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ENHANCING
HUMAN PERFORMANCE
Issues, Theories, and Techniques
Daniel Druckman and John A. Swets, Editors
Committee on Techniques for the Enhancement of Human Performance
Commission on Behavioral and Social Sciences and Education
National Research Council
NATIONAL ACADEMY PRESS
Washington, D.C. 1988
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NATIONAL ACADEMY PRESS . 2101 Constitution Avenue, NW . Washington, DC 20418
NOTICE: The project that is the subject of this report was approved by the Governing
Board of the National Research Council, whose members are drawn from the councils of
the National Academy of Sciences, the National Academy of Engineering, and the Institute
of Medicine. The members of the committee responsible for the report were chosen for
their special competences and with regard for appropriate balance.
This report has been reviewed by a group other than the authors according to procedures
approved by a Report Review Committee consisting of members of the National Academy
of Sciences, the National Academy of Engineering, and the Institute of Medicine.
The National Academy of Sciences is a private, nonprofit, self-perpetuating society of
distinguished scholars engaged in scientific and engineering research, dedicated to the
furtherance of science and technology and to their use for the general welfare. Upon the
authority of the charter granted to it by the Congress in 1863, the Academy has a mandate
that requires it to advise the federal government on scientific and technical matters. Dr.
Frank Press is president of the National Academy of Sciences.
The National Academy of Engineering was established in 1964, under the charter of the
National Academy of Sciences, as a parallel organization of outstanding engineers. It is
autonomous in its administration and in the selection of its members, sharing with the
National Academy of Sciences the responsibility for advising the federal government. The
National Academy of Engineering also sponsors engineering programs aimed at meeting
national needs, encourages education and research, and recognizes the superior achieve-
ments of engineers. Dr. Robert M. White is president of the National Academy of
Engineering.
The Institute of Medicine was established in 1970 by the National Academy of Sciences
to secure the services of eminent members of appropriate professions in the examination
of policy matters pertaining to the health of the public. The Institute acts under the
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Medicine.
The National Research Council was organized by the National Academy of Sciences in
1916 to associate the broad community of science and technology with the Academy's
purposes of furthering knowledge and advising the federal government. Functioning in
accordance with general policies determined by the Academy, the Council has become the
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Academy of Engineering in providing services to the government, the public, and the
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Academies and the Institute of Medicine. Dr. Frank Press and Dr. Robert M. White are
chairman and vice chairman, respectively, of the National Research Council.
Library of Congress Cataloging-in-Publication Data
Enhancing human performance : issues, theories, and techniques /
Daniel Druckman and John A. Swets, editors.
p.
cm.
"Committee on Techniques for the Enhancement of Human Performance,
Commission on Behavioral and Social Sciences and Education, National
Research Council."
Bibliography: p.
Includes index.
ISBN 0-309-03792-1.
ISBN 0-309-03787-5 (soft)
1. Self-realization-Congresses. 2. Performance-Psychological
aspects-Congresses. I. Druckman, Daniel, 1939-
II. Swets,
John Arthur, 1928-
. III. National Research Council (U.S.).
Committee on Techniques for the Enhancement of Human Performance.
BF637.S4E56 1987
158-dc19
87-31233
CIP
Copyright @ 1988 by the National Academy of Sciences
Printed in the United States of America
COMMITTEE ON TECHNIQUES FOR THE
ENHANCEMENT OF HUMAN PERFORMANCE
JOHN A. SWETS, Chair, Bolt Beranek and Newman Inc., Cambridge,
Mass.
ROBERT A. BJORK, Department of Psychology, University of
California, Los Angeles
THOMAS D. COOK, Department of Psychology, Northwestern
University
GERALD C. DAVISON, Department of Psychology, University of
Southern California
LLOYD G. HUMPHREYS, Department of Psychology, University of
Illinois
RAY HYMAN, Department of Psychology, University of Oregon
DANIEL M. LANDERS, Department of Physical Education, Arizona
State University
SANDRA A. MOBLEY, Director of Training and Development, The
Wyatt Company, Washington, D.C.
LYMAN W. PORTER, Graduate School of Management, University of
California, Irvine
MICHAEL I. POSNER, Department of Neurology, Washington
University
WALTER SCHNEIDER, Department of Psychology, University of
Pittsburgh
JEROME E. SINGER, Department of Medical Psychology, Uniformed
Services University of Health Sciences, Bethesda, Md.
SALLY P. SPRINGER, Department of Psychology, State University of
New York, Stony Brook
RICHARD F. THOMPSON, Department of Psychology, Stanford
University
DANIEL DRUCKMAN, Study Director
JULIE A. KRAMAN, Administrative Secretary
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Contents
PREFACE
vii
I
OVERVIEW
1
1
Introduction
3
2
Findings and Conclusions
15
3
Evaluation Issues
24
II
PSYCHOLOGICAL TECHNIQUES
37
4
Learning
39
5
Improving Motor Skills
61
6
Altering Mental States
102
7
Stress Management
115
8
Social Processes
133
III PARAPSYCHOLOGICAL TECHNIQUES
167
9
Paranormal Phenomena
169
REFERENCES
209
APPENDIXES
233
A Summary of Techniques: Theory, Research, and
Applications
235
B Background Papers
246
C Committee Activities
248
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CONTENTS
D
Key Terms
252
E
Military Applications of Scientific Information
262
F
Biographical Sketches
282
INDEX
289
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Preface
The Army Research Institute in 1984 asked the National Academy of
Sciences to form a committee to examine the potential value of certain
techniques that had been proposed to enhance human performance. As
a class, these techniques were viewed as extraordinary, in that they were
developed outside the mainstream of the human sciences and were
presented with strong claims for high effectiveness. The committee was
also to recommend general policy and criteria for future evaluation of
enhancement techniques by the Army.
The Committee on Techniques for the Enhancement of Human Per-
formance first met in June 1985. The 14 members of the committee were
appointed for their expertise in areas related to the techniques examined.
The disciplines they represent include experimental, physiological, clin-
ical, social, and industrial psychology and cognitive neuroscience; one
member is a training program director from the private sector. During
the next two years, the committee gathered six times, met in toto or in
part on several occasions with various representatives of the Army,
conducted interviews and site visits and sent subcommittees on several
others, and commissioned 10 analytical and survey papers. The committee
also examined a variety of materials, including state-of-the-art reviews
of relevant literature, reports commissioned by the Army Research
Institute, and unpublished documents provided by institutes, practition-
ers, and researchers. The report that follows describes the committee's
activities, findings, and conclusions. Though cast largely in terms of the
sponsor's setting, this report is relevant to other settings, for example,
industry. The next few paragraphs present some background.
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PREFACE
That the United States Army should be concerned to enhance the
performance of its personnel is self-evident. We know that young
volunteers must become not only soldiers who do well in battle but also
technicians who skillfully operate and maintain complex equipment in
peace and war. We are aware, moreover, that personal skills are not
enough: individuals are heavily dependent on each other within small
groups, and groups of various sizes must work very effectively together
to germit survival and ensure success. And, of course, all must be ready
togive peak performances in situations of great hardship, uncertainty,
ang stress. In the face of these staggering requirements, one must realize
th& turnover of personnel is high and that the training time available-
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to mpart the necessary cognitive, physical, and social skills-is brief.
So it comes as no surprise that the Army is on the lookout for techniques
that can help enhance human performance. The Army Research Institute
is charged with seeking out and developing such techniques: it does so
bygemploying researchers in the human sciences and by supporting
appropriate research in universities and other public and private organi-
zagions. It focuses largely on promising new techniques as they appear
inChe mainstream of behavioral, physiological, and social research.
However, given the pressures and given a view of mainstream research
as low, narrow, and insufficiently targeted, it also comes as no surprise
that some influential officers and certain segments of the Army want to
cast a broader net to snare promising enhancement techniques. To do
this, they look beyond traditional research organizations and practices
to what are viewed as extraordinary techniques. These techniques are
thought possibly to provide such unusual benefits as accelerated learning,
learning during sleep, superior performance through altered mental states,
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beater management of behavior under stress, more effective ways of
influencing other people, and so on. There is also an initiative within the
Agny to consider techniques based on paranormal phenomena, for
example, extrasensory perception to view remote sites and psychokinesis
toinfluence the operation of distant machines.
Along with these urgings to examine, to try, or to implement extraor-
dinary techniques come difficult new problems for those in the Army
responsible for evaluation, as well as for those in the Army responsible
forpersonnel and training practices. One issue is that proponents of such
techniques are usually not content with traditional evaluation procedures
or scientific standards of evidence, often giving more weight to personal
experience and testimony. Furthermore, a typical technique of this kind
does not arise from the usual research traditions of experiments published
in refereed journals and peer review of cumulated evidence, but rather
appears full-blown as a package promoted by a commercial vendor. What
does the Army Training and Doctrine Command or the base commander
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PREFACE
do when the need is great, the package is ready, the claims are for
miracles, some senior officers are vocally supportive, and the evaluation
criteria are fluid? What do Army intelligence agencies do when the same
conditions apply and other nations are said to be active in investigating
paranormal effects?
The committee decided to assess a representative set of the techniques
in question and resolved to address the surrounding issues in an open-
minded and thorough way. We therefore divided ourselves into a number
of subcommittees organized according to the behavioral processes ad-
dressed by the several techniques: accelerated learning, sleep learning,
guided imagery, split-brain effects, stress management, biofeedback,
influence strategies, group cohesion, and parapsychology. In addition, a
subcommittee on evaluation issues was formed to examine practices and
standards relevant to all the techniques. Each chapter of the report was
prepared by the appropriate subcommittee, but interactions were frequent
and so the report represents a collaborative effort of all the members.
Chapter 1 provides a context for the committee's task and the Army's
interest in enhancing performance, characterizes some particular tech-
niques, and introduces some general issues in evaluating them. Chapter
2 presents the committee's findings about the techniques examined and
conclusions about appropriate evaluation procedures. Chapter 3 treats
the relevant evaluation issues more systematically and presents the
committee's philosophy of evaluation as it pertains to the matter at hand.
Chapters 4 through 8 deal with particular techniques but are organized
in terms of more general psychological processes. Chapter 9 considers
parapsychological techniques.
The report concludes with six appendixes. Appendix A briefly sum -.
marizes the key elements of each enhancement technique. Appendix B
lists the ten papers commissioned by the committee and their authors.
Appendix C lists the members and activities of the subcommittees and
also the activities of the committee as a whole. Appendix D lists key
terms used in the research on particular techniques. Appendix E discusses
the application of scientific research by the military. Appendix F contains
biographical sketches of the committee members.
As committee chair, I am now in the pleasant position of recounting
the several contributors to the total committee process, a process that
went remarkably well. Definition and guidance for the committee's task
came primarily from Edgar M. Johnson, director of the Army Research
Institute. Administrative and technical liaison was ably provided by
project monitor George Lawrence, who worked closely with the com-
mittee in its various activities. They were supported well by several
senior Army officers, including Colonel William Darryl Henderson,
Commander of the Army Research Institute; Major General John Crosby,
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PREFACE
Assistant Deputy Chief of Staff for Personnel; and General Maxwell R.
Thurman, Vice Chief of Staff. The committee met with members of a
resource advisory group that included Lieutenant General Robert M.
Elton, chair, Deputy Chief of Staff for Personnel; Lieutenant General
Sidney T. Weinstein, Assistant Chief of Staff for Intelligence; Dr. Louis
M. Cameron, Director of Army Research and Technology; Major General
Maurice O. Edmunds, Commander of the Soldier Support Center; and
Major General Philip K. Russell, Commander of the Medical Research
and Development Command. Among the Army staff who were very
helpful to the committee are Colonel John Alexander and Mr. Robert
KBus; the names of many others appear in Appendix C.
The committee's two consultants contributed special expertise: Paul
Howitz (of Bolt Beranek and Newman Inc.) joined the site visits of the
sumicommittee on parapsychology and advised on physical aspects of
experiments in that area; James Schroeder (of Southwest Research
Ingitute) attended the committee's meeting at Fort Benning, Georgia,
and advised on the application of scientific research by the military (see
Appendix E). The committee also received special expertise by commis-
signing papers. These papers and their authors are listed in Appendix B.
