman.
.
In conclusion, this evaluation has clearly failed to support Hyman's
claim of a significant relationship between the presence of procedural flaws
and the statistical significance (Z-scores) of the experiments in the data
base in three of the four cases. Only in the case of randomization could
some supportive evidence be found, but the level of significance was
marginal and it was selected from among two equally plausible significance
tests of the relationship. Thus, an appropriate correction for the
duplicate analysis would render it nonsignificant. Moreover, even if it were
left to stand, it would now constitute the only significant case among nine
procedural flaws considered (including the three multiple-analysis flaws
incorporated in Hyman's first factor analysis). In short, there is no
credible positive evidence in support of a relationship between the flaws
considered by Hyman and the outcomes of the experiments in the data base.
This result places the burden fully on Hyman's argument that the
presence of the flaws constitutes sufficient cause in itself to reject the
experiments in the data base as evidence for psi. I agree with Hyman's
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guarantee that the flaw had no causal effect on the outcome. As he argued,
the fact that each flaw is not independent of other flaws or procedural
variables allows that suppressor variables might serve to obscure a real
relationship. For example, the reason that the mean Z-score of experiments
using single target sets did not significantly exceed the mean Z-score of
the other experiments could be that the experimenters in the flawed category
whose results were nonsignificant took more care to avoid the possibility
that agents would contaminate the target pictures in the course of handling
them than did those in the flawed category whose results were significant
(perhaps due to the flaw). Likewise, demonstrating that all the studies in
subsamples defined by the lack of particular flaws remain collectively
significant is not an adequate rebuttal, because it implicitly assumes that
only one flaw is operative in the data base. However, Honorton did not seem
to be denying that flaws could account for the results. The real question
is what kind of a case can be made for the proposition that they did account
for the results.
To answer this question, we must first consider the plausibility of the
mechanisms of the causal agents implied by the flaws under consideration.
What other assumptions must be granted in order to conclude that these flaws
accounted for the results? Let us consider the flaws individually.
Single Targets. If an agent and percipient had colluded to produce a
bogus hit in any of the experiments cited for this flaw, it would have been
a relatively simple matter for the agent to introduce cues onto the target
picture detectable by the percipient. Since both Honorton and Hyman seem to
have assumed honesty on the part of the experimenters, this possibility is
really relevant only to those trials where the percipients brought their own
agents. As noted, this seems to be the root cause of Hyman's concern that
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If the agent did not intentionally introduce cues, is it possible that
a percipient might still identify cues introduced unintentionally through
normal handling? In an experiment conducted by the reviewer designed to
answer this question (Palmer & Kramer, in press), it was found that
"percipients" were indeed able to detect fingerprints left on the target
photographs by "agents" who simply held them and lightly traced the index
finger over them.
This criticism does not apply to those studies which used slides as
targets. Palmer and Kramer found no support for a related suggestion that
percipients are able to detect the slide previously exposed to the agent
because it might have been more faded than the control slides. Moreover,
the four studies which used slides and to which this criticism might apply
collectively produced a Z-score less than zero.
. Secondly, caution should be exercised in generalizing the Palmer-Kramer
results to the procedure used in nine ganzfeld experiments where the targets
were View-Master slides. Although fingerprints could have been introduced
inserting or removing the slide from the projector, agent handling was less
in these experiments than in those involving pictures, because the slide was
being viewed while inside the projector. Because the projector uses only
ambient room light, heat cues are quite unlikely. Finally, the judge
evaluates the slides primarily while they are inside the projector,
providing less opportunity for perception of fingerprints, etc. In short,
creation and detection of sensory cues would seem somewhat less likely with
this paradigm than with the one tested by Palmer and Kramer, although direct
empirical evidence to this effect obviously would be desirable.
Returning to the experiments using photographs as targets, it should be
noted that the fingerprints in the Palmer-Kramer study were not so obvious
that they would draw the attention of someone not looking for them. In
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reinforced by an earlier free-response ESP experiment by Palmer (1983), who
systematically manipulated whether or not the photograph handled by the
agent was included in the judging set. In most cases the agents and
percipients were friends who shared an interest in parapsychology. No
significant results were obtained in either condition, even though
percipients (blind to the manipulation) were encouraged to look for "psychic
vibrations" on the photographs in the judging sets.
In conclusion, the single-target hypothesis seems most viable in cases
where the percipients are (1) aware of the possibility of detecting the
target by means of sensory cues and (2) exert some effort to look for them.
In cases where the percipients are "psychics" out to make a reputation for
themselves or, at the other extreme, college students uninterested in the
subject matter but wanting to help the experimenter "make the experiment
work," the hypothesis seems quite plausible. However, in most of the
experiments in the data base, especially those which were cited for the flaw
and obtained significant results, the subjects seemed to be more like those
in the Palmer (1983) experiment: volunteers who were oriented to assessing
their psychic talents. For this kind of subject population the hypothesis
seems
less plausible, although it is still possible that such subjects might
respond to subliminal cues or for some other reason take advantage of cues
consciously perceived. However, the data from Palmer (1983) do not support
such speculations.
Feedback. Failing to randomize the order of pictures in the judging set
could bias the results if the target consistently appeared in one location
that corresponded to the response biases of the subjects. For instance, in
my experience subjects tend to have a bias favoring the first picture they
see.
If the targets were consistently placed first in the judging set, a
spurious rate of excess hits could result.
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This flaw was cited in those cases where randomization was achieved by
hand shuffling of the members of the target set (these all turned out to be
View-Master slides) or the method was not reported. The adequacy of the
former depends on the care with which the shuffling was done. The latter is
really a documentation flaw and cannot be evaluated.
Another possible way in which the feedback flaw could manifest in
studies with the single-target flaw, which was not considered by Hyman, is
replacement of the target in the set in a different orientation (i.e.,
upside down) from the other pictures in the set. Only a handful of the
reports stated explicitly that this possibility was avoided.
Documentation. Failure to break down the results in terms of the
relation of the agent to the percipient is only a flaw if there is reason to
believe that it would make a difference, and in this case it only makes a
difference if the possibility of fradulent agent-percipient communication
has not been eliminated. Thus, this documentation flaw is really a
by-produce of the sensory-cue and security flaws and need not be treated
separately for present purposes. In other words, if one grants proper
security against sensory communication, failure to report the breakdown at
issue is at worst a minor transgression.
Security. This category cannot be evaluated for plausibility because
Hyman never proposed how he thought certain failures to constantly monitor
the agent and/or percipient could have allowed cheating to occur. Absence
of such monitoring does not in and of itself mean that security was lacking.
Honorton cited one experiment (Braud et al., 1975) where considerable care
was taken to avoid sensory cues despite the involvement of only one
experimenter, which was one of the criteria Hyman used to assign the flaw.
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Statistics. Since Hyman and Honorton both computed their own
statistics, which were essentially equivalent, the statistical indiscretions
of some of the original authors do not affect the analyses at issue.
Randomization. Apart from incomplete or inadequate descriptions of the
randomization methods in many of the reports, the crux of the issue here is
Hyman's disapproval of a method used in one of the most successful
laboratories, which involved selecting the target by shuffling a deck of 31
cards. Shuffling is not necessarily an inadequate method; Epstein (1977),
for example, noted that six dovetail shuffles can adequately randomize a
deck of cards. Thus, the method is only inadequate if one 'assumes that the
shuffling was not done thoroughly. Again, the real flaw may be inadequate
description of how thoroughly the shuffling was carried out. The very same
point applies to the RNT and REG methods which Hyman found more acceptable.
For instance, we saw in the discussion of the Maimonides dream experiments
how improper use of a random number table can lead to biases that are likely
to be more severe than those caused by casual shuffling. The point here is
that the method of randomization is less important than how it is
implemented. The fact remains, however, that it is easier to document
proper application of REG and RNT methods than of shuffling methods, and in
that sense the former methods are clearly superior. Unfortunately, as Hyman
notes, the precise methods of randomization were rarely described even in
those ganzfeld studies which used REGs or RNTs; this general deficiency of
documentation is really his most potent criticism.
I cannot agree with Honorton's claim that the potential bias due to
...
(inadequate) shuffling is minimized in cases where the randomization is
performed separately for each trial. If shuffling is inadequate, the
composition of the deck may not change sufficiently from trial to trial,
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during the course of the experiment. This could result in one of the
targets being selected more frequently than chance allows. If this happens
to be a picture that corresponds more closely to spontaneous mentation in
the ganzfeld (discounting psi) than do others, a spurious level of hitting
could result.
Nevertheless, the bias would have to be fairly extreme to compromise
the results of experiments with the small number of trials characteristic of
this data base. The shuffling-bias hypothesis is particularly strained in
three experiments (mean Z=1.23), where two or more cards were used to select
a slide from the binary target pool of 1024 slides, which itself was ordered
in a very complicated and nonlinear manner with respect to content . (Smith,
Tremmel, & Honorton, 1976; Terry, 1976; Terry, Tremmel, Kelly, Harper, &
Barker, 1976).
It also should be kept in mind that any randomization method will
occasionally produce ordered sequences that will correspond with subjects"
response biases and thus leave the potential for spurious rates of hitting.
This of course is the kind of thing reflected in the specification of the
Type I error rate and is allowed for in the kinds of meta-analyses conducted
by Honorton and Hyman.
*
Conclusion
The purpose of the above exercise was not to excuse the flaws cited by
Hyman. In most cases they could have and should have been avoided and the
experimenters deserve to be criticized for them. Nonetheless, a reviewer
who is assigned the task of interpreting the significant results in the data
base must be concerned with the question of how serious the flaws are, how
likely they are to account for the results.
In most cases the flaws are attributable wholly or in part to
inadequate documentation in the reports. In fact, the only flaw which
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single target sets.
It should be kept in mind that the objective of the ganzfeld research
was not to satisfy critics about the existence of psi but to explore a
technique for enhancing the reliability of ESP in the laboratory. Most were
written with the assumption that the primary audience would be other
parapsychologists who would be interested in the studies primarily from the .
point of view of the objective which guided them and willing to take for
granted that their colleagues would exercise basic experimental competence.
This at least partly explains why the reports lacked details of interest to
the critic, whose primary concern is whether any evidence for ESP exists at
all.
With respect to duplicate target sets, it should be borne in mind that
time and expense are often involved in creating such duplicate sets. This
is particularly true in the case of the pool of 1024 specifically designed
"binary target pool" slides (Honorton, 1975) used in several experiments;
only a few of such pools were in existence. In the early days of the
ganzfeld, and given the objectives of the research, it is understandable
that researchers would want to forego that time and expense until the
reliability of the procedure had been better established, especially since
at the time it was reasonable to conclude that the possibility of biasing
the results by handling cues was remote.
In retrospect, this may not have been a wise decision. Nonetheless,
given the considerations discussed above, this and the other "flaws" Hyman
uncovered do not seem to be of the nature that would justify an inference of
.
general sloppiness in the conduct of the experiments.
In the final analysis, Hyman has failed to make a case that the flaws
he uncovered provide an adequate explanation for the significant results in
the data base. First, his internal analyses of the data have failed to
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plausibility of the "normal" hypotheses suggested by the flaws, and my own
analysis suggests that -- assuming reasonable competence and honesty on the
part of the experimenters -- the hypotheses are not particularly plausible.
On the other hand, the possibility that collectively these hypotheses can
account for the results cannot be ruled out. To show this seems to have
been Hyman's minimal objective and to that extent he has succeeded.
In conclusion, the ganzfeld experiments offer a genuine anomaly for
which no adequate explanation exists. The explanation can only be obtained
by further research. 2
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NOTES
1
There is strong circumstantial evidence that Hyman did not in fact utilize
his second feedback criterion (agent-percipient communication before
feedback) since: (1) the second criterion was not mentioned in the
discussion of this flaw in the text of Hyman's paper; (2) all experiments
to which Hyman assigned this flaw used single target sets, a precondition
for the first criterion but not the second; (3) there were only two
experiments to which Hyman assigned the flaw and Honorton (who only coded
the first criterion) did not, and in one of these it is easy to see how a
miscoding vis-a-vis the first criterion could have occurred.
2
Brief commentaries by other researchers on the ganfeld debate, as well as
a reply by Hyman to Honorton's defense, are scheduled to appear in a
forthcoming issue of the Journal of Parapsychology.
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Chapter 5
RANDOM-EVENT-GENERATOR RESEARCH
I. Schmidt Research Program
Perhaps the most important methodological advance in experimental
parapsychology during the past 15 years has been the introduction of
electronic random event generators (REGs), also called random number
generators (RNGs), for testing restricted-choice ESP and, more
predominantly, PK. Although the REG was first used in psi research in the
1930s (Tyrrell, 1936) its emergence as a standard piece of apparatus in the
psi laboratory can be traced to the work of physicist Helmut Schmidt (1969b,
1970c) .
Schmidt's device is representative of the REGs presently being used in
psi research. Electrical pulses pass a gate and arrive at a rapid rate
(e.g., one million per second) at a switch, which advances one step each
time. The switch is periodically stopped at one of its locations.
To
introduce a random element into this system, the choice of this location is
influenced by a time delay based on the arrival and registration of a beta
particle from a radioactive source (strontium-90) at a Geiger-Müller tube
or by the peaking of the output of an electronic noise source. The location
at which the switch stops defines the target selected by the REG. This
selection is recorded on mechanical counters inside the machine and in some
cases is also registered on paper-punch tape for a permanent record.
In
other applications, the REG can be interfaced to a computer and the results
recorded on disk or tape. The selection is also fed back to the subject by
the lighting of a lamp on the machine's face or by means of the attachment
of the machine to a peripheral output device. This description will be
further elaborated momentarily when particular applications are discussed.
Although the use of REGs has become widespread in parapsychology, by
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strongest and most consistent results have been from Schmidt 's own
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research program. Therefore, the first section of this chapter will be
devoted to a review of this program.
There are certain characteristic features of Schmidt's program that are
worthy of mention at the outset. Whereas most REGs are either boards that
fit inside microcomputers (especially the Apple II) or are otherwise bound
to main-frame computers or other laboratory hardware, Schmidt's machines are
self-contained and portable. This allows them to be used "in the field"
(e.g., subjects“ homes), which provides for a more relaxed and informal
testing environment. Schmidt feels this is crucial for obtaining positive
results. He also places a great deal of emphasis on properly motivating his
subjects and likes to have them "play" with the machine (i.e., do practice
tests) prior to formal tests, often undertaking formal tests only at times
when the subject is doing well on the practice tests.
Schmidt has published 14 experimental reports dating from 1969 to the
present. The methodology has evolved through four somewhat distinct phases.
Phase 1. In this phase, when the emphasis was primarily on testing for
ESP, the subject initiated each trial by pressing one of four buttons each
located under a lamp on the machine. This button-press caused the machine to
randomly select one of its four states as a target, which was indicated to
the subject by the lighting one of the lamps. In the first experiment
(Schmidt, 1969b), this was presented to the subject as a precognition task,
i.e., the subject was asked to guess which option the machine would select
and indicate his guess by pressing the button underneath the lamp of choice.
However, Schmidt recognized that the subject could also be successful either
by pressing the button at just the right time (precognition) or by forcing
the machine by PK to select the option guessed. In a subsequent experiment
(Schmidt & Pantas, 1972), Schmidt attempted to distinguish these
possibilities (at least to a degree) by building into the machine an option
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got a hit only when the target "4" was selected by the machine. This
mechanism precluded simple precognition as a possible explanation of a
significant result. The feedback was set up such that subjects were blind
as to whether the machine was functioning in this "PK" mode or the standard
precognition mode. Scores were significantly above chance to about the same
degree in both modes. Simple PK was ruled out in another version of the
experiment that was designed to test for clairvoyance (Schmidt, 1969a). In
this case a sequence of targets derived from a random number table and
prepared by an outsider was fed into the machine and substituted for the
machine-generated targets.
·
Phase 2. In this and subsequent phases, Schmidt's focus shifted
exclusively to PK. Instead of the subject activating each single trial by a
button press, a whole series of trials (or a run) was so initiated. The
number of trials per run varied from 100 to 1000, and the rate of event
generation varied from 1 to 300 per second. Runs were short, lasting from a
minimum of a few seconds to a few minutes each. The number of target
alternatives were generally two (i.e., binary) rather than four as in the
previous phase, although in later years probabilities as low as 1/64 were
utilized. Different modes of feedback were also explored. In the first
experiment of this phase (Schmidt, 1970b), the lamps on the machine were
arranged in a circular display and each hit or miss caused the light to
advance in the "right" or "wrong" direction around the display in a kind of
"random walk". Auditory feedback such as clicks or variable-frequency tones
were also utilized, as well as continuous polygraph tracings (e.g., Schmidt,
1973). In some cases where fast event generation rates were used, the
feedback was integrated over blocks of trials. In two experiments, the
subjects were animals and the feedback was selected so as to have
reinforcing properties. In one case, the subject was a cat placed in a cold
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'degrees Celsius) environment, and generation of the target events caused
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a heat lamp to be turned on (Schmidt, 1970a). In another case, generation
of target events allowed cockroaches to avoid electric shocks (Schmidt,
1970a, 1979a).
Phase 3. In the mid-1970s, Schmidt published a mathematical model of
psi inspired by physicists" attempts to interpret the "measurement problem"
in quantum mechanics (Schmidt, 1975). From an experimental point of view,
the most important implication of the model was that the choice of which
alternative the machine selects on a given trial is not determined at the
time of event generation but rather at the time the outcome of the event is
"measured" (observed) by a conscious entity, i.e., at the time of feedback
(Schmidt, 1976). If the observer happens to be a "psi source," the
probabilities of the occurrence of the possible outcomes diverge from their
a priori expected values in a manner related to the intent or wishes of the
observer, thereby producing significant evidence of psi. Schmidt's model is
an example of the so-called "Observational Theories."
In the methodologies of the preceding phases, recording of each event
on the internal counters of the machine and feedback of that event to the
subject occurred virtually simultaneously. The new model inspired Schmidt
to develop a methodology in which these procedures are separated in time by
minutes or even days. The most common procedure was to record a sequence of
events on magnetic or paper tape and later to have a subject listen to or
observe the tape or some other representation of its content.
In most
cases, the tape was presented in such a way that the subjects were led to
believe they were receiving immediate, contemporaneous feedback as in an
ordinary PK task (e.g., a Schmidt machine was used with the feedback being
defined by the tape). Usually, the subjects were asked to attempt to
influence the feedback (e.g., increase the number of randomly produced
clicks), although in a few cases they were asked to merely observe it
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click (i.e., a hit), which terminated the run (Schmidt, 1976, [Exp. 1]).
Results with these "pre-recorded" events were compared with results of
control conditions consisting either of contemporaneously generated events
or of pre-recorded events which were statistically evaluated but never
observed on a trial-by-trial basis. In one experiment, for example, pairs
of sequences were generated for each run and one member of each pair was
randomly selected to be presented to the subject as feedback. Only the
observed sequences proved to be statistically biased (Schmidt, 1976,
[Exp. 1, confirmation series] ).
Phase 4. In this most recent phase, the focus on PK with pre-recorded
events has continued. However, instead of each trial being generated
randomly and therefore susceptible to PK influence, true random selection is
limited to a "seed number" consisting of just a few digits. The
pseudo-random sequence of events fed back to the subject is generated from
the seed number by an algorithm which is impervious to PK (Schmidt, 1981).
The point seems to be that the seed number is selected so as to produce a
statistically biased sequence of events even though it is not directly
observed by the subjects. However, the theoretical rationale for the
procedure has not been fully developed or at least not fully articulated.
Statistical Evaluation
The output of Schmidt's REGs is amenable to simple and straightforward
statistical evaluation by normal Z-tests, or critical ratios (CRs) as they
are called in parapsychology. Schmidt has stuck to such tests almost
exclusively, although slight modifications have occasionally been necessary,
as in cases where results of machines having different a priori hit
probabilities are to be pooled (e.g., Schmidt, 1976, [Exp. 3]).
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Main Results
There is virtually no doubt that the results of the Schmidt REG
experiments cannot be attributed to chance. The 14 articles I reviewed
cited results of 33 experimental series, including 10 labeled "preliminary,"
"pilot," or "exploratory." Based on Z-tests of the total pooled trials in
each series, 25 of the 33 (76%) were significant at the .05 level,
two-tailed. In two of the seven nonsignificant studies, one of the two
experimental conditions yielded significant results (Schmidt, 1979b; Terry
& Schmidt, 1978). Of the remaining clearly nonsignificant series, four
involved tests on sub-mammalian species (e.g., algae, fruit flies) where it
is not clear whether significant results were expected (Schmidt, 1979a). In
one of the others, which also involved an infra-human species (cat),
significant scoring occurred in the first half of the test and the cat
seemed to have been noticeably less oriented toward the reward stimulus
during the nonsignificant second half (Schmidt, 1970a).
Of the 29 series where the direction of the results could be determined
from the report, scoring was in the direction presumably intended by the
subject in 21 of them (72%). When the direction of the Z-scores was defined
relative to the subject's intent (which was assumed to be for hitting unless
specified otherwise) and cumulated across series by the Stouffer method
(Mosteller & Bush, 1954), the resuling Z was a whopping 9.92. This figure
is somewhat conservative, because in four cases psi-missing was predicted by
Schmidt although presumably not intended by the subjects (Schmidt, 1970a,
confirmatory series; 1970b, confirmatory series, Schmidt & Pantas, 1972,
both series with groups). When the direction of the individual Z-scores was
defined in terms of Schmidt's predictions, the cumulative Stouffer Z was
14.85.
Because the a priori probability of a hit varies so much from
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However, estimates can be provided for the ESP studies (Schmidt, 1969a, b;
Schmidt & Pantas, 1972), all of which used P=1/4, and all but one of the PK
studies where P=1/2 was used (Schmidt, 1970a [cockroach experiment], 1970b,
1973, 1974, 1976, [Exps. 2 and 3], 1978). (The cat experiment [ Schmidt,
1970a] had to be eliminated because full data were reported for only half
the trials. ) Using the trial as the unit of analysis, the mean percentage of
hits for the ESP studies (MCE=25%) was 26.50%; for the PK studies
(MCE=50%), the mean was 50.53%. However, two-thirds of the trials in the PK
sample came from one experiment, which produced an abnormally low hit rate,
possibly because of an unusually rapid rate of event generation. With these
trials removed, the mean is elevated to 51.26%, which I think is a more
representative figure.
Results:
Independent Variables
As a general rule the rather modest variations of experimental
procedure that Schmidt employed in his experiments did not significantly
affect the results.
Subjects. In his early ESP experiments, Schmidt (1969a,b) gave a large
number of trials to a handful of subjects who had clearly shown promising
results on screening tests. Later on, larger samples of subjects were used
for whom screening was either minimal or absent, and there was no noticeable
dropoff in scoring rates. However, Schmidt did insist on providing his
subjects some opportunity to play with the machine prior to testing and he
attributed one of his unsuccessful series to the fact that in this
particular case subjects were not given that opportunity (Schmidt, 1978).
Feedback. Neither the type of feedback display nor the rate of feedback
has affected scoring in Schmidt's experiments, although fully controlled
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Pre-recorded events. Results of series with pre-recorded events
(including pre-recorded seed numbers) have been comparable to those in
series with real-time events. This conclusion also applies to experiments
where the two types of trials were compared in the same series (Schmidt,
1976 [Exp. 2], 1979b).
There is some evidence that the following two variables might affect
scoring, but the evidence is equivocal.
Rate of event generation. In one PK experiment with a binary REG,
Schmidt (1973) found that the scoring rate was significantly lower when the
machine generated targets at 300 per second (50.4%) than at 30 per second
(51.6%). However, this conclusion must be viewed cautiously, because
subjects were not assigned randomly to the two conditions, some subjects
participated in both conditions, and subjects were not always blind to the
generation rate. In two subsequent experiments (Schmidt, 1974), results
with a machine generating trials at 100 per second were compared to results
with a machine generating trials at one per second. In these experiments,
trials from the two machines were interspersed and subjects were blind as to
which generator produced each trial. In the pilot experiment with four
subjects, scoring was significantly higher with the slow REG than with the
fast one (58% vs. 51.2%). In the confirmatory experiment with 35 subjects,
the difference was in the same direction but not significant (55.3%
vs. 53.8%). Two experiments with pre-recorded targets (Schmidt, 1976
[Exps. 2 and 3]) also used generation rates of 300 per second and although
no systematic comparisons are possible, the mean hit rate on these (fast
rate) trials (51.8%) is actually higher than the overall average (51.26%).
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Intent. In one experiment (Terry & Schmidt, 1978), trials where
subjects were asked to use PK to alter the REG output were compared, within
subjects, to trials where they were not to attempt PK influence but merely
to attend to the feedback tones. Significant scoring was restricted to the
intentional PK condition, although results were unexpectedly in the missing
direction and significant by only one of the two tests the authors used. No
statistics comparing results in the two conditions were reported.
One other
experiment in which subjects were asked to listen to the feedback without
attempting to influence the REG yielded clearly significant positive results
(Schmidt, 1976 [Exp. 1]). Collectively, these results suggest that
"intent," at least in the sense of conscious effort to influence the REG, is
not necessary to achieve the predicted effect but might be facilitative.
Criticisms
The two major critics of Schmidt's experiments have been C.E.M. Hansel
(1980) and Ray Hyman (1981). Their principle concerns have been inadequate
security against fraud and inadequate randomization tests.
Security. Hansel, who only considered the work of Schmidt through 1970,
focused his criticism on the fact that in most of these experiments the
target was changed during the course of the experiment. In two of the three
ESP series (Schmidt 1969a, b) subjects sometimes aimed for hits and sometimes
for misses. In the PK experiments (Schmidt, 1970a, b) the target was changed
halfway through the experiment. Hansel's concern was that the nonresettable
electronic counter inside the REG did not take account of the change in
target and actually recorded chance outcomes in the series where the changes
occurred. Although the changes were recorded on the paper tape that
constituted the other independent record and the two records matched, Hansel
felt that this was not an adequate provision. Hansel was somewhat vague in
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his criticism (perhaps for legal reasons). but it would appear that his
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concern was less with innocent recording errors than with the possibility
that Schmidt could have cheated by improperly assigning the target direction
after the data had been collected.
1
Hansel seemed reasonably satisfied that the machine precluded fraud by
the subject (at least he did not raise this possibility explicitly), but
Hyman expressed concern that Schmidt seemed to place too much trust on the
machine to provide security and that " ... subjects, for the most part, are
unsupervised and unobserved" .(p. 37).
Randomization tests. For Schmidt's experiments to be evidential of psi,
it is generally considered necessary that the output of the REG be unbiased
in the absence of attempted PK influence. Although acknowledging that
Schmidt did indeed conduct randomization tests, both Hansel and Hyman were
. concerned that the tests were not conducted systematically. For the most
part, Schmidt conducted long series of control trials periodically during
the course of an experiment. Hyman in particular felt that such tests might
be insensitive to short-term biases that might operate in actual
experiments, where the runs consist of many fewer trials. For example, the
machine might only be biased for the first few trials after it is turned on
and this would not show up in long control sequences. The critics suggested
that a better procedure would have been to collect runs in pairs, randomly
assigning one member of the pair as the experimental run each time.
Hyman also criticized the fact that the randomization tests did not
check for biases beyond the second (doublet) level.
Evaluation
Security. Although the use of a machine like Schmidt's REG does
minimize opportunities for subject fraud, it is nonetheless reasonable to
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unsupervised and unobserved is incorrect. Although the reports tend not to
be as thorough on this point as one would like, it is clear that Schmidt is
either with the subject or with the REG in most cases. In one case Schmidt
(1969b) noted an exception for one subject but also noted that the results
of the experiment did not depend on that subject.
The possibility of subject fraud is further minimized in the
experiments using pre-recorded targets, as the subject is not present when
the target sequence is generated. Subject fraud is remote indeed if an
independent record of the target sequence is kept elsewhere while the
targets are being observed by the subject. Such records were reported as
being kept in experiments where the subject was allowed to take the tape
home (Schmidt, 1976 [Expt. 1], Schmidt, 1978), but it is not clear whether
they were kept in the other experiments. If independent records were not
kept, it is conceivable that a subject might somehow substitute a biased
tape for the one in which the target sequences had been recorded. However,
this would require a fairly elaborate ruse on the part of multiple subjects,
many of whom were relatively unselected volunteers with no apparent
investment in being certified as psychic ..
Fraud by the experimenter is, of course, always more difficult to rule
out, and the fact that Schmidt usually works without a co-experimenter makes
the hypothesis particularly tempting to some critics. It is difficult to
understand why Hansel harps on the nonresettable counters in this
connection, however, because it would have been easy for Schmidt, who builds
the machines, to tamper with the counters either before or after a session
if he were inclined to cheat, even if he were using the set-up Hansel
recommends. Moreover, Hansel's critique fails to note that the goal for
each set of trials (high-aim or low-aim) is registered on the paper tape
along with the events themselves.
Schmidt has recently taken the experimenter-fraud criticism to heart,
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is responsible for generating the (pre-recorded) event sequence while the
second experimenter determines the random order of target directions across
runs or determines which of the recorded tapes are to be observed by the
subject and which are control tapes. Thus, neither experimenter by himself
can artifactually produce significant results by generating a faulty
sequence. Variations of this procedure have now been tried in two
experiments (Terry & Schmidt, 1978; Schmidt, Morris, & Rudolph, in press),
once with significant results. Of course, this procedure does not rule out
collusion by the two experimenters and so far all the experimenters have
been sympathetic to parapsychology.
1
Randomization tests. The critics are correct in pointing out that
Schmidt's early randomization tests do not adequately exclude the
possibility of short-term biases, at least those that might occur just after
the REG is activated for a run. However, the argument is weakened by the
fact that the critics have so far not been able to articulate a mechanism
that would produce such a bias. Short-term biases that would occur
intermittantly at other times would have to be consistent in direction to
account for the results Schmidt found in his experiments, yet in that case
they also would accumulate and thus be revealed in the randomness tests
Schmidt did undertake.
1
1
The one piece of empirical evidence that can be cited against
short-term bias of the former type as an explanation for Schmidt's results
is the fact that the deviations covaried with changes in target.
Ironically, it is the very procedure that Hansel criticized for security
reasons that provides this evidence. For example, the bias hypothesis would
have to explain why the direction of these biases would suddenly and
consistently change when a subject started aiming for misses instead of hits
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how the bias hypothesis can account for such covariations without taking on
unparsimonious ancillary assumptions.
In Phase 3, Schmidt began using control procedures which conformed more
closely to those demanded by his critics (Schmidt, 1976). In the first two
experiments described in this paper, Schmidt reported control runs of the
same length as the test runs. Furthermore, in two of the experiments from
this phase (Schmidt, 1976 [Expt. 1], Terry & Schmidt, 1978), pre-recorded
control tapes were made at the same time as the pre-recorded experimental
tapes; which tape was which was determined randomly -- a procedure very close
to that suggested by the critics.
It should be mentioned, however, that Schmidt is not consistent in his
reporting of randomization tests. Half of the 14 reports I reviewed did not
report randomization tests and the descriptions in the others varied in
degree of detail. However, I could find no relationship between the
adequacy of the randomization test as reported and the significance of the
results.
Finally, what about the possibility of dependencies between random
events beyond the second level?
Such dependencies would, strictly speaking,
violate the assumptions of the statistical tests Schmidt used. However, if
they were to have biased the results of Schmidt's experiments they would
have had to manifest at the singlet level as well, and if that were the case
a singlet bias would also have appeared in the randomization tests. If the .
higher level dependencies did not favor the target at the singlet level,
they would also have tended to diminish the likelihood of significant
results in the experiment proper. Thus, the possibility of higher level
dependencies does not appear to provide a plausible explanation of Schmidt's
findings.
Data selection. A possible criticism not made directly by other critics
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is attributable to selective publication of positive findings. Schmidt
often refers in his reports to exploratory testing with various outcomes.
He acknowledges a preference for testing subjects formally only at times
when they are doing well informally, which implies that sometimes subjects
do not do well informally. REG experiments are very economical timewise,
and it is conceivable that Schmidt has accumulated vast amounts of
nonsignificant and unreported data.
However, Schmidt's procedure is not a problem if certain subgroups of
trials are specified beforehand as formal tests and reported irrespective of
outcome. Barring outright dishonesty on Schmidt's part, this provision
seems to have been met by the 14 experiments in the articles I reviewed
which Schmidt defined as "confirmatory" or "main" experiments. The
collective results of these experiments are actually better than the overall
average (Stouffer Z-15.60).
A related potential artifact concerns optional stopping, in particular
not specifying in advance the-number of trials in the experiment. I
determined that in 15 of the series reviewed, it is stated or clearly
implied in the report that the number of trials was stated in advance. In
two of these cases, two alternatives were specified in advance but the
degree of selection could not conceivably account for the strong results
obtained (Schmidt, 1969a, b [Exp. 2]). In a third, case, a range of from
55,000 to 70,000 trials was specified (Schmidt, 1969b [Exp. 1]). . Here the
possibility of the artifact being fatal is still remote, but nonetheless
conceivable. Discounting this experiment, the remaining 14 experiments with
clearly prespecified numbers of trials have a Stouffer Z of 8.42. It is
likely that in most of the other experiments the number of trials was also
prespecified even though it was not formally stated.
Some commentators have expressed concern over Schmidt's procedure of
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high-scoring subject when scores began to decline. However, it seems clear
that such a procedure is statistically acceptable as long as the total
number of trials is prespecified.
Source of the effect. An interesting point of disagreement among those
who at least tentatively interpret Schmidt's research as providing evidence
for a paranormal principle is whether the source of the effect is really
Schmidt's subjects or Schmidt himself. Several points can be made in favor
of the latter hypothesis:
1. Although other investigators have achieved significant effects in
REG research, no one has done so as consistently as Schmidt or has achieved
such strong (by parapsychological standards) effects.
2. There are growing indications that directing effort toward achieving
a psi effect is not necessary for the effect to occur. This was
demonstrated in one of Schmidt's own experiments (Schmidt, 1976 [Exp: 1]) as
well as in experiments by others (e.g, Palmer & Kramer, 1984; Stanford,
Zenhausern, Taylor, & Dwyer, 1975). These experiments suggest that it is
the need to achieve a certain outcome in contrast to the effort to achieve
it that is crucial. If so, then Schmidt, as the experimenter desirous of
positive results, becomes at least a potential psi source.
Schmidt's model assumes that observation (feedback) of the trials of an
experiment is necessary for influencing them. In one of his later
experiments, he indeed established that only those pre-recorded event
sequences observed by his subjects (and not control tapes generated at the
same time) were biased, thereby suggesting that the subjects biased the
original generation of the sequences retroactively at the time of feedback
(Schmidt, 1976 [Exp. 1]). However, coming from a more traditional
theoretical orientation, one could argue that it was Schmidt who used PK
proactively to bias the event sequences at the time they were being
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generation which member of each pair of sequences would be the experimental
one and which the control, this lack of knowledge does not necessarily
preclude his having used psi, albeit without conscious intention to do so.
Schmidt himself has been foremost among those parapsychologists arguing that
psi is "goal directed" which implies, among other things, that one can
achieve a desired goal by PK without knowing the mechanism needed to produce
it. One of Schmidt's other experiments (Schmidt, 1974) has shown that
significant results can occur without subjects" knowing which machine is
operative on a given trial. Subjects in another experiment (Schmidt, 1981)
did not realize that their real target was a random seed number and not the
pseudo-random event sequence derived from it and to which their attention
was directed; in fact, they never observed the seed numbers at all. Thus,
it is questionable whether Schmidt's ignorance of the contingencies at the
time he generated the pre-recorded event sequences is any greater or more
important than the ignorance of the supposed subjects when they observed
them.
3. In one experiment (Schmidt, 1970a) the subjects were cockroaches and
the REG was biased so as to increase the number of painful shocks they
received. At least from the standpoint of motivation theory, this result
makes little sense if one assumes that the cockroaches were the psi sources.
It makes somewhat more sense if one assumes that Schmidt was the psi source,
especially if one is safe in assuming that Schmidt does not like
cockroaches!
II. Princeton Research Program
The other major research program in parapsychology using REGs is being
undertaken by Robert Jahn, Dean of the School of Engineering at Princeton
University, in collaboration with psychologists Roger Nelson and Brenda
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Im broda annoont to Schi
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Instead, the output of a commercial electronic noise source is filtered,
amplified, and sampled by a train of gate pulses. The target is determined
by the sign of the noise (above or below the zero crossing) at the time of
each sampling.
The Jahn team uses different terminology than does Schmidt to define
the sampling regimen. To maintain uniformity of exposition, I will
translate Jahn's terminology into Schmidt's, as the latter is more standard
within parapsychology.
In his formal tests, Jahn collected runs each consisting of 200 trials
generated at either 100 or 1000 per second. Thus, Jahn's runs were much
shorter than Schmidt's. Unlike Schmidt, Jahn alternates the target (from
the point of view of the REG) between trials; i.e., positive and negative
noise alternate as hits on successive samplings. The subject, whose task is
to use PK to bias the REG output in the target direction, can activate the
REG in one of two modes. In manual mode a button press activates only a
single run.
In automatic mode it activates a sequence of 50 runs. The
subject receives continuous feedback on LEDs consisting of the number of
runs so far completed, the number of hits in the last run, and the running
average of run scores completed in the test. The latter is displayed most
prominently.
The number of hits in each run is registered in the REG, which also
computes and records the mean and standard deviation of the run scores of
each 50-run block. These data are eventually transferred to magnetic tape
for statistical analysis by computer. To provide redundancy, data are also
recorded on paper tape and manually in a logbook.
Like Schmidt, Jahn tries to maximize the comfort of the subject and
provides for practice runs prior to formal testing.
Subjects are encouraged
to undertake formal tests only when they are in the mood. Subjects can also
determine the length of each session, provided it includes at least five
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possible.
Each session consists of some runs where the subject aims for a high
score (PK+) and some runs where the subject aims for a low score (PK-). The
sequence of target aims is sometimes determined by the subject's
preference- volitional mode -- and sometimes by means of an objective random
process-instructed mode -- the nature of which is not specified in the
report.
Interspersed among the PK runs are also a number of baseline runs
initiated by the subject but for which the subject attempts no PK influence.
These serve in effect as randomization tests.
The sessions were organized into series, which range from 500 to 7500
runs per condition. The formal experiments consisted of 61 series
contributed by 22 subjects. Each subject contributed from 1 to 14 series,
with 44% of the series contributed by two individuals. The total number of
runs was 569,450 (or 113,890,000 trials). The latter is approximately 189
times the number of trials in all of Schmidt's published experiments
combined.
Statistical analyses of the data consisted primarily of single-mean
t-tests comparing mean run scores to MCE (=100), using an empirical variance
estimate. This is in contrast to Schmidt, who uses Z-tests with a
theoretical variance estimate.
Jahn also uses various graphical representations of his data, in
particular, plots of the cumulative deviation of mean run scores over runs
for PK+, PK-, and baseline runs, respectively. These are capable of
reflecting variations in a subject's performance over time.
Results
The main presentation of results was restricted to those formal series
consisting of 200 trials per run. These comprise 390,200 runs, excluding
baseline runs. The mean number of hits per run for the PK+ runs (exactly
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half the total) was 100.04 (t=2.68, P <. 004, one-tailed). The mean number of
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hits for the PK- runs was 99.97 (t-2.16, p =. 016, one-tailed). Defined in
terms of the subject's intent (i.e., missing in PK- runs equals hitting),
the combined results were associated with t=3.42, p=3x10-4, one-tailed. The
percentage of hits was 50.02%. This is much lower than the 51.26%, or the
more conservative 50.53%, estimated for Schmidt (see p. 103).
Jahn also broke down his data in terms of three independent variables:
mode of activation (manual vs. automatic), mode of target-aim selection
(instructed vs. volitional), and rate of event generation (100 vs. 1000 per
second). These analyses revealed, first, that the significance was entirely
attributable to runs where the target aim was selected voluntarily
(volitional). The hit rate for these runs was 50.04% (t=4.24, p<10-5,
one-tailed) compared to 50.01% for the runs where the target aim was
determined randomly.
Both event generation rates yielded significant overall results.
However, the slower rate (100 per second) yielded slightly higher scores
(50.05%) than did the faster rate: (50.02%), especially in the PK- condition.
I computed a t-test of the difference based on the data reported by the
authors and determined that the superiority of the slower generation rate
(for both PK+ and PK- runs combined) was significant (t=2.04, p <. 05).
However, this analysis may be misleading and will be discussed further in
the evaluation section. Mode of activation had no significant effect on the
results.
Examination of the cumulative run score graphs led the authors to
conclude that their subjects had individual scoring patterns, which they
called "signatures," that were consistent within each subject for a given
specification of test parameters.
However, no statistical analyses were
offered to support this conclusion.
The mean of the 179,250 baseline runs was 100.005, which was acceptably
close to the expected value of 100. The variance of the scores was also
within chance limits, but a graph of the distribution exhibited a marked
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excess of scores right at 100.
The authors later presented a separate set of analyses with the series
as the unit (Jahn, Nelson, & Dunne, 1985). According to this analysis, the
displacement of the mean Z-score remained significant for the PK+ runs
(mean=+.377; t[60]=2.59, p <. 02, one-tailed) but not for the PK- runs
(mean --. 262, t[60]=1.61). As expected, the mean for the baseline was very
close to chance (mean=+.023).
However, this analysis revealed some curious differences in variances.
The variance of the series scores for the PK+ runs was suggestively high
(F[60, OO ]=1.295, p <. 20) whereas that for the PK- runs was significantly
high (E[60, CO ]=1.616, p <. 02). It is likely that the high variance was
responsible for the failure of the mean to reach significance in the PK-
condition. The really curious finding, however, was a corresponding
restriction of variance of the series scores for the baseline runs that
approached significance (F[49,00 ] =. 663, p <. 10). The restriction was
caused by an absence of any Z-score values greater than +1.645 or less than
-1.645 in the distribution. . (The p-values reported here are more
1
conservative than those reported by the authors, presumably because the
latter were using one-tailed tests. I find two-tailed tests more appropriate
for this application.)
In addition to the formal series, 34 exploratory series comprising a
total of 103, 950 test runs (PK+ or PK-) have been conducted (Nelson et al.,
1984). Two subjects contributed all but one of the series. The procedure
differed from that of the formal series in that the number of trials per run
was 100 or 2000 instead of the usual 200, or the number of runs per
condition per series was low (approximately 1000).
Only the cumulative results of five series with 2000 trials per run
provided by one of the two subjects tested with this protocol (who happened
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Results from the remaining subject, who completed only one series at this
rate, were close to chance.
Finally, 12 exploratory series totaling 60,000 test runs were conducted
with the event sequence being generated from an algorithm as opposed to the
REG. Such a pseudo-random sequence presumably cannot be influenced by a PK
force, so success would appear to be possible only by entering the sequence
at a point that would yield a "biased" subset of numbers embedded in it.
Significant results in line with the formal series were nonetheless achieved
in the cumulated seven series performed by the same subject who obtained the
significant results in the previous series. The two subjects who completed
the remaining series provided only chance results.
Baseline scores in the combined exploratory series, and specifically in
each of those subsets which provided significant results in the experimental
conditions, did not deviate significantly from chance expectation.
Criticisms
No critiques of Jahn's research by outside commentators have yet been
published, to my knowledge.
Evaluation
Controls and security. The Jahn team has done a better job than Schmidt
in providing adequate baseline tests, as Jahn's baselines were were all
collected in the same sessions as the experimental data and were of
identical structure. Jahn also reported more extensive tests of the
machine's performance outside the test sessions, including checks on the
function of separate components. Internal checks during all operations were
used to assure that proper input voltage of the noise diode was maintained
and that internal temperature was not correlated with machine performance.
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The one deficiency I can cite regarding security is that Jahn does not
fully document what precautions were taken to preclude data tampering by
subjects. This omission is particularly significant because an experimenter
was not present in the room with the subject during formal sessions. As it
would appear that the fundamental hardware for testing, including the REG
itself, was located in the same room as the subject, tampering with the
equipment is a theoretical possibility. On the other hand, such tampering
would seem to require computer sophistication on the part of the subject as
well as (in all likelihood) knowledge of the particular setup being
employed. If failsafes were utilized to preclude such tampering, they are
not described in the reports.
Data selection. The Jahn team appears to have been conscientious in
reporting all the exploratory and formal- series they have undertaken.
However, it is less clear that the distinction between these two subclasses
of experiments was made in advance. The exploratory series yielded somewhat
weaker effects overall than the formal series (50.01% hits vs. 50.02% in the
formal series). If all the series reported were pooled, it is not certain
that the overall result would differ significantly from chance.
However, this issue loses importance when one considers how the
significance is distributed among the various subjects tested.
In the
formal series, only two of the 22 subjects tested provided independently
significant results. The bulk of the significance is attributable to one of
these subjects, who contributed 14 of the 61 formal series (23%). In these
series, this subject achieved a hitting rate (in terms of his or her intent)
of 50.05% over 105, 150 runs (Z=4.49, p<10-4).
When the results of this
subject are eliminated, the remaining series are no longer significant
(50.01%, Z=1.36). This subject's scoring rate is significantly higher than
that of the other subjects combined (2-3.14, p <. 005)
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Moreover, this subject is the same subject who provided the significant
results, and the only significant results, in the exploratory series. The
overall results of this subject are clearly significant and consistently in
the expected direction, i.e., above-chance scoring in the PK+ runs and
below-chance scoring in the PK- runs. Twenty-eight of the 35 series (80%)
in which this subject participated produced higher scores in the PK+
condition than in the PK- condition, which in itself is a significant
outcome (x-[1]=12.60, p <. 001). The mean t of the 35 series is +0.84,
s.d .= 1.35, which is significantly different from zero (t[34]=3.70, p <. 001).
The one puzzling finding is the failure of this subject to maintain his or
her usual scoring level in the short 1000-run series, which were otherwise
methodologically identical to the formal series.
A more uniform distribution of scoring across subjects is suggested by
analyses using the subject as the unit. A mean run score on the
experimental runs was computed for each subject by reversing the direction
of the PK- scores and taking the average of the PK+ and PK- scores, weighted
by the number of runs in each condition. The mean of these scores was
100.03 which is significantly above chance, although barely so (t[21]=1.74,
P <. 05, one-tailed). However, when the experimental scores are contrasted to
the baseline scores using a dependent t-test, the result falls just short of
significance (t[21]=1.67). Neither analysis would be significant were the
high-scoring subject eliminated, but this analysis nonetheless provides some
evidence that the effect is uniformly distributed within the sample.
However, the evidence is weak and can only be considered suggestive.
Optional stopping. It is not stated whether the total number of trials
and the number of trials completed by each subject were specified in
advance. In principle, this leaves the Jahn research open to the criticism
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hypothesis is suggested by the fact that the degree to which optional
stopping was potentially operative seems to have varied from series to
series. In 24 of the series, the number of runs in the PK+ and PK- modes
was identical. In 23 of these, the number of runs per type was either 2500
or 5000; in the remaining series it was 3000 runs. It is very unlikely
that optional stopping was a factor in these series. Thus, if the
optional-stopping hypothesis were correct, one would expect lower scoring in
these series than in the other 37. As a dependent variable, I chose the
t-score supplied by the authors which reflected the difference in scoring
between the PK+ and PK- conditions for each series. The mean t-score for
the 24 "uniform" series is +0.74, which is higher than the mean of +0.22 for
the remaining series (t[59] =- 1.51, n.s.) and opposite to the direction
predicted by the optional-stopping hypothesis. In fact, the mean for the
uniform series is independently significant (t[23]=3.38, p <. 005). Thus, the
optional-stopping hypothesis can be safely discounted.
Independent Variables
The interpretation of the results relating scoring levels to mode of
target-aim selection and rate of event generation is complicated by the fact
that not all subjects contributed equally to the various levels of these
independent variables. Only three subjects contributed runs at the slow
generation rate. Further analysis of the data reveals that the apparent
superiority of scoring at the slower rate (see p. 115) is attributable to
the fact that these three subjects had higher scores overall than the other
subjects. (Note that the authors never claimed superiority for the slower
rate, but it might be inferred from one of their tables.) Mode of target-aim
selection (volitional vs. instructed) was more evenly balanced, but 12 of
the 22 subjects contributed to only one of the two conditions. However, the
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that when to
anafriende room inndonato in anamient fre it mig.

