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MAY 3 - 1975
JEEE - EDITORIAL
NEW YORK
--
College of Humanities
& Social Sciences
Department of Psychology
& Sociology
(215) 895-2455
1
C
April 26, 1976
Mr. Robert W. Lucky, Editor
Proceedings of the IEEE
345 East 47th Street
New York, New York
10017
Dear Mr. Lucky:
I have just read, with considerable interest, an article in the March issue of
the Proceedings of the IEEE by I. E. Puthoff and R. Targ entitled "A Perceptual
Channel for Information Transfer Over Kilometer Distances: Historical Perspective
and Recent Research. " These authors have undertaken a series of potentially
significant studies into a topic of obvious interest to an increasingly large number
of individuals, doing so utilizing what appears to be appropriate techniques taken
from the scientist's arsenal of objective methodologies, many of which the authors
have previously distinguished themselves using in research in the natural sciences,
It is certainly an understatement to say that such a controversial topic as ESP re-
quires extraordinarily precise and careful methods, especially well suited to exclude
the basis for all those nagging criticisms often irreverently hurled at the para-
psychologist -- fraud, inadequate controls, imprecise and incomplete reporting of detalla,
Improper statistics, proper statistics improperly used, and, especially, the presence
of numerous confounding variables which vary with the independent variables in their
experimental designs in such a way that these other uncontrolled variables remain to
potentially account for the given results. Indeed, the authors themselves apparently
set out to achieve this goal, what they refer to as their "principal responsibility --
to resolve under unambiguous conditions the basic issue of whether or not this class
of paranormal perception phenomenon exists" (pps. 334-335) . Unfortunately, the model
for their study follows the traditional stratagems of the parapsychologists in the
United States and Europe, rather than the method they no doubt otherwise use in their
non-behavioral research in the natural sciences (and I might add that is largely
followed in experimental psychology) . As we shall indicate, the consequence of this
is that they must necessarily fall far short in fulfilling their stated "principal
responsibility. "
It is the essence of the experimental method -- in contrast to naturalistic
observation, the survey technique, correlational procedures, field studies, and the
"Theoretical Model" of the parapsychologists (Girden, 1962, p. 360) == to in fact creato
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the conditions necessary for "unambiguous" resolution of fundamental questions since
only this method permits manipulation and control of potentially confounding variables
by the eminently sensible method of varying the critical factors under study, and
systematically observing their effects upon other selected and measurable variables
while holding these potentially confounding variables under tight control via auch
techniques as randomization, constancy, counterbalancing, matching, etc. The mani-
pulated variables are called independent variables (IVs), and the variables sensitivo
to the effects of the IV is called the dependent variables (DVs). This has been
expressed quite eloquently by Ebbinghaus (1964, p. 7; original: 1885) in his
incorporation of this experimental method into his researches into human memory,
A successful effort which weut far in illustrating in 1885 the power of this method
in scientifically understanding human behavior -- including perception:
"We all know of what this method consists: an attempt is
made to keep constant the mass of conditions which have proven
themselves causally connected with a certain result; one of
these conditions is isolated from the rest and varied in a way
that can be numerically described; then the accompanying change
on the side of the effect is ascertained by measurement or
computation. "
The simplest experiments, therefore, are those employing but a single IV and
a single DV, and, in the fundamental situation in which an effort is being made to
demonstrate the sheer existence of a phenomenon (as in the present study, without
inquiring further into its composition and contingencies), the two bnoic values or
levels or variates of the IV may be simply designated the "experimental" (i.e., the
factor appears -- operationally defined -- in some amount) and "control" condition
(i.e., the factor appears as a zero amount) .
A helpful example might be a drug study in which we only wanted to know if the
drug makes running a maze difficult -- or not! In this situation, we would experi-
mentally compare the drug condition's effects to a condition otherwise identical in
which, however, the drug is absent!
This would constitute one of the most fundamental
empirical control conditions used in experimental science in general, and experimental
psychology in particular, although of course other empirical control conditions are
possible, depending on what one is controlling for. We speak, by the way, of "control
condition", and not "controlled" condition, since we assume all conditions in the
experiment are controlled in some way. This is apparently a source of much confusion
in the parapsychological literature, where constant reference is made to "controlled
laboratory conditions, " "scientifically controlled conditions, " and so on, thereby
creating the illusion that basically well conceived control conditions are being used.