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At the National Research Council, David Goslin, executive director of
theCommission on Behavioral and Social Sciences and Education, once
again provided wise counsel and support. Ira Hirsh, commission chair,
and William Estes, also representing the commission, gave valuable
adgice and encouragement. Thomas Landauer, a member of the NRC's
Committee on Human Factors, provided liaison in the areas of our
committees' mutual interests. The reviewers of this report gave us a good
measure of reinforcement along with helpful critiques. Eugenia Grohman,
associate director for reports, lent experience and wisdom to this report.
Special gratitude is extended to Christine McShane, the commission's
edgor: her skillful editing of the entire manuscript contributed substantially
toits readability, and the coherence of the volume owes much to her
suggestions for organizing the material. Julie Kraman, as administrative
secretary to the committee, earned its considerable appreciation for
setting up efficient meetings and for handling all manner of tasks graciously
and smoothly.
Daniel Druckman, study director of the project, receives the commit-
tee's great appreciation for his intellectual contributions across the broad
range of topics considered as well as for his logistic support. Working
closely with the authors of chapters and commissioned papers, he provided
an integration of the several contributions as well as much of the
introductory and interstitial material. He also served on two subcommit-
tees in areas of his expertise.
The ultimate debt of anyone who finds this report useful, and my large
xi
PREFACE
personal debt, is to the members of the committee. As individuals, their
capabilities are broad and deep. As a group, they gave generously and
productively of their time, were always engaged, responded to every
challenge, and, especially, showed an exceptional talent for reaching
consensus in a collegial, advised, and efficient way.
JOHN A. SWETS, Chair
Committee on Techniques for the
Enhancement of Human Performance
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PART
I
Overview
PART I CONSISTS OF THREE CHAPTERS. Chapter 1 sets the stage for the
report. It describes the committee's task, provides background on
the Army's interest in enhancement techniques, characterizes specific
techniques examined by the committee, and identifies the main issues in
evaluating the relation between techniques and human performance.
Chapter 2 presents the committee's findings and conclusions. We draw
general conclusions about the process of consideration given to any
technique and state specific findings and conclusions for each of the areas
of human performance examined.
Chapter 3 presents the committee's philosophy of evaluation as it
pertains to enhancement techniques. Some of the issues involved concern
the conduct of basic research; others concern the conduct of field tests.
With respect to basic research, issues include the plausibility of inferences
about novel concepts, causation, alternative explanations of causal
relations, and the generalizability of causal relations. With respect to
field tests, a number of questions are of interest: Does the enhancement
program meet genuine Army needs? Is the resulting program implement-
able, given program design and resources? Do unintended side effects
limit utility? Is the program more cost-effective than its alternatives?
These questions underscore the reality that evaluation research is largely
a pragmatic activity influenced by the organizational context in which it
occurs.
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1
Introduction
THE COMMITTEE'S TASK
At the request of the U.S. Army Research Institute, the National
Research Council formed a committee to assess the field of techniques
that are claimed to enhance human performance. The Institute asked the
Council to evaluate the claims made by proponents of selected existing
techniques and to address two general additional questions: (1) What are
the appropriate criteria for evaluating claims for such techniques in the
future? (2) What research is needed to advance our understanding of
performance enhancement in areas related to the proposed techniques?
The objectives of the committee's study are to provide an authoritative
assessment of these questions for policymakers in research and devel-
opment who are consumers of the techniques, as well as to consider their
possible applications to Army training.
Many of the techniques under consideration grew out of the human
potential movement of the 1960s, including guided imagery, meditation,
biofeedback, neurolinguistic programming, sleep learning, accelerated
learning, split-brain learning, and various techniques to reduce stress and
increase concentration. Many of these techniques have gained popularity
over the past two decades, promoted by persons eager to provide answers
to problems of human performance or to prosper from them. While often
using the language of science to justify their approach, these promoters
are for the most part not trained professionals in the social and behavioral
sciences. Nonetheless, they do appeal to basic needs for human perform-
ance, and the Army, like many other institutions, is attracted to the
prospect of cost-effective procedures that can improve performance.
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ENHANCING HUMAN PERFORMANCE
These institutions must evaluate the effects of such procedures, however.
Issues include the appropriateness of a quick-fix approach, the distinction
between the impact of an experience and actual change, and the plausibility
of evidence indicating that something is happening even if the effects are
not reproducible or the benefits uncertain.
A more conservative atmosphere in the 1980s is reflected in the way
techniques are advanced. Motivation in the 1980s may be primarily
entrepreneurial, not ideological, as it was in the 1960s. Advocates focus
ongelating the techniques to specific tasks, such as marksmanship, foreign
language acquisition, fine motor skills, sleep inducement, and even combat
effectiveness. Some techniques are in fact rooted in a scientific literature.
For these reasons the various techniques have attracted the interest of
ingitutions that have rejected, and would probably continue to reject,
comtercultural trends in society. Indeed, much attention has been given
toghese techniques by industrial, government, and military policymakers,
asovell as by the general public. For this reason especially, it is important
to address the issues surrounding the claims made for effectiveness.
elaborate training programs have grown, nourished by their developers'
enthusiasm and salesmanship in a social context receptive to quick cures.
Fofmany of these programs, success in the marketplace is used to justify
the approaches. For others, more esoteric concepts, including the role
of neurotransmitters, the physics of neuromuscular programming, brain
wave patterns, hemispheric laterality, high-access memory storage, pre-
ferred sensory modalities, and low-gain innervation of muscles, are used
to Attempt to provide scientific justification for the claims. The chapters
the follow evaluate the evidence and theories used to support the claims
of several popular techniques. Before turning to these evaluations,
however, we provide some background on the Army's interest in these
techniques, as well as a discussion of issues surrounding enhanced
performance and issues in evaluating the relation between techniques
and performance.
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THE ARMY'S NEEDS
The Army motto, "Be all that you can be," symbolizes the current
ethos of the institution, an army of excellence. Emphasis is placed on
attaining certain ideals, such as fearlessness, cunning, courage, one-shot
effectiveness, fatigue reversal, and nighttime fighting capabilities. These
ideals are assumed to be realizable through training, even if the most
effective techniques have not as yet been identified. The culture of
improvement is further reinforced by the dilemma created by an all-
volunteer Army and the demands of complex new computer technologies.
Many civilians enter military service with only the required minimum of
5
INTRODUCTION
formal education; most of these volunteers enlist in the Army. For this
reason, the Army's emphasis on skill training is well founded.
The importance of the human element in combat is recognized in the
Army Science Board's 1983 report "Emerging Concepts in Human
Technology," which phrases the issue in terms of high yield at relatively
low investment. Human capital is considered to be the best potential
source for growth in Army effectiveness, both in terms of return on
investment and as a moral imperative "if we are to commit our soldiers
to fight outnumbered and win." The technologies singled out in the report
are those that can improve creativity and innovation, learning and training,
motivation and cohesion, leadership and management, individual, crew,
and unit fitness, soldier-machine interface, and the general productivity
of the Army's human resources.
The Board's report largely bypasses issues of systematic evaluation of
enhancement techniques within the Army context, while addressing
mechanisms for integrating them with Army activities. Little concern is
shown for adducing relevant criteria to determine whether implementation
is feasible. The Army's ambitious goals, combined with a reluctance to
deal with the complexities surrounding issues of human performance,
make this institution potentially susceptible to a variety of claims made
by technique developers. It would therefore seem prudent to devise
criteria for evaluating those claims.
A SELLER'S MARKET
Techniques for enhancement of human performance have received
much attention in the popular press. They have been actively promoted
by entrepreneurs who sense a profitable market in self-improvement. The
American Society for Training and Development "estimates that com-
panies are spending an astounding $30 billion a year on formal courses
and training programs for workers. And that's only the tip of the iceberg"
(Wall Street Journal, August 5, 1986). They are also taken seriously by
the U.S. military, who are at times accused of losing the "mind race"
to the Soviets (see, for example, Anderson and Van Atta, Washington
Post, July 17, 1985). The Army has shown particular interest in techniques
that help people acquire, maintain, or improve such skills as classroom
learning, communication and influence, creativity, and accuracy in the
execution of tasks requiring motor skills. Those that are cost-effective
and produce relatively rapid results are likely to receive the most attention,
along with research breakthroughs that could be a basis for new training
programs. What are these techniques? What claims are being made for
them? Is there evidence that substantiates these claims?
Examples of techniques include biofeedback (information about internal
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ENHANCING HUMAN PERFORMANCE
processes), Suggestive Accelerative Learning and Teaching Techniques
(a package of methods geared primarily toward classroom learning),
hemispheric synchronization (a machine-aided process based on assump-
tions about right brain-left brain activities), neurolinguistic programming
(procedures for influencing another person), and Concentrix (a procedure
used to improve concentration on specific targets). Also of interest to
the, Army are such processes as group cohesion and stress reduction, as
well as the claims for sleep learning, peak performance, and parapsy-
ch&logy. Together, these techniques and processes cover the major types
ofskills-motor, cognitive, and social. Several of them are described
he& briefly, along with illustrative claims found in brochures and course
merial.
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Suggestive Accelerative Learning and Teaching Techniques (SALTT)
is an approach to training that employs a combination of physical
re@xation, mental concentration, guided imagery, suggestive principles,
arg baroque music with the intent of improving classroom performance.
Some applications have included language training, typing instruction,
ang high school science courses. Attempts have been made to evaluate
the applications, and many of these evaluations are published in the
Journal of the Society for Accelerative Learning and Teaching (Psy-
chology Department, Iowa State University). The following is a sampling
of claims made in brochures and convention announcements: "A proven
method which has broad potential application in U.S. Army training";
" will significantly reduce training time, improve memory of material
learned and introduce behavioral changes that positively affect soldier
poformance-self-esteem, self-confidence, and mental discipline"; and
lost students will prove to themselves that they have learned a far
greater amount of material per unit of time with a greater amount of
plasure than they have ever previously done."
"Neurolinguistic programming (NLP) refers to a set of procedures
developed to influence and change the behaviors and beliefs of a target
person. Its goals are mostly therapeutic, but its proponents also advocate
tff use of the techniques in advertising, management, education, and
ingerpersonal activities. A small research literature, published primarily
inthe Journal of Counseling Psychology, has developed. Practitioners
can be trained and certified at various institutes, and the National
Association for Neurolinguistic Programming distributes a newsletter to
its membership, currently about 500 persons. Illustrative claims and
testimonials found in advertising materials include: "[NLP] has evolved
a unique technology which encompasses a set of specific techniques
enabling you to produce well-defined results" and "NLP ... is clear,
easy to learn, and brilliant." A typical slogan is that found in a brochure
from the Potomac Institutes, Silver Spring, Maryland: "The difference
7
INTRODUCTION
that makes the difference, for education, management, psychotherapy,
psychiatry, business, law, health care, and the arts."
Hemi-Sync™, which is short for hemispheric synchronization, is a
technique that consists of presenting two tones slightly differing in
frequency to separate ears with stereo headphones to produce binaural
beats. The long-known result is a tone that waxes and wanes at a
frequency equal to the difference between the original tones. Pioneered
as an enhancement technique by Robert Monroe of the Monroe Institute
of Applied Science in Faber, Virginia, the technique is based on the
assumption of a frequency following response (FFR) in the human brain.
The FFR refers to a correspondence between sound signals heard by the
ear and electrical signals recorded by an electroencephalograph (EEG).
It is claimed that, by altering sound patterns, it is possible to alter states
of awareness. Stated applications are in the areas of language learning,
stress management, reading skills, and creativity and problem solving.
Claims of effectiveness stated in the Monroe Institute's brochure are
wide-ranging, covering education (e.g., "77.8 percent of a class reported
improvement in mental-motor skills"), health (early recuperation, lower
blood pressure), psychotherapy (stress reduction, working with terminally
ill patients, teaching autistic children), and sleep restorative training (e.g.,
"forty of forty-five insomniacs reported that one-month use of Hemi-
Sync@ tapes was at least as effective as medication, without the drug
side effects").
SyberVision® is a scripted videotape that presents an expert (e.g., a
world-class athlete) repeatedly performing fundamental skills of his or
her activity (e.g., golf) without verbal instructions. It is based loosely on
principles of vicarious learning, guided imagery, and mental rehearsal.