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held up in the data of the one significant subject but was actually stronger
among the remaining subjects. In fact, the hit rate among the remaining
subjects in the voluntary mode was 50.03% (Z-3.19, p <. 01), providing further
evidence that some of these other subjects may have exhibited some psi in
the experiment.
Baseline
.
Although the statistical evidence for restricted variance in the
baseline runs is in my judgment less than the authors claim, the suggestive
trends that were uncovered are perhaps worthy of some tentative
interpretation. Could it be, for example, that subjects unwittingly exerted
a PK influence in order to assure that the baseline data were "good
baselines," i.e., conformed closely to MCE? Such an interpretation would
coincide with the assumption of Stanford's (1974a, b) PMIR model that PK does
not require intention and effort on the part of the subject.
Intuitive Data Sorting
Up to this point, we have assumed that if the REG data are ultimately
explainable by some paranormal principle, that principle implies some causal
influence on the REG; i.e., it involves PK. An alternative interpretation
is suggested by a model called "intuitive data sorting" (IDS) proposed by
May, Radin, Hubbard, Humphrey, and Utts (1985) to account for REG PK data
generally. According to this model, significance occurs because of a
psi-mediated selection of the starting point of the sequence of random
events so as to capture locally "biased" subsequences. For example, if
significance is defined as p <. 05, one of every 20 sequences from a truly
random source should be significantly "biased." If such sequences were
captured more frequently than 1 in 20 times, a cumulatively significant
deviation could result. An attractive feature of the IDS model is that it
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statistical significance to increase as N increases, a trend that is evident
in the actual data base (May et al., 1985). It is also noteworthy that
Schmidt had considered a similar hypothesis several years earlier (see
p. 98).
May's model could be more appropriately labeled "intuitive data
selection," since no sorting is thought to actually take place. In other
words, favorable subsequences are selected from the total, ongoing sequence,
but there is no preordained set of outcomes that are sorted into different
categories. A true sorting model could, however, be applied to Jahn's data
by hypothesizing psi-mediated assignment of "random" run scores to the PK+,
PK-, or baseline categories. The fact that results were better in the
"voluntary" mode than in the "instructed" mode could be interpreted as
supporting such an interpretation, since the latter gives the subject more
flexibility and control in selecting the run type. Such selection is
possible in the "instructed" mode but it would require some kind of
psi-mediated selection of the random number which is the direct cause of the
determination of run type, and the decision would then be forced for the
entire 50-run block.
An important implication of this model is that the total distribution
of scores, irrespective of type, must conform to a true Gaussian. This
criterion is met when the run is taken as the unit of analysis, but when the
series is taken as the unit, there are not enough scores in the middle of
the distribution to form a true Gaussian. This latter result, however, is
not
necessarily inconsistent with the sorting model. The expectation that
the
series scores should form a Gaussian distribution in this case assumes
that the run scores are randomly assigned to type (PK+, PK-, or baseline)
within the series. If this is not true, distortions of the distributions of
series scores could easily result. For instance, the depressed variance of
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be closer to 50:50 than expected by chance. One could speculate, for
example, that as subjects noted an unusually high proportion of outcomes in
one direction in the baseline condition they began to produce outcomes in
the opposite direction to compensate. High variance in the PK+ and PK-
conditions could result if assignment of higher run scores to the PK+
condition occurred only in some of the series, an assumption which is
consistent with the already stated conclusion that the anomalous scoring in
these conditions seemed to be largely attributable to one of the subjects.
Such a situation would cause a distribution of series t-scores which
includes a small group of highly positive t-scores added to a larger group
of t-scores closely conforming to a true Gaussian, thereby increasing the
variance of the distribution as a whole. The important point is that the
variance effects uncovered at the series level can be obtained by simple
rearrangement of a perfectly random "chance" distribution of run scores.
Strictly speaking, the sorting model implies that the proper unit of
analysis is not the run but whatever number of runs a subject completes in
succession without having the option to change run type (e.g., PK+ to PK-).
It is not stated in the reports what this unit is, and it may have varied
from series to series or even within series. In any event, the same
principles apply taking this as the unit of analysis as with taking the run
as the unit. Assuming these new unit scores, summing over type, form a true
Gaussian, judicious assignment of them to type could produce the effects
uncovered at the series level.
Finally, it should be stressed that all these models are speculative,
and at this stage there is no reliable basis for selecting among them.
However, it is worthy of mention that a paranormal model need not assume a
causal effect on the mechanism of the REG to account for the results of
Jahn's experiments or, for that matter, REG data generally. The issue is
important, because its resolution could influence the kinds of applications
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NOTE
1
The Z-scores are based on all trials, pooled over experimental conditions.
When Z-scores were provided for only one condition, total Z-scores are
estimated assuming chance scoring (Z=0) in the condition not reported.
When
no Z-score was reported at all, it is assumed to be zero.
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Chapter 6
THE DELMORE EXPERIMENTS
Perhaps the most dramatic psi results to be produced by a single
subject in the last twenty years have been provided by Bill Delmore (B.D. ),
who at the time was a law student at Yale University. He was tested in a
series of formal restricted-choice ESP experiments at J.B. Rhine's Institute
for Parapsychology in the early 1970s. The principal experimenters were
Dr. B.K. Kanthamani, a psychologist and experienced parapsychologist, and
Dr. E.F. Kelly, a cognitive psychologist who had only recently become
involved in parapsychology. Secondary contributions were made by Dr. Irvin
Child, a senior psychologist and professor at Yale. I will begin by
describing the methods and results of the three main elements of the
research program with B.D.
Single-Card Clairvoyance
Method
The single-card clairvoyance (SCC) method was devised to be the better
controlled of the two card-guessing methods utilized (Kanthamani & Kelly,
1974a, b). Ten identical decks of standard playing cards were thoroughly
mixed and scattered face down inside the bottom drawer of a desk. (These
decks were periodically rescattered or replaced during the course of the
experiment. ) The experimenter was seated at the desk facing B.D., who was
seated at the other side of the desk six to eight feet away. For each trial
the experimenter "randomly" picked out a card from the pile in the drawer
and, without looking at it, placed it inside a 3 3/4"x2 3/4" opaque folder.
The experimenter then held the folder up to B.D. such that the back side of
the card inside the folder was facing him. B.D. called out his response,
after which the experimenter recorded the call, removed the card from the
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sheet. For most trials, B.D. received immediate feedback as to whether the
response was correct. In one series, B.D. was asked to make "confidence
calls"; i.e., to note those trials where he felt particularly confident
that the response was correct. (B.D. reported that this procedure was
stressful, raising the possibility that he might have earmarked certain
trials for extra effort and then chose them for confidence calls.) Each run
consisted of 52 trials, with a break generally occurring after each 26
trials.
A preliminary experiment of 65 runs was conducted. with Child as the
experimenter, which later was reported as having been extended to 74 runs
(Kelly, Kanthamani, Child, & Young, 1975). The main experiment consisted of
46 additional runs divided into four series. For Series 1 through 3,
Kanthamani was the experimenter, whereas in Series 4 her husband, also a
psychologist and parapsychologist, served as experimenter. In Series 2
through 4 the one who was not the experimenter was present in the room as an
observer. Other observers were sometimes present as well. Confidence calls
were invited in seven of the ten runs of Series 3. Feedback was withheld in
179 of the 2392 trials at B.D.'s request. The number of runs for each
series was specified in advance.
The principal method of analysis was a procedure devised by R.A. Fisher
(1924) for just this kind of task. Briefly, a composite Z-score is
generated based upon the deviations from the expected values for each of the
nine possible combinations of hits and misses on the attributes of number,
color, and suit. The statistic was supplemented by various other chi-square
tests
based on the same general "goodness-of-fit" principle.
Results
The results of the Child experiment were marginal and not reported in
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he DeImore Experiments
upturn of scoring on the last nine runs of this experiment was also noted,
although it is not stated whether the Fisher Z was independently significant
for these runs. The upturn is probably attributable to the fact that these
runs were administered during the same period of time as the more successful
main experiment.
The Fisher Z for the main experiment (Kanthamani & Kelly, 1974a, b) was
highly significant (Z=10.73) and was independently significant for each of
the four series except the first. The effect was concentrated in an excess
of "exact hits" (getting the card completely correct) which was three times
the expected number (Z=13.00). The number of exact hits also exceeded that
expected given the hit rate on the component attributes (Z=5.8). With the
exact hits removed, there was still an excess of hits on numbers (Z>7) but,
surprisingly, a significant deficit of hits on suits (Z =- 3.2). B.D. scored
somewhat better on the 179 nonfeedback trials than on a control set of 289
feedback trials from the same runs (no statistics reported), but
interpretation of this finding is ambiguous because the nonfeedback trials
were selected by B.D. at those times he felt "hot," as the authors note.
Finally, of the 20 confidence calls, 14 were exact hits, which comprised
over 50% of the 25 exact hits in the runs where confidence calls had been
invited. The authors also note the related point that B.D.'s scoring
success tended to occur in "bursts" throughout the experiment.
The data from the main experiment were later subjected to additional
analyses in search of systematic errors in B.D.'s misses that might shed
light on the cognitive processes involved (Kelly et al., 1975). To provide
a baseline for these analyses, B.D. completed 75 runs in which the targets
were slides of playing cards projected on the screen through a tachistoscope.
at 1/125 of a second. B.D. reported that the perception of these slides
corresponded to the visual images of the targets he experienced during the
ESP tests.
Multidimensional scaling (MDS), canonical correlation, and other
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tasks in his pattern of errors in detecting the cards" numbers. Although
the lower information rate prevented the demonstration of a statistically
significant error structure in the ESP data, the pattern that did emerge was
found to correlate significantly with the more reliable pattern uncovered in
the visual data. Moreover, the correlation was found to be attributable
almost entirely to the half of the ESP runs where the scoring level was
highest, as one would expect. Also as one would expect, the confusions on
both tasks consisted primarily of confusing the face cards with each other
and the Ace, 2, and 3 with each other. MDS could not be applied to an
analysis of errors regarding suits, but chi-square tests revealed in both
sets of data a tendency for B.D. to confuse suits of the same color, the
significant correlation again being attributable to the high-scoring ESP
runs.
(Further analyses by Kennedy [1979] revealed other confusion
structures in the chance-scoring ESP runs [including, in some cases,
confusing suits of opposite color], whereas no confusion structure seemed to
be present in the low-scoring [psi-missing] runs.) Kelly et al. concluded
that their results demonstrate "an overall structural resemblance between
ESP errors and visual errors" (Kelly et al., 1975, p. 26) and they
interpreted the finding as evidence that "on a significant fraction of
occasions on which B.D. obtains ESP information, he encodes it in the form
of visual imagery" (p. 27).
Following a discussion of possible artifacts (to be dealt with later),
the authors concluded that "The procedures employed in these experiments
seem sufficiently rigorous to create a strong presumption that the effects
reported are genuine ESP effects" (Kanthamani & Kelly, 1974b, p. 24).
Shuffle Method
For each run, the experimenter shuffled one of over 24 decks of
standard playing cards ("target" deck), to which B.D. was reported to have
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shuffled another of these decks ("call" deck) as many times as he wished,
attempting to duplicate the order of cards in the first deck. In the first
two series, check-up occurred by the experimenter first recording the order
of cards in the target deck and then the order of the call cards as
B.D. turned them over successively. In the third series, the "calls" were
not recorded or announced until B.D. had removed each card in the call deck
from its pile and transferred it to a new pile face down. The effect of
this exercise, suggested by B.D., was to delay somewhat his knowledge of the
results. In Series 4, B.D. shuffled the cards inside a cardboard box with
holes through which his arms could be inserted. The box was retained in
Series 5 and 6, with B.D. also transferring the cards inside the box during
check-up, and in Series 6 he was actually encouraged not to transfer the
cards sequentially but to select a card from anywhere in the deck to match
each target card announced by the experimenter. Confidence calls were also
invited in Series 5 and 6. A few other modifications, one of which will be
discussed later, were occasionally introduced.
The six series comprised a total of 55 runs of 52 trials each.
Kanthamani served as the experimenter for all series, although various
witnesses were said to be present during Series 4 through 6. The methods of
statistical analysis were the same as described above for the SCC
experiment.
Results
The Fisher Z for the total trials was highly significant (Z=12.88), and
was significant for each of the six series separately. Even more so than
with the SCC method, the significance was concentrated in an excess of exact
hits amounting in this experiment to four times the expected number (Z=22).
In contrast to the SCC series, the numbers of suit and number hits per se
were close to chance expectation. Thus, the significant scoring would
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annear to be entirely attributable to exact hits.
All 50 of the confidence
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calls were correct and they comprised 68% of the 67 exact hits in the runs
where confidence calls had been invited.
Analysis of the misses by
specialized chi-square methods revealed no evidence of systematic errors on
either the number or suit attributes. The authors concluded that "The
procedures of Series 1-4 appear to us to have been sufficiently rigorous to
guarantee that the psi effects reported for them are genuine" (Kanthamani &
Kelly, 1975, p. 216).
REG Experiments
The results of several preliminary series of experiments with B.D. were
reported (Kelly & Kanthamani, 1972). Those using REGs are. worthy of mention
because of the relative security provided by this automated methodology.
Because these studies were preliminary, the methodological descriptions
are rather sketchy. The most data were collected in ESP (precognition)
using a four-button Schmidt REG (see Chapter 5) with a radioactive source of
randomness. The authors stated that the device "in extensive tests covering
.millions of trials has never shown even minor departures from randomness"
(p. 190), but details of these tests were not provided.
Several informal tests were recorded in which no hard copy of the
results was obtained. The best controlled of these sessions, in which the
tests were witnessed by J. B. Rhine and Helmut Schmidt, produced 180 hits
over 508 trials (35.4%), with 25% expected by chance, which was highly
significant (Z=5.4). The results of eight formal tests with automated
recording of the results on paper tape yielded 1542 hits over 5377 trials
(28.7%) with Z=6.24. Scores inclined over sessions from a nonsignificant
27.0% in the first session to 30.8% in the last session.
The cumulative Z
reached significance by the end of the second session.
The only other REG test involved B.D. and another subject jointly
attempting to influence the output of a different Schmidt machine which
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1000-trial test yielded a modest but significant Z of 2.6.
Published Criticisms
The only scientist who has critically addressed the B.D. research
program in print is Persi Diaconis (1978). In a paper published in Science,
Diaconis did not discuss the experiments described above but instead focused
on a demonstration of card guessing that B.D. had given earlier at Harvard
in front of an audience. Diaconis was present at the performance and
claimed that B.D. had used sleight of hand and the trick of "multiple end
points" (not defining a successful outcome in advance) to create an illusion
of psi. He then implied on the basis of these observations that the reports
of the more formal experiments with B.D. cannot be trusted: " ... the
similarity of the descriptions of the controlled experiments with B.D .... to
the sessions I witnessed convinces me that all paranormal claims involving
[B.D. ] should be completely discounted" (p. 133).
In a rebuttal, Kelly (1979) argued that it was illegitimate to equate
an informal, admittedly uncontrolled demonstration to formal, controlled
experiments. He noted that the experiments were designed specifically to
eliminate the kinds of artifacts that Diaconis claimed subverted the Harvard
demonstration. For instance, multiple end points were excluded because the
criterion for a successful outcome was specified in advance by the
experimenters. As a secondary point, Kelly noted that Diaconis had not
actually observed cheating but only inferred it.
In his reply to Kelly, Diaconis (1979) elaborated his position by
stipulating that "ESP experiments done by known sleight-of-hand users must
include, as part of the protocol, magicians skilled at detecting sleight of
hand" (p. 30). In other words, the formal experiments with B.D.
should be
discounted because a skilled magician was not present to observe.
In his final rebuttal, Kelly (1980) argued that it is " ... not all that
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by any subject including a magician" (p. 123) and that significant results
with a magician present could always be explained away by the argument that
the subject was more skilled than the magician. Diaconis" (1980) final
rejoinder introduced no new points on this issue.
Evaluation
I will begin with an evaluation of the research methodology based on
the experimental reports and then consider the more far-reaching issues
raised by Diaconis.
Sensory Cues
The SCC procedure as described in the report seems to successfully
preclude sensory contact with the target card once it is placed in the
folder. However, it is conceivable that, under certain circumstances,
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B.D. could have caught a brief glimpse of the card being transferred to the
folder from the desk drawer. Specifically, if the subject were seated on
the other side of the desk from the experimenter and had a pocket mirror in
his lap, he might have been able to get a brief look in the mirror at the
card being transferred. He would only need to do this on a few trials to
obtain the reported. results.
One feature of the data that is consistent with such a hypothesis is
the similarity between the confusions structures on the ESP trials and
tachistoscopic presentation of the targets. The kind of brief visual
exposures of the targets in the tachistoscopic trials is very similar to the
kind of brief exposures B.D. would have received were the sensory-cue
hypothesis to be correct.
This hypothesis would be precluded, however, if it could be documented
that the desk used for the SCC experiment had a back which extended down
close to the floor. Fortunately, I was able to obtain
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the Institute for Parapsychology where the B.D. experiments were conducted.
Without revealing my specific purpose, I asked her if she recalled and/or
could show me the desk that was used for the SCC experiments. She stated
that it was one of a set of very similar large, light brown wooden desks
still at the Institute, but she could not recall which particular one it
was.
All the desks but one had backs. When I asked her specifically if the
desk had a back, she said she was fairly certain that it did. She noted in
particular that the desk was her own office desk and that she recalled
having frequently rested her feet against the back of the desk when seated
at it. Earlier in the interview she had also mentioned that B.D. would
customarily sit facing sideways with his legs stretched out along the back
of the desk. This would be a natural way to sit if the desk had a back,
since if he were to sit facing the experimenter his legs would be jammed up
against the back.
In summary, I came away from the interview with reasonable but not
complete certainty that the desk used for the B.D. experiment did have a
back and that my sensory-cue hypothesis was not applicable.
The shuffle procedure, on the other hand, seems somewhat more
problematic, in that B.D. was allowed contact with the call deck after the
target for each trial had been announced, thus allowing the possibility of
either rearranging the deck or substituting new cards in order to
fraudulently create hits. The authors acknowledge this as a problem in the
last two series (in which B.D. had contact with the cards inside the box,
outside the experimenters" view), in addition to the possibility of tactile
heat cues from the cards, so-called "dermo-optic perception." However, the
fact that no observers were present during Series 1-3 renders this
hypothesis, while still not likely, more plausible than the authors
acknowledge in their report. The best argument against this hypothesis is
an appeal to two runs in Series 4 in which B.D. was not allowed any contact
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runs were reported as being comparable to the other runs in the series, but
it was not stated whether the scores of these runs were independently
significant.
Sensory cues do not appear to be a problem in REG experiments with
Schmidt machines, so barring unusual circumstances this criticism would not
apply to this series.
Randomization
In the main SCC series, the authors submitted the actual sequence of
targets in the 46 runs to analysis for singlet and doublet biases. A
significant but modest singlet bias was in fact uncovered (statistical test
not reported), which could easily happen if target cards from previous
trials were not replaced in the pile in an entirely random manner. However,
subsequent analyses revealed that these biases were not correlated with
B.D. s hits and cannot account for the results.
.
Biases due to inadequate randomization seem more plausible in the case
of the psychic shuffle series. Although ten shuffles seem adequate in
principle, in practice its adequacy rests on how the shuffles were
performed. The problem is particularly acute in cases when the decks are
ordered in corresponding ways to begin with, such as would be the case when
decks are new. Unfortunately, it is not clear from the report how often
such correspondences might have been obtained, nor were the actual sequences
submitted to the kinds of analyses reported for the SCC series. The fact
that the hitting was restricted to exact hits exclusively does seem
consistent with such an interpretation.
The faulty-randomization hypothesis seems unlikely in the case of the
REG series, but it would be desirable to have more information about how
comparable the conditions in the randomness test were to those in the actual
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Recording
Duplicate recording and counting of hits was not applied in any of the
card-guessing series. However, in order to achieve the high levels of
scoring obtained, errors of this type would have had to amount to gross
negligence. Recording errors were apparently ruled out in the REG
experiments using the paper tape. Errors in the counting of hits were also
precluded, assuming that the Schmidt machine displayed hit totals.
Data Selection
Optional stopping was ruled out in all the card-guessing experiments
because the number of trials per series was specified in advance. The
authors appear to have been conscientious in reporting all the experiments
conducted with B.D., including the exploratory experiments. In any event,
the results were so highly significant that they could not easily be "washed
out" by unreported negative findings.
Statistical Methods
The analyses of the data show a great deal of sophistication.
The
methods were standard, simple (except in the case of the secondary analyses
of "confusions"), and appropriate. Biases due to uncorrected multiple
analyses can be ruled out first by the extreme levels of significance
obtained and second by the fact that the different methods of analysis
yielded comparable conclusions.
Diaconis Critique
I agree with Diaconis to the extent that he argued there is prima facie
cause for suspicion of subject fraud in the B.D. experiments.
Although
Kelly is correct that Diaconis inferred cheating by B.D. in the Harvard
demonstration rather than directly observed it, I consider Diaconis"
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example regarding the use of "multiple evidence," Diaconis cited not only a
successful outcome but a whole pattern of behavior on B.D.'s part that
suggests the use of procedures and principles that are very common in stage
magic. Whether or not B.D. used tricks at Harvard, his behavior there
indeed compelled particular circumspection during the formal experiments.
At a minimum, the authors should have consulted with someone having
expertise in conjuring about the adequacy of the experimental procedures.
Although Kelly argued that it is not difficult to design experiments
impervious to cheating by magicians, it is precisely Kelly's qualification
to make that remark which Diaconis questioned. Even though the authors did
consider and control for some possible forms of cheating, the absence in the
reports of information that would render the mirror hypothesis inapplicable
suggests that the authors were not sensitive to this particular possibility.
This reinforces Diaconis' point, whether or not the mirror hypothesis is
applicable in fact.
A second ground for suspicion is that in all the card experiments
procedural modifications were instituted at B.D.'s request. The
modification most likely to have impact on the results was the provision for
B.D. to handle the call deck post-feedback in the psychic shuffle
experiment. However, as noted previously, this modification was not in
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force throughout that experiment, and no one has yet suggested how
B.D. could have used the modification to effect the results.
On the other hand, Diaconis should be faulted for apparently jumping to
the conclusion that the Delmore experiments must be nonevidential simply on
the basis of the Harvard demonstrations and his general impression of other
parapsychologists. Such glib generalizations are clearly unwarranted. For
instance, the level of performance exhibited in the formal experiment, while
impressive in that context
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the necessary outcome, whether or not he possessed, and knew he possessed,
genuine psychic ability. However, the more important point is that the
kinds of standard tricks Diaconis claimed were used at Harvard were
precluded in the formal experiments, and Diaconis offered no
counterhypotheses of his own to account for the results in these
experiments.
In conclusion, whereas the authors should have exhibited more concern
about the apparent magical skills of B.D. and less confidence in their own
abilities to detect their use, Diaconis" critique lacks scientific weight.
In the absence of even a plausible hypothesis as to how B.D. might have
achieved his results fraudulently, they remain a genuine anomaly.
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Chapter 7
CORRELATIONAL STUDIES
The research projects we have considered so far were designed primarily
to demonstrate the existence of psi by producing statistically anomalous
results under conditions that preclude orthodox explanations of those
results. However, much of the research in parapsychology is conducted with
the more modest objective of determining psychological correlates of psi
scores or of determining how such scores are affected by the manipulation of
experimental conditions. Such research does not tell us anything directly
about the likelihood that the anomalies are paranormal, because the
correlations uncovered could conceivably be predicted from orthodox as well
as from paranormal theories. However, demonstrations of reliable
relationships between psi scores and external variables are important for at
least three reasons:
1
(1) They reveal at least a rudimentary coherence and lawfulness of the
anomalies. When anomalies collected under diverse circumstances relate in
the same way to external variables it suggests that the mechanism which
underlies them is uniform; i.e., it is reasonable to talk about a coherent
class of events;
(2) They may point to factors that if controlled or exploited could
improve the reliability of psi scores;
(3) They can serve as the building blocks for theories about the
anomalies or about how they interact with other psychological or physical
processes.
It is important to stress that one need not have established "the
existence of psi" (i.e., paranormality) for such research to be fruitful.
Quite to the contrary, embedding the anomalies in a nomological net of
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Progress in uncovering correlates of the anomalies in laboratory
contexts has been excruciatingly slow. There are at least two reasons for
this.
The first is the lack of an adequate theory to guide the selection of
variables. The second, and perhaps the more important, is the low internal
reliability of psi scores, which is a by-product (at least in part) of the
low signal-to-noise ratio. For example, even in Schmidt's ESP experiments
with the REG, which were raving successes by parapsychological standards,
the rate of successful guessing was only 1.5% above MCE. While this problem
can be alleviated somewhat by collection of a large number of trials, this
strategy can strain resources (especially in ESP experiments where
individual trials cannot be accumulated rapidly) and it increases the
difficulty of maintaining uniform control of extraneous biasing factors. To
make matters worse, the reliability and validity of the psychological
measure one seeks to correlate with psi scores is often far from ideal.
This is not to suggest that the task is hopeless, but these factors may help
account for the slow progress to date.
The above considerations suggest that correlations between psi scores
and other variables are unlikely to be consistently replicable even if
"real." In fact, most failures to replicate such effects can be attributed
to error variance alone. This is not to suggest that unexpected
correlations should be accepted at face value but rather that they should
not be rejected out of hand. At the present state of parapsychology's
development, the only way to reach a conclusion is to perform meta-analyses
on large groups of studies addressing the same relationship to see if the
distribution of outcomes departs from that expected by the null hypothesis.
As we shall see later, this approach is not without problems of its own, but
it is still "the best game in town" and in my opinion has provided useful
hints about some future lines of investigation that might prove profitable.
Only a handful of external variables have been used in enough
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for which such analyses have been undertaken in any systematic fashion and
these will be reviewed below. All are restricted to ESP scores as the
dependent variable; only recently has an interest developed in uncovering
the correlates of PK. All the predictors are psychological as opposed to
physical variables. In all cases, the relationships have been classified
simply as significant or nonsignificant; in no cases have attempts been
made to assess the actual magnitude of the relationship or the "effect
size!"
Personality Correlates
Personality variables or "traits" can be defined as "behavioral
dispositions or tendencies that are relatively stable over time for a
particular individual and are so structured that each individual can be
placed on a continuum for which that trait is an appropriate label" (Palmer,
1977, p. 175). A great deal of research has been done attempting to
identify the underlying structure of personality. Factor-analytic
approaches have tended to support the existence of two fundamental
dimensions of personality, namely (1) "extraversion" and (2) "neuroticism"
or "anxiety" (e.g., Cattell, 1965; Eysenck, 1960). It therefore is not
surprising that these are the two traits which have been studied frequently
enough in parapsychology to merit meta-analytic treatment.'
Extraversion
From 1945 to the present there have been numerous attempts to correlate
scores on ESP tests with scores on various personality tests claiming to
measure extraversion. The most commonly used of these scales have been:
the Cattell 16PF (and the version for adolescents called the High School
Personality Questionnaire), the Maudsley (later, Eysenck) Personality
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(MMPI).
The first meta-analysis of the extraversion-ESP relationship was by
Palmer (1977), who sampled studies published in the major parapsychological
journals. Using the experimental series as the unit of analysis, Palmer
uncovered 33 series published in 11 reports which provided sufficient
information to be evaluated. Palmer was not interested in the number of
significant relationships per se, but rather the ratio of positive to
negative relationships among the significant series as well as among all
series. He found that 23 of the 33 series (70%) were in the positive
direction (i.e., extraverts scoring higher than introverts) whereas all
eight of the significant relationships were positive. This pattern proved
to differ significantly from the pattern expected by chance, i.e., an equal
number of experiments (and significant experiments) in the two directions.
Palmer thus concluded that "there is evidence for a positive relationship
between extraversion and ESP scoring" (Palmer, 1977, p. 186).
A more up-to-date meta-analysis was later reported by Sargent (1981).
His survey included twelve reports not published at the time Palmer wrote
his review, seven of which were from his own laboratory. He also included
eight earlier reports not evaluated by Palmer. In seven of these cases,
Palmer had not included the report because it gave no indication of the
direction of the relationship. For reasons that are not clear, Sargent did
not cite four of the reports cited by Palmer. In any event, the samples in
the two surveys do not overlap as much as one might expect.
Unlike Palmer, Sargent was primarily interested in the proportion of
significant outcomes. He also based his analysis on the number of reported
relationships rather than the number of series, although these tended to be
equivalent. From a total of approximately 54 relationships (it is not clear
that this figure is exact), Sargent found 19 that were significant (35%) and
18 of these (95%) were in the positive direction." This led Sargent to
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correlated with successful performance in ESP tasks" (Sargent, 1981,
p. 141).
Neuroticism
Neuroticism can be defined for present purposes as "tendencies toward
maladaptive behavior caused either by anxiety or defense mechanisms against
anxiety" (Palmer, 1977, p. 178). This definition subsumes anxiety as a
special case of neuroticism, although the two terms tend to be used
interchangeably in the parapsychological literature. All of the major
personality scales cited above in the section on extraversion have subscales
measuring neuroticism or anxiety, and scores on the subscales have also been
correlated with ESP scores. Scales uniquely measuring neuroticism or
anxiety that were used in more than one study were the Taylor Manifest
Anxiety Scale and the projective Defense Mechanism Test (DMT).
Palmer's (1977) meta-analysis cited 21 reports that gave sufficient
information for evaluation. When all series were considered, there was no
evidence of a significant relationship between neuroticism and ESP scores.
However, a post-hoc analysis revealed that a relationship did exist if the
analysis is restricted to series in which subjects were tested individually
or in pairs. (Palmer speculated that group testing might have alleviated
state anxiety in the test situation among high-anxious subjects, thereby
rendering trait anxiety an ineffective predictor.) Be that as it may, 18 of
24 series (75%) with subjects tested individually or in pairs yielded a
negative relationship between neuroticism and ESP (higher scoring among less
neurotic subjects) and all seven of the significant relationships were
negative. These patterns differ significantly from the null hypothesis of
equality, leading Palmer (1977) to conclude that " ... there is evidence for a
consistent negative relationship when Ss are not tested in groups" (p. 183)
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There also appeared to be differences in Palmer's survey in the
"success" rates of the various predictor scales. The Manifest Anxiety Scale
was the least successful and if anything tended to correlate positively with
ESP scores. The most successful predictors were Cattell's neuroticism
subscales and the Defense Mechanism Test. The latter is a projective
technique in which the subject is asked to describe a threatening scene
repeatedly displayed tachistoscopically at increasingly slower speeds. The
defensiveness score is determined by how many exposures it takes for the
subject to recognize the threat and the nature of the perceptual or
interpretational errors made on preceding exposures. In a recent review of
research correlating DMT scores with scores on restricted-choice ESP tests,
which included seven experiments not reported at the time of Palmer's
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review, it was claimed that all ten experiments in the sample yielded a
positive relationship; i.e., high ESP scores correlated with low
defensiveness. In three of these studies the relationship was significant
by a two-tailed test and in seven by a one-tailed test (Johnson &
Haraldsson, 1984). The authors concluded modestly that " ... the DMT seems to
be a useful instrument in predicting the scoring direction in an ESP test"
(p. 197).
Attitudes
The only attitudinal variable that has been extensively explored in
relation to ESP scoring is belief in ESP, the so-called "sheep-goat"
variable -- i.e., "sheep" are "believers" and "goats" are "skeptics."
Actually, the sheep-goat variable comprises four related attitudinal
dichotomies which can be described in relation to orthogonal dimensions of
generality and personal reference (Palmer, 1971): general-impersonal ("Do
you believe ESP exists?"); general-personal ("Do you believe you have
psychic ability?" or "Have you had psychic experiences?");
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ESP?"); and specific-personal ("How well do you think you scored [will
score] on this ESP test?"). One or more items of this type are incorporated
into homemade rating scales. In most experiments the items are scored
separately, and in no experiment published in the parapsychological
literature has a scale been used which has undergone systematic test
construction.
The one meta-analysis of the attitude variable was conducted over ten
years ago by Palmer (1971). He used as his basis an experiment by
Schmeidler (Schmeidler & McConnell, 1973/1958) comparing restricted-choice
clairvoyance scores to attitudinal ratings on an item of the
specific-impersonal type. The experiment consisted of seven series of
individual testing and 14 series of classroom testing. Overall, 1308
subjects took part. Because undecided subjects were included among the
sheep, only 505 subjects (39%) were classified as goats. Results were in
the predicted direction in 18 of the 21 series (sheep scoring higher than
goats) and results for all individual series combined and all group series
combined yielded highly significant sheep-goat differences in each case.
Palmer (1971) proceeded to review 22 experimental reports, including the
original Schmeidler and McConnell report, which tested for attitude-ESP
relationships. These were broken down into 24 "experiments" according to
criteria that seemed reasonable from the structure of the reports but
sometimes comprised more than one series. Formal meta-analysis was
restricted to 17 experiments which could be uniformly reanalyzed by the
Z-test of the number of hits per condition and used the standard
card-guessing procedure with an expected mean score of five hits per run.
Criteria were defined for classifying undecided subjects with respect to
each of the four item types and applied as uniformly as possible throughout
the sample. In cases where more than one predictor was employed, the
direction was determined by majority vote; e.g., if two of three
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the study as a whole. In none of the experiments with multiple predictors
were inconsistencies regarding significance of the relationship noted.
It was found that 13 of the 17 experiments (76%) were in the expected
direction (sheep > goats). All six of the significant experiments were in
the predicted direction. Moreover, it was shown that this distribution of
outcomes closely approximated what one would expect if the true mean
difference approximated the mean difference of +.17 hits per run found in
Schmeidler and McConnell's combined group series, by far the largest sample
available. Palmer (1971) concluded that " ... the data presently available
support the hypothesis of a genuine SGE [sheep-goat effect], although the
relationship is very slight and difficult to demonstrate with small samples"
(p. 405). Finally, a comparable rate of information was found among the
experiments not included in the formal experiments (Palmer, 1971) and among
experiments published in the early 1970s (Palmer, 1977).
Hypnosis
Although a great many variables have been incorporated in experimental
manipulations designed to influence scoring in psi tasks, only one variable
has been systematically manipulated in enough studies to be used for
meta-analysis. What I mean by "systematically manipulated" is the results
of an experimental treatment being compared to results in a control
condition, either "within subjects" or "between subjects." The variable in
question is hypnosis or, more precisely, hypnotic induction.
The attempt to facilitate ESP by means of hypnotic induction has a long
history in psychical research (see Dingwall, 1968). However, the early
research was poorly controlled and, because much of it was linked to the
cult of Mesmerism, it was also tainted. J.B. Rhine did not find hypnosis
helpful in facilitating card guessing and discouraged its use. However,
beginning in the late 1950s a number of card-guessing studies
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Several studies also appeared using free-response methodology in the context
of the "hypnotic dream," but few of these studies involved control
conditions.
The experiments used fairly simple hypnotic induction procedures which
were usually combined with suggestions for high scores on the ESP test.
With one exception (Ryzl, 1962), deep hypnosis or training in hypnosis over
a series of sessions were not employed. Subjects were ordinary volunteers
claiming no special psychic or mediumistic talents and in most cases they
were not even prescreened for hypnotic susceptibility.
The first meta-analyses of the hypnosis-ESP literature appeared in the
late 1960s (Honorton & Krippner, 1969; Van de Castle, 1969). Each
concluded that hypnosis indeed facilitated ESP scoring. However, the
present review will focus on a more recent meta-analysis by Schechter
(1984).
As was the case in the previous meta-analyses reviewed in this chapter,
Schechter based his review on experiments published in the major
parapsychological journals. He cited 20 reports which were classified as
comprising 25 independent experimental series. Twenty of these were
considered appropriate for the analysis, i.e., the experiment was designed
to compare performance in the hypnosis and control condition, higher scoring
in the hypnosis condition was expected, and the results were reported in
such a way that the direction and significance of the difference could be
determined. Schechter found that 16 of the 20 series yielded results in the
expected direction (hypnosis > control) and that all seven of the
significant outcomes were in this direction. Noting that the probability of
seven of the 20 studies yielding significantly positive results by chance
was slight (p =. 000034 by an exact probability test), Schechter (1984)
concluded that ", .. the apparent difference between ESP hitting after
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Criticism and Evaluation
There are three questions that I will try to address in this section.
First, have the meta-analyses reviewed in the previous section demonstrated,
within the samples evaluated, genuine relationships between ESP scores and
the independent variables considered? Second, what, if anything, can be
said about the interpretation or meaning of these relationships? Third, to
what extent, if any, can the results of the meta-analyses be generalized
beyond the samples included? In other words, is it reasonable to believe
that the relationship will hold up in new samples?
Validity
It was stated at the beginning of the chapter that the objective of
this review was not to confirm the anomalous nature of the ESP scores in the
studies considered but rather to assess the reliability of the scores
insofar as this follows from their consistent relationship with external
predictors. For this reason, no attempt will be made to evaluate the
possibility of artifacts in individual studies, an effort which would in any
event be prohibitive from a practical standpoint because of the large number
of studies involved. Moreover, several of these experiments have already
been competently critiqued in a recent review by Akers (1984). Akers
focused on the kinds of flaws or alleged flaws discussed in previous
chapters of this review and found that most of the studies he considered
were guilty of one or more of them. I think it is fair to say on the basis
of his review that the prevalence and seriousness of the flaws found in the
studies included in the present chapter closely approximate those of the
ganzfeld experiments reviewed by Hyman (see Chapter 4). Thus, my analysis
of the likelihood of the flaws uncovered by Hyman being the true
explanations of the effects in the ganzfeld research applies to this chapter
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his meta-analytic review of the hypnosis literature and found that none of
them correlated significantly with the ESP scores.
Psychological Test Administration Following ESP Feedback.
There is one
flaw uncovered by Akers that deserves special treatment, however, because it
affects the validity of the relationship between ESP scores and the
predictor variables rather than the "validity" of the scores themselves.
With reference to those experiments in which ESP scores were related to
scores on personality or attitude questionnaires, Akers noted several
instances in which the predictor scales were administered to the subjects
after they had received feedback of their scores on the ESP test. This
raises the possibility that subjects" psychological responses to the
feedback may have influenced" their responses to the items on the personality
or attitude scale, thereby creating an artifactual correlation between the
scores on those scales and the scores on the ESP test.
In attempting to assess the impact of this artifact on the studies
which contributed to the previously reviewed meta-analyses, I first
discovered that the order in which the personality and ESP tests were
administered was often not reported, particularly in the studies conducted
prior to 1970. Nonetheless, it still proved possible to come to conclusions
about the possible impact of the artifact on the samples generally.
The artifact hypothesis can most clearly be rejected in the case of the
sheep-goat effect. In only one of the studies included in the Palmer (1971)
review could the Akers criticism apply (Nash & Nash, 1958). This was a
nonsignificant study with results in the positive direction (sheep > goats)
which was not, however, included among the 17 standard card-guessing
experiments. All other experiments gave subjects no feedback of ESP scores
before administering the attitude scale.
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them (29%), whereas the description of methodology was insufficient to
render an interpretation in another 16 (33%). However, the artifact proved
to be unrelated to study outcome either with respect to significance or
direction. The artifact applied definitely to only three of the 18
significantly positive experiments (17%) and definitely did not apply to 12
of them (67%).
The relationship for which the artifact appears most viable as an
explanation is the one involving neuroticism. Of the seven significant
confirmations in Palmer's (1977) review, the artifact is clearly applicable
to three of them and may have been applicable to two others. In only three
studies from the entire sample was the artifact clearly nonapplicable, and
two of these provided nonsignificant reversals of the predicted trend (i.e.,
neurotic > nonneurotic).
There are several factors that militate against the Akers artifact
accounting for the relationship, however. In each of the four significant
and flawed studies involving objectively scored personality tests as
predictors, subjects did not complete the personality test immediately after
the ESP test but either at a separate session or in one case (Nicol &
Humphrey, 1953) at home. Thus, any subtle mood shifts created by feedback
of the ESP scores would have had time to dissipate. In the study cited by
Akers to illustrate the potential effect of ESP feedback on psychological
test scores, the psychological test (in this case a test of imagery skill,
not personality) was given immediately after the ESP test (Palmer &
Lieberman, 1975), and the test is especially susceptible to response biases.
Three of the seven significant experiments were components of a series of
four experiments by Kanthamani and Rao (1973). In one of these four
experiments the artifact did not apply (the personality test was given
before the ESP test), yet the neuroticism effect was still significantly
confirmed. Since the procedure in the four experiments was otherwise quite
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variable.
The other two significant studies from Palmer's (1977) review involved
the DMT. In neither study was it clear from the report whether the artifact
was applicable or not. However, in the five studies from the larger, more
recent DMT sample where the criticism clearly does not apply, all five were
in the predicted direction and three of these were significant. Thus, again
it would appear that the effect is not dependent upon the potential for the
artifact being present. Particularly in the absence of any positive
evidence that these personality scales are susceptible to influence by ESP
feedback, it seems reasonable to conclude that the neuroticism-ESP
. relationship being attributable to the artifact suggested by Akers is
unlikely. Nonetheless, he should be commended for bringing the potential
artifact to our attention.
One other point about the methodology in the reviews requires brief
comment. In all the reviews except Sargent's and Schechter's, a uniform
criterion of significance was applied to all the studies considered.
In
Palmer's (1971) sheep-goat review this was the Z-test, because that was the
only suitable alternative. In Palmer's (1977) neuroticism and extraversion
reviews, conclusions were reached by averaging the results of the
alternative analyses. There were no instances in which a study was
classified as significant in which one analysis was significant and another
analysis of the same relationship was not.
Interpretations
The existence of a correlation between ESP scores and a predictor
variable says nothing directly about what psychological process or processes
might be mediating it. Seeking first to establish the reliability of the
correlations, parapsychologists have done little theoretically-oriented
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been published regarding the meaning of these relationships, all of which
are based on the implicit assumption that ESP scores reflect paranormal
processes.
Extraversion.
Regarding the extraversion-ESP relationship, for
example, two competing hypotheses have been proposed. The first, initially
proposed by and based upon the psychobiological theory of Eysenck (1967), is
that extraverts obtain higher scores on ESP tests because of a tendency
toward low cortical arousal. A difficulty with this hypothesis is that it
cannot explain why introverts tend to score below chance rather than at
chance; at any rate, the positive deviation of extraverts seems no greater
on the average than the negative deviation of introverts.
The second hypothesis is that extraverts are more at ease in the ESP
test situation than are introverts. This hypothesis might also explain why
less neurotic subjects and subjects who believe in the existence of psi also
seem to achieve relatively high scores on ESP tests. In fact, there are
some indications of overlap among these three predictors. One of the more
successful predictors of ESP scoring has been the Cattell scales, on which
the extraversion and neuroticism subscales are correlated and contain some
overlapping items. This suggests that the low-scoring ESP subjects in these
experiments may have been the introverted subjects who also showed signs of
neuroticism. Such subjects would also be expected on commonsense grounds to
be the most uncomfortable in a psi test situation, but no direct evidence of
this has been provided. Thalbourne (1981) has consistently found a low
positive correlation between extraversion and belief in ESP, suggesting some
overlap between these variables as well.
Hypnosis. Alternative hypotheses also exist about the facilitative
effect of hypnosis on ESP scores. One hypothesis is that hypnosis
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attention is focused on internal processes, whereas the other attributes psi
facilitation to the implicit or explicit suggestions of scoring success
associated with the hypnotic inductions. Only one study compared these
elements directly in a factorial design (Casler, 1962), and a reanalysis of
this experiment which I conducted using analysis of variance supported the
suggestion interpretation. However, trends in some of the other studies
seemed to favor the state interpretation (Honorton & Krippner, 1969). The
suggestion interpretation implies a possible link between the hypnosis and
sheep-goat effects, in that hypnosis can be seen as a manipulation of the
same belief variable that is simply being measured in the sheep-goat
studies. A problem with this analogy is that the hypnotic suggestions have
primarily manipulated belief in one's own ability to achieve a high score,
whereas items which ask this question directly have been relatively poor
predictors in the sheep-goat experiments. However, the failure of this item
to discriminate scoring in sheep-goat experiments may be attributable to the
highly restrictive range of responses to this item in most such experiments;
ratings of high confidence are quite rare. Attempts to manipulate belief in
ESP by means other than hypnosis have yielded mixed results (Layton &
Turnbull, 1975; Taddonio, 1975).
Somewhat more arcane alternative hypotheses having to do with
inadequacies in the design of many of the hypnosis-ESP experiments have
recently been discussed by Stanford (in press). He noted first that in the
great majority of the studies within-subjects designs were employed.
He
argued that subjects might be expected to score better in the hypnosis
condition than in the control condition simply because of demand
characteristics, i.e., the subjects knew they were supposed to score better
under hypnosis and adjusted their expectations and motivation to perform
accordingly. He also noted that in seven of these studies, there was either
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The fact that these studies tended to be less