In the present example, if one is concerned that the procedure of injection causes
errors to be made on the maze, then we need a placebo control in which S is treated
identically as in the drug condition, but saline rather than the drug is injected.
In this case, we "control for" the injection procedure's effects on the DV by holding
this potentially confounding variable constant and can thereby evaluate it and prevent
it from creating the erroneous impression that the drug, per se, produced the errora S
made on the maze, when in fact the drug injection procedure itself may have produced
that effect on the DV.
As we know, in the present study, the basic procedure described was carried out
with all the subjects (six in number for section III studies through subsection "D",
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two more in section "E", and five more in section "F"; we limit our critique to the
more detailed accounts given in sections A-D rather than the very sketchy material
in sections E and F, although all these studies used essentially the same procedure
and varies mainly on the basis of subject characteristics.).
That is, all the
subjects were administered, as it were, the same basic treatment condition, and were
thus all part of the same "clairvoyant" or "remote viewing" group, consisting
essentially in the Ss making an effort to somchow envision a remote target. Actunily,
all we know of the instructions to the S, so critical in determining the operational
definition of this condition, is that the "remote-viewing subject was asked to
describe his impressions of the target site into a tape recorder and to make any
drawings he thought appropriate (p. 335) , " since the authors do not give us the actual
instructions. In any case, for each S, there did indeed exist a "remote target"
designated by a "target team" or "demarcation team" situated at some geographical
location nearby the SRI laboratory, although the theoretical rationale for this team's
existence and its role in the procedure is never really logically presented by the
author save only for an historical precedent established working informally with
Mr. Ingo Swann (p. 334) and perhaps the anecdotal "pilot experiment" (p.330) where
one of the authors functioned in this capacity as a "demarcation team" and, we infer,
grew quite excited and impressed with a subject's descriptions of some sites he
visited, where the subject supposedly had no particular prior information about the
site in question. This situation, we shall detail later, results in considerable
ambiguity in the designation of the "target" (is it. the "target=perceived-by-the-team",
or is it the physical stimulus of the target, and so on?) ,
The whole procedure, carried out under what the authors describe as "rigidly
controlled scientific conditions (p.334)", and including the subsequent judging
procedure we shall discuss in some detail later, could have been called an "experi-
mental" condition comparable to the "drug present" condition in the example above if
there had been a control condition with which to compare it (comparable to the "placebo
or "no drug" conditions in our example), that is, a condition in which all of the
preceding procedures were exactly followed but in the absence of what was previously
operationally and objectively defined as the "remote-viewing" condition (note the
importance of objective specification of the conditions under which the "remote-viewing;
is to occur, because without that there can be no objective controlled variation of
the condition since one would never know quite when the experimental condition existed
in the first place!). As the matter stands, since only one condition was run in this
study, we really have neither experimental nor control conditions (because the terms
are defined relative to each other); and since that is the case, we really have no IV;
and since we have no IV, we actually do not even have one experiment (let alone the 50
or so claimed by the authors in this single publication -- p. 330).
The DV, of course, also deserves careful scrutiny, since hypothesized IV effecta
are evaluated in terms of changes in DV measures. In this study, the actual "number"
obtained as the basic raw datum was the individual ranking or "match" number of a
subject's tape recorded description (supposedly of a "target"), with some aspect
(perhaps) of a nearby geographical location. The number could assume any value from
"1" to "9", where "l" referred to the judge's estimate of a "best" match, through "9"
which was assigned to a match if it was a "worst" match for a given target, . Nine tar-
gets and nine descriptions were obtained for each S. This was apparently an ordinal
scale of measurement. We must assume, in the absence (also) of a specific report of
the instructions to the judge, that the judge knew exactly what his task was in deter*
mining the degree of correspondence between the Ss' descriptions and the judge's own
unspecified perceptions when physically present. at the so-called target.