Developed and marketed by SyberVision Systems Inc., San Leandro,
California, the package includes a cassette and instruction manual with
an appendix on the "simple physics of neuro-muscular programming."
The appendix presents a scientific rationale for the technique, for example,
"the more you see and hear pure movement, the deeper it becomes
imprinted in your nervous system . .. and the more likely you are to
perform it as a conditioned reflex," and "The decomposition of what is
seen and sensorily experienced into an electromagnetic wave form is
accomplished by a complex mathematical operation (Fourier Transform)
by the brain" (Instruction Manual on Golf with Patty Sheehan). Support
for enhanced performance is, however, based on testimonials rather than
experiments, for example, Killy on skiing, a Stanford tennis coach on
tennis, Professional Golf Association members on golf, Peters (In Search
of Excellence) on achievement, Salk on leadership, and a variety of
corporate executives and educators on self-improvement. Claims range
from sweeping statements (e.g., "We owe these two men a large debt of
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ENHANCING HUMAN PERFORMANCE
gratitude") to rather precise statements (e.g., "In 47 days I have lost 25
pounds [191 to 166], yet I look like I lost 40") (in the United Airlines
magazine, Discoveries). This technique involves a significant marketing
effort that builds on users' willingness to be quoted and the use of
acknowledged academic experts (e.g., Stanford neuropsychologist Karl
Pribram), whose role in the program is advertised as being central.
Stress management techniques are procedures designed to alleviate
argiety or tension. Catering to an age of anxiety, self-help books, groups,
ara clinics on managing stress proliferate. A good example of the approach
isethe recent book by Charlesworth and Nathan (1982), which emphasizes
fiBess, nutrition, managing time, general life-styles and life-cycles, as
well as strategies such as progressive relaxation, autogenic training, and
ingage rehearsal. Appendixes provide the reader with home practice
cfarts, a guide to self-help groups, and suggested books and recordings.
Te groups offer their members information, emotional support, and a
s&se of belonging. Often stress management procedures are combined
with a number of other techniques into a single package. The promoters
offen emphasize the total package rather than particular techniques; the
packages usually combine several processes that, when acting together,
ark thought to produce significant effects.
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TThe Army's needs for techniques that can improve performance make
it subject to the sorts of claims illustrated above. While they and other
consumers can avoid the more obvious pitfalls, the proliferation of choices
fd products and the lack of scientific evidence allow marketplace criteria
& become the bases for decisions. But there are exceptions. Some
techniques have received the attention of the scientific community, and
idence is available to be used as criteria in such areas as biofeedback,
gided imagery, sleep learning, cohesion, and even for some aspects of
tychic phenomena and neurolinguistic programming.
The literature has alerted us, for example, to the distinction between
the effects of biofeedback on fine motor skills and on stress, to the
different effects of mental and physical rehearsal, to placebo and Haw-
tBorne effects in stress research, to the priming and repetition effects of
material presented during sleep, to some dysfunctions of group cohesion,
to the difficulties of replicating experiments on extrasensory perception,
aid to the implausibility of specialized sensory modalities as postulated
by NLP (see Appendix D for key terms). These findings make evident a
complex relation between technique and performance.
IMPROVED PERFORMANCE:
COMPLEX ISSUES, SIMPLE SOLUTIONS
The research literature in such traditional areas of experimental psy-
chology as learning, perception, sensation, and motivation suggests
9
INTRODUCTION
complex relations between interventions and improved performance.
Many technique promoters appear to pay little attention to this literature,
preferring an alternative route to invention: rather than derive a procedure
from appropriate scientific literature, they create techniques from personal
experiences, sudden insights, or informal observation of "what works."
Science may enter the process after the technique is developed and used,
for example, to legitimize its use or to endorse methods for evaluation.
Research follows rather than precedes the invention. This sequence
increases the likelihood that important considerations will be missed. We
highlight some of these considerations in this section.
The lack of easy avenues to improved performance may well be due
to the complexity of the behavior in question. One definition of skills
emphasizes the importance of the coordination of behavior: "A skilled
response ... means one in which receptor-effector-feedback processes
are highly organized, both spatially and temporally. The central problem
for the study of skill learning is how such organizations or patterning
comes about" (Fitts, 1964:244). This definition implies that skill learning
involves an orchestration of diverse processes, making the topic an
interesting one to various subfields of psychology. It also makes evident
a number of unresolved issues, including whether different skills are
learned and retained in different ways. The research findings obtained in
this literature contribute to our understanding of the necessary, if not
sufficient, conditions for improved performance.
Research on skill acquisition addresses such basic questions as What
are the stages of learning? and What is learned? Distinctions made
between short-term and long-term memory storage and between schemas
and details have contributed to our understanding of basic processes (see
Welford, 1976). Other questions have more direct consequences for
application: for example, what contributes to the acquisition and main-
tenance of skills? How can the adverse effects of stress, fatigue, and
monotony be avoided? These questions are the basis for programs of
research that can be divided into several parts, each defined in terms of
empirical issues (Irion, 1969; see also the other chapters in Bilodeau and
Bilodeau, 1969). Some examples of empirical issues are practice effects
(differences due to distributed versus massed practice, long versus short
rest periods, short versus long sessions), the whole-part problem (differ-
ences due to learning a task as a whole versus learning it by its constituent
elements), feedback (differences due to delays in receiving knowledge of
results and to type of information during the delay period), retention
(differences due to whether the the task is motor or verbal), and transfer
of training.
These and related considerations suggest that skill learning is an
incremental process likely to differ from one type of skill to another.
Whether intending to enhance motor, verbal, problem-solving, or social
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performances, technique designers can ill afford to ignore these lessons
from the experimental literature on skill acquisition and maintenance. It
is also the case, however, that the agenda of unexplored issues is much
larger than the accomplishments to date, and this is recognized particularly
in the rapidly growing field of cognitive psychology, in which the
"information-processing revolution" is just beginning.
9606791R060206320
,Practical applications are, however, not automatic. Many excellent
aglications do not spring from basic science; some are the result of craft
afi experience. More important perhaps are the indirect contributions
n&de in both directions-from basic to applied and vice versa. A
s&stematic approach taken in both domains serves to vitalize each, as
vBen applied investigations reveal new phenomena that need explanation
when a new package incorporates basic principles discovered originally
ig the laboratory. Such an approach is likely to facilitate the design of
appropriate techniques for skill acquisition. At issue is whether a particular
technique can produce and sustain desired changes.
One conclusion from the research accumulated to date is that effective
interventions are those that are continuous and self-regulating and take
&count of both context and person (see, for example, Lerner, 1984).
Particularly relevant is the difference between short-term and long-term
Ranges. Effects obtained by many techniques for performance enhance-
ment may be short-term in their effects. This distinction is made by Back
(1973, 1987) in his evaluation of the sensitivity training movement. The
Ganges observed by sensitivity trainers and documented by evaluators
may well reflect the impact of the experience per se. Such situation
affects are unlikely to be sustained in different environments, an obser-
Vation supported by the literatures in both developmental and social
rBychology (Druckman, 1971; Frederiksen, 1972). These literatures cau-
toon against hasty generalizations from observed, situation-specific effects;
ffey also explain why long-term effects may be difficult to produce with
grief exposures to "treatments." Like the sensitivity trainers of the 1960s
and 1970s, many of the promoters (and consumers) of the 1980s pay little
&tention to issues of causality and intrinsic motivation, preferring instead
dwell on single dimensions of treatments or to offer a mixed package
Constructed in arbitrary ways and producing diffuse effects that reflect
the experience.
The issue of expected benefits from techniques provides a bridge
between research and application. Research can be designed to evaluate
techniques, as well as to discover possible unintended side effects.
Indeed, a research literature has developed in some of the areas examined
in this book, namely biofeedback, stress, and guided imagery. For many
other techniques, however, a relevant body of research does not exist;
this lack applies to some of the techniques examined by the committee,
11
INTRODUCTION
as well as to those yet to appear on the market. It is these techniques
that present a problem for us as evaluators. Evaluation without data is
difficult, but not impossible. Our approach is to place the techniques into
broader categories corresponding to the key processes being influenced,
for example, learning, motor skills, and influence. By so doing, the claims
can be evaluated within the frameworks of existing theories and metho-
dologies. They can also be judged against results obtained in related
areas. This approach serves as the organizing theme for the chapters that
follow.
EVALUATING THE TECHNIQUES
Evaluations properly hinge on answers to a standard set of questions
proposed in a paper entitled "Evaluating Human Technologies: What
Questions Should We Ask?" by Hegge, Tyner, and Genser (1983) at the
Walter Reed Army Institute for Research:
. What changes will the technique produce?
. What evidence supports the claims for the technique?
. What theories stand behind the technique?
. Who will be able to use the technique?
. What are the implications of the technique for Army operations?
. How does the technique fit with Army philosophy?
· What are the cost-benefit factors?
These questions served as guidelines for the committee's evaluations.
Appendix A is a summary description of each technique, organized along
the lines of the Hegge, Tyner, and Genser questions, covering theory,
research, and application. For many of the categories, however, the
desired information is either too limited to be useful or simply not
available; in such cases we have considered other strategies for evaluation.
The committee faced a number of difficulties in evaluation that stem
from recurrent problems posed by the technologies. One is the tendency
for some promoters (and consumers) to rely primarily on testimonials or
anecdotal evidence as a basis for application. Another is a general lack
of strong research designs to provide evidence of effects. These problems
are considered also in the context of specific techniques discussed in the
chapters of Parts II and III.
Practitioners of techniques often emphasize the value of personal or
clinical experience and marketplace popularity as bases for judging the
techniques. They are generally less inclined to seek research evidence
or to support research evaluation programs. These attitudes may be
related to the fact that few practitioners are trained as researchers. For
some it is sufficient to let others do the research. For others, research is
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viewed, in varying degrees, as a threat to their product. At one extreme,
research is regarded as a debunking enterprise, engaged in by scientists
who have little interest in providing human services. At another extreme,
the problem is one of educating the researchers in nuance, context, and
a clinical approach that emphasizes adapting techniques to changed
situations and client tastes. The result is a gap in communication
epitomized by two cultures-scientists searching for evidence and prac-
titigners seeking effects and cures. A step toward bridging the gap would
coBist of mutual education through joint ventures. These ventures would
expose scientists to the goals (and motives) of practitioners and would
als make practitioners aware of the general analytical approaches used
byScientists.
Experimentation is an appropriate vehicle for evaluating performance-
enhancing techniques; the problem is usually defined in terms of effects
of Techniques (procedures) on performance (behaviors). It is also appro-
prote at an earlier stage in the process, when products are being
degeloped. Products evolve in a kind of trial-and-error fashion similar in
many respects to scientific discoveries. One model for integrating research
wifi product development is engineering research and development
(R&D). A strenuous applied research effort accompanies the development
process in many firms, as does a quality-control program designed to
evaluate products both during development and after they have been
placed on the market. With a few exceptions, this model has not been
adopted by firms or institutions in the field of performance enhancement.
Experimental evidence has accumulated in some areas related to
techniques. Although not linked specifically to product development in
the manner of an R&D operation, this work does address the question,
What evidence supports the claims for the technique? In fact, so strong
is@the experimental tradition in some areas that a body of work has
developed programmatically within a generally accepted paradigm (e.g.,
gujded imagery). The benefits of a long research tradition can be seen in
these areas. Meta-analyses have been performed and can be used as a
basis for evaluation. For other areas, we are presented with the prospect
ofgrelying on scattered experiments or using other criteria as a basis for
evaluation, or both (see Appendix A for summaries of the state of the
science in each of the areas).
However, the benefits of experimental evidence derive primarily from
the general approach rather than from the particular experiments. This
idea is captured by Kelman, who noted that "an experimental finding
. . . cannot very meaningfully stand by itself. Its contribution to knowledge
hinges on the conceptual thinking that has produced it and into which it
is subsequently fed back" (1968:161). We emphasize here the contribution
13
INTRODUCTION
of an analytical approach to thinking about behavior, as distinct from the
establishment of laws about psychological processes. It is the cumulation
of a series of experiments that winnows out the useful parts of treatments
or techniques. It is the self-correcting progression of new experiments
that refines treatments, saving those that work and discarding those that
do not (or that work only under very restricted conditions). This process
contributes equally well to the goals of theory development and product
development.