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successful than those which employed proper counterbalancing suggested to
Stanford the possibility that hypnosis might only be successful when the
hypnosis trials are presented first. Moreover, all five studies which
avoided such problems by using between-subjects designs failed to assign
subjects randomly to the hypnosis and control conditions, raising the
possibility that differences in subject characteristics might be the real
cause of the effects observed. Finally, in all studies the experimenter
administering the ESP test was not blind to the condition assigned to the
subjects they were testing, which raises the possibility that the
experimenters may have unwittingly provided more encouragement to subjects
in the hypnosis condition or otherwise interacted with them differently from
subjects in the control condition.
Stanford's point about the problems associated with within-subjects
designs is well taken, especially in view of the fact that when subjects are
asked to perform in two psychologically distinct conditions in other kinds
of ESP experiments they tend to score above chance in one condition and
below chance in the other (Rao, 1965). Parapsychologists have traditionally
felt that differences in motivation can affect psi performance (e.g., Rhine,
1948), although the actual empirical evidence for this proposition is scant
(Weiner & Geller, 1984). Nonetheless, the possibility that demand
characteristics account for much if not all of the hypnosis-ESP effect must
be taken seriously.
The seriousness of the lack of counterbalancing in some of the studies
is substantially ameliorated by the failure of these studies to achieve the
same rate of success as those more properly counterbalanced. Even if
Stanford's suspicion that the hypnosis-ESP effect is limited to cases where
the hypnosis runs were not preceded by control runs is correct, the basic
integrity of the effect would not be challenged. Most process-oriented
research in parapsychology derives its conclusions totally or at least in
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and there is almost never a firm basis for inferring that a relationship
would hold up over repeated testing, especially given the low reliability of
ESP scores. There is some evidence for decline in ESP scores during the
course of a session (Palmer, 1978) that might also lead one to doubt whether
scores obtained later in a session would correlate as well with predictors
as scores obtained earlier in a session.
The seriousness of the lack of random assignment of subjects to
conditions in the between-subjects experiments depends upon the nature of
the alternate procedure employed. These vary from subjects assigning
themselves to conditions at one extreme (Moss, Paulson, Chang, & Levitt,
1970) to the experimenter assigning subjects alternately to conditions at
the other (Casler, 1962), the latter being a perfectly acceptable procedure
in this reviewer's judgment. Unfortunately, the one between-subjects study
which provided a significant superiority of the hypnosis over the control
condition (Sargent, 1978), seemed (as far as one can tell from the report)
to use one of the more arbitrary and therefore suspect assignment
procedures. On the other hand, the similar distribution of outcomes of the
between- and within-subjects experiments suggests a common mechanism in
both, and this would militate against subject-population differences being
the effective cause. However, it certainly cannot be ruled out.
Finally, given the extensive evidence for the experimenter expectancy
effect in psychology (Rosenthal, 1966), one cannot discount the possibility
of the hypnosis-ESP effect being somehow related to the experimenters not
being blind to the experimental condition. However, it should be noted that
it is difficult (although probably not impossible) to guarantee such a blind
in an experiment where one condition involves the subject being in an
altered state likely to be identifiable by the person administering the
test. It also should be noted that insofar as these demand characteristics
affect the expectations and motivations of the subject, they cannot be
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induction, which is also to increase the subject's motivation and
expectation of success. This was previously discussed as one of the
"nonartifactual" interpretations of the hypnosis-ESP effect (p. 152).
Belief. The sheep-goat effect has generally been interpreted as the
ESP scores reflecting the needs and motivations of the respective subgroups;
i.e., sheep and goats score in such a way as to confirm their previous
belief systems (e.g., Palmer, 1972). Empirical evidence for this
proposition has been provided by Lovitts (1981), who found a reversal of the
sheep-goat effect among subjects who were led to believe that high scores
would favor an alternative interpretation to ESP, namely subliminal
perception. Although critics have not addressed the correlational
literature from this point of view, one could reasonably hypothesize that
sheep would be more likely than goats to be motivated to obtain high scores
by cheating. However, this hypothesis would not account for the significant
psi-missing by goats in some studies and in most studies it is not clear how
subjects could have cheated.
In conclusion, interpretation of the correlational patterns discussed
in this chapter must be considered speculative at this time. Furthermore,
the viability of these or any other interpretation is obviously affected by
the generality of the patterns themselves. It is to this question that we
now turn.
Generality
If the findings of the meta-analyses discussed in this chapter are both
valid and the samples on which they were based representative of the general
population of such samples, then the trends should be preserved in
experiments conducted after the meta-analyses were undertaken. One of
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studies.
The ideal way to confirm the generality of the patterns would be to
commission a planned series of replications from a variety of laboratories.
Such a project presents obvious logistical problems and in any event has yet
to be undertaken. Although informal surveys have seemed to confirm the
continuation of the patterns found in some of the earlier meta-analyses
(e.g., Palmer, 1977, 1978), these surveys are suggestive at best.
Some discouragement regarding the potential generality of the patterns
is provided by a series of eight ESP experiments conducted by Michael
Thalbourne and colleagues (Thalbourne, Beloff, & Delanoy, 1982; Thalbourne,
Beloff, Delanoy, & Jungkuntz, 1983; Thalbourne & Jungkuntz, 1983).
Subjects were mostly naive college students, high-school students, or
volunteers from the community, with sample sizes ranging from 14 to 246
(mean=117.38). The dependent variable was the score on a ten-item
restricted-choice clairvoyance test called "Consumer's . Choice" in which the
targets were brand names of consumer goods. The independent variables were
belief in ESP and extraversion.
Belief was measured by a ten-item
sheep+goat scale created by the authors, and extraversion was measured by
relevant subscales of either the EPI, 16PF, or MMPI. For purposes of
analysis, subjects were divided into two groups on each of the independent
variables. In the first two studies dichotomization was based on the means
of the student populations from which the sample was derived; in the later
studies the method of dichotomization was not reported but would seem to
have been comparable to the original method.
Four of the eight sheep-goat relationships were in the predicted
direction and one of these four was significant. This pattern seems tilted
in the right direction (thanks to the one significant study) but is hardly a
ringing confirmation of the sheep-goat effect. More distressing is the fact
that in six of the eight studies, introverts scored higher than extraverts.
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last two experiments were each significant (favoring introverts) by a
secondary, but more sensitive, correlational. analysis. Although this
pattern is not definitive even within Thalbourne's samples and is not
sufficient by itself to overcome the large pattern in the opposite direction
reviewed by Sargent, it does raise legitimate questions about the generality
of this positive extraversion-ESP relationship.
It is now time to step back and examine the appropriateness of previous
meta-analyses as bases for inferences to new samples. To put this somewhat
differently but also more usefully, how can the populations which the
meta-analytic samples truly represent be defined?
Only in the Palmer (1971) review were the publication. sources sampled
explicitly named. However, it is clear that the sources in all cases
consisted almost exclusively of English-language parapsychology journals and
abstracts of convention proceedings. The reviewers did not exhaustively
consult nonparapsychological psychology journals and other scientific
journals. The authors who publish in these journals are generally skeptical
regarding psi and such journals tend to favor articles supporting the
skeptical viewpoint. This failure to review exhaustively these journals may
have led to an overestimate of the number of significant confirmations of
the "expected" relationships, and the author knows of a couple such cases he
"missed" in his reviews. However, the number of experimental parapsychology
papers published in nonparapsychological journals is so small relative to
the number published in parapsychological journals that the bias is slight.
The File-Drawer Problem. Thus, the sampled experiments are reasonably
representative of the relevant published experiments conducted by those
parapsychologists who were conducting experiments of those types prior to
the date of the review. But what about experiments conducted but not
published, the so-called "file-drawer problem"? This is a potentially
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studies (and in the ganzfeld experiments discussed in Chapter 4) because the
former type of experiments is easier and more economical to conduct.
Sheep-goat questions, in particular, are economical to introduce and could
easily go unreported in studies when they yielded no significant
relationships.
It is well known that in the behavioral sciences "significant"
experiments are more likely to be both submitted and accepted for
publication than "nonsignificant" ones. However, this factor is not
relevant to most meta-analyses reviewed in this chapter because they were
concerned with the ratio of positive to negative relationships among the
significant studies or among all the studies in the sample. Publication bias
with respect to the direction of relationships is much less plausible than
publication bias with respect to the significance of relationships,
especially prior to the publication of the meta-analyses (which alerted
investigators to the importance of directional trends). However, even
allowing for the new awareness, it is difficult for me to conceive of a
significant reversal of a relationship being suppressed, given the on-going
mentality and practices of both researchers and the parapsychological
journals. The major journals are forbidden by the Parapsychological
Association from rejecting papers due to nonsignificant results and this
would extend by implication to reversals as well. Actual data about
unpublished experiments would obviously be superior to the preceding
ruminations, but I think it is a good bet that the relationships uncovered
in the meta-analyses are not attributable to the file-drawer problem.
The Experimenter Effect. There is another factor which I think is much
more likely as compromising the generality of these patterns, and that is
the so-called experimenter effect. It is widely agreed among both psi
proponents and critics that some investigators are consistently more able
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than others to obtain significant results in their experiments.
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was not taken into account in any of the meta-analyses under consideration,
since separate series by the same investigator or laboratory were treated as
independent. There is nothing illegitimate about this, but it does obscure
the possible mediating effect the identity of the investigator might play in
accounting for the relationship. In all the reviews there were several
instances where a particular investigator contributed more than one series.
The ratio of investigators to series was:
15/24 in Palmer's (1971)
sheep-goat review (12/17 for the standard card-guessing experiments), 7/24
in Palmer's (1977) neuroticism review (minus group experiments), 8/33 in
Palmer's (1977) extraversion review, 19/53 (approx.) in Sargent's (1981)
extraversion review, and 10/20 in Schechter's (1984) hypnosis review
(scorable studies). Discounting Palmer's extraversion review, which is
largely subsumed by Sargent's, the number of investigators is approximately
42% of the number of series, an average of 2.37 series per investigator.
The extent to which the significant relationships depended on a small
number of investigators varies from review to review. This factor is
revealed most clearly by considering the studies which significantly
confirmed the general trend. The least effect of investigator uniformity
was in Palmer's (1971) sheep-goat review, where six of the seven significant
outcomes were obtained by different investigators. The greatest effect was
in the neuroticism review of Palmer (1977), where only three of the seven
significant studies were by different investigators and a single
investigator (Kanthamani) was involved in five of them. The situation was
not quite so severe in Palmer's (1977) extraversion review, where the eight
significant studies were contributed by five investigators, but three were
again contributed by Kanthamani. In Sargent's (1981) extraversion review,
11 of the 19 significant outcomes were by different investigators. However,
six were by Sargent himself. Finally, four investigators produced the seven
significantly confirmatory outcomes in Schechter's (1984) hypnosis review,
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It is especially noteworthy that the two investigators who contributed
most heavily to the personality-ESP patterns both have excellent track
records as "psi-conducive" experimenters in other contexts. Sargent is
known for getting significantly overall positive results in ganzfeld
experiments (although it should be noted that the significant
personality-ESP correlations were generally obtained in these same
experiments), and Kanthamani was the principal investigator in the Delmore
experiments (see Chapter 6).
The final way to look at experimenter uniformity in these reviews is to
calculate the proportion of experimenters who failed to obtain even a single
significant confirmatory result. There were nine of fourteen (64%) in
Palmer's (1971) sheep-goat review, four of seven (57%) in Palmer's (1977)
neuroticism review, three of eight (38%) in Palmer's (1977) extraversion
review, eight of 19 (42%) in Sargent's (1981) extraversion review, and six
of ten (60%) in Schechter's (1984) hypnosis review. Discounting Palmer's
extraversion review which is largely subsumed by Sargent's, 54% of the
sampled experimenters failed to obtain a significant result.
Taken as a whole, this analysis suggests that the significant outcomes
were not evenly distributed among the investigators responsible for them.
This is the case in all the meta-analyses except possibly the sheep-goat
one.
To the extent this is true, it suggests that an important factor in
determining the probability that any of these other effects will be
replicated is the identity of the investigator attempting the replication.
This point is relevant to the case of Thalbourne, whose unsuccessful series
of replications was discussed earlier. Thalbourne's research, because of
its recency, has not been included in any of the reviews under consideration
and he is not known as a "psi-conducive experimenter" in other contexts.
Nonetheless, some encouragement can be derived from the fact that 46%
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a rather unique bunch. With but one known exception the experimenters were
all parapsychologists positively inclined toward the existence of psi.
Most
have a keen interest in the subject. Many are in the field precisely
because they have had at least a modicum of success in producing psi effects
in the laboratory. In other words, they define a highly specialized
population, the definition of which probably cannot be legitimately extended
to include the garden variety psychologist who must someday succeed in
replicating these patterns if they are ever to achieve the stature of
genuine psychological laws.
There is not yet an adequate explanation of the "experimenter effect"
in parapsychology. Speculative hypotheses include differences in
experimenter honesty and competence, different social skills in handling
subjects, use of subtlely different subject populations, and paranormal
mediation by the experimenter (i.e., it is the experimenter, not the
subjects, who produces the psychic effect). It is probably naive in any
case to suspect a bivariate correlation between ESP scores and any external
variable not to interact with other variables (Palmer, 1977). However, when
one such variable is the investigator, special problems are created, since
the important scientific principle that an effect (whether simple or
complex) can in principle be replicated by any competent researcher is
undercut. The message that should be drawn from this is not that psi is an
artifact or that parapsychology is a waste of time, but rather that priority
must be given to understanding the experimenter effect so its deleterious
effects can be circumvented.
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Chapter 8
PSI-MEDIATED INSTRUMENTAL RESPONSE
Critics of parapsychology often claim that the field lacks any serious
theorization (e.g., Alcock, 1981). Although the level of theoretical
development in parapsychology is indeed primitive in comparison to other
sciences, this criticism is an overstatement. In order to illustrate the
maximum level of theoretical development which has so far been attained in
parapsychology, I have decided to review a research program undertaken in
the 1970s by Dr. Rex Stanford related to a concept called psi-mediated
instrumental response (PMIR). Stanford was trained as a psychologist and
his research program is typical of what one finds in psychology. It
addresses psychological issues pertaining to psi, in particular how psi is
processed cognitively and how it interacts with the needs and motivations of
the organism.
Stanford's research program contains a number of features normally
associated with a sound theoretically-oriented approach in psychology.
These include the following:
(1) Development of a model of broad scope that integrates previous
experimental findings as well as anecdotal observations;
(2) Presentation of the model as a series of clearly stated
propositions that are testable;
(3) Experimental testing of these propositions by means of an
appropriate and standardized methodology.
As is perhaps evident from the discussion of other research projects in
this review, this degree of logical development is not representative or
typical of parapsychology in general. Although low-level theorizing and
hypothesis testing is rather common in parapsychology, it does not possess
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The PMIR Model
The essence of the PMIR model is summarized as follows by Stanford
(Stanford & Stio, 1976, p. 55): " ... [an] individual, through extrasensory
means, actively scans his environment for objects and events (or information
related thereto) which are relevant to his needs and that when such
information is discovered he tends to respond to it in accordance with his
typical dispositions toward such objects and events."
What is novel about this proposition is the assumption that the
individual is constantly and actively seeking out information in the
environment by means of a paranormal process (Stanford, 1974a). In order
that this scanning not interfere with normal cognitive activity, it is of
course necessary to postulate further that the scanning is unconscious.
Specifically, Stanford postulated that the scanning and the response made as
a result of the need-relevant information obtained by the scanning (i.e.,
the psi-mediated instrumental response) can occur "(a) without a conscious
effort to use psi; (b) without a conscious effort to fulfill the
need ... (c) without prior sensory knowledge ... of the need-relevant
circumstance;
(d) without the development of conscious perceptions (e.g.,
mental images) or ideas concerning the need-relevant circumstance; and (e)
without awareness that anything extraordinary is happening" (p. 45). These
assumptions vastly broaden the population of potential psi events, which
traditionally have been restricted to cases where a person has a conscious
"psychic" experience (spontaneous experience) or consciously intends to use
psi (as in an experiment). The PMIR model subsumes such cases but deals
with others as well.
A typical "PMIR experience" cited by Stanford is that of a couple who
wanted information about good vegetarian restaurants in Washington, D.C.
While eating lunch at a restaurant en route to Washington, they chose to sit
in a booth where they overheard a conversation between the people in the
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model, the couple was scanning the environment psychically for the needed
information and, having received the information, responded in such a way as
to fulfill the need (i.e., by choosing the "right" restaurant and the
"right" booth at the "right" time), all of this being done without awareness
that they were using psi to obtain this information.
Stanford also postulated certain psychological mechanisms which lead to
psi-mediated responses. Following an earlier theory by Roll (1966), he
hypothesized that psi does not introduce new cognitions into the individual
as such but rather that it facilitates or triggers the selection of
cognitions (e.g., memories) or behaviors which already exist in the
individual's repertoire. Stanford proposed that this response is
accomplished as economically as possible through a variety of mediating
vehicles, including (1) modification of the timing of an already selected
response; (2) forgetting or remembering to do something; (3) making a
mistake (e.g., dialing a "wrong" number); (4) a thought coming to mind that
leads by a normal chain of associations to the intention to make the
response; and finally (5) the direct (conscious) cognition of the
need-relevant circumstance, as in a traditional "psychic experience."
The strength of the disposition toward PMIR was postulated to be
associated with "the importance or strength of the need(s)," the degree of
relevance of the need-relevant object or event, and the "closeness in time
- -
of the potential encounter with the need-relevant object or event"
(Stanford, 1974a, p. 45). The likelihood or effectiveness of PMIR was
postulated to be influenced by certain situational and/or psychological
factors, in particular competing cognitive activity that increases the
rigidity or stereotypy of thought or behavior. Certain psychological traits
such as neuroticism, guilt, or a low self-concept may cause the individual
to use PMIR masochistically to counter his or her apparent best interests.
In a later paper, Stanford (1974b) extended the PMIR con
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(i.e., paranormal) as well as normal in nature. Just as in the case with
ESP, the model assumes that PK can function unconsciously; i.e., "PK ... can
occur as a response to extrasensory or sensory information which has never
been in the conscious focus of the PK ... agent ... " (p. 350). This of course
implies that PK can occur nonintentionally. Even when PK is used
intentionally, the model postulates that it is facilitated "when the goal
event is not in the conscious focus of the PK agent [although it] has
definite motivational salience" and in particular when the goal event has
"just left the focus of consciousness without having been realized"
.
(p. 349). In fact, the probability of PK is actually "reduced during [a]
period of focused attention and wishing" (p. 350). Shifting responsibility
and capacity for PK away from oneself and onto an external agency (as, for
example, one does in prayer) tends to discourage direct focusing of
attention on the problem and is thus PK-facilitory.
Stanford also noted that those forms of telepathy in which the agent
actively "sends" information to the percipient can be construed as a
subcategory of PK. This so-called "active-agent telepathy" was renamed by
Stanford "mental or behavioral influence of an agent" (MOBIA), which he
postulated is "the most frequent PMIR function of PK" (p. 349). MOBIA
follows the same laws within the model as do other forms of PK.
The above discussion represents a condensation of 18 formal postulates
presented in the two papers, and the quotations I have cited were taken
directly from those postulates. Although not stated explicitly in the
papers, the model is obviously linked to the basic principles of
reinforcement theory in psychology and thus provides at least a potential
bridge between psychology and parapsychology.
In the course of his presentations Stanford cited numerous experiments
in the parapsychological literature in which psi effects occurred in the
absence of direct intention by the subject or were influenced by aspects of
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the target situation of which he or she was not aware ..
Examples include
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effects on ESP scoring as a function of whether or not target cards were
paired with erotic photographs (Carpenter, 1971), performance on a classroom
exam being influenced by the unknown presentation of hidden answers to some
of the questions (Johnson, 1973), and success on dice-throwing tasks when
the subject was unaware which face had been chosen as the target (e.g., Fisk
& West, 1958).
Methodology
--
Stanford developed a standardized methodology to test various
propositions of the PMIR model. In general terms, the approach was to have
subjects engage in a covert psi task, i.e., a task which the subject did not
realize involved testing for psi. If the subject's performance on this task
met a certain prespecified criterion, he would be allowed to escape or avoid
some unpleasant, boring task and engage instead in a pleasant, interesting
task. Thus, if the responses on the covert psi task were indeed psi
mediated, they could determine an outcome relevant to the subject's needs.
Stanford has published five experiments using this methodology
(Stanford & Associates, 1976; Stanford & Rust, 1977; Stanford & Stio,
1976; Stanford & Thompson, 1974; Stanford et al., 1975). Subject samples
ranged in size from 29 to 72 and consisted exclusively of college student
volunteers. In all but one study (Stanford & Rust, 1977) the subjects were
exclusively males.
In all but one of the experiments the covert psi test involved ESP.
In
these cases the test was introduced to subjects as a standard test of word
association.
In this type of test the subject is presented with a taped
stimulus word and is asked to respond with the first word that comes to
mind. Thirteen words were used, the first three serving as buffers to
acclimate the subject to the procedure. The remaining ten words were chosen
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latency -- how long it took the subject to respond- which was recorded on a
microswitch-activated electric timer. In most of the studies this timer was
accurate to .1 sec although in the Stanford and Rust experiment the accuracy
was improved to .01 sec.
For each subject, one of the ten words was randomly chosen by means of
a random number table to be the key word. If the response latency on this
word was the shortest of the ten (or, in some predesignated cases, the
longest) or was tied for this distinction, the subject was subsequently
invited to engage in a "pleasant" task. Otherwise, the subject was asked to
engage in an "unpleasant" task. The subject was told nothing about these
subsequent tasks at the time of the word-association test and was not told
of any contingency involving the test.
In terms of the PMIR model, the specific cognitive mechanism available
to the subject for determining his fate is what Stanford calls the
"unconscious timing mechanism." In other words, it is the psi-mediated
timing of the response, rather than its occurrence per se, that is
instrumental.
In all but one experiment, the "pleasant" task consisted of male
subjects- rating photographs of nude or semi-nude women. In the remaining
case, the male subjects received relaxation suggestions from an attractive
female research assistant (Stanford & Stio, 1976). The most common
"unpleasant" task was for subjects to use a photocell stylus to track a
small patch of light on a pursuit rotor turning at a boringly slow speed.
Other unpleasant tasks were circling any of three designated letters the
subject should find on three sheets of paper filled with all the letters of
the alphabet in random order (Stanford & Thompson, 1974) and an ESP
card-guessing task (Stanford & Stio, 1976) -- an interesting commentary on how
Stanford views such tests! In all cases the task was introduced as a
genuine part of the experiment, designed to collect useful psychological
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In one experiment (Stanford & Rust, 1977), the subject who experienced
the pleasant or unpleasant task was not the same subject who had taken the
word-association test. This experiment was designed to determine if PMIR
might be used altruistically.
In the one PK experiment (Stanford et al., 1975), the subject began by
engaging in the pursuit-rotor task. Unknown to the subject, an REG in the .
next room was left running. The machine was programmed to have P=1/6 for a
hit and generated trials at a rate of one per second. The machine produced
a maximum of 2700 trials per subject, equivalent to 45 minutes on the
pursuit-rotor task. (This was done in five-minute intervals with one-minute
breaks in between). The REG counted hits in blocks of ten. When and if
there were seven or more hits in a block (p <. 0003), the subject was removed
from the pursuit-rotor task and allowed to engage in the picture-rating
task. The chance probability of this occurring for any subject was .072.
Scoring
In the ESP test, the primary dependent variable was a standardized
transform of the response latency on the key stimulus word. This was
obtained by applying a log transform to all the response latencies and
subtracting for each subject the latency to the key word from the mean of
all ten latencies and dividing by their standard deviation. In the REG
experiment, the dependent variable was simply the proportion of hits
produced by the REG while it was active.
In all the experiments a possibly more appropriate, although less
sensitive method, would have been the number of subjects who actually
escaped the unpleasant task.
Stanford did not evaluate this measure in the
first three ESP experiments because the prevalence of ties in the response
latencies of particular subjects meant that the chance probability of
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(1977) experiment, so the discrete dependent variable (number of subjects
escaping the unpleasant condition) was used in this case, although it is not
clear from the report whether this or the standard scores were construed as
the primary measure. The discrete scores were also computed in the PK
experiment (Stanford et al., 1975), but in this case the continuous
(proportion of hits) scores were stipulated as primary. The standard scores
were evaluated using common parametric tests such as t tests and analysis of
variance. Exact probabilities were used to evaluate the discrete scores.
Results
In terms of overall scoring, the results of these experiments are not
particularly impressive. Only in the PK experiment were the overall scores
significant on the continuous measure. However, the discrete scores were
significant in both studies where such scores were computed (Stanford et
al., 1975; Stanford & Rust, 1977). In all five studies all the results
reported were in the predicted direction -- i.e., above chance. However, in
most of the experiments the psi scores were related to independent variables
measured for the purpose of testing specific propositions of the PMIR model.
The results of these tests can be summarized as follows:
(1)
Overt Psi Tasks. In two experiments, the proposition that
unconscious and nonintentional psi is the same process as conscious and
intentional psi was tested by correlating scores on the covert psi test to
scores on a standard (overt) psi test conducted at the same session. In the
Stanford and Thompson (1974) experiment the overt test was a precognition
task in which the subject had to predict which segments of a printed "radar
screen" would later be randomly chosen to contain targets. The correlation
was positive and significant, confirming the hypothesis (r =. 39, p <. 025,
one-tailed).
In the PK experiment, subjects took an 80-trial overt PK test
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in the positive direction but not significant (r =. 20).
(2) Ready Responses. The PMIR model postulates that PMIR is more likely
to be facilitated by readily available cognitions than by more submerged
ones.
In the context of word-association theory, this means that primary
responses (the most common responses in the population according to
published norms) to the stimulus words are more likely to be good mediators
than are other responses. Since primary responses are generally associated
with short reponse latencies, Stanford reasoned that PMIR would be more
likely to occur in conjunction with short-latency responses (likely to be
primary) than long-latency responses. In the Stanford and Stio (1976)
experiment, this hypothesis was tested by manipulating whether the shortest
or longest latency was instrumental in escaping the unpleasant task. As
predicted, the mean standard score for the fast-contingency condition was
significantly above chance (p <. 02, one-tailed) and significantly higher than
the mean standard score for the slow-contingency condition (p <. 02,
one-tailed).
(3) Need Strength. The PMIR model postulates that the disposition
toward PMIR is positively related to the strength of the need served by it.
Capitalizing on the erotic nature of the picture-rating task, Stanford and
Stio (1976) atttempted to manipulate need stength (orthogonally to
response-speed contingency) by having half of their subjects listen to an
erotically arousing record before engaging in the word-association test, the
idea being that the record would increase the "need" to participate in the
picture-rating task. The other subjects heard the record after the
word-association test. The manipulation failed to affect psi scores, but
the authors suggested retrospectively that the record may not have really
been erotically arousing.
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In another experiment (Stanford & Associates, 1976), the authors
attempted to manipulate need-strength by merely manipulating the sex (and
therefore the sexual attractiveness) of the experimenters conducting the
word-association test. As predicted, subjects tested by female
experimenters scored higher than subjects tested by male experimenters
(p =. 025, one-tailed), although the mean score of the former subjects was not
significant by itself. These subjects also scored significantly above
chance (p <. 05, one-tailed).
Although not construed as a test of the need-strength hypothesis, the
results of the two experimenters in the PK experiment (Stanford et al.,
1975) were also compared. Results collapsed over both the overt and covert
PK tests were significantly higher for subjects tested by the more
extraverted of the two experimenters (p <. 01). Subjects tested by this
experimenter also scored significantly above chance as a group on both the
covert
(p <. 01) and overt (p <. 05) tasks. Parapsychologists generally assume
that extraverted experimenters are better able to motivate subjects in psi
experiments than are introverted experimenters (e.g., Sargent, 1980).
(4) Self-Concept. The PMIR model postulates that a positive
self-concept leads to use of PMIR in support of the subject's self-interest
whereas a negative self-concept can lead to the reverse. Stanford and
Associates (1976) attempted to create a positive self-concept in half of
their subjects (orthogonal to the need-strength manipulation) by giving them
complimentary feedback on their performance on a word-association test
administered immediately prior to the "psi" word-association test. For
ethical reasons the authors chose not to induce a negative self-concept in
the remaining subjects but rather gave them no feedback on the first
word-association test. The manipulation was found to have no significant
effect on the psi scores.
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In summary, six hypotheses based on propositions from the PMIR model
and involving relationships to independent or predictor variables were
tested. Three of the six were significantly confirmed, and in all six cases
results were in the predicted direction.
Criticisms
Neither the PMIR model nor the research program surrounding it has been
the object of critical review either inside or outside of parapsychology.
Ironically, the one serious criticism directed to the model exclusively has
been by Stanford himself. Stanford (1978) came to question the assumption,
which the PMIR model shares with all traditional conceptualizations of psi,
that "ESP at the most fundamental level is a form of communication" of
information across a channel (p. 198). With respect to PK, he specifically
questioned the assumption that PK is guided cybernetically by unconscious
ESP (e.g., ESP must be used to monitor the ongoing status of the tumbling
die so that PK can ultimately guide it to come to rest with the target face
uppermost). Stanford labels these assumptions collectively as the
"psychobiological model of psi ... function" (p. 198).
Stanford based his questioning of the psychobiological model on
research evidence suggesting that psi scores do not seem to be related to
the complexity of the information source in ESP or the complexity of the
target system in PK. For example, ESP performance does not seem to
deteriorate if information from several sources must be integrated to make a
response, and PK performance does not seem related to the complexity of an
REG. In other words, the psychobiological model implies that as the
requirements for cognitive processing capacity increase, psi performance
should deteriorate. That does not seem to be the case.
Stanford thus chose to substitute the term conformance behavior for the
term psi- mediated instrumental.
response.
The
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retains the dispositional assumptions of the PMIR model but eliminates the
objectionable "psychobiological" assumptions.
A novel feature of the model
is the use of the REG as a general metaphor for the object of psi influence.
Most notably, in the case of ESP the brain is conceptualized as an REG. The
source of psi is a "disposed system" that influences the "REG" in such a way
that an outcome is produced that is serving the needs of the disposed
system. Thus, in ESP the brain is biased much like an REG to produce a
cognition or behavior that serves the organism's needs. A particularly
important corollary of the conformance model is that conformance is
facilitated to the extent that the object of psi influence is labile; that
is, that it exhibits properties of randomness or "free variability."
The relationship between the conformance model and the earlier PMIR
model is not clearly stated but it would be reasonable for a reader to
conclude that the conformance model is intended to replace the PMIR model.
In any event, the PMIR research program was abandoned and Stanford no longer
incorporates the PMIR model into his writings in a substantive manner.
Although the conformance model has inspired some research both by Stanford
and others (e.g., Braud, 1980), it has failed to generate the kind of
systematic research program produced by the PMIR model.
Evaluation
Insofar as one is willing to allow paranormal constructs into
scientific theorizing, I find little to criticize in the PMIR model per se.
Its validity rests of course on its empirical track record, but the model
appears to be internally consistent, its terms clearly defined and
operationally definable. Its propositions are not expressed quantitatively,
but this is true of most theorizing in psychology. In fact, given the poor
reliability of psi measures it could be argued persuasively that any attempt
at a quantitative theory or model at this stage of the field's development
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would be premature.
Therefore, I will devote my evaluation primarily to the