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We should, therefore, consider the precise meaning of a "hit" under these
circumstances. Evidently, a "hit" for the Es occurred when the geographical locus
they called the "target" is judged to correspond to the S's description obtained
while the "demarcation team" was visiting a particular site. This was also, therefore,
a situation where the S's corresponding desciption was assigned a rank of "l". Since
9 targets were "experimented" with a
given S, we have 9 separate judgments of rank
carried out by a single given judge. The sum of ranks for the given S of all the
descriptions for the theoretically associated targets was then compared to a probability
distribution for that statistic, a situation we claim is really improperly serving as
a substitution for a test based on some statistic (which could be the sum of ranka)
obtained from the comparison of the matches for this hypothetical "remote viewing"
data to the matches obtained under similar judging conditions where there was no
remote viewing possible (other control conditions will be described below) .
; However, there are numerous peculiarities about this judging process possibly
unresolvable on the basis of the authors' scanty and ambiguous description of this
critically important aspect of their study. Let us consider a few of these problems.
.
1.
What was the judge judging?
The judge for a given S's performance for a
given target (what the authors refer to incredibly as an "experiment") was successively
driven to cach geographical location previously visited by the peripatetic Es. Since,
as we previously noted, we do not know precisely what aspects of the geographical
location constituted a "target" in the original "experiment" when the demarcation
team, was present, and since it is even more ambiguous now what the judge was viewing,
as well as what he was supposed to be looking at while he reviewed the S's packages of
9 descriptions, we seem in this procedure, therefore, to actually be dealing with two
(and perhaps three) recognizably distinct categories of "targets": one is constituted
by the perceptions of the demarcacion team; a second by the perceptions by the judges;
and a third by direct physical aspects of some geographical location (photographe aro
used in the report and labelled "target" to further complicate target delineation".
e.g., Figure 4). It is difficult to evaluate how potentially dissimilar these various
"targets" were in the absence of clarifying and detailed accountsof the specific
instructions to the teams and to the judge. After all, the judge or demarcation team
may have fixated the horizon, focused on passing vehicles, noticed a sign, and so on.
Consequently, the reporting of the target simply as a "target location", or "remote
location" (c.g., "Marina, Redwood City") as the authors do, belies the fact that we
are dealing here with both their clairvoyance belief and in the perceptual theory
that the way things appear to a viewer and the way they are physically constituted
may not be at all identical (c.g., the sensation "red" of n perceived stop sign, and
the atomic structure of the paint pigments on its metal surface). The possible con-
sequence of this lack of precise definition of the target is that the judge han
considerable latitude in fitting S's description to the scene as he. perceives it,
possibly even looking for certain aspects of the scene before him that seem to be
present in some of S's descriptions.
2.
How reliable is the Judge's "Matching" Measure?
A direct consequence of
the preceding consideration bears directly upon the integrity of the measurement used
for the authors' basic datum, namely, the problem that we do not know specifically what
constitutes the "standard" (the target" in some sense) against which our "comparison
stimuli" (S's descriptions) are measured by the judge, resulting in what must be an
impressively unrealiable measure (DV) . Furthermore, this potentially highly unreliable
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1976
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measure, therefore, becomes potentiallyeven more unreliable when one recalls thet only
one judge was used for cach subject's data, and he performed only one judging (a serios
of nine evaluations) for a given target. The report tells us nothing of any efforts
to "train" the judge in this procedure, or otherwise to determine some initial
reliability coefficient for this kind of task for a naive judge. This question or
doubt about the status of our measuring instrument, our "aensor" as it were, is
especially preplexing in light of the highly refined and instrumentally sophisticated
dependent variables the authors surely use in all their other research in the physical
sciences; why they have avoided use of such techniques in this so-called "remote-
viewing" research, and furthermore not used the appropriate control procedures experi-
mental psychologists and psychophysicists have laboriously developed starting with
Wundt's work in Leipzig in 1879, remains rather enigmatic, to say the least.
3.