Other evaluation criteria elucidated by Hegge, Tyner, and Genser
(1983) include theories, uses, and implications for Army operations and
philosophy. A problem with these criteria is that they tend to be vague
and somewhat idiosyncratic, making it difficult to propose general cate-
gories on which most people would agree. Without precisely defined
categories for judging techniques, it is difficult to address issues of transfer
of performance from one situation to another or to evaluate newly
emerging techniques. A similar problem exists with respect to developing
taxonomies in broadly defined fields: there is little agreement on a set of
categories for the fields of human learning, performance, motivation,
perception, and social and organizational processes. More mature sub-
disciplines provide an empirical basis for taxonomies, allowing for more
tightly constructed systems of tasks and situations: for example, rote
learning, short-term memory, concept learning, problem solving, work
motivation, and team functions (see Fleishman and Quaintance, 1984).
An advantage of such systems is that they capture rather precise
relationships between task and performance.
This discussion serves only to introduce the issues and identifies several
themes that receive more detailed attention in the chapters to follow.
First, any evaluation must take into account the status of the available
evidence. Confidence placed in judgments about a technique should be
based on the quality of the evidence produced by researchers. Second,
the evaluator cannot afford to rely exclusively on a single criterion for
judging effectiveness. Theoretical and applied issues are also important,
as are considerations of values served or violated by use of the technique.
Third, technique development issues are not isolated from research or
analytical issues. Each step in the process of product design can be
regarded as an empirical issue; decisions made about procedures and
packaging can be the result of experimental outcomes. Fourth, the subject
of enhancing human performance is not new. It has been a topic of
interest for centuries and an area of scientific work for several decades.
The literatures on learning and skill acquisition should be consulted by
developers, and insights derived from these literatures should be used in
product design.
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These themes are woven throughout the discussions of specific tech-
niques. Each chapter discusses relevant literature, describes the specific
techniques, points to directions for further research when appropriate,
and notes possible applications in military and industrial settings. Despite
the common coverage, however, each chapter is also unique in that each
is tailored to the particular problems associated with its focus.
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2
Findings and Conclusions
The committee's first major task was to evaluate the existing scientific
evidence for a wide range of techniques that have been proposed to
enhance human performance. This evaluation was intended by our Army
sponsors to suggest guidelines for decision making on Army research and
training programs. In our evaluation we draw conclusions with respect
to whether more basic or applied research is warranted, whether training
programs could benefit from new findings or procedures, and what, in
particular, might be worth monitoring for potential breakthroughs of use
to the Army. In many of the areas examined it appears feasible to pursue
carefully designed programs that build on basic research; however, such
programs should be monitored closely.
The committee's second major task was to develop general guidelines
for evaluating newly proposed techniques and their potential application.
We are aware that the use of basic and applied research in decision
making is a complex issue. Although payoffs from basic research can
often be realized in the long run, the value of research findings to the
Army depends on developing a way of putting them into practice. With
regard to applied or evaluation research, further complexities are evident:
multiple, sometimes conflicting, criteria must be satisfied at each of
several stages in the evaluation process, from assessing a pilot program
to implementing the program in an appropriate setting. Another problem
is that of choosing among alternative techniques when none of them has
been subjected to a systematic evaluation. In the absence of evaluation
studies, the Army needs guidelines for selecting packages and vendors.
The committee's evaluation has produced several answers to questions
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of how best to improve performance in specific areas. On the positive
side, we learned about the possibilities of priming future learning by
presenting material during certain stages of sleep, of improving learning
by integrating certain instructional elements, of improving skilled per-
formance through certain combinations of mental and physical practice,
of reducing stress by providing information that increases the sense of
control, of exerting influence by employing certain communication strat-
ezies, and of maximizing group performance by taking advantage of
coganizational cultures to transmit values. On the negative side, we
Dcovered a lack of supporting evidence for such techniques as visual
training exercises as enhancers of performance, hemispheric synchroniz-
acon, and neurolinguistic programming; a lack of scientific justification
the parapsychological phenomena considered; some potentially neg-
ave effects of group cohesion; and ambiguous evidence for the effec-
Veness of the suggestive accelerative learning package.
"The remainder of this chapter presents the committee's findings and
Bnclusions, which are presented in two parts: general conclusions
ggarding the process of evaluating any technique being considered by
he Army and specific findings and conclusions for each of the areas of
Eman performance examined. Whenever appropriate, we make recom-
mendations for research, evaluation, and practice.
GENERAL CONCLUSIONS
"The committee suggests that the Army move vigorously, yet carefully
gd systematically, to implement techniques that can be shown to enhance
Performance in military settings. Such an effort would be timely because
of recent developments in the relevant research areas. Moreover, the
payoff is likely to be very high if techniques are selected judiciously.
ASthough the desire for dramatic improvements in performance makes
some extraordinary techniques attractive, techniques drawn from main-
steam research in relevant areas of performance may be more effective.
The Army's concern for enhancing human performance and its substantial
resources for evaluating techniques place it in a favorable position to
take advantage of developments. The Army might also consider the
possibilities of transferring its findings to the civilian sector.
Collectively, the committee's conclusions call for the adoption of
scientifically sound evaluation procedures; however, these procedures
must be adapted to institutional needs and must take into account problems
of implementation. We summarize these considerations below.
SCIENTIFIC EVIDENCE
Techniques and commercial packages proposed for consideration by
the Army should be shown to be effective by adequate scientific evidence
17
FINDINGS AND CONCLUSIONS
or compelling theoretical argument, or both. A technique's utility should
be judged in relation to alternatives designed for similar purposes, and
the estimated utility should be of significant magnitude. Specific stages
of analysis can be incorporated in pilot or field testing, and such testing
should be carried out by investigators who are independent of the
technique's originators or promoters.
TESTIMONIALS AS EVIDENCE
Personal experiences and testimonials cited on behalf of a technique
are not regarded as an acceptable alternative to rigorous scientific
evidence. Even when they have high face validity, such personal beliefs
are not trustworthy as evidence. They often fail to consider the full range
of factors that may be responsible for an observed effect. Personal
versions of reality, which are essentially private, are especially antithetical
to science, which is a fundamentally public enterprise. Of course, a
caution about testimonials should not be confused with a lack of openness
to new and unusual ideas. Such openness is consistent with the require-
ment that the evidential criteria of science be satisfied.
The subject of testimonials as evidence has received considerable
attention in recent research on how people arrive at their beliefs. These
studies indicate that many sources of bias operate and that they can lead
to personal knowledge that is invalid despite its often being associated
with high levels of conviction. The committee recommends that this
research be disseminated, as appropriate, in the Army. It may then be
applied whenever testimony is used as the primary evidence to promote
an enhancement technique.
CONDITIONS FOR IMPLEMENTATION
Two kinds of evidence should be sought to support decisions to
implement a technique: successful field tests and an analysis of imple-
mentability. It would also be useful to analyze the impact of the technique
or package on the larger system in which it is to be embedded. These
analyses would aid in explaining why the procedures are necessary and
why certain consequences are expected. In general, any description of
what a technique accomplishes should be accompanied by an explanation
of why it accomplishes what it does. Such an explanation would provide
a more fundamental understanding of processes affected by exposure to
the technique and permit optimal implementation.
RATIONAL DECISION MAKING
The considerations that must be entertained in selecting a technique
for practical use in a military setting are different from the considerations
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needed to verify the existence of an enhancement effect in a scientific
setting. For example, the benefits of correct decisions and the costs of
incorrect decisions, that is, the risk calculus, may differ in the two
settings. Furthermore, what is viewed as a timely decision will also differ.
The specific differences as they apply to particular decisions should be
made explicit.
MECHANISMS FOR ADVICE
PIt would be useful to provide valid information about useful techniques
Army commanders and other interested staff on a regular basis. Special
ansideration should be given to ways in which technique-related infor-
Ration can be transferred from scientists to practitioners. The charac-
istics of a transfer agent could be defined, and such a position might
established within an appropriate office.
"The committee recommends that the Army Research Institute formalize
Re ways in which it receives and provides advice about specific tech-
ques. A committee to review experimental designs and statistical
Analyses could be convened to improve the evaluation of techniques.
Special and standing committees could also be used to make program
Recommendations and to review proposals for intramural and extramural
fèsearch.
BIDDING PROCEDURES
Purchase by the Army of a commercial enhancement package should
ake place within the context of a set of well-defined procedures. The
committee recommends that an open-bid procedure be followed, based
on a full presentation of the Army's stated objectives. This would
Encourage competitive evaluation of techniques. The following informa-
"Gon, presented in a standard format, should be required: the objectives
of the technique, a description of its procedures, evidence that it produces
The claimed effects, and the vendor's record of past achievements in
Relevant areas.
2 Lack of professional training and research experience in human per-
gormance by a designer or advocate should not preclude consideration
«of the proposed package; it should, however, signal the need for a more
stringent analysis by the Army.
SPECIFIC FINDINGS AND CONCLUSIONS
We present below findings and conclusions for each of the areas
investigated. Some statements take the form of suggested actions based
19
FINDINGS AND CONCLUSIONS
on what we know; others consist of suggestions for more work or for
research that has not yet been done.
LEARNING DURING SLEEP
1. The committee finds no evidence to suggest that learning occurs
during verified sleep (confirmed as such by electrical recordings of brain
activity). However, waking perception and interpretation of verbal ma-
terial could well be altered by presenting that material during the lighter
stages of sleep. We conclude that the existence and degree of learning
and recall of materials presented during sleep should be examined again
as a basic research problem.
2. Pending further research results, the committee concludes that
possible Army applications of learning during sleep deserve a second
look. Findings that suggest the possibility of state-dependent learning
and retention (i.e., better recall of material when learned in the same
physiological and mental state) may be applicable to fatigued soldiers.
Furthermore, even presentations of material that disrupt normal sleep
may be cost-effective, as may presentations that coincide with stages of
light sleep.
ACCELERATED LEARNING
1. Many studies have found that effective instruction is the result of
such factors as the quality of instruction, practice or study time, motivation
of the learner, and the matching of the training regimen to the job
demands. Programs that integrate all these factors would be desirable.
We recommend that the Army examine the costs, effectiveness, and
longevity of training benefits to be derived from such programs and
compare them with established Army procedures.
2. The committee finds little scientific evidence that so-called super-
learning programs, such as Suggestive Accelerative Learning and Teach-
ing Techniques, derive their instructional benefits from elements outside
the mainstream of research and practice. We observe, however, that
these programs do integrate well-known instructional, motivational, and
practice elements in a manner that is generally not present in most
scientific studies.
3. We find that scientifically supported procedures for enhancing skills
are not being sufficiently used in training programs and make two
recommendations to remedy this problem. First, the basic research
literature should be monitored to identify procedures verified by laboratory
tests to increase instructional effectiveness. Second, additional basic
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research should be supported to expand the understanding of skill
acquisition for both noncombat and combat activities.
4. We conclude that the Army training system provides a unique
opportunity for cohort testing of training regimens. The Army is in a
position to create laboratory classroom environments in which competing
training procedures can be scientifically evaluated.
5. The committee recommends that the Army investigate expert teacher
programs by identifying and evaluating particularly effective programs
within the Army. In addition, transferable elements of effective instruction
3can be reported to the larger instructional community.
IMPROVING MOTOR SKILLS
1. The committee concludes that mental practice is effective in en-
»hancing the performance of motor skills. This conclusion suggests further
work in two directions: (1) evaluation studies of motor skills used in the
Army and (2) research designed to determine the combination of mental
and physical practice that, on average, would best enhance skill acquisition
and maintenance, taking into account both time and cost.
2. The committee concludes that programs purporting to enhance
cognitive and behavioral skills by improving visual concentration have
. not been shown to be effective to date. In our judgment, these programs
are not worth further evaluation at this time.
3. The committee concludes that existing data do not establish the
generality of observed effects from programs that train visual capabilities
to increase performance.
4. Similarly, the committee concludes that the effects of biofeedback
on skilled performance remain to be determined.
5. The committee recommends additional research to establish the
potential of these techniques in the domain of specific skilled perform-
ances.