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research.
The word-association ESP test strikes me as basically sound, again
assuming reasonable competence in its execution. The fact that subjects
were not told they were taking an ESP test reduces considerably the
possibility of subject fraud, at least insofar as members of the subject
pool were not tipped off as to the true nature of the study by previous
subjects. It appears that some debriefing sometimes took place at the end
of the sessions, so the possibility of "leaks" cannot be entirely ruled out.
Even so, the possibility of sensory cues was apparently eliminated by
keeping the person administering the word-association test blind to the key
stimulus word and the response contingency; i.e., it is unlikely that
subjects could have cheated even if they had known the experimental
hypothesis and were motivated to cheat.
It is not clear to what degree possible errors in recording the
response latencies were precluded. In the Stanford and Thompson (1974)
experiment the method is not described at all. In the subsequent
experiments it is indicated that an electric timer was used, but it is not
clear if the device automatically recorded the latency or whether this was
done by hand. More importantly, it is not clear what steps were taken to
assure uniformity across trials in the starting and stopping of the timer
with respect to the subject's utterances. In at least one experiment
(Stanford & Thompson, 1974), the recording was performed by the subjects
.
themselves. However, even if the recording of latencies was not error-free,
the fact that the tester was blind to the key stimulus word assured that
there was no systematic bias in the recording; at worst, error variance was
introduced.
The key stimulus word was chosen separately for each subject by means
of a random number table. Although the exact method of target selection was
the number of digits in the table minimizes the possibility of the kinds of