Were the Judgments Independent? After the first "target" site was visited,
we know the judge was taken, according to some unspecified procedure (the authors nay
"in turn, " but "in turn" of what -- demarcation team visits, random sequence just for
.
the purposes of judging, or simply (and necessarily) "one after the other?") to another
target. Way he then given the same nine descriptions in precisely the same way? If
so, how was the procedure handled? Were precautions taken to prevent cues associated
with previous correct 'hits' from subsequently influencing later matches, since,
obviously, information that a previous description had been correctly matched (a "hit")
reduces by one those descriptions in the pool that he draws from to "match, " thereby
significantly increasing the probability of making subsequent hits.
This
could easily occur if an informed E drove the judge to the different siten for the
judging, and then, having noticed what we would assume to be an accidental "hit" by
the judge, indicated as much through perhaps an unconscious cue to the judge. The
point is, not that we think the authors really overlooked such an obvious source of
bias, but rather that we need special reassurance specifically chat a naive driver
with explicit driving instructions was used to merely drive the judge to the different
locations -- and that is all! After all, he cannot cue the judge about previous
Accomplishments, if he knows nothing of the research. Of course, the judge may have
driven himself to the site, which would largely eliminate this source of confounding
in the measurement series, but we do not know what happened here since these pertinent
details are omitted from the report.
To summarize our concerns with the dependent variable to this point, we may any,
firat, it appears to need considerable specification, a detailed operational definition
second, its reliability should be ascertained, and doubt that it is inherently very
unreliable removed; third, it should be used for determining experimental condition
("Clairvoyance") hit rates in the matching task, as well as for appropriate control
conditions! ("No clairvoyance, " "no clairvoyance and no demarcation team, " and so on)
hit rates, so that an appropriate statistic based on the net differences in "hit rateo'
could be tested for the degree to which this difference measure is statistically
signficant.
Since this idea of an appropriate controlcondition seems to be so alien to the
parapsychological so-called "experimental" literature, but is everywhere else in
experimental science recognized to be of the essence of the logic of experimentation
in the first place, let us consider in some detail what the minimal requirements would
be in order to actually run an experiment on this "remote viewing" hypothesis, rather
than merely report curious observations of possibly purely coincidental events.
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Apparently, "clairvoyance" seems to be viewed or interpreted as some kind of
non-sensory "seeing clearly" of an object not immediately available to sensory
surveillance and scanning. It would seem, therefore, that for objective experi-
mental purposes it may be operationally defined either by specifying instructions
to a subject concerning his potential task of envisioning distant objects, or by
controlling the very existence of a target to be seen "remotely" (or any other
way for that matter). Therefore, each of these procedural details can serve as
an IV in a well controlled 2-factor design. For the "target" IV, we would seem
to need only the two basic levels of this IV, namely, a condition in which a
remote target is available for alleged "remote viewing, " hypothetically facilitated
in some inscrutable fashion by a "demarcation team" actively observing the target
according to explicit, replicable directions, and a condition in which no such
remote target or team exists. The former instance would theoretically permit
clairvoyance to operate (if it exists), since one's reported imagery could be matched
or compared to the actual selected target, as discussed in detail above; the latter
control condition would not, since there would be no selected target to see
clairvoyantly or otherwise.
Furthermore, on the basis of an operational definition of remote-viewing in
terms of the instructions to S establishing his remote-viewing task, we can proceed
to require him to draw pictures or verbally describe anything he can imagine for,
say, a 5-minute period (commensing and ending at our signal), but in the experi-
mental condition further telling him to attempt to view a remote target, whereas
refraining from such a demand in the control condition. The overall design then
would be:
.
.
INSERT DIAGRAM HERE
Procedurally, this would mean we begin by creating a large pool of nearby
geographical sites to function as potential "targeta" (This is an attempt to
perserve the authors procedures wherever feasible, since it would hardly otherwise
be very advisable to use such complex stimuli as these targets when little is known
of these effects with simple stimuli), and then randomly assign targets to the 4 celle
of our experimental design until, say, each cell has five (5) targets (or perhaps more
depending somewhat on resources and the type of statistical test to be used). An for
our "instruction" variable, we will basically require S to give a detailed phenome-
nological report of his "stream of consciousness" experiences at designated moments,
but, for half of the targets (cells A and B) we would have in addition asked S to
attempt to "visualize" some geographical scene (we would provide our rendere in the
later report with detailed, replicable, instructions so the reader could evaluate
the degree to which we may have given our S any information about the type, condition
or location of the target, all of which information may help diminish the population
of total targets S thinks might be under consideration, thus significantly increasing
the probability of making a hit -- a circumstance that may help account for auch out-
standing "hits" in the authors' report as that of White Plaza) .' The differential
.