ALTERING MENTAL STATES
1. Time did not allow the committee to explore the evidence for a
- wide variety of specific methods for relating mental states to changes in
performance. Such methods include forms of self-induced hypnotic states
and peak performance resulting from high levels of focused concentration
and meditation. We recommend that reviews of the literature in these
areas be undertaken to ascertain whether any practical results might be
obtained by the use of such methods.
2. The committee finds that, while the study of mental computations
in language and imagery has progressed in recent years, the effort to
understand how such computations are modulated by energetic factors
21
FINDINGS AND CONCLUSIONS
such as arousal, stress, emotion, and high levels of sustained concentration
has not been fully developed. For example, the claims that certain mental
states produce general improvements in performance derive from the
idea, supported by research, that arousal affects mental computations
and that there ought to be an optimal level of arousal for the performance
of such computations. We recommend this as an important area for
investment of basic research funds.
3. The committee's review of the appropriate literature refutes claims
that link differential use of the brain hemispheres to performance. Further
evaluation of these claims depends on developing valid and reliable
measures of hemispheric involvement.
4. The committee finds no scientifically acceptable evidence to support
the claimed effects of techniques intended to integrate hemispheric
activity, for example, Hemi-Sync@. Attempts to increase information-
processing capacity by presenting material separately to the two hemi-
spheres do not appear to be useful. We conclude that such techniques
should be considered further by the Army only if scientific evidence is
provided to and evaluated by the Army Research Institute.
STRESS MANAGEMENT
1. Existing data indicate that stress is reduced by giving an individual
as much knowledge and understanding as possible regarding future events.
In addition, giving the individual a sense of control is effective. On the
basis of these findings, the committee recommends a systematic program
of research and development that would address three questions: (1) How
relevant is this finding for stress reduction in the Army? (2) To what
extent does stress reduction realized in training transfer to combat
situations? (3) What are the limitations on providing knowledge and
understanding of future events and a sense of control in the Army setting?
Pending the outcome of this research, we suggest that consideration be
given to including the material in training programs for company grade,
field grade, command, and staff officers.
2. We find that, while biofeedback can achieve a reduction of muscle
tension, it does not reduce stress effectively. It is therefore not a promising
research topic in that respect. We recommend that funding be directed
toward investigation of more promising stress management procedures.
3. We recommend that information be gathered on the costs of stress
in terms of organ breakdown, loss of efficiency, and loss of time. This
information would have implications for training programs.
INFLUENCE STRATEGIES
1. The committee finds no scientific evidence to support the claim that
neurolinguistic programming is an effective strategy for exerting influence.
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23
We advise that further Army study of this aspect of NLP be made only
in comparison with other techniques.
2. There are no existing evaluations of NLP as a model of expert
performance. We conclude that further investigation of such models may
be worthwhile and suggest that NLP be examined in comparison with
several other techniques.
3. Concerning the process of technology transfer, we recommend that
studies be conducted to develop training regimens for those who train
others to wield social influence. The large literature on this topic in social
psychology would provide a basis for such packages.
GROUP COHESION
1. We find few scientific studies that address the possible relationship
between group cohesion and performance; however, such a relationship
"may well be found with more extensive research. There is a need for
Fresearch to consider the possibility of negative effects from inducing
cohesion and methods of avoiding such effects. The committee recom-
Amends continued study of cohesion and related group processes.
2. We are favorably impressed with the evaluation studies of the
Army's COHORT system. We endorse the investigators' plan to proceed
beyond measures of attitudes to measures of group performance.
3. We recommend that the Army, as well as independent investigators,
study the possible impacts of cohesion beyond the COHORT system, for
"example, on intergroup performance.
PARAPSYCHOLOGY
1. The committee finds no scientific justification from research con-
"ducted over a period of 130 years for the existence of parapsychological
phenomena. It therefore concludes that there is no reason for direct
involvement by the Army at this time. We do recommend, however, that
presearch in certain areas be monitored, including work by the Soviets
and the best work in the United States. The latter includes that being
done at Princeton University by Robert Jahn; at Maimonides Medical
Center in Brooklyn by Charles Honorton, now in Princeton; at San
Antonio by Helmut Schmidt; and at the Stanford Research Institute by
Edward May. Monitoring could be enhanced by site visits and by expert
advice from both proponents and skeptics. The research areas included
would be psychokinesis with random event generators and Ganzfeld
effects.
2. One possible result of the monitoring mentioned above is the proposal
FINDINGS AND CONCLUSIONS
of specific studies. In that situation the committee recommends the
following procedures: first, the Army and outside scientists should arrive
at a common protocol; second, the research should be conducted
according to that protocol by both proponents and skeptics; and third,
attention should be given in such research to the manipulability and
practical application of any effects found to exist.
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3
Evaluation Issues
Implementation of an enhancement technique, in the committee's view,
should depend on two general kinds, or levels, of evaluation. The first
examines primarily the scientific justification for the effectiveness of the
technique and the potential of the technique for improving performance
in practice. The second kind examines field tests of a pilot program
incorporating the technique to determine how feasible it is and to what
extent it brings about effects that Army officials consider useful.
Convincing scientific justification can come only from basic research,
that is, from carefully controlled studies that usually take place in
laboratory settings and that preferably are related to a body of theory.
Such research can provide evidence for the existence of the causal effect
on which a technique is based and can help explain, or indicate a
mechanism for, the effect. Analysis in connection with basic research
should go beyond scientific justification to operational potential and likely
cost-effectiveness. Only field tests can assess a program's actual opera-
tions and effects, however, and for such tests a broader array of evaluative
criteria are needed, related primarily to the technique's utility.
Because strong claims of support from basic research have been made
for some of the techniques the committee examined, we review here
what it takes to justify a scientific claim, specifically, we review some
standards for evaluating basic research. We then examine in more detail
some standards for evaluating field tests of pilot programs. In the third
section of this chapter, we set forth briefly some of our impressions of
how the Army now manages the solicitation and evaluation of new
performance-enhancing techniques. This chapter concludes with a note
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EVALUATION ISSUES
on informal, qualitative approaches to evaluation, which are sometimes
suggested as alternatives to basic research and field tests.
This chapter does not aspire to a comprehensive treatment of evaluation
issues, and it barely touches on research methods. Articles, journals,
books, and handbooks testify to the scope and complexity of this
burgeoning field (e.g., Barber, 1976; Cook and Campbell, 1979). Our
objective here is to highlight the topics that have impressed us as most
germane. The various sources just mentioned would need to be consulted
for even a minimal elaboration of these topics, and other committees
would be required if recipes for evaluation of the Army's enhancement
programs were sought as extensions of our work. Still, we believe this
chapter will help the Army set general evaluation standards.
STANDARDS FOR EVALUATING BASIC RESEARCH
The purpose of basic research is to permit inferences to be drawn in
accordance with scientific standards, including inferences about novel
concepts, about causation, about alternative explanations of causal
relations, and about the generalizability of causal relations.
For novel concepts, evidence must be gathered that both the purported
enhancement technique and the relevant performance have been (1)
defined in a way to highlight their critical elements, (2) differentiated
from related variables that might bring about similar effects, and (3) put
into operation (manipulated or measured) in ways that include the critical
parts. The burden is on the evaluator to analyze how the components of
each new technique differ from concepts already in the literature. The
need for this standard is illustrated well by packages for accelerated
learning, as discussed in Chapter 4.
Evidence needs also to be adduced that supposed cause and effect
variables vary together in a systematic manner. Relevant procedures
include comparison of performance before and after introduction of the
technique, contrasts of experimental and control groups in an experimental
design, and calculation of statistical significance. Illusory covariation can
occur more easily in nonstatistical studies, which are used often to support
the existence of paranormal effects, as discussed in Chapter 9.
Especially demanding is the need for evidence that the performance
effect observed is due to the postulated cause and not to some other
variable. Ruling out alternative explanations or mechanisms requires
intimate knowledge of a research area. Historical findings and critical
commentary are needed to identify alternatives, determine their plausi-
bility, and judge how well they have been ruled out in particular sets of
experiments. Common threats to the validity of any presumed cause-
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effect relation include effects stemming from subject selection, unexpected
changes in organizational forces, the spontaneous maturation of subjects,
and the sensitizing effects of a pretest measurement on a posttest
assessment. Experiments with random assignment of subjects to treat-
ments are preferred, but some of the better quasi-experimental designs
are also useful. Another class of threats to validity is associated with
subject reactions to such conceptual irrelevancies as experimenter ex-
„pectations about how subjects should perform or subjects' performing
better merely because they are receiving attention. Procedures that have
evolved to reduce this sort of threat include double-blind experiments,
placebo control groups, mechanical delivery of treatments, and the
elimination of all communication between experimenters and subjects or
among subjects. These safeguards, however, are not certain, and imple-
penting them is not a simple matter.
Finally, for a technique to be of value, one must ascertain that a causal
selation observed in one setting is likely to be observed in other settings
in which the technique is to be employed. Replication of an experiment
By an independent investigator is a first step. Another step is to produce
che cause and effect with different samples of people, settings, and times.
Systematic reviews of the literature, perhaps aided by what is referred
Co as meta-analysis of studies (as illustrated in Chapter 5), are also helpful.
Beyond these steps, a thorough theoretical understanding of causal
processes, which is a fundamental goal of science, permits increased
practical control.
Our point-perhaps seeming obvious to many but nonetheless needing
Emphasis here-is that a planned or existing program for implementing
En enhancement technique is much more likely to bear fruit if evidence
for the technique's effectiveness is properly derived from basic research.
& complex set of ground rules exists for conducting and drawing inferences
Com basic research, and waiving those rules greatly increases the chances
incorrect conclusions.
STANDARDS FOR EVALUATING
FIELD TESTS OF PROGRAMS
An adequate appraisal of an actual enhancement program requires
affention to three general factors. First, the organizational (i.e., political,
administrative) context in which the program is embedded should be
described. That context strongly influences the choice of evaluation
criteria, the types of evaluations considered feasible, and the extent to
which evaluation results will be used. Second, the program's conse-
quences should be described and explained, including planned and
unplanned, short-term and long-term consequences. The way the program
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EVALUATION ISSUES
is construed influences the claims resulting from an evaluation and the
degree of confidence that can be placed in what was learned. Third, value
or merit should be explicitly assigned to a program. Valuing relates an
enhancement technique to an Army need and to feasible alternatives. In
the following sections we comment on these three factors in turn.
THE ORGANIZATIONAL CONTEXT
A description of the broader context of an enhancement program would
include an assessment both of the various constituencies with a stake in
its implementation and of the priorities of the larger institution. We do
not discuss stakeholder interests in general at this point because we refer
to some specifically later in this chapter, in the section on the committee's
impressions of current Army evaluation practices. We do comment here
on the Army's institutional priorities as they may relate to scientific
standards.
We understand that the Army, like other organizations in society, may
have-and quite possibly should have-different standards for evaluating
knowledge claims, or technique effectiveness, than science has. The
scientific establishment is conservative in the tests it administers to
discipline its conjectures; in particular, its goal is to reduce uncertainty
as far as possible, no matter how long that takes. In the Army, by
contrast, the need for timely information and decisions may lead to an
acceptance of greater uncertainty and a higher risk of being wrong.
There is no Army doctrine of which we are aware concerning the
degree of risk that is acceptable in evaluations of pilot programs. Yet
surely one objective of evaluations of pilot programs should be to describe
the costs to the Army of drawing incorrect conclusions so that inferential
standards can be made commensurate with those costs. If the costs are
relatively low, the riskier approach of most commercial research (as, for
example, in management consulting or marketing) may be preferred to
the more conservative approach of basic science.
DESCRIBING A PROGRAM'S CONSEQUENCES
In evaluating a program, it is desirable to present an analysis and
defense of the questions probed and not probed, together with justification
for the priorities accorded to various issues. Primary issues usually
include the program's immediate effects and its organizational side effects.
Immediate Effects
A primary problem in evaluation is to decide on the criteria by which
a program is to be assessed. The major sources for identifying potential
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criteria include program goals, interviews with interested persons, con-
sideration of plausible consequences found in the literature, and insights
gained from preliminary field work.