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abuse uncovered in the Maimonides dream studies (see Chapter 2). Moreover,
Stanford is one of the more careful psi researchers when it comes to these
kinds of subtleties.
Finally, the methods of statistical analysis were appropriate and
straightforward. Separate scores were computed for each subject and efforts
were made to assure that the distributional assumptions of the parametric
tests were met. Only in the case of the Stanford and Rust (1977) experiment
did a problem arise as to which of two analyses of the same hypothesis was
considered the primary one, and this does not affect the overall evaluation
of the success of the research program one way or the other.
Most of my criticisms concern the procedures used to test the various
hypotheses about psi. My major criticism in this connection is the lack of
any checks to determine if the experimental manipulations had the desired
effect. How do we know that the picture rating was pleasant and the
pursuit-rotor task unpleasant? At a minimum, there likely were individual
differences in subjects" responses to these tasks, especially to the
picture-rating task, that could have been partialed out of the results.
Even more problematic were the manipulations of need strength and
self-concept. In fact, Stanford conceded retrospectively that one of his
need-strength manipulations was unsatisfactory, based on informal comments
by the subjects. Finally, it would have been relatively simple to check if
short latencies to the stimulus words indeed were positively related to the
choice of primary responses, as demanded by the "ready-responses"
hypothesis.
Regarding the latter hypothesis, it will be recalled that it was tested
in the Stanford and Stio (1976) experiment by manipulating whether the
fastest or slowest response to the key word caused the subject to enter the
"pleasant" condition.
In this case the hypothesis was confirmed. However,
this same manipulation was introduced in two other experiments but the
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never reported (Stanford & Thompson, 1974:
Stanford &
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Associates, 1976). Even though this manipulation was not designated in
these studies as tests of formal hypotheses, they nonetheless bear upon the
robustness of the finding by Stanford and Stio and should have been
reported.
Although adequate randomization procedures were always used in choosing
the key stimulus word, the same cannot always be said unequivocally for the
assignment of subjects to experimental conditions. In the Stanford and
Associates (1976) experiment, it is clearly stated that a random number
table was used to assign the response contingency and an appropriate
alternation method was used in the assignment of subjects to the
self-concept conditions. A similar alternation method was also used in
assigning subjects to experimenters in the PK experiment (Stanford et al.,
1975). However, in the other cases the method of assigning subjects to
conditions was not clearly specified, although it always seemed to involve
some kind of randomization.
My final criticism concerns what I consider to be the premature
abandonment of the PMIR research program. Although there is some merit to
the argument that psi does not operate entirely in line with what would be
expected by the information-processing assumptions of the psychobiological
model, this is only one element of the PMIR model and is not necessarily the
most important one. The assumptions about the unconscious and
nonintentional nature of much psi functioning, as well as the psychodynamic
assumptions, have not been challenged. Although the cybernetic guidance of
PK indeed appears absurd after Stanford's analysis, it is less clear why the
available evidence suggests so sweeping an abandonment of
information-processing concepts as the conformance model seems to imply.
ESP, at least, must at some stage interact with the cognitive processes of
the brain if a meaningful response is to be elicited.
The various cognitive
mechanisms postulated in the PMIR model.
such as the unconscious timing
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mechanism. need not be abandoned. They are not in fact inconsistent with the
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conformance model, since any response, even conformance behavior, requires
some kind of cognitive mediation at some stage. Stanford (1982, p. 19)
acknowledges all this, but his use of the term "psychobiological" to label
the model he proposes to replace implies a more radical revision than either
logic or the data justify, or than he really intends.
It seems to me that a much better strategy would have been to modify
the PMIR model rather than to abandon it in favor of a whole new model. The
conformance model lacks all the conceptual elegance of its predessessor.
The vagueness of its basic premise has led to much confusion and has
triggered heated and unenlightening controversy about such things as whether
the model is causal or whether it predicts that nonliving matter has psi
(e.g., Beloff, 1979). The research it has inspired has been related almost
exclusively to the corollary proposition of lability, which could have been
attached to the PMIR model just as easily as to the conformance model.
Stanford (1967) himself had introduced a very similar notion in the 1960s,
which even antedated the PMIR model.
The PMIR model' has been one of the most promising developments in
parapsychology in the past 20 years. We can only hope that some day it will
be resurrected, even if it must wear a slightly different wardrobe.
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Chapter 9
METAL BENDING
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Most of the PK research taken seriously by the parapsychological
community is of the type exemplified by the REG experiments discussed in
Chapter 5. This is often called micro-PK because the effects are of slight
magnitude and require for their detection the application of statistical
tests over a series of trials. In contrast, macro-PK refers to larger scale
effects each of which is detectable by the naked eye. Many effects, i.e.,
single-trial effects detectable only by electronic amplification, fall in
between these two extremes but are generally included under the heading of
macro-PK.
i
Because of the rampant fraud associated with Spiritualist "physical
mediums" of the 19th and early 20th centuries, macro-PK has been a taboo
subject in parapsychology, especially in Britain and the United States. The
recent revival of interest in macro-PK in general, and metal bending in
particular, can be attributed to publicity surrounding the controversial
Israeli psychic, Uri Geller. Perhaps the most important consequence of the
Geller craze from the researcher's standpoint was that a number of less
celebrated individuals, particularly children and teenagers, reportedly were
able to bend metal after watching Geller do it. These "mini-Gellers" seemed
to be a more promising research population than Geller himself, particularly
since some of them appeared to be able to produce effects without touching
the specimen.
The most extensive metal-bending research has been conducted by
Dr. John Hasted, Professor of Experimental Physics at Birkbeck College,
University of London. His most substantive work, which will be the focus of
this review, has been published in five experimental reports in the Journal
of the Society for Psychical Res
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Robertson, 1979. 1980, 1981). This research, along with other generally
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less formal work which includes such exotic fare as teleportation and
levitation, is summarized in a book entitled The Metal-Benders (Hasted,
1981).
The research to be reviewed here involves protocols in which the
subject was not allowed to touch the specimen. Exact procedures varied
somewhat from session to session and procedures were almost never reported
in precise detail. Nevertheless, certain general features can be described.
In the beginning of the research the specimens were latch keys, but in
later research these were replaced by metal strips or bars, usually of
aluminum or an aluminum alloy. The measuring instruments of primary
interest were resistive strain gauges mounted either on the surface of the
specimen or between layers of the metal sealed by epoxy resins. The strain
gauges were connected by wires to a polygraph for amplication and recording
of the signals. The wires were also used to mount the specimens; i.e., the
specimens hung from the wires. The subject was seated in front of the
specimen and generally allowed to point at it as long as the finger remained
at least several inches away.
The primary control against the touching of the specimen was visual
observation of the subject. However, since sessions often lasted up to two
hours, Hasted conceded that full attention by the observer(s) throughout the
period could not be maintained. Supplementary controls both against
external physical force and electrostatic or electromagnetic artifacts
included: (a) electrode sensors designed to register touching of the metal,
(b) electrical shielding of the strain gauges, (c) dummy loads, and (d)
video recording of target strain gauges. None of these controls, except
possibly the first, were utilized in all sessions, although anomalous
phenomena were recorded in the presence of each. However, details about the
implementation of the controls, e.g., the precise locations of the dummy
loads, were rarely reported.
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The subject population consisted primarily of middle-class British
teenagers, frequently coming from families with academic backgrounds.
According to The Metal Benders (p. 30), Hasted has achieved positive results
with 20 subjects, although he claims to have worked extensively with only
six of these. Two subjects, Nicholas Williams and Stephen North, both
adolescents, contributed the vast majority of the data to be covered in this
review.
Several generalities about the anomalous signals have been reported.
The signals vary in strength from a few millivolts to a few volts and are
generally two to three times the background noise. Compared to signals
produced by physically touching the specimen, they have sharp peaks and
short rise times (approx. 200 ms). It is not clear whether Hasted is
claiming that signals with these characteristics cannot be reproduced by
touching or whether typical touches do not have these characteristics.
Permanent bends, which are reflected in baseline changes of the chart
records of nearby strain gauges, sometimes are observed and sometimes are
not.
Several specific experiments or, more precisely, groups of sessions
using the same basic protocol, will now be summarized.
Basic
Effects
Numerous signals were recorded from a strain gauge mounted on a latch
key in a two-hour session with Nicholas Williams as subject (Hasted, 1976).
A complete record of the chart tracing was published. Three successive,
permanent bends of approximately 10, 50, and 12 degrees were determined by
tracing onto paper. The last two of these apparently occurred after
cessation of effort, but the report is not entirely clear on this point.
It
also would appear that the final "bend" was actually a restraightening.
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"Synchronicity"
Sometimes, multiple specimens were employed at a single session,
ranging in number from two to six. The configuration of the specimens
varied from session to session. On the horizontal plane, they were either
arranged "radially" from the subject (on a straight line outward from the
subject), "equidistant" (subtending an angle of about 30 degrees as if on
the rim of a circle with the subject at the center) or "opposite" (the
subject is in between the specimens, one in front and one in back). In
other sessions, one or more of the specimens in either the radial or
equidistant horiztonal plane was displaced vertically with respect to the
others.
Two major experiments with this procedure were reported. The first,
with Nicholas Williams as subject, consisted of eight sessions and was
limited to two or three specimens. The last session was videotaped (Hasted,
1977). It would appear from Hasted's diagrams that the sensors were at
least one meter apart and the subject at least one meter from the closest
sensor, except during the first session when he was somewhat free to move
about.
It seems that a total of 54 signals appeared during the course of the
experiment, of which 34 were designated as "synchronous" and 20 as
"nonsynchronous." The classification was apparently made by visual
inspection. Only in the equidistant, purely horizontal configuration did
nonsynchronous signals seem to predominate. Although Hasted did not perform
statistical tests, a chi-square test I performed comparing the proportion of
synchronous signals in this configuration to the combined totals for the
other configurations was significant. Permanent bends of the keys were
detected in two of the sessions but the videotaped session was not among
them.
The second experiment involved six sessions with Stephen North as
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(Hasted & Robertson, 1980). Adjacent specimens were apparently closer to
each other than in the previous experiment. Apparently in contrast to the
earlier sessions, dummy loads were uniformly applied as controls in these
sessions. It would appear that a total of 66 signals were obtained.
I
could not determine precisely the proportion that were considered
synchronous, but it seems to be comparable to that obtained in the previous
experiment.
In both experiments, the proportion of synchronous signals appeared to
be greatest with the radial-vertical configuration. This led Hasted to
postulate a "surface of action" as a kind of vertically-oriented field
extending outward from the subject.
Rotation
In a session with Nicholas Williams, Hasted (1977) took two strips of
aluminum alloy, folded one around the other, and placed them on a table
inside an empty room. Hasted and Williams waited outside. On this and
subsequent occasions, one of the strips was later found to have been twisted
around its vertical axis over part of its length. The effect only occurred
when no one was watching. Hasted tentatively interpreted the effect as
involving a rotation of the surface of action.
Extensions and Contractions
These studies were designed to determine whether the signals seemed to
represent the kinds of forces necessary to produce bending. To detect this
it was necessary to place sensors across the width of the specimen.
In a preliminary study of six sessions with three subjects, metal
strips (mostly aluminum) were employed with sensors on the upper and lower
surfaces (Hasted, 1981). The bars used were of different thicknesses,
although thickness was not varied independently across subjects,
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was printed indicating that the ratio of "bending" to "stretching" signals
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decreased as the thickness of the specimen increased, but no supporting
statistics were provided.
In a more elaborate study involving three sessions with Stephen North,
six strain gauges were implanted across the width of an aluminum bar or in
between strips of an eutetic alloy sealed together by epoxy resin (Hasted &
Robertson, 1979). In both cases the four internal sensors were actually
inside the specimen, not on the outer surface. To produce a bend, extension
signals would need to be produced on one surface and contraction signals on
the opposite surface, with the internal sensors expected to yield smaller
signals of the same polarity as the external sensor closest to it.
However, the data revealed no such consistency. Of the 119 arrays
recorded, only 17 (14%) corresponded to a simple bend or stretch pattern (no
gradient changes). Most of the arrays had either one, two, or three
gradient changes. In other words, the signals within the arrays seemed to
distribute themselves randomly, as if they were independent of one another.
Hasted labeled the effect "metal churning" in contrast to "metal bending."
The effect seemed to imply that a visible bend can only occur on those
relatively rare occasions when the forces across the width of the specimen
happen to align themselves the "right" way. This of course is consistent
with the observation that the number of signals detected on the chart
recorder was much greater than the number of bends detected in Hasted's
experiments.
Direction
In order to assess the direction of the forces operating on the surface
of the metal, five sessions, four with North and one with another subject,
were conducted using metal squares or discs instead of bars (Hasted &
Robertson, 1979). A configuration of three strain gauges was set up on the
surface of each specimen, two pointing orthogonally to each other and a
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Metal Bending
Page 184
extension and contraction vectors could be calculated for each signal.
According to Hasted, the application of positive stress should produce
extension along one diameter and an equal contraction along the opposite
diameter. Again, however, the results were not as orderly as this
hypothesis would lead one to expect. First of all, no preferred directions
of strain could be detected. Moreover, there were no consistent ratios
between the magnitudes of the corresponding extension and contraction
signals. In fact, in about 25% of the cases extensions were accompanied by
extensions or contractions by contractions: "metal churning" again.
;
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Location
Two experiments were conducted to determine the localization of the
ostensible strain along the length of a metal strip. In the first
experiment, consisting of three sessions, three strain gauges were aligned
along the surface of the strip (Hasted, 1978). In a later experiment, which
involved five sessions with North as the subject, the number of sensors was
increased to five (Hasted & Robertson, 1980). Dummy loads were also
utilized in this latter experiment.
In both experiments the output tended to be greatest from the middle
sensor. Hasted equated the distribution of signal strengths along the
lengths of the specimen to a Gaussian distribution. Although it strikes me
as problematic to define a curve by five and especially by three data
points, it seems fair to say that the strength of the signals tended to fall
off monotonically and symmetrically from the center.
Electrical Effects
Occasionally during the course of the research the electrodes which had
been mounted for the purpose of detecting touches by the subject responded
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impedance operational amplifier supposedly immune to such effects was
attached to the electrode. Only North seemed able to affect the apparatus
in this way (Hasted & Robertson, 1981).
To further test for electrical effects, North participated in a series
of seven sessions using two metal bars in a radial configuration.
Both the
electrodes and strain gauges were utilized as sensors. Almost half the
signals (44%) registered exclusively on the electrodes, with 24% exclusively
on the strain gauges and 32% on both. The proportion of electrode
activations increased over sessions. Hasted speculated that North's
awareness of the increasing interest in the electrode effects contributed to
their increased prevalence.
In a subsequent series of ten sessions with North, an attempt was made
to determine whether the effect was on the electrodes themselves or on the
surrounding atmosphere. Two electrodes separated by distances ranging from
0.4 to 6.2 cm were given charges of +9V and -9V, respectively, the
potentials being reversed every 11 seconds. Their hypothesis predicted that
under the conditions of their experiment, if the signals were associated
with atmospheric ionization charge bursts would appear uniformly at the
oppositely charged electrode, whereas no such correlation would be found if
the signals originated from the electrodes directly. It was found that
95.1% of the 1123 recorded signals behaved in accordance with their
atmosphere-ionization hypothesis.
However, this conclusion was contradicted in yet another experiment
(Hasted & Robertson, 1981). Hasted came to realize that previous results
could be accounted for by assuming the origin of the charge to be on the
subject's body and that it travelled through the atmosphere to the target
along what he called a "temporary "pranormal conduction" path" (p. 181). He
reasoned that the atmosphere-ionization hypothesis would be refuted if it
could be shown that a high-frequency signal could be transferred from a
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drift or diffusion, the base for the atmospheric-ionization hypothesis.
Thus, a 10 kHz potential was transferred to Stephen North's body by placing
close to him a 10 khz oscillator connected to a metal plate or "antenna." As
predicted by the "conduction path" hypothesis, the 10 kHz signal was also
momentarily transferred to or induced on a partially screened electrode in
the vicinity of North. This effect was not obtained with control subjects.
Piezoelectric Sensors
In the most recent phase of his research, Hasted has shifted from
strain gauges to piezoelectric sensors (Hasted, Robertson, & Arathoon,
1983). As used by Hasted, piezoelectric sensors measure the rate of change
of stress rather than the level of stress per se. This makes them more
sensitive than the strain gauges to the rapidly varying pulses that seem to
characterize the ostensible PK effects. However, in order to minimize
electrostatic artifact, Hasted had to eliminate much of this added
sensitivity by connecting the high resistance piezoelectric transducer
across a relatively low resistance (3.5 K ohms). Nonetheless, the overall
piezoelectric system was still more sensitive than the strain gauges to the
signals of interest.
Hasted briefly reported results from eight sessions with Stephen North
and two other subjects. The sessions with North and one of the other
subjects were held in an electrically shielded room. Control against
touching or fraud continued to be through observation by the experimenters
and (in some cases) observers. A dummy channel (unscreened input
resistance) was situated somewhere inside the screened room and connected to
a separate amplifier and recorder as a check for electrical artifacts
originating inside the room. None were found.
In most of the sessions, at least, a strain gauge and piezoelectric
sensor were mounted back to back on a thin metal specimen. In the first
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and only nine on the strain-gauge channel. Only four of these signals were
synchronous. In subsequent sessions, both with North and the other
subjects, there were virtually no signals on the strain-gauge channel,
whereas the density of signals on the piezo channel remained about the same
on the average.
Although Hasted speculated that this change may have had something to
do with an increase in sensitivity of the piezo channel following the first
session due to improvements in the electronics, it is difficult to see how
this could account for the lack of strain-gauge signals.
Hasted also reported the ability of Stephen North to exert some control
over the timing of the signals in this phase of the research, but the
details were sketchy.
Criticisms
To this reviewer's knowledge, no comprehensive critiques of Hasted's
research have yet been published. Perhaps the closest approximation is a
review of The Metal Benders by Stokes (1982). Wood (1982) raised technical
objections to the interpretations Hasted placed upon his "strain" signals,
expressing particular concern about their small magnitude. He also
questioned Hasted's assumption that the extension and contraction vectors
should be equal for the metal disc experiment (p. 184), and he noted that
the rotation effect (p. 182) could be produced normally because such twists
are caused by shear rather than by extension forces. Hasted had assumed the
latter in arguing for the effect being paranormal. Hasted replied to Wood's
criticisms in the same article.
Also worthy of mention at this point are brief comments by an
electronics expert named Horowitz (cited by Randi, 1982), who maintained,
apparently rather indignantly, that the signals which appeared on the chart
recorder in Hasted's experiment are readily explicable as electrical
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applicable to Hasted's earlier work (which may have been all Horowitz had
access to), its applicability to the later work in which a dummy load was
utilized is less certain.
A thorough, albeit sympathetic, critique of Hasted's experiments has
appeared in an unpublished doctoral dissertation by Isaacs (1984). A
particularly valuable aspect of this review is that Isaacs obtained
information directly from Hasted about certain procedural details which did
not appear in the latter's published reports.
These critics" points are generally included among those arrived at
independently by myself and my consultant. Therefore, I will leave further
discussion of them to the following evaluation section.
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Evaluation
The first general question to be addressed about Hasted's work is
whether the effects he has reported can be attributed to normal, i.e.,
artifactual processes. This question must be addressed separately for the
gross metal-bending (deformation) effects and the more subtle effects
detected on the chart recorders.
Deformations
Because of the physical setup, it is hard to imagine how the subjects
could have physically bent the specimens while they were attached to the
recording devices without detection by an experimenter (or, the video
recording, when used), or without leaving an obvious tell-tale trace on the
chart record. This comment does not apply to the twisted metal strips,
however, which were left unobserved in a room. In this case, documentation
is insufficient to rule out someone entering the room undetected and
manipulating the specimen. Although twists as tight as those observed seem
difficult to produce, even granting that shear forces are involved,
the
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be assessed without extensive control tests.
In none of the cases is information given to reassure the reader that
either physical deformation of the specimens or substitution of an already
deformed specimen was precluded as a possibility at some point during the
session (e.g., before the specimen was mounted). In particular, I could
find no mention of specimens having been marked. Although no positive
evidence of such manipulations exists, Hasted's lack of sensitivity to this
issue in his reports reduces the confidence one can place in the observed
deformations being truly anomalous. The fact that his subjects were
teenagers is not an argument against trickery being employed, although
Hasted sometimes implies that it is.
Chart-Record Signals
The signals on the chart records could in principle be produced
artifactually either by direct interaction with the specimen (or the
.
sensor(s) attached to it) or interaction with the peripheral devices (i.e.,
amplifiers, chart recorder, etc.). Possibilities for direct interaction
with specimen and sensor include touch, air currents (e.g., blowing on the
specimen), auditory stimuli (e.g., ultrasonic sounds), thermal stimuli, and
localized electrical signals.
Even granted the unreliability of long periods of human observation, it
seems unlikely that a subject could consistently get away with touching a
specimen without being detected. This is especially true in the case of
Nicholas Williams, who customarily stationed himself several feet from the
specimens. Also, it again should be noted that some sessions were
videotaped, and touch detectors were sometimes employed.
Blowing on the
specimens would be more difficult to detect, however. According to Isaacs
(1984), only air currents powerful enough to cause the rigidly mounted
specimens to swing would be powerful enough to be detected by the
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amplication and recording system.
However, Isaacs stopped short of saying