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. REMOTE-VIEW
(EXPERIMENTAL)
B
C
D
.
DV : NUMBER OF CORRECT
MATCHES ( "HITS")
TARGET
IV #2
PRESENT
(EXPERIMENTAL )
ABSENT
(CONTROL )
C
1
DO NOT
REMOTE-VIEN
(CONTROL )
.
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-- in. Robert W. Lucky
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presence of such information, varying with the "instruction" IV, would be an
excellent example of a confounding variable in an experiment of this type. In any
case, the use of these control conditions (no target, no remote-viewing demand in
various combinations designated by cells A, C and D) permits an empirical deter-
mination of the extent to which such "hits" in matching may occur simply by virtue
of the similarities judges may read into this matching material due to its inherent
unstructured subjective quality, much as human observers of Rorschach ink blots see
a map of Ireland or a bust of Caeser, an organization imposed on perceptual materiale
that perceptual theorists refer to as "Gestalts, " often reflecting unconscious needs
of the observer (such as, "I have psychic powers I must demonstrate! ").
As for the sequence to be followed in actually running S through these different
treatment combinations, a simple randomized arrangement would suffice, that is,
assuming 20 targets, with numbers 1-5 in cell A, 6-10 in cell B and so on, we simply
run the treatment combination according to the next number in the random series
(c.g., if 13 is the first random number, we run S according to the conditions
obtaining for cell C). Later the judge can in random sequence consider one cell block
of descriptions and targets after the other, until all four cells have been "matched, "
where naturally the judge is not informed of the treatment combination condition. Hit
rates are determined, for example, and then appropriate statistical tests for simple
effects, main effects, and possible interactions determined. The "remote-viewing"
hypothesis would be confirmed if cell "B" had significantly more hite than cell "A"
(no target), cell "C" (target, no R-V instruction), and certainly than cell "D" (where
both target and appropriate instructions are absent). The present reported study,
by the way, consists only in cell "B", making appropriate comparison impossible. In
any case, lack of such significant differences will merely disconfirm this para-
psychological hypothesis (not "disprove"), thereby providing no one with any empirical
reason for affirming belief in the existence in this unusual phenomenon's existence --
at least, as evaluated in this suggested experimental design.
Furthermore, the underlying logic should be clear, that the clairvoyant hypo-
thesis cannot be evaluated when matches or hits (cell "A") are compared to some
hypothetical "chance" level (no matter how accurate the statistical test be according
to individual statisticians, pronouncements of statistical associations, or as found
in statistics texts) that fails to represent the normal or average number of hits
that might be really expected under these identical conditions when. clairvoyance does
not exist (as cells "D" especially, and also "A" and "C" establishes, as explained
above).
The essential experimental invalidity of this parapsychological tactic of
comparing their so-called "experimental data" to some hypothetical "chance" level,
especially in the absence of experimental control conditions, is perhaps most clearly
illustrated in the psychokinetic ("mind over matter") literature. In those studies,
classically championed by Rhine some years ago (e.g., 1947), a tumbler might toan
out onto a table some 600 dice; the S being evaluated for his alleged "psychic" skille
makes some effort to mentally or "psychically" influence each die and have, sny, Of
many 5s turn up as he can. A tabulation is made, and it is found that, say, 235
Ss have indeed turned up -- a startling result, indeed, especially when it is considered
that only 100 should have so turned up by "chance, " The problem of this interpretation
is the same as that in the present "remote-viewing"study. This "chance level" is a
theoretical, mathematical abstract model of the behavior of 600 ideal dice, not
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necessarily related to the die actually being used in the study at all, not to
mention to the procedures and physical conditions operating in actually uning and
"tossing" them. An empirical control condition is necessary to obtain this "atan-
dard" for comparison, one representing the actual concrete die used in the study,
and accounting for such potentially confounding variables influencing the throw such
as non-horizontal tables, loaded dice, etc. (all as discussed above) . This control
condition would exactly duplicate the experimental condition, save only for the
omission of some critical factor under study in the experiment, such as (in this
case) psychokinesis itself! In other words, we run a non-PK condition, in which
all is done as in the experimental condition, but S does not "PK" when the dic lo
thrown.