Such criteria specify only potential effects, however. They do not
speak to the matter of whether the relation between a supposed cause
and effect is truly causal. In this respect, a fundamental issue of
methodology is the use of randomized experiments. Although logistic
reasons abound in any practical context for not going to the trouble to
ose such research designs, one might nonetheless argue that the Army is
n a better position to conduct randomized experiments than are organi-
zations in such fields as education, job training, and public health. The
reason for going to such trouble is that randomized experiments give a
tower risk of incorrect causal conclusions than the alternatives.
Alternatives at the next level of confidence are quasi-experimental
designs that include pretest measures and comparison (control) groups.
Relatively little confidence can be placed either in before-after measure-
ments of a single group exposed to a technique without an external
pomparison, or in comparisons of nonequivalent intact groups for which
pretest measures are not available.
Side Effects
Unintended side effects include impacts on the broader organization,
and these should be monitored. For example, trainers from other (non-
Experimental) units may copy what they think is going on, or they may
Pimply be upset by the implementation of new instructional packages in
che experimental units. Units not treated in the same way as the
Experimental units may be unwilling to cooperate when cooperation
"would seem to be in their best interest. They may also suffer by
Acomparison, as is thought to be the case, for example, when COHORT
anits are introduced into a division (see Chapter 8). Evaluators should
Istrive to see any program as fitting into a wider system of Army activities
on which it may have unintended positive or negative effects.
ASSIGNING VALUE TO PILOT PROGRAMS
The described consequences of a program tell us what a program has
achieved but not how valuable it is. Three other factors are important in
inferring value: Does the new technique meet a demonstrable Army need
to the extent that without it the organization would be less effective?
How likely is it that the program can be transferred to other Army
settings, either as a total package or in part? How well does the new
EVALUATION ISSUES
program fare when compared with current practice and with alternatives
for bringing about the same results?
Meeting Needs
Representatives of the commercial world who seek outlets for their
products often confound wants with needs, enthusiasm with proof, and
hope with reality. While it is axiomatic that all field tests should aim to
meet genuine Army needs, it is not clear how needs are now assessed
when the developers of new products approach Army personnel for
permission to do general research or field tests. It is clear that a needs
analysis should be part of the documentation about every field test.
What should a needs analysis look like? At the minimum, it should
document the current level of performance at some task, why the level
is inadequate, what reason there is to believe that performance can
change, and what the Armywide impacts would probably be if the
performance in question were improved. In addition, an analysis should
question why a particular program is needed for solving the problem.
Such an analysis would describe the program, critically examine its
justification in basic research, identify the financial and human resources
required to make the program work, relate the resources required to the
funds available, examine other ways of bringing about the same intended
results, and justify the program at hand in terms of its anticipated cost-
effectiveness. To facilitate critical feedback, such reports should be
independent of the persons who sponsor a program, though based on a
thorough, firsthand acquaintance with the program and its developers
and sponsors.
As just described, needs analysis is a planning exercise to justify
mounting a pilot program. It is not a review of program achievements
relative to needs, for which a description of a program's consequences
is required. At that later stage in evaluation a judgment is required about
whether the magnitude of a program's effects is sufficient to reduce needs
to a degree that makes a practical difference. More is at stake than
whether the program makes a statistically reliable difference in perform-
ance. Size of effect relative to need is the crucial concern. When the
magnitude of change required for practical significance has been specified
in advance, it is easy to use such a specification to probe how well a
need has been met. But the level of change required to alleviate need is
not usually predetermined, and there are political reasons why developers
are not always eager to have their programs evaluated in terms of effect
sizes they themselves have clearly promised or that others have set for
them.
Needs can be specified only by Army officials, and it is vital that such
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officials inspect the results a program has achieved, relating them to their
perception of need. Since the Army is heterogeneous, it would be naive
to believe that there are no significant differences within it about how
important various needs are and how far a particular effect goes in
meeting a particular need. Some theorists relate needs primarily to the
number of persons performing below a desired level, while others
emphasize the seriousness of consequences for unit performance, for
which deficiencies in only one or two persons may be crucial. Some
practitioners are likely to think a deficit in skill X is worse than a deficit
in skill Y, while others may believe the opposite. Evaluators who take
the concept of need seriously have to take cognizance of such hetero-
geneity, perhaps using group approaches like the Delphi technique to
bring about consensus on both the level of need and the extent to which
a particular pattern of evaluative results helps meet that need.
Likelihood of Transfer
Although some local commanders may sponsor field trials for the benefit
of their command alone, the more widely a successful new practice can
be implemented within the Army, the more important it is likely to be.
Consequently, evaluations of pilot programs should seek to draw conclu-
sions about the likelihood that findings will transfer to populations and
settings different from those studied.
In this regard, it is particularly important to probe the extent to which
any findings from a pilot study might depend on the special knowledge
and enthusiasm of those persons who deliver or sponsor the program.
Such persons are often strongly committed to a program, treating it with
a concern and intensity that most regular Army personnel could not be
expected to match. While it is sometimes possible to transfer such
committed persons from one Army site to another in order to implement
@a program, in many instances this cannot be done. Transfer is partly a
question of the psychology of ownership; authorities who did not sponsor
a product will sometimes reject out of hand what others have developed,
including their immediate predecessors. Since Army leaders in any
position turn over with some regularity due to transfers, promotions, and
retirement, successors will probably not identify with a program as
strongly as the original sponsors and developers did.
The likelihood of transfer also affects the degree to which program
implementation is monitored. Pilot programs are likely to be more
obtrusively monitored than other programs. Not only is this obtrusiveness
due to developers' and evaluators' fussing over their charge, it is also
due to teams of experts brought in to inspect what is novel and to
responsible officers wanting to show others the unique programs they
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EVALUATION ISSUES
are leading (and on which the success of their careers may depend). For
at least these reasons pilot programs tend to stand out more than the
regular programs they may engender. Research suggests that the quality
with which programs are delivered may in fact increase when outside
personnel are obviously monitoring individual and group performance.
It is naive to believe that one can go confidently from a single pilot
program to full-blown Armywide implementation. Even if this were
feasible politically, it would not be technically advisable unless there
were compelling evidence from a great deal of prior research indicating
that the program was indeed built on valid substantive foundations. Given
a single pilot program, decisions about transfer are best made if the
program is tested again, at a larger but still restricted set of sites and
under conditions that more closely approximate those that would pertain
if the new enhancement technique were implemented as routine policy.
Only then might serious plans for Armywide implementation be feasible.
Contrast with Alternatives
Most of the evaluation we have discussed contrasts a novel program
with standard practices that are believed worth improving; yet rational
models of decision making are usually predicated on managers' having
to choose among several different options for performing a particular
task. One would hope that every sponsor of a novel performance
enhancement technique is conversant with the practical alternatives to it
and has cogent arguments for rejecting them.
Many novel techniques have some components that are already in
standard practice or can be clearly derived from established theories.
Upon close inspection, pilot programs often turn out to be less novel
than their developers and sponsors claim. Of course, the Army may often
find it convenient to order complete packages in the form offered and
may not have much latitude to interact with developers in order to modify
package contents to emphasize what is truly a novel alternative and to
downplay that which is merely standard practice.
Ultimately, alternatives have to do with costs. Although many forms
of cost are at issue-including those associated with how much a new
practice disrupts normal Army activities and how much stress it puts on
personnel-the major cost usually considered is financial. Cost analysis
is always difficult, nowhere more so than in the Army, which uses many
ways to calculate personnel costs. Nonetheless, in planning an evaluation,
some evidence about the total cost of a pilot program to the Army will
usually be available and can be critically scrutinized. It is also useful, as
far as possible, to ascribe accurate Army costs to each of the major
components of such an intervention. In our view, what is called cost-
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effectiveness analysis lends itself better than what is called cost-benefit
analysis to the comparison of different programs. The purpose of cost-
effectiveness research is to express the total cost for each program in
dollar terms and to relate this to the amount of effect as expressed in its
original metrics-unlike cost-benefit research, in which even the effects
have to be expressed in dollar terms. Sophisticated consumers of eval-
uation should want something akin to cost-effectiveness knowledge, for
it reflects decisions they should be making. Is it not useful to know, for
example, that the best available computer-assisted instruction packages
are much less cost-effective than peer tutoring?
CURRENT STATUS OF ARMY EVALUATIONS
We set forth here some of our impressions of the way in which the
Army currently manages the solicitation and evaluation of novel tech-
niques to enhance performance. We must stress that these are only
impressions, gained through the limited investigative capabilities of a
committee such as ours, not hard conclusions based on systematic
research directed at the particular question. Furthermore, although the
opinions that follow are largely critical of Army procedures, they are not
accompanied by much detail. As noted earlier, the focus here is on the
identification of the various Army constituencies that have a stake in
enhancement programs and on the role they play in evaluation.
How the Army decides which among competing proposals should be
sponsored for development or for field tests is not clear. What is clear is
that decision making is diffuse both geographically and institutionally.
Sponsorship may come from senior managers in the Pentagon or from
local personnel of varying rank. While differences in the quality of
program design, implementation, or evaluation may be correlated with
the source of sponsorship, such a correlation is not clear at present in
the Army context.
A particular concern is that Army sponsors of pilot programs may base
their judgment about the value of a program either on their own ideas
about what is desirable or effective or on the persuasiveness of the
arguments presented to them by program developers, who stand to gain
financially if the Army adopts their program. Judgments of value should
depend on broader analysis of Army needs and resources, as well as on
realistic assessment of the quality of proposed ideas based on a thorough
and independent knowledge of the relevant research literatures. Sponsors
should examine what is being advocated at every stage: proposal, testing,
and implementation.
Also of concern when pilot programs are planned is how decisions are
reached about funding and about the quality of implementation expected
EVALUATION ISSUES
from them. Although systematic evidence is lacking, it seemed to
committee members that pilot programs are not generally implemented
well and, except for fiscal accountability, are not closely monitored by
their Army sponsors. Evaluations of pilot programs should try to char-
acterize resources required by the program and the resources actually
available.
We found little evidence that sponsors, advocates, or local implementers
had aspirations to evaluations that use state-of-the-art methods. We found
no guidelines about the standards expected for evaluative work, whether
in the form of published minimal standards or published statements of
preferred practices. When it comes to field trials of novel ideas for
enhancing human performance, the monitoring of evaluation quality does
not seem to be part of the organizational context. Given the absence of
formal expectations in these regards, it is not surprising that the pilot
programs we saw and the evaluation materials we read were usually
disappointing in the technical quality of the research conducted. In
settings in which program sponsors or advocates control an evaluation,
weaker evaluations (e.g., based on testimony) will sometimes be preferred
to stronger methods (e.g., experiments) because the latter are usually
more disruptive when implemented and are more likely to result in effects
that are disappointing, however much more accurate they may be. The
weaker methods are easier to implement when few units are available,
are less disruptive of ongoing activities, are easier to manipulate for self-
interested ends, and need not be as expensive for data collection.
We saw little evidence that the Army requires evaluations by persons
independent of the pilot program under review. Moreover, the noninde-
pendent evaluations we saw did not seem to have been subjected to any
of the peer review procedures to which research results (and plans) are
subjected not only in academic sciences, but also in much of the corporate
world, as with, say, pharmaceutical testing. While in-house evaluation is
highly valuable for gaining feedback for program improvement, many
experienced evaluators contend that it is inadequate for assigning overall
value because in-house evaluators cannot divorce themselves from their
own stake in the program under examination. Although it is not easy to
specify organizational standards adequate for a high-quality field test of
some novel technique, it is also not difficult to detect the inadequacies
associated with local program sponsors' having few clear expectations
about the desirable qualities of program operations or evaluative practices.
In the absence of such expectations, program developers and evaluators
may believe that few officials care about the small-scale field tests of
techniques on which the developers'-and, all too often, the evaluators' --
own welfare depends.
Since the organizational climate we have just described is not optimal
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for gaining trustworthy information about program value, future evaluators
of Army field trials might do well to characterize: (1) what program
managers expect in terms of the quality of the program and its evaluation;
(2) who is paying attention to the trials; and (3) for what purposes they
want to use any information provided by the evaluation. This kind of
information, as mentioned above, contributes to a description of the
organizational context of a program, which is a major part of an adequate
evaluation.