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that such effects are impossible, and no control trials have been reported
to assess this potential artifact systematically. Issacs maintained that
Hasted's amplification and filtering system would have precluded auditory
effects from being recorded. In some sessions, Hasted controlled against
thermal effects, which could also produce air currents, by employing thermal
sensors.
Although one can imagine many sources of gross electrostatic or
electromagnetic artifacts, localizing them to a particular specimen is a
different matter. However, as Hasted recognized, it is possible that a
strain gauge could be triggered either by the subject building up an
electrostatic charge in his body and moving a finger, say, 'close to the
specimen, or by creating dynamic electrostatic induction through gross body
movements.
On the other hand, such potential effects, even if the requisite
movements had escaped visual detection by the experimenter(s), would have
needed to overcome the electrical shielding of specimens routinely applied
in Hasted's later work. Electrostatic effects should also have been picked
up by the touch detectors; the problem here, of course, is that on some
occasions these detectors were triggered, and some of the anomalous chart
recordings are now conceded to have been electrical in origin. For the
reasons cited above, it is unlikely that all these triggerings of the touch
detectors can be attributed to undetected touch, but what they are
attributable to remains uncertain.
Another argument against hypotheses based upon localized artifacts is
the frequent occurrence of "synchronous" signals associated with sensors
located up to several feet apart. The problem is that the signals could
conceivably radiate out from the vicinity of one sensor to another, even
over the distances of separation utilized. If the signals were truly
synchronous, this hypothesis might be precluded. However, Hasted's
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the time it would take for the radiation to propagate. Hasted's
"synchronous" signals can only be considered synchronous in a loose sense of
the term.
The main control against global artifacts (and indeed the most
important control in all of Hasted's work) was the use of a dummy load with
its own amplifier. The dummy load would be expected to pick up gross
electrical artifacts due to the switching on and off of appliances, etc., as
well as most signals from simple devices that might be smuggled into the
laboratory by a subject with intentions of fraud. However, no data were
reported comparing empirically the effects of various signals on the dummy
loads and the strain gauges. Such data would have made this control more
reassuring.
The remaining potential source of artifact in this category is direct
interaction with the chart recorder or the chart recorder pens (Randi,
1975). Hasted (1981) claims, however, that the equipment was always kept
well out of the subject's reach.
In conclusion, assuming normal experimental competence and honesty, it
appears unlikely but possible that the effects on Hasted's chart records can
be explained away as mundane artifacts.
Process-Oriented Data
The second general question to be addressed in evaluating Hasted's
research is of a more process-oriented character; namely, what can be said
about the mechanism underlying the effects, assuming they are not mere
artifacts as discussed above?
Unfortunately, as also was the case in the REG research (Chapter 5),
Hasted's research methods do not lend themselves well to drawing conclusions
of a process-oriented nature. Three distinct classes of deficiencies can be
cited:
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(1) Methods of recording the anomalous signals were not well suited to
providing precise characterizations of them. Most importantly, the chart
recorders Hasted used were too slow (approximately .1 sec) to record
reliably the rapidly rising signals of primary interest, which could have
resulted in the loss of data. In general, signals were not recorded or
reported in such a way as to allow confident determination of their nature.
The problem is not so much the strength of the signals, as suggested by Wood
(1982), but rather their qualitative characterization.
(2) Principles of good experimental design were largely ignored. One
never finds systematic comparisons of experimental and control conditions in
Hasted's work. Successive tasks were not counterbalanced to eliminate
possible order effects. Most importantly, potential psychological and
physical effects were continually confounded. No efforts were made to keep
subjects blind to experimental manipulations and hypotheses, thus making it
impossible to distinguish basic physical characteristics of the phenomena
from characteristics associated with, and thus constrained to, the
psychological needs, attitudes, and intentions of the subjects. As
different tasks were given to different subjects, it is difficult to assess
the generality of the process-oriented data obtained or to make proper
between-subject comparisons.
(3) Although many of the effects upon which conclusions were based did
not occur consistently, the conclusions were not backed up by the requisite
statistical analyses, a point also stressed by Stokes (1982).
Examples of how these deficiencies contribute to ambiguity in the
interpretation of Hasted's results will now be given. Perhaps the most
important of these examples concerns the basic nature of the recorded
signals. Although the signals are often referred to in passing as
reflecting strain (i.e., extension, contraction, or bending of the metal
specimen)
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recent work has indeed illustrated that many of the signals in that work
seem to be electrical in nature, which raises the possibility that some of
the effects in the earlier work may also have been electrical. Only in
those sessions where the signals were shown to conform to permanent
deformations of the specimen does the case for their representing actual
strain effects appear to be strong (Hasted, 1977). The incapacity to
characterize the remaining signals is attributable in part to the suboptimal
recording techniques mentioned above.
.
Hasted's conclusions regarding the "surface of action" are also
problematic, even if one accepts the loose definition of "synchronous." This
concept is based on observations of data from North and Williams that
synchronous signals are more prevalent when the specimens are in a
radial-vertical configuration with respect to the subject than in some other
configuration. However, no statistical analyses were offered to support the
significance of this trend. In the case of Williams' data (Hasted, 1977),
12 of 15 (80%) signals in the vertical or radial-horizontal-vertical
configurations were synchronous as compared to 22 of 39 (56%) with the other
configurations. This difference is associated with a corrected chi-square
value of 1.67, which with one degree of freedom is clearly nonsignificant.
The trend in North's data seems somewhat stronger (Hasted & Robertson,
1980), but I was unable to perform a statistical analysis from the available
data. Since the order of presentation of tasks to the subjects was not
counterbalanced, the trends that were uncovered might be due to order
effects (e.g., a subject might do relatively well with a particular
configuration simply because it was presented in an early or late session).
Although the surface of action is presented as a basic physical
characteristic of the phenomenon, it could just as easily be a reflection of
a possible psychological preference of North and Williams; there is
certainly no basis for drawing conclusions about the generality of the
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Finally, there are problems with the concept itself. Since it is
little more than a metaphor for certain empirical observations, its
theoretical value is limited; it does not seem to be, or at least has not
been shown to be, a source of hypotheses or predictions that might increase
our insight into the mechanisms involved. Also, as noted by Stokes (1982),
subsequent assumptions about the surface of action moving outward from the
subject (Hasted' & Robertson, 1981) seem to contradict the data that signals
appear synchronously on sensors at different radial distances form the
subject. The willingness to add on assumptions about the movement of the
surface of action threatens to render the concept unfalsifiable.
The data concerning the localization and direction of the ostensible
, psychokinetic forces and whether they are extensions or contractions suffer
from comparable ambiguities to those addressed in the preceding paragraphs.
As noted by Wood (1982) regarding the experiments with the metal discs, it
is not always clear what a strain hypothesis would predict. For instance,
one would not expect symmetries of the type postulated by Hasted to be found
if the strain were localized on particular sensors. However, even if one
were justified in adopting, say, a simple bending hypothesis, failure to
confirm it could not be interpeted. As noted previously, the signals which
could confirm such a hypothesis might never have been registered due to
deficiencies in the recording procedure. This recording problem could have
added noise to virtually all of Hasted's process-oriented data. On the
other hand, the failure to detect regularities in support of a strain
hypothesis, for whatever reason, reinforces concern that the signals may not
be strain signals at all.
Finally, the nature of the "electrical effects" reported by Hasted is
still not clearly resolved. The experiment supporting the "paranormal
conduction path" is not sufficient by itself to settle the matter. In
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In conclusion, Hasted has presented us with a set of intriguing
anomalies about which we can say little, despite his generally
process-oriented approach. Much of the problem may be due to the quality of
his research reports, which I consider the most deficient of any considered
in this review.
As noted at the beginning of this chapter, this review has been limited
to the better controlled of the effects reported by Hasted. Particularly in
his book, Hasted (1981) intersperses accounts of these experiments with more
informal observations. These commentaries sometimes project an aura of
credulity which has been alluded to by sympathetic (Collins & Pinch, 1982),
unsympathetic (Randi, 1982), and neutral (Stokes, 1982) reviewers of his
work. This is particularly true of the chapter in his book devoted to
informal (and often poor) observations or inferences of ostensible
teleportation, often in the vicinity of Uri Geller. When a scientist
writing a scientific book starts describing the teleportation of a liver
from his Christmas turkey, even his more controlled observations are likely
to lose credibility in the eyes of many scientists. Hasted (1976) has
defended the presentation of such material and even maintains that "one's
own credibility is relatively unimportant" (p. 382). However, the problem
as I see it is not the reporting of anomalous phenomena per se (even very
anomalous phenomena), but rather the according of evidential weight (by
implication, at least) to poorly controlled observations. At a minimum, I
think Hasted has used poor judgment in his presentation of this material.
Although I personally am less willing than many scientists to draw
inferences about the reliability of experimental reports from such ad
hominem considerations, I do feel they should be placed on the table for the
benefit of readers who might think otherwise.
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Structural Changes
As a general rule, metal-bending experiments are only considered valid
if protocols are used which prevent the subject from touching the specimen.
However, experiments which allow touch are sometimes considered worthy of
serious attention if it can be shown that structural changes in the metal
were produced that are inconsistent with a physical-bending hypothesis.
The most impressive results of this type have been provided by
experiments conducted by the French metallurgists Charles Crussard and
J. Bouvaist (1978) with a subject named Jean-Paul Girard. During the course
of the research Girard deformed or transformed 150 specimens, but the
authors considered only 20 of these episodes to be evidential. Eight of the
20 were selected for detailed review in their report.
The exact procedures varied from trial to trial, but in most cases it
involved Girard holding a metal bar first outside and then inside a stopped
glass tube. Observations to determine whether the specimen had been bent
were made before the trial, before the specimen was placed in the tube, and
after the trial.
Structural analyses were generally performed before and
after the trial. Finally, simulations sometimes were performed on control
specimens to assess what structural changes occur when deformations are
produced by normal physical means.
The first two specimens were bars of aluminum alloys. In each case,
bends of the bar were observed. The second bar was submitted to laboratory
tests which confirmed that the force needed to bend it physically was twice
that exerted by the strongest man who had previously attempted to bend the
bar with his hands.
The second two specimens were stainless steel cylinders 7 mm in
diameter and 85 mm long. Visible bends were detected only in the first
specimen. However, both bars exhibited local magnetism that was not
exhibited prior to the trial.
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martensite, which accounted for the magnetism, was not of a type that
results from heating or cooling, but rather from deformation. However, the
quantity of martensite in both cases was considered to be far greater than
expected, given the degree of bending observed. The localization of the
martensite was also considered surprising. Physical bending (30 degrees
back and forth) of a control specimen from the same batch as the test
samples caused the specimen to assume an S-shape which had not been observed
with either of the test specimens. Also, the distribution of the magnetism
in the test bar differed from that expected and observed in the control.
The final four specimens were Duralumin plates which Girard was asked
to "compact," i.e., to harden. Although bending was observed in only one of
the four specimens, measures with a Vickers microdurometer revealed
increased hardening in all four cases, varying from 6% to 12%. The result
for the fourth specimen was independently confirmed in Hasted's laboratory.
Further tests revealed that the changes in hardness were associated with a
modification of the residual longitudinal stress in the hardened zones.
Moreover, tests of the first two specimens revealed an anomalous
microstructure in the hardened zones consisting of a high density of small
(200 angstroms) dislocation loops. It is not clear whether these
deformations were not found in the remaining two samples or not tested for.
Several simulation tests were also performed with control samples.
Achieving the degree of hardening observed in the test specimens by bending
back and forth was shown to require a permanent deformation greater than
what was actually observed in any of the test specimens. Also, the physical
bending did not produce the small dislocation loops. A local compression
test duplicated the requisite hardness but again without producing the
dislocation loops. Also, when the equivalent degree of hardness was
physically generated, the thickness of the plate was reduced 13%, compared
to a maximum of 2% in the plates handled by Girard. The most successful
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features of the test specimens except that it dulled the surface. However,
the surface shine could be restored by polishing.
The authors exhibited a commendable degree of caution in interpreting
the results of their experiments. Labeling the effects as "abnormal" rather
than "paranormal," they asserted that while their data " ... rule out for the
moment any explanation by known physical mechanisms or by tricks," they
acknowledged the possibility that "a more insightful investigator may
conceive a mechanism of which we did not think" (p. 13). They concluded
that to overcome their controls, Girard "would have to be not only an
accomplished illusionist ... but also a first-class metallurgist." (p. 13).
Evaluation
As frankly noted by the authors, the results with Girard must be
interpreted in light of the fact that he possesses conjuring skills; it
turns out that he was even enrolled in the "Magician's Register." It is to
Girard's credit, however, that he apparently volunteered to the authors
during the course of the investigation the fact that "he had practiced
prestidigitation" (p. 14). Less reassuring is the assertion by one of
several magicians consulted by the authors that he discovered "a sign of
trickery in a film J. P. Girard had obtained for us without telling us it
was faked" (p. 14).
If trickery was used to obtain the effects, it seems unlikely that it
involved physical bending of the specimen by Girard during the trial itself.
All the trials were conducted in the presence of multiple witnesses and at
least two of the trials were filmed. The deformations that were observed
would require more force than that producible by a normal human. Finally,
and most importantly, the structural changes found in most of the specimens
did not conform to what would be expected by simple bending.
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specimen for the test specimen. The primary control the authors provided
against this possibility was to mark the specimens.
The methods used to
mark the two aluminum bars was not specified. The stainless steel bars were
marked with an electric pencil and the Duralumin plates with some kind of
"iron".
To defeat these controls by substitution, Girard would have needed to
take the following steps:
(1) Know in advance the type of specimen to be employed, obtain one or
more examples of the specimen, and perform the necessary transformations.
(2) Duplicate on this specimen or specimens the markings made on the
test specimen (after knowing the latter).
(3) Substitute his own specimen(s) for the test specimen at some
point(s) during the trial.
Too little information is given in the report to allow the first step
to be precluded. In particular, we lack information as to how much access
Girard or an accomplice may have had to the labs or lab facilities at times
other than the experimental sessions. We also lack sufficient information
concerning how far in advance Girard knew the types of specimens that were
to be employed at a given session. We do know in the case of the stainless
steel cylinders, however, that Girard had the unmarked test specimens in his
possession for several days prior to the trials.
Regarding the second step, the opportunity for Girard to mark the
duplicate specimen is greater the longer the time interval between the
marking of the specimen, or (more importantly) Girard's knowledge of the
marking, and the trial. In the case of the second aluminum bar and the four
Duralumin plates, we are not told when the markings were made. We are told
that the stainless steel cylinders were marked at the beginning of the
session, which certainly would restrict Girard's opportunities to mark
duplicate specimens, but not necessarily preclude them. Such opportunities
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aluminum bar, however, since it was marked immediately before the trial.
This also was the one specimen that Girard was not allowed to touch at any
time during the trial prior to verification of the deformation.
In the case of the second aluminum bar, distinctive flaws in the
structure of the bar were cited as serving the same function as the
markings. However, it is not clear how distinctive these flaws really were
and whether they could also have appeared in other bars from the same batch.
The control against the third step (i.e., actual substitution) was the
filming referred to earlier. However, I would not want to conclude
unequivocally that a skilled illusionist could not overcome this control,
especially in the absence of detailed information about how the filming was
done.
Yet another possible mechanism for trickery is for Girard to have
performed transformations on the test specimen itself prior to the session.
This hypothesis seems precluded in the cases of the first aluminum bar and
the steel cylinders, since tests for deformation and (in the latter case)
magnetism were performed at the beginning of the session. The hypothesis
also seems precluded for the second aluminum bar and first Duralumin plate,
since successive deformations were observed during the course of the trial.
No information is provided in the report that would preclude this
possibility for the other Duralumin plates.
The evidential weight of the findings that emerged from the structural
analyses per se is less than might have been hoped for. The effects on the
second aluminum bar (the first was not evaluated this way) seem to conform
to what would be expected by the application of ordinary physical force,
even though the force is greater than that which could be generated by an
unaided human. The authors concede that the effect on the Duralumin plates
could have been duplicated by a combination of shot-peening and polishing.
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Metal' Bending
different than expected given the amount of permanent deformation observed.
However, this conclusion rests heavily on the outcome of one control sample.
Is it safe to generalize widely from this one outcome, or might a larger
sample of such control specimens yield a distribution of outcomes which
might include (albeit as a distinct minority) an outcome analogous to that
found with the test specimens? The fact that the authors had to resort to a
control sample at all suggests that the answer to this question may not be
knowa.
Based on the information available in report, all the results except
those with the first, and possibly the second, aluminum bars are potentially
explainable by some form of substitution or pretransformation of specimens.
We must also remember that the subject is known to have conjuring skills and
might have used them at least once in the context of the research. On the
other hand, several factors weigh in favor of the results being truly
anomalous. As I argued in my discussion of the Delmore research (Chapter
6), the fact that a subject possesses conjuring skills is not by itself
sufficient grounds for discounting evidence obtained with that subject under
well-controlled conditions. The authors were aware of the possibility of
fraud, consulted with magicians, and in fact took several precautions to
preclude fraud. As a result, alternative hypotheses needed to account for
the results by trickery seem unparsimonious. Finally, the straightforward
results with the first aluminum bar seem especially resistant to normal
explanation. For these reasons, it is my opinion that the modest
conclusions reached by the authors are justified, and the "abnormal" results
they have uncovered deserve to be taken seriously. Assuming that no more
credible explanations of the Crussard results are forthcoming, further
research with Girard is warranted (despite what independent evidence there
may be of his use of conjuring) as well as a search for other subjects who
might be able to produce comparable effects.
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Chapter 10
SUMMARY AND
CONCLUSIONS
This review began with the premise that no adequate critique of the
experimental evidence for psi is possible without first addressing
philosophical issues about how research questions in parapsychology have
been formulated. In Chapter 1 it was maintained that the traditional demand
of a "conclusive experiment" as a necessary condition to verify the
existence of psi is inappropriate because it is inherently unfalsifiable.
Replicability is also inadequate as a criterion, because the replicability
of an effect says nothing about its cause.
The problem was pursued further by critiquing the formulation of
parapsychology's fundamental question; i.e., "Does psi exist?" This
question both reflects and reinforces the conflation of "psi" as subject
matter and "psi" as explanatory principle. A more appropriate question is
then proposed :
"How can ostensible psychic events (OPEs) be best
explained?"
This new question has several important implications.
First, it
implies that in order to demonstrate "psi" as a paranormal principle,
researchers must empirically confirm a theory or model embodying such a
principle, something parapsychologists themselves concede they have been
unable to do. Therefore, the conclusion that parapsychologists have
established "psi" can be rejected on logical grounds prior to evaluation of
the data per se.
On the other hand, absence of an adequate paranormal explanation of
OPEs does not imply the presence of an adequate conventional explanation. A
second implication of the new question is that the burden of proof falls on
anyone who claims to have explained OPEs either paranormally or
conventionally. Thus, the important question to be addressed by examination
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can be considered scientifically adequate. The standards for evaluating
conventional explanations of OPEs are the same empirical standards used in
the rest of science. For present purposes, these include internal evidence
for the hypothesis from within the experiment itself, empirical support for
the hypothesis in related contexts, and the plausibility of the hypothesis.
The remaining chapters have critically reviewed ten major
parapsychological research programs, eight from single laboratories and two
from multiple laboratories, employing the perspective described above.
Following is a brief summary of each of those reviews.
The Maimonides Dream Experiments
The first set of free-response ESP experiments to be touted as
providing strong support for the existence of psi was a series of
experiments on ESP in dreams supervised by Drs. Montague Ullman and Stanley
Krippner at Maimonides Medical Center. Each night, a subject was awakened
by the experimenter each time physiological monitors of his brain waves and
eye movement activity suggested that he had been dreaming. The subject then
was asked to give a dream report. Meanwhile, an agent located in another
room periodically attempted to telepathically influence the subject's dream
content by concentrating on a randomly selected art print. At the
completion of each series, outside judges attempted to match up the dream
reports (generally supplemented by the subject's morning-after associations
to his taped dream reports plus a "guess for the night") to the targets on a
blind basis. In most cases, the subjects also served as judges.
Eleven formal series were defined for the review, of which three
involved one trial per subject and the rest, multiple trials per subjects.
Two of the former group of studies were screening experiments used to select
subjects for the more definitive latter group of studies. In addition, the
results of several hundred pilot sessions were reported.
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Using a crude method of analysis based on how frequently the judges
ranked the target in the top half of the distribution, the combined results
for the multiple-trial-per-subject series and the pooled results of the
pilot sessions were both significantly positive, whereas the combined
results for the single-trial-per-subject series were not.
Attempts to replicate two of the significant studies by noted dream
researcher Dr. David Foulkes at the University of Wyoming, in consultation
with the Maimonides team, both failed. Critic Hansel attributed the failure
to tighter controls against fraud in the Wyoming experiments, whereas
parapsychologist Van de Castle, one of the subjects in both the Maimonides
and Wyoming experiments, stressed the debilitating effect of the skeptical
attitude of the Wyoming team.
-
Other criticisms of the Maimonides experiments included the claim that
the experimenter was not blind to the target, lack of a baseline or control
condition, and possible lack of intrajudge independence of the ratings or
rankings within a series.
The evaluation began with a meta-analysis of the eleven formal
Maimonides experiments using, where necessary, a worst-case approximation of
the variance to allow for the dependency problem. The suggestion that the
experimenter was not blind to the targets was attributed to a misreading by
Hansel of an ambiguous passage in one of the experimental reports. Control
judgings were considered to be unnecessary because, for each trial, the
other trials in the series served as an internal control. However, a
previously undiscovered flaw in the way the targets were randomized in
several of the significant Maimonides experiments and possibly in the
Wyoming replications was revealed. However, for this flaw to have had
practical consequences, certain other assumptions, the status of which is
indeterminate, must be satisfied. They include such things as whether the
original order was determined randomly. Also. this criticism does not anniy