Would not such a comparison change our interpretation of this whole situation
if it was found that again about 230 dice came up "58"? We would then obviously
look for those other alternative, non-parapsychological explanations for the high
5's count (such as the possibility of loaded dice). An excellent review of the
PK literature through 1962, and general critique of this "theoretical model", ia
that of Girden (1963) .
-
It may be true, as the parapsychologists claim, that ESP is real and represente
a great latent power of the human mind, one day to emerge in full recognition by
science as another momentous step in the evolution of man and his mind; but its
truth remains to be demonstrated through use of the experimental method, and until
it. is, in the same way as Ohm's law or Pavlov's conditioned reflex paradigm has
been so demonstrated, parapsychologists ought not consider psychologists and other
scientists and engineers calcified conservatives blindly refusing to see the obvious
"fact" that ESP, etc., exists, because the parapsychologists themselves seem to
virtually intentionally avoid using the only techniques which in the long run will
prove persuasive to the scientific community, and those are objective experimental
procedures.
Perseverance of belief in ESP and related phenomena built upon such shabby
and preposterous evidence as is usually offered as "scientific proof" on behalf
of the ESP proponents (and the present study is to some extent an example) itself
requires some explanation, since such perserverance is often cited ns itself somehow
evidence for the existence of these "paranormal" phenomena (important people
wouldn't believe it if it wasn't true!). It is not hard to find such an explanation
in the literature of the social psychology of social movements and cults, since
therein it is well understood how organized groups of individuals may band together
with their own ideologies, their own clubs, their own in-group publicationa ond
sacred works, their own symbols, passwords and slogans, in the interest often of
providing some sense to life, some direction, some compensation for a sense of
personal loss, insignificance, or inferiority, which is provided by becoming a "true
believer," as Hoffer (1951) put it, in some special and unique movement, Especially
is this true of ideologies that persist despite virtually universal rejection on
some rational grounds, suggesting, in contrast, that the belief in question answers
to needs other than those that are rational. The particular difficulty the para-
psychologists seem to encounter in that (most fortunately for humanity) the sciencific
method represents one of the few really pristine exemplars of the rational use of the
human mind, thereby guaranteeing a clash with their own vested irrational ideological
systems. Add to this the consideration that we are presently witnessing a strong
resurgence of popular interest in the occult and supernatural, with a proportionate
increase in the volume of superstitutious behavior prevalent, we can see that the
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present study decidedly fits into the "Zeitgeist" of contemporary dementin.
This is
especially unfortunate for psychology, since this also means considerable talent
and potential expertise that could have pushed back frontiers of new understanding
of the normal complex realities of human perception and its relation to the nervous
system, and physical reality, should instead to diverted into inquiry into the
bizarre circuitous vagaries of the so-called "para-normal".
REFERENCES
1.
Ebbinghaus, H. Memory: A Contribution to Experimental Psychology.
New York:
Dover Publications, 1964 (original: 1885)
2.
Girden, E. . A Review of Psychokinesis (PK).
Psychological Bulletin, 1962, 59,
353-388.
.
3.
Hoffer, E.
The True Believer.
New York:
New American Library, 1964 (original
1951).
4.
Puthoff, H. E., and Targ, R. A Perceptual Channel for Information Transfer over
Kilometer Distances: Historical Perspective and Recent Research.
Proceedings
.
of the IEEE, 1976, 64, 329-354.
5. :
Rhine, J. B. The Reach of the Mind.
New York: W. Sloane Associates, 1966
Sincerely yours,
Gamos di Calvins
James L. Calkins, Ph. D.
Associate Professor
JLC:rm
G
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