QUALITATIVE APPROACHES
Alternatives to experimentation are the largely qualitative traditions,
which rely mostly on direct observation, sometimes supplemented by
archival data. Investigative journalists operate in this mode; so do many
cultural anthropologists, political scientists, and historians. These profes-
sions use clues to suggest hypotheses about possible causes and investigate
the empirical evidence in ever-greater detail in an attempt to rule out
hypotheses until they are left with just one. A critical aspect of their
work is the use of substantive theories and ad hoc findings from the past
to help in ruling out alternative explanations. Also working in this tradition
are committees of psychologists who seek to make statements about the
causes of enhanced human performance. Rarely conducting studies
themselves, they instead sift through historical evidence provided by
reviews of the literature and make on-site observations in the manner of
detectives, pathologists, investigative journalists, and cultural anthropol-
ogists.
These traditions rely strongly on personal testimony. Respondents'
reports are taken seriously and, indeed, should be. Any method can, in
principle, generate strong causal evidence, provided that plausible alter-
natives to a preferred hypothesis have been ruled out. The general issues
are: Can personal testimony usually rule out all the plausible alternative
interpretations? Does use of it engender the very threats to validity that
militate against strong inferences? Dale Griffin, in a paper prepared for
the committee (see Appendix B), suggests "no" to the first question and
"yes" to the second. His analysis of biases that operate when people
attempt to explain how and why they changed after an experience reveals
many of the shortcomings associated with relying on testimony as a major
means of testing causal hypotheses.
While testimony can be regarded as a form of confirmatory evidence,
it does not provide any of the disconfirming evidence needed to reduce
uncertainty. Rarely are there the kinds of comprehensive probes needed
to discover why respondents believe that the effects are due to a treatment
rather than to maturation, statistical regression, or the pleasant feelings
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EVALUATION ISSUES
aroused by the experiences. People are typically weak at identifying the
range of such alternatives, however simply they may be described, and
at distinguishing the different ways in which the causal forces might
operate. How can people know how they would have matured over time
in the absence of an intervention (technique) that is being assessed? How
can people disentangle effects due to a pleasant experience, a dynamic
leader, or a sense of doing something important from effects due to the
critical components of the treatment per se? Much research has shown
that individuals are poor intuitive scientists and that they recreate a set
of known cognitive biases (Nisbett and Ross, 1980; Griffin). These include
belief perseverance, selective memory, errors of attribution, and over-
confidence. These biases influence experts and nonexperts alike, usually
without one's awareness of them. Scientists hold these biases in partial
check by using random assignment instead of testimony and by the
tradition of public scrutiny to identify and analyze alternative interpre-
tations for observed events. Such methodological traditions can be
transmitted to consumers and producers of enhancement techniques
through courses on statistical inference and formal decision making.
These courses would have the salutary effect of calling attention to the
shortcomings of testimony as evidence.
We submit that experimental methods facilitate causal inferences better
than the alternatives. They reduce more uncertainty by ruling out more
of the contending interpretations for observed effects. However, we refer
here to the relative superiority of experimentation; such superiority
should not be confused with either the perfection or even the adequacy
of experimentation. Its problems include the facts that experiments
cannot be implemented under all conditions and that experimentation has
its own set of unintended side effects. Thus, experimental methods do
not guarantee causal inferences and so cannot obviate the need for critical
analysis that, on a case-by-case basis, is sensitive to the contexts and
traditions of particular institutions or communities, such as the Army,
on one hand, and the various promoters of new enhancement techniques,
on the other. Moreover, well-conceived research is costly: it requires
specially trained investigators, equipped facilities, and programs that may
need extensive collaborations and review panels. It is also a demanding
craft that requires sensitivity to detail and precision in order to ensure
results that are interpretable.
On balance, the benefits derived from careful experimentation outweigh
the costs just mentioned. All other things being equal, experimentation
is much the preferred strategy for judging the efficacy of techniques that
purport to enhance performance, and it should be used whenever possible.
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PART
III
Parapsychological Techniques
0
F ALL THE SUBJECTS TREATED in this volume, none is more contro-
versial than parapsychology. While the flavor of the debates is
captured to some extent in this chapter, the subject is treated in the same
manner as the other techniques reviewed: we address the question of
whether the evidence warrants further consideration of parapsychological
techniques for research or application or both.
Emphasized here is information gathering by remote viewing and mind-
over-matter effects in controlling machine behavior, particularly machines
that generate series of random numbers, which are often used in para-
psychology experiments. Although scattered results are said to be statis-
tically significant, an evaluation of a large body of the best available
evidence does not support the contention that these phenomena exist.
If, however, future experiments, conducted according to the best possible
methodological standards, are more generally viewed as producing sig-
nificant results, it would be appropriate to consider a systematic program
of research. Such a program should include a concern for the need to
proceed from small effects to practical applications.
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9
Paranormal Phenomena
BACKGROUND
The primary purpose of this chapter is to evaluate the scientific evidence
on parapsychological techniques in selected areas. A more complete
understanding of the topic, however, requires that we provide background
on the military's interest in these phenomena and treat the conceptual
issue of how people come to believe as they do. This background section
includes a discussion of the phenomena and the military's interest in
them as well as an overview of the committee's focus. A brief examination
of the different kinds of justifications for the claims is followed by a more
detailed treatment of the evidence in areas that have produced large
literatures: remote viewing, random number generators, and what are
called Ganzfeld (whole visual field) experiments. In addition, we describe
experimental work that the committee actually witnessed by visiting a
parapsychological laboratory. Despite the growing scientific tradition in
some of these areas, many people continue to rely on qualitative or
experiential evidence to support their beliefs; we discuss the problems
associated with qualitative evidence in conjunction with the research on
cognitive and emotional biases, which is reviewed in the paper by Dale
Griffin (Appendix B). Finally, the chapter summarizes the committee's
major conclusions.
THE NATURE OF THE PHENOMENA
Parapsychologists divide psi-the term applied to all psychic phenom-
ena-into two broad categories: extrasensory perception (ESP) and
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psychokinesis (PK). Included in ESP are telepathy, precognition, and
clairvoyance, all of which refer to methods of gathering information about
objects or thoughts without the intervention of known sensory mecha-
nisms. Popularly called mind over matter, PK refers to the influence of
thoughts upon objects without the intervention of known physical proc-
esses.
A presentation to the committee by several military officers described
in some detail the results of experiments in remote viewing carried out
ort both SRI International and the Engineering Anomalies Research
Laboratory at Princeton University. In these experiments subjects are
said to have more or less accurately described a geographical location
being visited by a target team. Although the human subjects have no way
Bof normally knowing the target location, the examples recounted appear
Ro indicate, at first glance, some striking correspondences between their
descriptions and the actual sites. These studies have been related by
some persons to reported out-of-body experiences.
The presentation included discussion of psychic mind-altering tech-
miques, the levitation claims of transcendental meditation groups, psy-
Chotronic weapons, psychic metal bending, dowsing, thought photogra-
"phy, and bioenergy transfer. It was indicated that the Soviet Union is far
Sahead of the United States in developing potential applications of such
paranormal phenomena, in particular psychically controlling and influ-
Lencing minds at a distance. At the presentation, personal accounts were
agiven of spoon-bending parties, in which participants believe they have
Caused cutlery to bend with the power of their minds, as well as instances
of self-hypnosis to control pain and cure illness, walking barefoot on fire
and handling hot coals without being burned, leaving one's body at will,
Sind bursting clouds by psychic means.
The media and popular publications, especially in recent years, have
discussed various aspects of psychic warfare. Three recent books, by
"Ebon (1983), McRae (1984), and Targ and Harary (1984), have attempted
Ro document Soviet and American efforts to develop military and intel-
digence applications of alleged paranormal phenomena. These accounts
have been augmented by newspaper stories, magazine articles, and
Relevision programs. Many of these sources acknowledge the speculative
mature of the proposed applications, but others report that some of the
Techniques already exist and work.
The claimed phenomena and applications range from the incredible to
the outrageously incredible. The "antimissile time warp," for example,
is supposed to somehow deflect attack by nuclear warheads so that they
will transcend time and explode among the ancient dinosaurs, thereby
leaving us unharmed but destroying many dinosaurs (and, presumably,
some of our evolutionary ancestors). Other psychotronic weapons, such
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as the "hyperspatial nuclear howitzer," are claimed to have equally
bizarre capabilities. Many of the sources cite the claim that Soviet
psychotronic weapons were responsible for the 1976 outbreak of Legion-
naires' disease, as well as the 1963 sinking of the nuclear submarine
Thresher.
POTENTIAL MILITARY APPLICATIONS
Some people, including some military decision makers, can imagine
potential military applications of the two broad categories of psychic
phenomena. In their view, ESP, if real and controllable, could be used
for intelligence gathering and, because it includes "precognition," ESP
could also be used to anticipate the actions of an enemy. It is believed
that PK, if realizable, might be used to jam enemy computers, prematurely
trigger nuclear weapons, and incapacitate weapons and vehicles. More
specific applications envisioned involve behavior modification; inducing
sickness, disorientation, or even death in a distant enemy; communicating
with submarines; planting thoughts in individuals without their knowledge;
hypnotizing individuals at a distance; psychotronic weapons of various
kinds; psychic shields to protect sensitive information or military instal-
lations; and the like. One suggested application is a conception of the
"First Earth Battalion," made up of "warrior monks," who will have
mastered almost all the techniques under consideration by the committee,
including the use of ESP, leaving their bodies at will, levitating, psychic
healing, and walking through walls.
THE COMMITTEE'S FOCUS
Although such colorful examples provide the context for our agenda,
the cumulative body of data in the discipline of parapsychology enables
us to judge the degree to which paranormal claims should be taken
seriously. Since 1882 reports of both naturally occurring incidents and
phenomena in laboratory settings have been accumulated in journals,
monographs, and books. Just to survey the reports in the refereed journals
of parapsychology would be an enormous undertaking. As scientists, our
inclination is, of course, to restrict ourselves to the evidence that purports
to be scientific. But the alleged phenomena that have apparently gained
most attention and that have apparently convinced many proponents do
not come from the parapsychological laboratory. Nothing approaching a
scientific literature supports the claims for psychotronic weaponry,
psychic metal bending, out-of-body experiences, and other potential
applications supported by many proponents.
The phenomena are real and important in the minds of proponents, so
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we attempt to evaluate them fairly. Although we cannot rely solely on a
scientific data base to evaluate the claims, their credibility ultimately
must stand or fall on the basis of data from scientific research that is
subject to adequate control and is potentially replicable.
We divided the task into two parts. First, we looked at the best scientific
arguments for the reality of psychic phenomena. Our sponsors, as well
as our own appraisal of the current status of parapsychology, indicated
that the two most influential scientific programs were the experiments on
ISmote viewing and the experiments on psychokinesis using random
event generators. In addition, we looked at the research on the Ganzfeld
(8hole visual field) because this, in the opinion of many parapsychologists,
isthe most likely candidate for a replicable experiment. We also report
Da parapsychological experiment that the committee itself witnessed.
Second, we considered the arguments of proponents who rely on what
Rey call qualitative as opposed to quantitative evidence for the paranor-
gal. Such evidence depends on personal experience or the testimony of
@chers who have had such experience. Most, if not all, of this evidence
Ginnot be evaluated by scientific standards, yet it has created compelling
beliefs among many who have encountered it. Witnessing or having an
homalous experience can be more powerful than large accumulations of
gantitative, scientific data as a method of creating and reinforcing beliefs.
Because personal experience rather than scientific data has been the
source of most beliefs in the paranormal, we have devoted some of our
sources to considering this sort of cognitive method as a tool for
schieving knowledge.
STANDARDS OF EVIDENCE
"Diverse justifications have been offered for pursuing paranormal claims.
me argument asserts that paranormal phenomena may no longer be
agomalous, given the implications of contemporary quantum mechanics.
Indeed, a few physicists have supported some parapsychologists in
maintaining that certain forms of precognition and psychokinesis are
consistent with some interpretations of quantum theory. The other major
argument is that we have no choice but to get involved because the
Soviet Union already has a program to develop military applications of
psychic phenomena.
Several proponents, including some scientists, firmly believe that
paranormal phenomena have been scientifically demonstrated several
times over. At the same time, most scientists do not believe that psi
exists. Many persons on both sides believe this paradox to be the result
of irrational and dogmatic belief systems. The proponents accuse the
critics of being closed-minded and bigoted. The critics imply that the
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proponents have allowed wishful thinking to bias their judgment and that
they are incompetent scientists and are self-deceived. Both sides can
point to examples to back their positions.