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to all the successful series. As an explanation for the overall results,
this artifact is possible but highly improbable.
Remote Viewing
Several free-response ESP experiments using the remote viewing (RV)
procedure have achieved considerable publicity. The procedure was
originated by physicists Harold Puthoff and Russell Targ at SRI
International. In the initial series, with geographical sites as targets,
significant results were achieved by a group of nine subjects, with two
subjects, Pat Price and Hella Hammid, making the most substantial
contributions. Significant results were also obtained by a partly
overlapping sample of five subjects in a subsequent series where the targets
were pieces of office and lab equipment.
The main critics of the SRI experiments have been psychologists Richard
Marks and David Kammann. Their primary criticism was that failure to edit
the response transcripts combined with failure to randomize the materials
given to the judge allowed the judge to infer which transcript went with
which target site irrespective of the real accuracy of the subject's
description. An exchange of correspondence by the protagonists, which came
to include psychologists Charles Tart and Robert Morris as well, resolved
that the criticism was applicable to Price's data but may not have been
applicable to Hammid's data; however, other sources of biasing information
may have been present in the latter case. Rejudging of the Price data with
the biasing cues presumably removed from the transcripts confirmed the
criticism when the rejudging was conducted under the auspices of Marks and
Kammann, and refuted the criticism when it was conducted under the auspices
of Tart, Puthoff, and Targ. Unfortunately, neither of the rejudgings was
entirely adequate methodologically.
A somewhat related criticism was proposed by psychologist Ray Hyman.
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and the subject received feedback after each trial, the subject could have
gained unfair advantage by not including descriptors characteristic of
targets in preceding trials in his responses on subsequent trials. The
researchers countered that the criticism did not apply because redundancy of
target characteristics was introduced into the target pool. This is an
adequate rebuttal in theory, but more information about the targets would be
needed to confidently assess its adequacy in practice.
A second major criticism by Marks and Kammann (part of which was later
retracted) concerned circumstantial evidence that unsuccessful trials were
either not reported by the SRI researchers or classified post hoc as
informal. Analysis reveals that much of their case is attributable to
self-serving and implausible interpretations of statements made by Puthoff
and Targ, yet ambiguities still remain.
Major series of successful replications of the. RV experiments have been
reported by John Bisaha and Brenda Dunne and by Marilyn Schlitz. Although
these experiments were methodologically superior to the earlier SRI studies,
only the final Schlitz experiment seems to have fully addressed the
sensory-cue criticisms of Marks, Kammann, and Hyman. This study achieved
only modest significance. Unsuccessful replications have been reported by
Marks and Kammann and by another researcher skeptical of psi, Edward
Karnes. These unsuccessful studies themselves contained methodological
flaws, although in the case of Marks and Kammann this could have been
motivated by a desire to duplicate faithfully the SRI procedure.
Success at obtaining significant RV results thus seems highly
correlated with the attitudes toward psi of the principal investigators.
Differences in the motivation and enthusiasm of the judges selected by these
investigators is suggested as one possible explanation of this finding.
Finally, the reluctance of the SRI team to share their data with critical
investigators is seen as damaging to their credibility, although it is
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such data as a basis for unsubstantiated insinuations of fraud.
The Ganzfeld Debate
Several major parapsychological laboratories have reported significant
results in free-response ESP experiments in which subjects are exposed to a
short-term perceptual deprivation procedure called the ganzfeld. A data
base of 42 such experiments from ten principal investigators was the subject
of an exchange between parapsychologist Charles Honorton and psychologist
Ray Hyman.
The first issue addressed by the protagonists was the validity of the
claimed 55% replication rate of the ganzfeld paradigm. Hyman made two kinds
of arguments :
first, the claimed success rate was too high because (1)
experimental cells which should be treated as separate experiments were
either pooled or arbitrarily excluded, and (2) unpublished failures,
particularly if they involved small sample sizes, likely went unreported.
Second, he claimed that the .05 level as a criterion for significance was
too low because the published significance levels were not corrected for
various types of multiple testing. Honorton's principal rebuttal consisted
of an analysis of 28 of the 42 experiments for which a uniform test of
significance could be applied and which yielded a highly significant
outcome. He also noted that over 400 nonsignificant and unpublished studies
would be necessary to reduce the overall data base to nonsignificance.
My evaluation supported the claim that the data base was of a
non-chance character. Selection of the unit of analysis is somewhat
arbitrary and choosing the cell as the unit would be expected to yield a
lower success rate in the kind of analysis Hyman employed simply as a result
of. reduced power. Honorton's new analyses seem to adequately address the
problem of multiple testing; moreover, the uncorrected p-values are the
appropriate ones to use when the purpose is to assess experiments jointly as
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great majority of the studies yielded results in the same (positive)
direction.
The second major issue addressed by the protagonists was the
methodological adequacy of the experiments in the data base. Hyman cited
six categories of flaws each of which applied to 24%-74% of the studies.
They included :
failure to use duplicate target sets for judging, inadequate
randomization of targets, inadequate randomization of judging materials,
inadequate documentation, inadequate security against cheating by subjects,
and improper statistics. He concluded that the pervasiveness of these flaws
indicated general sloppiness in the conduct of the experiments. He
undertook several multivariate analyses to show that these flaws could
collectively account for the apparent significance of the results and could
explain why some experimenters achieved more successful results in ganzfeld
experiments than other experimenters. Honorton acknowledged the presence of
the flaws but argued that Hyman exaggerated their pervasiveness by coding
many studies as flawed that failed to meet his (Hyman's) stated flaw
criteria. Honorton's statistical consultant, Dr. David Saunders, questioned
the validity of Hyman's multivariate analyses, primarily on the basis of
probability pyramiding, statistical dependencies among the variables, and
insufficient sample size.
My statistical consultant agreed with Saunders" critique of Hyman's
multivariate analyses. Moreover, the significant bivariate correlations
between Hyman's flaw codings and study outcomes were attributable to coding
errors on Hyman's part. The one exception was that studies which achieved
target randomization by shuffling or similar informal methods did achieve
significantly better outcomes than those using more reliable randomization
procedures. In general, it was concluded that Hyman had not provided
empirical evidence of a link between methodological flaws and study
outcomes.
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On the other hand, the fact remains that the flaws must still be
considered in evaluating the data base. As Hyman points out, a flaw that
fails to discriminate successful from unsuccessful studies might still exert
a causal influence by interacting with other procedural factors. The
various flaws were analyzed in terms of the plausibility of the scenarios
they imply and found to be of questionable plausibility. In one case
(failure to use duplicate target sets) empirical research of relevance to
this issue exists. Given the objectives of most of these experiments, it is
my opinion that generalized sloppiness cannot be inferred from the flaws
that were uncovered, especially since most are reducible to incomplete
documentation in the reports.
Random-Event-Generator Research
The pioneer of, and the major contributor to, systematic research with
random event generators in parapsychology has been Helmut Schmidt of the
Mind Science Foundation. His 15 years of research with REGs have yielded 14
experimental reports and can be divided into four phases. In the first
phase, ESP methodology predominated, with the subject guessing which of four
states the REG would select for each trial. In the second phase, subjects
attempted to bias a rapidly generated sequence of events by PK. In the
third phase, a version of the "observational theories" was tested by having
subjects observe or listen to prerecorded sequences of targets and thereby
attempt to bias them retroactively. In the fourth phase, the targets were
pseudo-random sequences derived by applying an algorithm to a seed number
generated by an REG.
Highly significant results in the direction of the subject's intent
were manifested consistently in all phases of Schmidt's research program.
The modest experimental manipulations Schmidt employed generally had little
effect on the results. Type or rate of feedback, and whether the targets
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There were some indications that slower target generation rates were
associated with higher scoring and that actual effort to influence the REG,
as opposed to just observing the feedback, facilitated scoring but was not
necessary for PK to occur. However, since these variables were not
manipulated in proper experimental designs, interpretations must be made
cautiously.
The most important criticism against Schmidt's research has been that
the randomization tests of his REG were either inadequate or inadequately
described, in particular that they might not preclude short-term biases.
The fact that scoring covaried with changes of target and the adoption of
better control tests in later experiments reduce the force. of this
criticism.
The fact that Schmidt has been more consistently successful than other
investigators in obtaining significant results in REG experiments, coupled
with evidence from his research and others" that motivation in the absence
of directed effort is sufficient to obtain such effects, raises the
possibility that Schmidt himself is the source of the effects in his
experiments.
The other major research program using REG methodology is being
conducted under the supervision of Dr. Robert Jahn of Princeton University.
So far, 22 subjects have completed 61 formal series involving a total of
569,450 runs of 200 trials each.
Subjects were asked to use PK to either
increase (PK+) or decrease (PK-) the generation of a binary target that was
alternated from trial to trial. About one-third of the runs were baseline
runs for which no PK influence was attempted.
Using the run as the unit of analysis, results indicated a significant
displacement of the mean in the intended direction in both the PK+ and PK-
conditions.
Otherwise, the distributions were normal. The mean of the
distribution of baseline runs did not differ significantly from MCE. Using
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variance was significantly large for the PK- series and approached
significance for the PK+ series. There was a suggestive restriction of
variance in the baseline series.
The significant effects with the run as the unit were attributable to
runs where the subject chose if the run was to be PK+, PK-, or baseline.
It
also seems to be the case that the results are largely if not exclusively
attributable to one subject who contributed 14 of the 61 series. The
results of this subject are independently significant, whereas the results
of the remaining subjects generally are not. This subject also contributed
the bulk of the significance in 34 exploratory series involving various
minor changes in test parameters. It is possible that some of the other
subjects in Jahn's research could have also achieved significant results had
they completed as many runs as this one subject, but that remains to be
demonstrated.
Internal analyses suggest that data selection by post-hoc
classification of series as exploratory or optional stopping, if either had
occurred, would not impact the positive conclusions from the research.
Checks on proper functioning of the apparatus and failsafes against
recording errors appear to have been extensive. On the other hand, no
systematic efforts were made to monitor subject behavior during the test
sessions. However, it would appear that data tampering would require
computer sophistication on the part of the subject and knowledge of the
system.
Finally, it is noted that it is not necessary to assume a causal
influence on the functioning of the REG to explain Jahn's results. A simple
alternative, which could in principle account for all the significant
effects reported in the formal series (including the variance effects), is
judicious "sorting" of a random ("chance") distribution of run scores into
the PK+, PK-, and baseline categories. Whether this or a more
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research.
The Delmore Experiments
The Delmore experiments consisted primarily of restricted-choice
card-guessing studies conducted with a male law student (B.D. ) at
J. B. Rhine's Institute for Parapsychology in the early 1970s. The principal
investigators were Drs. B.K. Kanthamani and Edward Kelly.
The better controlled of the card-guessing methods was labeled
"single-card clairvoyance" (SCC). The experimenter, who was seated at a
desk, removed for each trial one of a large batch of ordinary playing cards
from a drawer, placed it inside an opaque folder, and exposed the folder to
B.D. who, seated on the other side of the desk, orally made his guess. Four
formal series totaling 46 runs of 52 trials each were completed with this
method.
The other method, called the shuffle method, involved the experimenter
and B.D. each shuffling a deck of cards and then matching up the two
sequences.
Six formal series totaling 55 runs were completed using this
method.
Results were evaluated by a statistic developed by Fisher which gave
independent assessments of the scoring rates for number, suit, and the two
combined (exact hits). For both methods, highly significant results were
obtained for exact hits. B.D. was especially successful in predicting when
he would achieve an exact hit:
with the SCC method he made 20 such
"confidence calls," of which 14 were exact hits; with the shuffle method,
all 50 confidence calls were exact hits.
With the SCC method, it was found that on high-scoring runs B.D. 's
misses revealed a systematic structure of errors or "confusions" that
matched the structure of errors he made when briefly exposed
tachistoscopically to slides of the playing cards, suggesting that the ESP
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Finally, eight formal tests (5377 trials) using an REG of the Schmidt
type also yielded highly significant results.
The major critic of the Delmore experiments has been statistician Persi
Diaconis, who argued that the experiments should be discounted because they
were not monitored by a magician. His concern was piqued because he had
witnessed B.D. give an informal demonstration of alleged psychic abilities
which convinced him that B.D. had utilized sleight-of-hand. Kelly responded
that it was illegitimate to generalize from such an informal demonstration
to formal experiments where sleight-of-hand could be precluded.
If B.D. were motivated to use magic tricks, it is conceivable that, in
the case of the SCC method, he could have occasionally seen cards being
transferred from the desk drawer to the opaque folder were he to have a
concealed pocket mirror on his lap. However, an interview with
Dr. Kanthamani suggests that the desk used in these experiments had a back,
which would preclude this hypothesis. The shuffle method seems generally
less secure against manipulation than the SCC method because in most cases
the subject had physical contact with the call deck after knowing the target
order. Sensory-cue or fraud hypotheses are strained in the case of the
automated REG experiments, however. It is concluded that although the
authors should have shown more sensitivity to the possible use of
sleight-of-hand by B.D., Diaconis" critique lacks scientific weight in view
of his failure to propose any counterhypotheses.
Target randomization was less than ideal with both card-guessing
methods. However, the effects are too strong for artifacts of this type to
be a likely explanation of the results. This conclusion is reinforced by
empirical examination of the target sequences in the SCC series. Other
sources of artifact appear to have been successfully precluded.
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Correlational Studies
Although studies of the correlations between psi scores and
psychological variables do not bear directly on the anomalous nature of the
former, they can make important contributions by demonstrating the existence
of a coherent class of events, identifying factors that may lead to improved
reliability of psi scores, and serving as the building blocks for theories.
However, due to the low reliability of psi scores, consistent confirmations
of correlational findings cannot be expected. Thus, "real" effects can only
be uncovered for those predictors which have been used frequently enough in
psi research to provide a sufficiently large data base for meaningful
meta-analysis.
The only predictors that have enjoyed sufficiently widespread use to
spawn systematic meta-analyses have been the personality factors of
extraversion and neuroticism, belief in psi (the "sheep-goat" variable), and
hypnosis. In the case of extraversion, Sargent reported 19 of 54
relationships with ESP scores to be significant, with the extraverts scoring
higher in 18 of the 19. Palmer found that 18 of 24 experimental series
where subjects were tested individually or in pairs revealed more negative
scores among the more neurotic subjects. A later survey of ten studies
using the projective Defense Mechanism Test as the predictor yielded lower
scoring by the more defensive subjects in all cases, with one-tailed
significance achieved in seven of the ten. "Sheep" (believers) scored
higher than "goats" in 18 of 21 series reviewed by Palmer. Schechter found
that in 16 of 20 series subjects scored higher under hypnosis than in the
"waking" state. All seven of the significant differences favored the
hypnosis condition. In all these cases, the trends across studies were
consistent to a statistically significant degree.
Evaluation focused on the validity, the interpretations, and the
generality of the relationships. Procedural flaws which impacted on the
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same type and prevalence as those uncovered by Hyman in his review of the
ganzfeld experiments. Special consideration was given to a criticism raised
by Charles Akers that subjects often knew their ESP scores before completing
the psychological questionnaires. Although this flaw was rather widespread
in the data base, further analyses suggested that it was unlikely to have
accounted for the results.
Little research has been done to evaluate possible interpretations of
the correlational effects reviewed in this chapter, although several have
been suggested. The extraversion-ESP relationship has been attributed both
to differences in cortical arousal and to adaptability to the social
situation of psi testing. The hypnosis-ESP relationship has been attributed
both to the implicit or explicit suggestions of success and to the altered
state of consciousness induced by hypnotic induction procedures. Stanford
noted various inadequacies in the control conditions of these studies that
might bear on the interpretation of results, including lack of
counterbalancing, nonrandom assignment of subjects to conditions, and
experimenters not being blind to the treatment. Although these artifacts
are considered less . problematic than Stanford suggests, they cannot be
completely discounted.
In the absence of a planned series of attempted replications, the
robustness or generality of the relationships considered in this chapter
cannot be assessed with great confidence, although the failure of one
investigator (Thalbourne) to confirm the extraversion-ESP effect in a series
of experiments argues for caution. Because the meta-analyses reviewed in
this chapter generally compared the ratio of positive to negative outcomes
rather than the proportion of significant outcomes per se, bias due to
nonpublication of chance studies is considered unlikely. Of greater
importance is the fact that the significant studies are not evenly
distributed among the investigators who conducted them, although studies by
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Moreover, parapsychologists as a group constitute a rather specialized
population when compared to scientists generally or even psychologists. The
explanation of the "experimenter effect" in parapsychology is not yet known,
but if adequate replicability is to be achieved, priority must be given to
its elucidation.
1
Psi-Mediated Instrumental Response
One of the more serious attempts at theorizing in parapsychology is Rex
Stanford's model of psi-mediated instrumental response (PMIR). The primary
postulate of the model is that " ... [an] individual, through extrasensory
means, actively scans his environment for objects and events ... which are
relevant to his needs and that when such information is discovered he tends
to respond to it in accordance with his typical dispositions toward such
objects and events." (Stanford & Stio, 1976, p. 55) An important implication
of the model is that psi can occur without the subject being aware of its
occurrence or intending to use it. PMIR occurs as economically as possible
through a variety of mediating vehicles, such as modification of the timing
of an already selected response. The disposition toward PMIR is governed by
the strength of the organism's needs, thereby linking the model to
reinforcement theory in psychology. The model also applies to PK, which
"can occur as a response to extrasensory or sensory information which has
never been in the conscious focus of the PK. .. agent ... " (Stanford, 1974b,
p. 350)
Stanford published five related experiments to test the model. A
covert ESP test was developed for these experiments. Subjects, generally
males, were given a 10-item word-association test and the response latencies
were measured. If the fastest (or, in some cases, slowest) latency was
associated with a randomly selected key word, the subject would subsequently
engage in a pleasant task; otherwise, he would engage in an unpleasant
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related to the standardized difference between the response latency to the
key word and the mean response latency to all the words. In the one PK
experiment, the method was simply to leave an REG running while the subject
was performing the unpleasant task. If the REG produced a significant
outcome, the subject escaped to the pleasant task.
Only in the PK experiment was the overall scoring level unequivocally
significant. However, the primary objective of all the experiments was to
test predictions from the PMIR model by manipulation of independent
variables. The predictions fell into four classes: (1) PMIR scores will
correlate with scores on standard (overt) psi tasks; (2) PMIR will most
likely be facilitated by readily available cognitions (operationally defined
as primary responses on the word-association test); (3) PMIR will be
related to the strength of the need which it subserves; and (4) the
direction of PMIR will be influenced by whether the subject has a positive
or negative self-concept. All six tests of these predictions yielded
results in the predicted direction, and three were significant.
The PMIR model and research program have not been addressed by outside
critics. However, Stanford himself eventually abandoned the model because
he found its "psychobiological" or cybernetic assumptions to be untenable.
He replaced it with a simpler "conformance model" which did not assume any
communication of information across a channel or assume that PK is guided in
a step-by-step fashion by unconscious ESP.
The above problems notwithstanding, the PMIR model and the basic test
paradigm seem sound. The major methodological objections were failure to
check on the efficacy of the experimental manipulations and failure to
report all potential tests of the hypotheses across experiments. How
subjects were assigned to conditions was not fully specified in all cases.
Finally, it would have been better to modify the PMIR model than to abandon
it wholesale. Many "psychobiological" assumptions must be retained even in
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research to which it has led does not follow from it uniquely.
Metal Bending
A renewed interest has recently developed among parapsychologists in
large-scale (macro) PK effects, particularly metal bending. The most
extensive research on metal bending has been conducted by Dr. John Hasted,
who has worked with 20 subjects, mostly adolescents. Subjects were asked to
bend or otherwise deform metal specimens (latchkeys or bars of aluminum
alloy) without touching them. The specimens were attached to resistive
strain gauges or (in later work) piezoelectric sensors.
Signals from these
devices were then amplified and registered on chart recorders.
Although actual bending was observed to have occurred in only a
minority of sessions, anomalous signals with rapid rise times frequently
appeared on the chart records. In some sessions, signals frequently
appeared simultaneously from sensors separated up to several feet from each
other. The fact that such "synchronous" signals seemed especially prevalent
when the specimens were aligned vertically led Hasted to postulate a
"surface of action" extending outward from the subject in a vertical plane.
Attempts to gain further information about the nature of the forces
involved by locating multiple strain gauges across the width or along the
length of a specimen generally failed to produce results consistent with
simple extension, contraction, or bending hypotheses. This led Hasted to
refer to his results more generally as "metal churning" as opposed to "metal
bending." However, the effects seemed to be somewhat localized in the middle
of specimens when strain gauges were distributed along their surfaces.
At least one subject seemed able to trigger electronic touch detectors
without actually touching the specimen, suggesting that some of the
ostensible strain effects may have been electrical in nature. Some unknown
form of conduction of electrical charge from the subject's body through the
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research with this subject.
Physical contact with the specimens during the trials generally seems
unlikely as an explanation of either the macro- or micro-effects, although
explanations of the procedures were inadequate to preclude substitution of
bent for unbent specimens. Localized artifactual influences on individual
specimens (e.g., air currents from blowing) seem unlikely but were not
thoroughly ruled out in all cases. They are not precluded by the claimed
synchronicity of signals from different sensors, because the operational
definition of synchronicity was not sufficiently precise to rule out
radiation of an electromagnetic signal from one point to several sensors.
Likewise, if one can trust Hasted's claim that the subject had no
opportunity to interact directly with the chart recorder, the employment of
dummy loads along with electrical shielding of the test channels minimize,
although they do not rule out, more global artifacts.
Even if one grants the paranormal origins of the signals, Hasted's
methodology makes it difficult to draw valid conclusions about their nature,
including whether or not they truly represent strain. Use of an
inadequately fast chart recorder, failure to adopt proper principles of
experimental design, and failure to use statistical analyses are the most
serious problems. In particular, it is impossible to distinguish basic
physical characteristics of the phenomena from those correlated with
preferences, attitudes, etc., of the subject or experimenter.
Although "no-touch" protocols are generally considered necessary in
metal-bending research, reports by the French metallurgists Charles Crussard
and J. Bouvaist of effects produced with touch by the subject Jean-Paul
Girard are nonetheless worthy of scientific attention, in part because
anomalous structural changes in the specimens were claimed. The authors
described eight of the 20 trials conducted with Girard which they felt were
conducted under adequately controlled conditions. The specimens were two
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plates. During the trials, Girard generally was allowed to touch and hold
the specimens sometimes inside and sometimes outside a sealed glass tube,
while at all times being observed by the experimenters.
Gross physical deformations (bending) were observed in only four of the
specimens.
Structural changes inconsistent both with a hypothesis of
physical bending and with results from physically bent control samples were
found for the stainless steel cylinder (excessive and anomalous distribution
of magnetic martensite converted from austenite) and the Duralumin plates (a
high density of small dislocation loops). The latter effect was found to be
reproducible by a combination of shot-peening and polishing, however. More
information about the base rates of anomalous results from the kinds of
control tests the authors used would have been desirable.
The fact that Girard is known to possess conjuring skills demands
caution in interpreting the above results. Despite extensive precautions by
the authors, including consulations with magicians, video recording of
trials, and the marking of test specimens, only in the case of the bending
of one of the aluminum bars do the controls as reported seem to completely
rule out the possibility of Girard substituting previously deformed
specimens for the test specimens.
Nonetheless, the assumptions that must be
made to explain away these results seem rather farfetched, at least those
assumptions of which this reviewer is aware.
Conclusions and Recommendations
My greatest difficulty in reviewing the research reports was the
inadequacy of the methodological descriptions in most of them.
It is likely
that many of the criticisms raised by myself and others would have been
answered if the reports had been more thorough. My general impression is
that investigators trained as experimental psychologists gave better reports
than those trained in the physical sciences or psychiatry. Perhaps the
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reporting in their own fields.
Because of my background as a psychologist,
I am more accustomed to the level of reporting found in the better
psychology journals, and by that yardstick I found many of the reports I
reviewed wanting. It seems to me that because so little is known about the
effects studied in parapsychology, and because the effects are so often
weak, unstable, and subject to "artifactual" influences, a higher degree of
specificity is required in parapsychology than in more established
disciplines. The Parapsychological Association is currently taking steps to
improve the quality of reporting in the major journals.
However, I would not want to go to the other extreme and suggest that
the documentation is so poor that the reports cannot be taken seriously.
In
virtually all cases, it was good enough to make critical reviews of the
reports possible and potentially enlightening, and further methodological
details sometimes came to light in exchanges with critics.
What are the conclusions that can be reached considering the research
programs as a whole? With the possible exception of the PMIR and
correlational programs, I think it fair to conclude that the results cannot
be attributed to "chance." In most of the programs the cumulative results
reach high levels of statistical significance. Because of these high
levels, artifacts due to such things as violation of statistical
independence, optional stopping, etc., are likely to be trivial and in most
cases were shown to be trivial. Likewise, absurdly large numbers of
relevant nonsignificant studies must be assumed in order to cancel out these
trends. In short, something is clearly going on in these research projects
that cannot be explained as statistical errors of measurement.
The question then becomes whether the results of these research
programs can confidently be attributed to conventional mechanisms. At the
risk of becoming a bore, I must again stress that the issue is not whether
such mechanisms are possible but whether they are scientifically adequate as
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evidence in the data to make this assessment, and even less frequently was I
able to cite relevant empirical evidence from other studies. Thus, to a
large extent I had to resort to plausibility, a disturbingly subjective
criterion.
The most prevalent of these conventional explanations as applied to the
projects considered in this review involve inadequate or inadequately
described randomization procedures. Problems include (1) crude or improper
methods of target selection in the Delmore experiments and in some of the
ganzfeld, remote viewing, and dream experiments; (2) inadequate
randomization of judging materials in some of the remote viewing and
.
ganzfeld experiments; and (3) baseline tests in some of Schmidt's REG
experiments which did not adequately duplicate the procedures used in the
experimental conditions.
However, it is doubtful that slight departures from randomness can
adequately account for the magnitude and consistency of results in these
research programs. Shuffling methods, for example, if undertaken with the
care one would expect from a conscientious researcher, should be expected to
yield sufficiently adequate randomization of targets for the purposes
required. On the other hand, only in the Delmore SCC experiments was the
adequacy of the actual target sequences evaluated. Research on the degree
to which biased sequences actually effect results in standard psi testing
paradigms would be useful. In the absence of such data, inadequate
randomization represents a possible but not particularly plausible
counterhypothesis for the results considered in this review.
The second major class of counterhypotheses are those concerning
sensory cues (in ESP) or physical manipulation (in PK). These "artifacts"
can be either incidental or intentional, i.e., fraudulent. If the latter,
the fraud can be on the part of the subject(s) or investigator(s), or both.
Opportunities for incidental sensory cueing seem possible in some of the
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sensitivity on the part of subjects and judges that seems implausible and
lacks an empirical basis. Where correlations between the possibility of
such leakage and psi scores have been computed (as in the ganzfeld and
hypnosis experiments), they have been found to be nonsignificant.
The concern about subject fraud is most acute in cases where the
subjects are psychics with a reputation to defend (or promote) and/or are
known to have conjuring skills. Of the research projects described here,
the Delmore and macro-PK projects are the ones where these conditions seem
most applicable. However, in neither case has anyone yet suggested a
cheating mechanism that would be allowed by the methods as described in the
reports.
Two other conventional possibilities, fraud on the part of an
experimenter and some unknown artifact that cannot be inferred from the
reports, cannot be assessed. However, the unreliability of ostensible
psychic events (OPEs), and in particular the "experimenter effect," are
likely to be reinforcing to anyone who is inclined to entertain these kinds
of hypotheses. On the other hand, any interpretations of these frustrating
characteristics of parapsychological data must be considered speculative at
this time.
The bottom line is that the data reviewed in this report constitute
genuine scientific anomalies for which no one has an adequate explanation or
set of explanations. They are of scientific interest because, when taken at
face value, they go beyond our present understanding of the most fundamental
principles on which conventional science is based. In other words, if they
are what they appear to be, their theoretical (and, eventually, their
practical) implications are enormous. On the other hand, if the anomalies
have conventional explanations, it is important to know this as well.
Research in parapsychology has much in common with research in other
scientific fields, particularly psychology. An understanding of "artifacts"
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in barapsychology could teach us much about how comparable artifacts impact
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these other fields, where we might ordinarily be less inclined to look for
them.
Progress in understanding OPEs has been frustratingly slow. There are
many reasons for this, perhaps the most important of which is the
elusiveness of OPEs. Yet little attention has been focused directly on
solving this problem, which constitutes another important reason why
progress in parapsychology has been so slow. Both parapsychologists and
their critics have been preoccupied with determining whether there exist
demonstrations of "psi" that preclude all conventional alternatives.
As I
have attempted to argue in Chapter 1, this approach is both futile and
regressive. If progress is to be made, investigators must learn to accept
the anomalies as such and then proceed to do process-oriented research to
uncover the mechanisms (paranormal or conventional) that account for them.
Research is especially needed to help us understand why OPEs occur so
erratically and more frequently in some labs than in others. Although, as I
mentioned in Chapter 1, much of the research in parapsychology is already
process-oriented, this research is unsystematic and relatively underfunded.
Although the projects covered in this report sometimes contained
process-oriented elements, only in the PMIR and Delmore experiments were
proper experimental designs consistently utilized. Funding agencies could
provide a valuable service toward advancing knowledge in this area by
discouraging investigations that merely give us one more demonstration of an
anomaly and by encouraging investigations oriented toward uncovering the
mechanisms that might be responsible for these anomalies or toward
increasing their reliability.
Investigators most likely to make progress in this area are those who
combine (1) knowledge of the literature in parapsychology and directly
related subdisciplines in other fields, (2) experience with psi testing, (3)
basic scientific competence, and (4) a sober, level-headed attitude.
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interpretation of the anomalies should be discouraged. A track record of
getting the anomalies to occur in one's lab is obviously desirable but not
necessary. A conventional theorist who cannot get the anomalies to occur
could still make important research contributions by doing basic research on
the conventional processes he or she thinks are responsible for others
getting them. Likewise, if an unsuccessful paranormal theorist were to
uncover a procedure that suddenly turned failure into success, the result
could be especially important.
1
A Note on Applications
If the effects reviewed in this report represent paranormal human
abilities, the potential for application is both obvious and significant.
What is at issue is a qualitative increase in the capacity of man to
interact with his environment, both in terms of acquiring information about
it (ESP) and manipulating it (PK). In a sense, it is misleading to restrict
discussion to particular applications such as medicine or police work. The
fact is that these alleged abilities are applicable to the entire range of
human activity. Society would never be the same if these abilities are real
and could be brought under control.
Determining whether "psi" can be applied effectively in practical
situations is the primary function of applied research in parapsychology.
This is in contrast to basic research in parapsychology, where the objective
is to understand the mechanism behind these effects and, in particular,
whether or not the mechanism is "paranormal." These different objectives
require different fundamental research strategies. Basic research requires
controls against "normal" mechanisms, attempts to uncover correlates of the
effects, and tests of hypotheses derived from paranormal theories. Strictly
speaking, none of the above is required for applied research. In concrete
terms, the purpose of applied research is to show whether psychics, doing
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hey do, are more successful at solving a particular problem than
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the best currently available expertise or technology. Whether the psychic
might be aided in achieving this objective by sensory cues, for example, is,
from the practical point of view, irrelevant. (Of course, if it were
exclusively sensory cues, the kinds of lofty outcomes alluded to in the
first paragraph would not be expected. ) For the above reasons, I prefer the
more theoretically neutral term "applied intuition" over "applied psi" to
label the process under study in applied parapsychological research.
One methodological implication of the preceding analysis is that some
of the constraints placed upon psychics in basic research might be relaxed
in applied research. Insofar as this improves the mood, confidence, and
relaxation of the psychic, and insofar as these positive psychological
attributes do indeed facilitate performance on "psi" tasks, psychics should
be somewhat more successful in applied research contexts than in many basic
research contexts. At the same time, it should be stressed that in other
respects the methodology of applied research must be as rigorous as that
demanded of basic research. In particular, the control expertise or
technology must be rigorously defined and executed, the results from the
psychic and control attempts must be directly and precisely comparable, and
proper principles of experimental design must be employed.
A useful principle that can be, and has been, exploited in applied
parapsychological research is the majority vote principle. It has been
demonstrated on more than one occasion that a single subject who is
acquiring a small degree of information can increase his or her reliability
by repeatedly guessing the same target (e.g., Ryzl, 1966; Puthoff, in
press). A related technique is to have multiple subjects attempt to acquire
information about a single target. In applied research, this translates
into having a group of psychics independently attempt to gather impressions
about a single target or target event. Standard statistical techniques can
be used to assess whether the degree of agreement among the psychics exceeds
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what would be expected by chance.
If it does, then in theory at least, the
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particular points on which the psychics agree should be the most accurate
ones.
An important implication of the majority-vote principle is that the
small magnitude of the effects found in most psi experiments need not
preclude their successful application.
It is the poor reliability of the
effects that creates the problem.
I have been able to find no applied research projects of sufficient
extent and scientific merit to justify detailed review by the criteria set
forth in Chapter 1, even granted the modifications presented above. The
best research I could find were two studies by Martin Reiser who, in
cooperation with the Los Angeles Police Department, attempted to assess the
ability of local psychics to provide practically useful information about
crimes (Reiser & Klyver, 1982; Reiser, Ludwig, Saxe, & Wagner, 1979). In
each study, twelve psychics were given a piece of physical evidence in a
concealed envelope from each of four crimes and asked to give their
associations. (In the first study, the psychics were also allowed to see
the evidence unconcealed. ) In the second study, two control groups (college
student's and homicide detectives) were used. A double-blind protocol was
applied in both experiments.
Although the methods of analysis were crude,
in neither experiment did the psychics succeed in providing useful
information. (In the first study, a post-hoc analysis I conducted revealed
that the four amateur psychics obtained significantly higher scores [low as
they were] than did the eight professional psychics!)
A much more ambitious project was recently undertaken by Stephen
Schwartz (1982), who asked a team of psychics, including Hella Hammid (see
Chapter 3), to use remote viewing in an effort to locate buried
architectural sites of ancient Egypt. These data were compared to judgments
rendered by archaeological experts. It is difficult to be critical of this
research because of the overwhelming logistical problems which the authors
faced and which are discussed at great length in the book. Nonetheless, the
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collected or evaluated in a way that allowed definitive conclusions to be
drawn. This difficulty is exacerbated by the fact that the book was written
more like a novel than a scientific report. However, the general approach
which Schwartz is taking provides a good model for applied parapsychological
research.
Perhaps the most important potential application of psi in the eyes of
the general public is unorthodox healing. Incredibly, I am not aware of a
single published report of a properly controlled experiment of psychic
healing of humans. I am, however, aware of such a study recently completed
at the Universtiy of Utrecht (The Netherlands) and which should soon be
available.
.
Despite countless testimonials in the popular media to dramatically
successful examples of applied intuition, the scientific evidence does not
suggest that this intuition is sufficiently reliable to compete with or even
usefully supplement presently available alternative methods. However, so
little properly controlled evaluation research has been done that any firm
conclusions about the efficacy of applied intuition appear premature.
Although such evaluation research can and should be undertaken, it is my own
opinion that applied intuition will never have a significant social impact
until the mechanisms underlying this intuition (or psi) are better
understood. Although such understanding is not logically necessary for
successful application, and there are precedents for successful application
in the absence of understanding, it seems to me that if such were the case
in parapsychology successful application would already have become evident
in the culture and routinely employed. Thus, it is my view that basic
research should be given precedence over applied research in parapsychology
at the present time.
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REFERENCES
Akers, C. (1984). Methodological criticisms of parapsychology. In S. Krippner
(Ed.), Advances in Parapsychological Research. Vol. 4 (pp. 112-164).
Jefferson, NC: McFarland.
Alcock, J.E. (1981). Parapsychology: Science or Magic? Elmsford, NY: Pergamon.
Beloff, J. (1979). In defence of the "psychobiological" paradigm. In W.G. Roll
(Ed.), Research in Parapsychology 1978 (pp. 11-12). Metuchen, NJ:
Scarecrow.
Belvedere, E., & Foulkes, D. (1971). Telepathy and dreams: A failure to
replicate. Perceptual and Motor Skills, 33, 783-789.
Bertini, M., Lewis, H.B., & Witkin, H.A. (1969). Some preliminary observations
with an experimental procedure for the study of hypnagogic and related
phenomena. In C.T. Tart (Ed.), Altered States of Consciousness, (pp.
95-114). Garden City, NY: Doubleday.
Bisaha, J., & Dunne, B.J. (1977). Precognitive remote viewing in the Chicago
area: A replication of the Stanford experiment. In J.D. Morris, W.G.
Roll, & R.L. Morris (Eds.), Research in Parapsychology 1976 (pp. 84-86).
Metuchen, NJ: Scarecrow.
Bisaha, J.P., & Dunne, B.J. (1979). Multiple subject and long-distance
precognitive remote viewing of geographical locations. In C.T. Tart, H.E.
Puthoff, & R. Targ (Eds. ), Mind At Large (pp. 109-124), New York:
Praeger.
Blackmore, S. (1980). The extent of selective reporting of ESP ganzfeld
studies. European Journal of
Parapsychology, 3, 213-219.
Braud, W.G. (1978). Allobiofeedback: Immediate feedback for a psychokinetic
influence upon another person's physiology. In W.G. Roll (Ed. ), Research
in Parapsychology 1977 (pp. 123-134). Metuchen, NJ: Scarecrow.
Braud, W.G. (1980). Lability and inertia in conformance behavior.
Journal of
the American Society for Psychical Research, 74, 297-318.
Approved For Release 2000/08/10 : CIA-RDP96-00789R003800360001-1
:

1
Page 230
References
Approved For Release 2000/08/10 : CIA-RDP96-00789R003800360001-1
Braud, W.G., & Wood, R. (1977). The influence of immediate feedback on
free-response GESP performance during ganzfeld stimulation. Journal of
the American Society for Psychical Research, 71, 409-427.
Braud, W.G., Wood, R., & Braud, L.W. (1975). Free-response GESP performance
during an experimental hypnagogic state induced by visual and acoustic
ganzfeld techniques: A replication and extension. Journal of the American
Society for Psychical Research, 69, 105-113.
Broad, C.D. (1953) . Religion, Philosophy and Psychical Research. New York:
Harcourt Brace.
Carpenter, J.C. (1971). The differential effect and hidden target differences
consisting of erotic and neutral stimuli. Journal of the American Society
for Psychical Research, 65, 204-214.
Casler, L. (1962). The improvement of clairvoyance scores by means of hypnotic
suggestion. Journal of Parapsychology, 26, 77-87.
Cattell, R.B. (1965). The Scientific Analysis of Personality. Baltimore:
Penguin.
Child, I.L. (in press). Psychology and anomalous observations: The question of
ESP in dreams. American Psychologist.
Child, I.L., & Levi, A. (1979). Psi-missing in free-response settings. Journal
of the American Society for Psychical Research, 73, 273-289.
Collins, H.M., & Pinch, T.J. (1982). Frames of Meaning: The Social
Construction of Extraordinary Science. London: Rutledge & Kegan Paul.
Crussard, C., & Bouvaist, J. (1978). Expériences psychocinétiques sur
éprouvettes métalliques. [Psychokinetic experiments with metal test
samples]. Memoires scientifiques de la revue de méttalurgie. 13-23.
Diaconis, P. (1978). Statistical problems in ESP research. Science, 201,
131-136.
Diaconis, P. (1979). Rejoinder to Edward F. Kelly. Zetetic Scholar, No. 5,
29-31.
Approved For Release 2000/08/10 : CIA-RDP96-00789R003800360001-1
1

I
References
Approved For Release 2000/08/10 : CIA-RDP96-00789R003800360803f-1231
Diaconis, P. (1980). Replies to Edward F. Kelly and Charles T. Tart. Zetetic
Scholar, No. 6, 131-132.
Dingwall, E.J. (1968). Abnormal Hypnotic Phenomena. London: Churchill (4
vols.).
Dunne, B.J., & Bisaha, J.P. (1979). Precognitive remote viewing in the Chicago
area: A replication of the Stanford experiment. Journal of
Parapsychology, 43, 17-30.
Dunne, B.J., Jahn, R.G., & Nelson, R.D. (1983). Precognitive remote
perception. Technical Note PEAR 83003. Engineering Anomalies Research
Laboratory, School of Engineering/Applied Science, Princeton University,
Princeton, NJ. (178 pp.).
Epstein, R.A. (1977). The Theory of Gambling and Statistical Logic. New York:
Academic Press.
Eysenck, H.J. (1960). The Structure of Human Personality (2nd Ed. ). London:
Methuen.
Eysenck, H.J. (1967). Personality and extra-sensory perception. Journal of the
Society for Psychical Research, 44, 55-71.
Fisher, R.A. (1924). A method of scoring coincidences in tests with playing
cards. Proceedings of the Society for Psychical Research, 34 (Part 91),
181-185.
Fisk, G.W., & West, D.J. (1958). Dice-casting experiments with a single
subject. Journal of the Society for Psychical Research, 39, 277-287.
Foulkes, D., Belvedere, E., Masters, R.E.L., Houston, J., Krippner, S.,
Honorton, C., & Ullman, M. (1972). Long-distance, "sensory-bombardment"
ESP in dreams: A failure to replicate. Perceptual and Motor Skills, 35,
731-734.
Glass, G.V., McGaw, B., & Smith, M.L. (1981). Meta-analysis in Social
Research. Beverly Hills, CA: Sage Publications.
Grad, B., Cadoret, R.J., & Paul, G. I. (1961). The influence of an unorthodox
ApprovedForRelease2000/08/101GARDA86007890003800360001-1f

Page 232
References
Approved For Release 2000/08/10 : CIA-RDP96-00789R003800360001-1
Parapsychology, 3 (No. 2), 5-24.
Habel, M.M. (1976). Varying auditory stimuli in the ganzfeld: The influence of
sex and overcrowding on psi performance. In J.D. Morris, W.G. Roll, &
R.L. Morris (Eds), Research in Parapsychology 1975 (pp. 181-184).
Metuchen, NJ: Scarecrow.
Hansel, C.E.M. (1966). ESP: A Scientific Evaluation. New York: Scribners.
Hansel, C.E.M. (1980). ESP and Parapsychology: A Critical Re-evaluation.
Buffalo: Prometheus.
Hasted, J.B. (1976). An experimental study of the validity of metal-bending
phenomena. Journal of the Society for Psychical Research, 48, 365-383.
Hasted, J.B. (1977). Physical aspects of paranormal metal bending. Journal of
the Society for Psychical Research, 49, 583-607.
Hasted, J.B. (1978). Merkmale paranormaler metallbiegephänomene. Zeitschrift
für Parapsychologie und Grenzgebiete der Psychologie, 20, 173-181.
Hasted, J.B. (1981). The Metal-Benders. London: Routledge.
Hasted, J.B., & Robertson, D. (1979). The detail of paranormal metal bending.
Journal of the Society for Psychical Research, 50, 9-20.
Hasted, J.B., & Robertson, D. (1980). Paranormal action on metal and its
surroundings. Journal of the Society for Psychical Research, 50, 379-398.
Hasted, J. B., & Robertson, D. (1981). Paranormal electrical effects.
Psychoenergetic Systems, 4, 159-187.
Hasted, J.B., Robertson, D., & Arathoon, P. (1983). PKMB research with
piezoelectric sensors. In W.G. Roll, J. Beloff, & R.A. White (Eds.),
Research in Parapsychology 1982 (pp. 39-42). Metuchen, NJ: Scarecrow.
Honorton, C. (1975). Objective determination of information rate in psi tasks
with pictorial stimuli. Journal of the American Society for Psychical
Research, 69, 353-359.
Honorton, C. (1976). Length of isolation and degree of arousal as probable
factors influencing information retrieval in the ganzfeld. In J.D.
-

References
Approved For Release 2000/08/10 : CIA-RDP96-00789R00380036080Ff_233
(pp. 184-186). Metuchen, NJ: Scarecrow.
Honorton, C. (1977). Psi and internal attention states. In B.B. Wolman (Ed.),
Handbook of Parapsychology (pp. 435-472). New York: Van Nostrand
Reinhold.
Honorton, C. (1978). Psi and internal attention states: Information retrieval
in the ganzfeld. In B. Shapin & L. Coly (Eds.), Psi and States of
Awareness (pp. 79-90). New York: Parapsychology Foundation.
Honorton, C. (1983). Response to Hyman's critique of psi ganzfeld studies. In
W.G. Roll, J. Beloff, & R.A. White (Eds.), Research in Parapsychology
1982 (pp. 23-26). Metuchen, NJ: Scarecrow.
Honorton, C. (1985). Meta-analysis of psi ganzfeld research: A response to
Hyman. Journal of Parapsychology, 49, 51-91.
Honorton, C., & Harper, S. (1974). Psi-mediated imagery and ideation in an
experimental procedure for regulating perceptual input. Journal of the
American Society for Psychical Research, 68, 156-168.
Honorton, C., & Krippner, S. (1969). Hypnosis and ESP performance: A review of
the experimental literature. Journal of the American Society for
Psychical Research, 63, 214-252.
Hyman, R. (1979). Psychics and scientists: A review of Mind Reach. The
Humanist, 37 (3).
Hyman, R. (1981). Further comments on Schmidt's PK experiments. Skeptical
Inquirer, 5 (No. 3), 34-40.
Hyman, R. (1983). Does the ganzfeld experiment answer the critics' objections?
In W.G. Roll, J. Beloff, & R.A. White (Eds.), Research in Parapsychology
1982 (pp. 21-23). Metuchen, NJ: Scarecrow.
Hyman, R. (1985). The ganzfeld psi experiment: A critical appraisal. Journal
of Parapsychology, 49, 3-49.
Isaacs, J.D. (1984). Some aspects of performance at a psychokinetic task.
Unpublished doctoral dissertation. University of Aston at Birmingham,
Appodvod For Release 2000/08/10 : CIA-RDP96-00789R003800360001-1

RAfsproved For Release 2000/08/10 : CIA-RDP96-00789R003800360004-134
Jahn, R.G., Dunne, B.J., & Jahn, E.G. (1980). Analytical judging procedure for
remote perception experiments. Journal of Parapsychology, 44, 207-231.
Jahn, R.G., Nelson, R.D., & Dunne, B.J. (1985, August). Variance effects in
REG series score distributions. Paper presented at the Parapsychological
Association convention, Tufts University, Medford, MA.
Johnson, M. (1973). A new technique of testing ESP in a real-life,
high-motivational context. Journal of Parapsychology, 37, 210-217.
Johnson, M., & Haraldsson, E. (1984). The defense mechanism test as a
predictor of ESP scores. Journal of Parapsychology, 48, 185-200.
Kanthamani, H., & Kelly, E.F. (1974a). Awareness of success in an exceptional
subject. Journal of Parapsychology, 38, 355-382.
Kanthamani, H., & Kelly, E.F. (1974b). Card experiments with a special
subject: I. Single-card clairvoyance. Journal of Parapsychology, 38,
16-26.
Kanthamani, H., & Kelly, E.F. (1975). Card experiments with a special subject:
II. The shuffle method. Journal of Parapsychology, 39, 206-221.
Kanthamani, B.K. [H.], & Rao, K.R. (1973). Personality characteristics of ESP
subjects: V. Neuroticism and ESP. Journal of Parapsychology, 37, 37-50.
Karnes, E.W., Ballou, J., Susman, E.P., & Swaroff, P. (1979). Remote viewing:
Failures to replicate with control comparisons. Psychological Reports,
45, 963-973.
Karnes, E.W., & Susman, E.P. (1979). Remote viewing: A response bias
interpretation. Psychological Reports, 44, 471-479.
Karnes, E.W., Susman, E.P., Klusman, P., & Turcotte, L. (1980). Failures to
replicate remote-viewing using psychic subjects. Zetetic Scholar, No. 6,
66-76.
Kelly, E.F. (1979). Reply to Persi Diaconis. Zetetic Scholar, No. 5, 20-28.
Kelly, E.F. (1980). Response to Persi Diaconis's reply. Zetetic Scholar, No.
6, 121-127.
Approved For Release 2000/08/10 : CIA-RDP96-00789R003800360001-1

References
Approved For Release 2000/08/10 : CIA-RDP96-00789R00380036000Ff _? 35
Kelly, E.F., & Kanthamani, B.K. [H. ] (1972). A subject's efforts toward
voluntary control. Journal of Parapsychology, 36, 185-197.
Kelly, E.F., Kanthamani, H., Child, I.L., & Young, F.W. (1975). On the
relation between visual and ESP confusion structures in an exceptional
ESP subject. Journal of the American Society for Psychical Research, 69,
1-31.
Kennedy, J.E. (1979). Consistent missing: A type of information-error in ESP.
Journal of Parapsychology, 43, 113-128.
!
Krippner, S. (Ed.) (1977). Advances in Parapsychological Research. Vol. 1:
Psychokinesis. New York: Plenum.
1
Krippner, S. (Ed.) (1978). Advances in Parapsychological Research. Vol. 2:
Extrasensory Perception. New York: Plenum.
Krippner, S. (Ed.) (1982). Advances in Parapsychological Research. Vol. 3. New
York: Plenum.
Krippner, S. (Ed.) (1984). Advances in Parapsychological Research. Vol. 4.
Jefferson, NC: McFarland.
Krippner, S., Honorton, C., & Ullman, M. (1972). A second precognitive dream
study with Malcolm Bessent. Journal of the American Society for Psychical
Research, 66, 269-279.
Krippner, S., Honorton, C., & Ullman, M. (1973). An experiment in dream
telepathy with the "Grateful Dead." Journal of the American Society of
Psychosomatic Dentistry and Medicine, 20, 9-17.
Krippner, S., Honorton, C., Ullman, M., Masters, R., & Houston, J. (1971). A
long-distance "sensory bombardment" study of ESP in dreams. Journal of
the American Society for Psychical Research, 65, 468-475.
Krippner, S., & Ullman, M. (1970). Telepathy and dreams: A controlled
experiment with electroencephalogram-electro-oculogram monitoring.
Journal of Nervous and Mental Disease, 151, 394-403.
Krippner, S., Ullman, M., & Honorton, C. (1971). A precognitive dream study
Approved For Release: 2000/09/1 of CIA-DOF06-00789R003800368001-1
1
:

kererences
rage 230
Approved For Release 2000/08/10 : CIA-RDP96-00789R003800360001-1
Research, 65, 192-203.
Layton, B.D., & Turnbull, B. (1975). Belief, evaluation, and performance on an
ESP task. Journal of Experimental Social Psychology, 11, 166-179.
Lovitts, B.E. (1981). The sheep-goat effect turned upside down. Journal of
Parapsychology, 45, 293-309.
Marks, D. (198la). On the review of The Psychology of the Psychic: A reply to
Dr. Morris. [Correspondence] Journal of the American Society for
Psychical Research, 75, 197-203.
Marks, D. (1981b). Sensory cues invalidate remote viewing experiments. Nature,
292, 177.
Marks, D. (1982). Remote viewing revisited. Skeptical Inquirer, 6(4), 18-29.
Marks, D., & Kammann, R. (1978). Information transmission in remote viewing
experiments. Nature, 274, 680-681.
Marks, D., & Kammann, R. (1980). The Psychology of the Psychic. Buffalo:
Prometheus.
May, E.C., Radin, D. I., Hubbard, G.S., Humphrey, B.S., & Utts, J.M. (1985,
August). Psi experiments with random number generators: An informational
model. Paper presented at the Parapsychological Association convention,
Tufts University, Medford, MA.
Morris, R.L. (1972). An exact method for evaluating preferentially matched
free-response material. Journal of the American Society for Psychical
Research, 66, 401-407.
Morris, R.L. (1980). Some comments on the assessment of parapsychological
studies: A review of The Psychology of the Psychic by David Marks and
Richard Kammann. Journal of the American Society for Psychical Research,
74, 425-443.
Moss, T., Paulson, M.J., Chang, A.F., & Levitt, M. (1970). Hypnosis and ESP: A
controlled experiment. American Journal of Clinical Hypnosis, 13, 46-56.
Approved For Release 2000/08/10 : CIA-RDP96-00789R003800360001-1
-

1
References
Approved For Release 2000/08/10 : CIA-RDP96-00789R003800360689-1237
Mosteller, F., & Bush, R.R. (1954). Selected quantitative techniques. In G.
Lindzey (Ed.), Handbook of Social Psychology, Vol. 1 (pp. 289-334).
Cambridge, MA: Addison-Wesley.
Nash, C.B., & Nash, C.S. (1958). Checking success and the relationship of
personality traits to ESP. Journal of the American Society for Psychical
Research, 52, 98-107.
Nelson, R.D., Dunne, B.J., & Jahn, R.G. (1984). An REG experiment with large
data base capability, III: Operator related anomalies. Technical Note
PEAR 84003, Princeton Engineering Anomalies Research, School of
Engineering/Applied Science, Princeton University. (159 pp.)
Nicol, J.F. , & Humphrey, B.M. (1953). The exploration of ESP and human
personality. Journal of the American Society for Psychical Research, 47,
133-178.
Palmer, J. (1971). Scoring in ESP tests as a function of belief in ESP. Part
I: The sheep-goat effect. Journal of the American Society for Psychical
Research, 65, 373-408.
Palmer, J. (1972). Scoring in ESP tests as a function of belief in ESP. Part
II: Beyond the sheep-goat effect. Journal of the American Society for
Psychical Research, 66, 1-26.
Palmer, J. (1977). Attitude and personality traits in experimental ESP
research. In B.B. Wolman (Ed. ), Handbook of Parapsychology (pp. 175-201).
New York: Van Nostrand Reinhold.
Palmer, J. (1978). Extrasensory perception: Research findings. In S. Krippner
(Ed.), Advances in Parapsychological Research. Vol. 2: Extrasensory
Perception (pp. 59-243). New York: Plenum.
Palmer, J. (1982). Methodological objections to the case for psi: Are formal
control conditions necessary for the demonstration of psi? Journal of
Indian Psychology, 4, 13-18.
Palmer, J. (1983). Sensory contamination of free-response ESP targets: The
Approved fffogeRelease:2009/08/16naCIA-RDP86.00789003800360001-1ca1
1
-

Page 238
References
Approved For Release 2000/08/10 : CIA-RDP96-00789R003800360001-1
Research, 77, 101-113.
Palmer, J. (1985, August). Terminological poverty in parapsychology: Two
examples. Paper presented at the Parapsychological Association
convention, Tufts University, Medford, MA.
Palmer, J., & Kramer, W. (1984). Internal state and temporal factors in
psychokinesis. Journal of Parapsychology, 48, 1-25.
Palmer, J., & Kramer, W. (in press). Sensory identification of contaminated
free-response ESP targets: Return of the greasy fingers. Journal of the
American Society for Psychical Research.
Palmer, J., & Lieberman, R. (1975). The influence of psychological set on ESP
and out-of-body experiences. Journal of the American Society for
Psychical Research, 69, 193-213.
Parker, A. (1975). Some findings relevant to the change in state hypothesis.
In J.D. Morris, W.G. Roll, & R.L. Morris (Eds.), Research in
Parapsychology 1974 (pp. 40-42). Metuchen, NJ: Scarecrow.
-
Parker, A., & Wiklund, N. (1982). The ganzfeld: A methodological evaluation of
the claims for a repeatable ESP experiment. Unpublished manuscript.
Puthoff, H.E. (in press) . Computer assisted psi amplification. In D.H. Weiner
& D. I. Radin (Eds.), Research in Parapsychology 1985. Metuchen, NJ:
Scarecrow.
1
Puthoff, H.E., & Targ, R. (1979). A perceptual channel for information
transfer over kilometer distances: Historical perspective and recent
research. In C.T. Tart, H.E. Puthoff, & R. Targ (Eds. ), Mind at Large,
(pp.13-76). New York: Praeger.
Puthoff, H.E., & Targ, R. (1981). Rebuttal of criticisms of remote viewing
experiments. Nature, 292, 388.
Puthoff, H.E., Targ, R., & May, E. (1979, January). Experimental psi research:
Implications for physics. Paper presented at the 145th National Meeting
of the American Association for the Advancement of Science, Houston, TX.
Approved For Release 2000/08/10 : CIA-RDP96-00789R003800360001-1
!
-

References
Page 239
Approved For Release 2000/08/10 : CIA-RDP96-00789R003800360001-1
Raburn, L. (1975). Expectation and transmission factors in psychic
functioning. Unpublished honors thesis, Tulane University, New Orleans,
LA.
Randi, J. (1975) . The Truth about Uri Geller. Buffalo: Prometheus.
Randi, J. (1982). Flim-flam. Buffalo: Prometheus.
Rao, K.R. (1965). The bidirectionality of psi. Journal of Parapsychology, 29,
230-250.
Rauscher, E.A., & Rubik, B.A. (1980). Effects of motility behavior and growth
rate of Salmonella typhimurium in the presence of a psychic subject. In
W.G. Roll (Ed.), Research in Parapsychology 1979 (pp. 140-142).
Reiser, M., & Klyver, N. (1982). A comparison of psychics, detectives, and
students in the investigations of major crimes. In M. Reiser (Ed. ),
Police Psychology: Collected Papers (pp. 260-267). Los Angeles: LAMI
Publications.
Reiser, M., Ludwig, L., Saxe, S., & Wagner, C. (1979). An evaluation of the
use of psychics in the investigation of major crimes. Journal of Police
Science and Administration, 7, 18-25. Metuchen, NJ: Scarecrow.
Rhine, J.B. (1948). Conditions favoring success in psi tests. Journal of
Parapsychology, 12, 58-75.
Rhine, J.B. (1974). Comments: A new case of experimenter unreliability.
Journal of Parapsychology, 38, 215-225.
Rhine, J.B., & Pratt, J.G. (1957). Parapsychology: Frontier Science of the
Mind. Springfield, IL: Charles Thomas.
Rhine, J.B., Pratt, J.G., Stuart, C.E., Smith, B.M., & Greenwood, J.A. (1940).
Extra-sensory Perception After Sixty Years. Boston: Bruce Humphries.
Roll, W.G. (1966). ESP and memory. International Journal of Neuropsychiatry.
2, 505-521.
Rosenthal, R. (1966). Experimenter effects in behavioral research. New York:
Appleton-Century-Crofts.
Approved For Release 2000/08/10 : CIA-RDP96-00789R003800360001-1
:

Page 240
References
Approved For Release 2000/08/10 : CIA-RDP96-00789R003800360001-1
Rosenthal, R. (1979). The "file drawer problem" and tolerance for null
results. Psychological Bulletin, 86, 638-641.
Rosenthal, R., & Rubin, D.B. (1984). Multiple contrasts and ordered Bonferroni
procedures. Journal of Educational Psychology, 76, 1028-1034.
Ryz1, M. (1962). Training the psi faculty by hypnosis. Journal of the Society
for Psychical Research, 41, 234-252.
Ryz1, M. (1966). A model of parapsychological communication. Journal of
Parapsychology, 30, 18-30.
Sargent, C.L. (1978). Hypnosis as a psi-conducive state: A controlled
replication study. Journal of Parapsychology, 42, 257-275.
Sargent, C.L. (1980). A note on personality differences between psi-conducive
and psi-inhibitory ganzfeld experimenters. In W.G. Roll (Ed.), Research
in Parapsychology 1979 (pp. 114-115). Metuchen, NJ: Scarecrow.
Sargent, C.L. (1981). Extraversion and performance in "extra-sensory
perception" tasks. Personality and Individual Differences, 2, 137-143.
Saunders, D.R. (1985). On Hyman's factor analysis. Journal of Parapsychology,
49, 86-88.
Schechter, E. I. (1984). Hypnotic induction vs. control conditions:
Illustrating an approach to the evaluation of replicability in
parapsychological data. Journal of the American Society for Psychical
Research, 78, 1-27.
Scheffe, H. (1959). The Analysis of Variance. New York: Wiley.
Schlitz, M., & Gruber, E. (1980). Transcontinental remote viewing. Journal of
Parapsychology, 44, 305-317.
Schlitz, M., & Gruber, E. (1981). Transcontinental remote viewing: A
rejudging. Journal of Parapsychology, 45, 233-237.
Schlitz, M., & Haight, J.M. (1984). Remote viewing revisited: An intrasubject
replication. Journal of Parapsychology, 48, 39-49.
Schmeidler, G.R. (1973). PK effects upon continuously recorded temperature.
r
:

References
Approved For Release 2000/08/10 : CIA-RDP96-00789R003800360064-241
Schmeidler, G. R., & McConnell, R.A. (1973/1958). ESP and Personality Patterns.
Westport, CT: Greenwood Press.
Schmidt, H. (1969a). Clairvoyance tests with a machine. Journal of
Parapsychology, 33, 300-306.
Schmidt, H. (1969b). Precognition of a quantum process. Journal of
Parapsychology, 33,. 99-108.
Schmidt, H. (1970a). PK experiments with animals as subjects. Journal of
Parapsychology, 34, 255-261.
Schmidt, H. (1970b). A PK test with electronic equipment. Journal of
Parapsychology, 34, 175-181.
Schmidt, H. (1970c). A quantum mechanical random number generator for psi
tests. Journal of Parapsychology, 34, 219-224.
Schmidt, H. (1973). PK tests with a high-speed random number generator.
Journal of Parapsychology, 37, 105-118.
Schmidt, H. (1974). Comparison of PK action on two different random number
generators. Journal of Parapsychology, 38, 47-55.
Schmidt, H. (1975). Toward a mathematical theory of psi. Journal of the
American Society for Psychical Research, 69, 301-319.
Schmidt, H. (1976). PK effect on pre-recorded targets. Journal of the American
Society for Psychical Research, 70, 267-291.
Schmidt, H. (1978). A take-home test in PK with pre-recorded targets. In W.G.
Roll (Ed.), Research in Parapsychology 1977 (pp. 31-36). Metuchen, NJ:
Scarecrow.
Schmidt, H. (1979a). Search for psi fluctuations in a PK test with
cockroaches. In W.G. Roll (Ed.), Research in Parapsychology 1978 (pp.
77-78). Metuchen, NJ: Scarecrow.
Schmidt, H. (1979b). Use of stroboscopic light as rewarding feedback in a PK
test with pre-recorded and momentarily-generated random events. In W.G.
Roll (Ed.), Research in Parapsychology 1978 (pp. 115-117). Metuchen, NJ:
Approved For Release 2000/08/10 : CIA-RDP96-00789R003800360001-1
P

References
Approved For Release 2000/08/10 : CIA-RDP96-00789R003800360001-1
Schmidt, H. (1981). PK tests with pre-recorded and pre-inspected seed numbers.
Journal of Parapsychology, 45, 87-98.
Schmidt, H., Morris, R.L., & Rudolph, L. (in press). Channeling evidence for a
psychokinetic effect to independent observers. Journal of Parapsychology.
Schmidt, H., & Pantas, L. (1972). Psi tests with internally different
machines. Journal of Parapsychology, 36, 222-232.
Schwartz, S.A. (1983). The Alexandria Project. New York: Dell.
Scott, C. (1972). On the evaluation of verbal material in parapsychology: A
discussion of Dr. Pratt's monograph. Journal of the Society for Psychical
Research, 46, 79-90.
Scott, C. (1982). No "remote viewing." Nature, 298, 414.
Smith, M., Tremmel, L., & Honorton, C. (1976). A comparison of psi and weak
sensory influences on ganzfeld mentation. In J.D. Morris, W.G. Roll, &
R.L. Morris (Eds.), Research in Parapsychology 1975 (pp. 191-194).
Metuchen, NJ: Scarecrow.
Smith, M.J. (1972). Paranormal effects on enzyme activity. Human Dimensions 1
(No. 2), 15-19.
Sondow, N. (1979). Effects of associations and feedback on psi in the
ganzfeld: Is there more than meets the judge's eye? Journal of the
American Society for Psychical Research, 73, 123-150.
Stanford, R.G. (1967). Response bias and the correctness of ESP test
responses. Journal of Parapsychology, 31, 280-289.
Stanford, R.G. (1974a). An experimentally testable model for spontaneous psi
events: I. Extrasensory events. Journal of the American Society for
Psychical Research, 68, 34-57.
Stanford, R.G. (1974b). An experimentally testable model for spontaneous psi
events: II. Psychokinetic events. Journal of the American Society for
Psychical Research, 68, 321-356.
Stanford, R.G. (1977). Conceptual frameworks of contemporary psi research. In
ApproVer For Helealandhos/og/ Perao:AD:296(00789R008800360001:1
..
!

Page 243
References
Approved For Release 2000/08/10 : CIA-RDP96-00789R003800360001-1
Van Nostrand Reinhold.
Stanford, R.G. (1978). Toward reinterpreting psi events. Journal of the
American Society for Psychical Research, 72, 197-214.
Stanford, R.G. (1979). The influence of auditory ganzfeld characteristics upon
free-response ESP performance. Journal of the American Society for
Psychical Research, 73, 253-272.
Stanford, R.G. (1982). On matching the method to the problem: Word-association
and signal-detection methods for the study of cognitive factors in ESP
tasks. In B. Shapin & L. Coly (Eds. ), Parapsychology and the Experimental
Method (pp. 1-18). New York: Parapsychology Foundation.
Stanford, R.G. (in press). Altered internal states and parapsychological
research: Retrospect and prospect. In D.H. Weiner & D. I. Radin (Eds.),
Research in Parapsychology 1985. Metuchen, NJ: Scarecrow.
Stanford, R.G., & Associates (1976). A study of motivational arousal and
self-concept in psi-mediated instrumental response. Journal of the
American Society for Psychical Research, 70, 167-178.
Stanford, R.G., & Rust, P. (1977). Psi-mediated helping behavior: Experimental
paradigm and initial results. In J.D. Morris, W.G. Roll, & R.L. Morris
(Eds.), Research in Parapsychology 1976. (pp. 109-110). Metuchen, NJ:
Scarecrow.
Stanford, R.G., & Stio, A. (1976). A study of associative mediation in
psi-mediated instrumental response. Journal of the American Society for
Psychical Research, 70, 55-64.
Stanford, R.G., & Thompson, G. (1974). Unconscious psi-mediated instrumental
response and its relation to conscious ESP performance. In W.G. Roll,
R.L. Morris, & J.D. Morris (Eds.), Research in Parapsychology 1973 (pp.
99-103). Metuchen, NJ: Scarecrow.
Stanford, R.G., Zenhausern, R., Taylor, A., & Dwyer, M.A. (1975).
Psychokinesis as psi-mediated instrumental response. Journal of the
Approvedo-SacRette afoe 2000109:4 ReselAcRDP96-100789R003800360001-1
-

Page 244
References
Approved For Release 2000/08/10 : CIA-RDP96-00789R003800360001-1
Stokes, D.M. (1978). Review of Research in Parapsychology 1976. Journal of
Parapsychology, 42, 70-76.
Stokes, D.M. (1982). Review of The Metal-Benders. Journal of the American
Society for Psychical Research, 76, 59-67.
Taddonio, J.L. (1975). Attitudes and expectancies in ESP scoring. Journal of
Parapsychology, 39, 289-296.
Targ, R., & Puthoff, H.E. (1977). Mind-reach. New York: Delacorte.
Targ, R., Puthoff, H.E., & May, E.C. (1979). Direct perception of remote
geographical locations. In C.T. Tart, H.E. Puthoff, & R. Targ (Eds.),
Mind At Large (pp. 78-106). New York: Praeger.
Tart, C.T. (1980). [Comments (on Karnes, et al., 1980)] Zetetic Scholar, No.
6, 85-86.
Tart, C.T., Puthoff, H.E., & Targ, R. (1980). Information transmission in
remote viewing experiments. Nature, 284, 191.
Terry, J.C. (1976). Comparison of stimulus duration in sensory and psi
conditions. In J.D. Morris, W.G. Roll, & R.L. Morris (Eds.), Research in
Parapsychology 1975 (pp. 179-181). Metuchen, NJ: Scarecrow.
Terry, J., & Schmidt, H. (1978). Conscious and subconscious PK tests with
pre-recorded targets. In W.G. Roll (Ed.), Research in Parapsychology 1977
(pp. 36-41). Metuchen, NJ: Scarecrow.
Terry, J., Tremmel, L., Kelly, M., Harper, S., & Barker, P.L. (1976). Psi
information rate in guessing and receiver optimization. In J.D. Morris,
W.G. Roll, & R.L. Morris (Eds.), Research in Parapsychology 1975 (pp.
194-198). Metuchen, NJ: Scarecrow.
Thalbourne, M.A. (1981). Extraversion and the sheep-goat variable: A
conceptual replication. Journal of the American Society for Psychical
Research, 75, 105-119.
Thalbourne, M.A. (1982). A Glossary of Terms Used in Parapsychology. North
Pomfret, VT: William Heinemann.
Approved For Release 2000/08/10 : CIA-RDP96-00789R003800360001-1

References
Page 245
Approved For Release 2000/08/10 : CIA-RDP96-00789R003800360001-1
Thalbourne, M.A., Beloff, J., & Delanoy, D. (1982). A test for the
"extraverted sheep versus introverted goats" hypothesis. In W.G. Roll,
R.L. Morris, & R.A. White (Eds.), Research in Parapsychology 1981 (pp.
155-156). Metuchen, NJ: Scarecrow.
Thalbourne, M.A., Beloff, J., Delanoy, D., & Jungkuntz, J.H. (1983). Some
further tests of the extraverted sheep versus introverted goats
hypothesis. In W.G. Roll, J. Beloff, & R.A. White (Eds.), Research in
Parapsychology 1982 (pp. 199-200). Metuchen, NJ: Scarecrow.
Thalbourne, M.A., & Jungkuntz, J.H. (1983). Extraverted sheep versus
introverted goats: Experiments VII and VIII. Journal of Parapsychology,
47, 49-51. (Abstract)
Tyrrell, G.N.M. (1936). Further research in extra-sensory perception.
Proceedings of the Society for Psychical Research, 44 (Part 147), 99-168.
Ullman, M., & Krippner, S. (1968, August). Experimentally induced telepathic
dreams with EEG-REM monitoring: The Van de Castle study. Paper presented
at the Parapsychological Association convention, University of Freiburg,
Freiburg, West Germany.
Ullman, M., & Krippner, S. (1970). Dream Studies and Telepathy: An
Experimental Approach. Parapsychological Monographs No. 12. New York:
Parapsychology Foundation.
Ullman, M., & Krippner, S. (1978). Experimental dream studies. In M. Ebon
(Ed.), The Signet Handbook of Parapsychology (pp. 409-422). New York: New
American Library.
Ullman, M., Krippner, S., & Feldstein, S. (1969). Experimentally-induced
telepathic dreams: Two studies using EEG-REM monitoring techniques. In
G.R. Schmeidler (Ed.), Extrasensory Perception (pp. 137-161). New York:
Atherton.
Ullman, M., Krippner, S., & Vaughan, A. (1973). Dream Telepathy. New York:
MacMillan.
Approved For Release 2000/08/10 : CIA-RDP96-00789R003800360001-1
1

References
Approved For Release 2000/08/10 : CIA-RDP96-00789R003800360069-146
Van de Castle, R.L. (1969). The facilitation of ESP scores through hypnosis.
American Journal of Clinical Hypnosis, 12, 37-56.
Van de Castle, R.L. (1977). Sleep and dreams. In B.B. Wolman (Ed.), Handbook
of Parapsychology (pp. 471-499), New York: Van Nostrand Reinhold.
Walker, E.H. (1975). Foundations of paraphysical and parapsychological
phenomena. In L. Oteri (Ed.), Quantum Physics and Parapsychology (pp.
1-44). New York: Parapsychology Foundation.
Weiner, D.H., & Geller, J. (1984). Motivation as the universal container:
Conceptual problems in parapsychology. Journal of Parapsychology, 48,
27-37.
Wolman, B.B. (1977). (Ed. ) Handbook of Parapsychology. New York: Van Nostrand
Reinhold.
Wood, R.H. (1982). On the importance of correct mechanics in paranormal
research. Journal of the Society for Psychical Research, 51, 246-249.
Zusne, L., & Jones, W.H. (1982). Anomalistic Psychology: A Study of
Extraordinary Phenomena of Behavior and Experience. Hillsdale, NJ:
Lawrence Erlbaum.
Approved For Release 2000/08/10 : CIA-RDP96-00789R003800360001-1
-
1