One essential question confronts the committee: What does an impartial
examination of the scientific evidence reveal about the existence of psi?
Such an examination assumes that clear standards exist for judging the
adequacy of the evidence, which, in turn, raises the issue of what
constitutes sufficient evidence. That issue involves many difficult philo-
sophical, theoretical, and methodological matters. For example, Palmer,
in his "An Evaluative Report on the Current Status of Parapsychology"
(1985), denies that current parapsychological experiments can provide
any evidence for the existence of psi. This is because psi implies
paranormality and, according to Palmer, we cannot argue that a given
effect has a paranormal cause until we have an adequate theory of
paranormality. He further argues, however, that parapsychological ex-
periments can and do provide evidence for the existence of anomalies.
By an anomaly, Palmer means a statistically significant deviation from
chance expectation that cannot readily be explained by existing scientific
theories. The burden of Palmer's paper is that just such anomalies have
been demonstrated.
Because parapsychologists other than Palmer do not make this distinc-
tion between demonstrating an anomaly and testing a theory of paranor-
mality, we do not carry on this distinction in our own assessment of the
evidence. We tend to agree with Palmer on this matter, however. When
we talk about evidence for psi in the remainder of this chapter, we are
using psi in the neutral sense of an apparent anomaly rather than in the
stronger sense of a paranormal phenomenon.
MINIMAL CRITERIA
Fortunately, critics and parapsychologists appear to agree on the
general requirements necessary to demonstrate psi in a parapsychological
experiment. Both Palmer (1985) and James E. Alcock (Appendix B)
discuss such criteria in their respective papers. As Palmer points out, psi
is defined negatively as a statistical departure from a chance baseline
that cannot be accounted for by chance, sensory cues, or known artifacts.
Such a negative definition implies the minimal criteria required to justify
a conclusion that psi has been demonstrated.
Given the statistical aspect, it is imperative that the data be collected
in such a way that the underlying probability model and assumptions of
the statistical test are fulfilled. This means that targets must be adequately
randomized and that each trial in the experiment must be independent of
the preceding ones-and, of course, the statistical procedures must be
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applied and interpreted correctly. Given that all ordinary explanations
must be ruled out, the experimenter must take special precautions to
ensure that sensory cues, recording errors, subject fraud, and other
alternatives have been prevented. Although it is impossible to rule out
completely every possible contaminant or to anticipate every alternative,
there are reasonable standards that most parapsychologists would agree
should be followed.
"Because different research paradigms have their own special require-
nEnts, no single set of standards can be specified in advance for all
parapsychological experiments. Experiments with electronic number
generators, for example, rarely have problems with data recording, but
thy do require special methods such as tests of randomness and attention
t&the immediate physical environment that are unnecessary with more
toditional parapsychological experiments. One requirement for assessing
the adequacy of a given experiment is that its procedures and methods
ofanalysis be adequately documented. Unless we know how the targets
were selected, how the results were analyzed, how the possibility of
0079TR00025
sgasory leakage was prevented, and how other such aspects of the study
være carried out, we have no basis for evaluating the quality of the
information provided by the experiment.
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GLOBAL CRITERIA
"The criteria mentioned in the preceding paragraphs apply to the
Blividual experiment. More global criteria come into play when one
Ints to evaluate an entire research program or set of experiments. Here
look for such things as replicability, robustness, lawfulness, manip-
umbility, and coherent theory. These criteria deal with the coherence
and intelligibility of the alleged phenomena. It is in terms of such global
cyteria that parapsychological research has been especially vulnerable.
"Much of the objectivity involved in assessing the adequacy of research
applies to judging individual experiments. But science is cumulative and
depends not so much on the outcome of a single experiment as on
consistent and lawful patterns of results across many experiments carried
ogt in a variety of independent settings. Lawful consistency in this sense,
a@ording to both parapsychologists and their critics, has never been
found in parapsychological investigations in the history of psychic
research. Recently a few parapsychologists have expressed the hope that
the experiments on remote viewing, random number generators, and the
Ganzfeld (the very ones we have chosen to examine in detail in this
report) may actually yield the long-sought replicability. The type of
replicability that has been claimed so far is the possibility of obtaining
significant departures from the chance baseline in only a proportion of
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the experiments, which is a kind of replicability quite different from the
consistent and lawful patterns of covariation found in other areas of
inquiry.
Despite the fact that scientific progress in a given area depends on the
accumulation of lawful and consistent patterns across many experiments,
the methods for deciding that such consistency exists are still quite
primitive in comparison with the standards for judging the adequacy of
a single experiment. Indeed, it is only within the past few years that
serious attention has been devoted to developing objective and standard-
ized procedures for evaluating the consistencies across a body of inde-
pendent studies. For the most part, judgment about what a body of
investigations demonstrates is still a surprisingly intuitive and haphazard
process. This probably has not been a serious drawback in those areas
of inquiry in which the basic phenomena are robust and experiments can
be conducted with high confidence that the predicted relations will be
obtained; but such impressionistic means for aggregating the outcomes
of several experiments in the domain of parapsychology open the door
to all the motivational and cognitive biases discussed in the paper prepared
for the committee by Griffin. Not only are the data and alleged correlations
erratic and elusive in this field, but their very existence is open to
question.
EVALUATION OF THE SCIENTIFIC EVIDENCE
To evaluate the best scientific evidence on the existence of psi, and
with the advice of proponents and our sponsors, we conducted site visits
to some of the most notable parapsychological laboratories. The para-
psychology subcommittee (see Appendix C) visited Robert Jahn's Engi-
neering Anomalies Research Laboratory at Princeton University, where
it witnessed presentations and demonstrations regarding psychokinetic
experiments on random number generators. Jahn and his associates also
briefed the subcommittee on the current status of their work in remote
viewing.
The subcommittee also visited Helmut Schmidt's laboratory at the
Mind Science Foundation, San Antonio, Texas. Schmidt pioneered the
use of random number generators in parapsychology experiments in 1969.
His is considered one of the two major research programs on psychokinesis
(the second is Jahn's).
As an additional posssible input, the committee agreed to participate
in a psychokinetic experiment of new design with Helmut Schmidt.
Specifically, Schmidt accepted the suggestion that the committee's con-
sultant, Paul Horwitz, be included in the conduct of the experiment. The
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work has not yet begun, however, and it now appears that we will not
have any results to report before our terms expire.
The chair of the parapsychology subcommittee also visited SRI Inter-
national, another major laboratory studying psychic effects on random
number generators. (This latter research group argues that the observed
effects are not due to psychokinesis but rather represent a special form
of precognition.) The subcommittee chair also attended the meetings of
the Parapsychological Association held at Sonoma State College in
California. The entire committee made a site visit to Cleve Backster's
Aboratory in San Diego (arranged to coincide with the committee's
Beeting in La Jolla, California).
6-00791F00020
These site visits enabled the committee to observe firsthand the
Experimental arrangements and equipment used by some of the major
contributors to parapsychological research. They also provided us an
Opportunity to discuss results, interpretations, and problems with a few
Unportant investigators. We were impressed with the sincerity and
Redication of these investigators and believe that they are trying to
conduct their research in the best scientific tradition. We also got the
Enpression that this type of research involves many unresolved problems
And still has a long way to go before it develops standardized, easily
Teplicable procedures. The information obtained from these site visits
does not provide an adequate basis for making scientific judgments. For
this we rely, as we would in other fields of science, on a careful survey
f the literature.
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RESEARCH ON REMOTE VIEWING
The SRI Remote Viewing Program
Since the early 1970s, probably the best known research program
n parapsychology has been the experiments in remote viewing initiated
by physicists Harold Puthoff and Russell Targ when they were at
SRI International. In a typical remote viewing experiment a subject,
or percipient, remains in a room or laboratory with an experimenter,
While a target team visits a randomly selected geographical site
@.g., a shopping mall, an outdoor arena, the Palo Alto airport, the
Hoover tower). Neither the experimenter nor the subject has been
given any information about the target. Once the experimenter and
the subject are closeted in the laboratory, they wait for 30 minutes
before the subject begins to describe his or her impressions of the
target site.
Meanwhile the target team, consisting of two to four members of
the SRI staff, obtains instructions for going to a randomly chosen
target site from another SRI staff member. They then drive to the
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designated target site and remain there for an agreed-on 15-minute
period (after allowing approximately 30 minutes to reach the site).
During the time that the target team remains at the target site, the
subject describes his or her impressions into a tape recorder and also
makes any drawings that would help to clarify those impressions.
When the target team returns to the laboratory, all the participants
listen to the tape recording of the subject's impressions. Then all
the participants go to the target site, where the subject is allowed
to see how closely his or her impressions agreed with the actual
target.
The first subject to participate in such a formal series of trials was
the late Pat Price. In the first series, consisting of nine sessions, the
duration of each session was 30 minutes. The transcript for each
session is rich in detail; the one published transcript in Targ and
Puthoff's first book runs to almost six printed pages (Targ and
Puthoff, 1977).
Given such data, how does one decide if the experiment was a
success? Did Price's descriptions, for example, convey correct knowl-
edge of the different target sites? In fact, two methods have been
used to demonstrate the effectiveness of remote viewing. One method
is simply to compare the description with the target and make a
judgment as to whether the correspondence is sufficient to claim a
"hit." The second method uses an independent judge to rank the
degree to which each description matches each site and then applies
statistical tests to decide if the association is greater than chance.
Unprecedented success was claimed for the early remote viewing
experiments in terms of both methods (Targ and Puthoff, 1974, 1977;
Puthoff and Targ, 1976). Many examples were supplied of dramatic
correspondences between impressions of the percipient and the physical
details of the actual target. Such correspondences, no matter how
dramatic and compelling, do not carry scientific weight, because it
is impossible to assess their probabilities. In addition, much psycholog-
ical research indicates how such subjective validation can create
strong, but false, illusions of matching (see below).
The more formal evidence from the rankings of independent judges
was also impressive. The first formal series of nine trials resulted in
seven of the transcripts being ranked 1 against their intended target
sites by the independent judge. Only one such ranking would be
expected by chance. Puthoff and Targ reported the probability of
such an outcome being due to chance as only 0.0000029. The second
formal series, using Hella Hammid, was equally impressive, producing
five first places and four second places in the rankings of transcripts
against target sites.
Although subsequent series by Targ and Puthoff, as well as by
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other investigators, have not always yielded such overwhelmingly
impressive results, most of them have continued to display highly
significant outcomes (Targ and Harary, 1984). On the surface, at
least, this is a reliable, simple, and highly effective recipe for
producing paranormal communication. Especially appealing is the
claim that remote viewing works with just about everyone. Targ and
Harary, for example, provide exercises for anyone who wants to
Bvelop and improve his or her ability to pick up information at remote
Res. Neither space nor time, its proponents assert, is a barrier. The
Brcipient can pick up information from the surface of Jupiter as well
from target sites that can be visited at some future time.
Scientific Assessment of Remote Viewing
After the first remote viewing experiments were conducted in the
Carly 1970s, many investigators throughout the world tried to follow
suit. Most of them believed that their findings supported the claims
the SRI International researchers. The majority of these experi-
Ments, however, consisted of informal demonstrations rather than
formal scientific experiments and relied solely on subjective matching.
mh the past 15 years, the number of formal experimental replications
of the SRI remote viewing experiments has been surprisingly few.
Targ and Harary (1984) include as an appendix in their book a
port by Hansen, Schlitz, and Tart that evaluates all the known
mote viewing experiments conducted from 1973 through 1982. "In
an examination of the twenty-eight formal published reports of
#tempted replications of remote viewing," write Targ and Harary,
@Hansen, Schlitz, and Tart at the Institute for Parapsychology
Found that more than half of the papers reported successful out-
comes." They concluded: "We have found that more than half
fifteen out of twenty-eight) of the published formal experiments
bave been successful, where only one in twenty would be expected
By chance."
2 Two comments may be in order with respect to the foregoing
Conclusion. First, given the enormous publicity and the unusually
Strong claims, 28 formal experiments in 10 years seems surprisingly
few. In comparison, the Ganzfeld psi experiments produced approxi-
mately twice as many formal experiments during the same interval.
Second, 13 of the 28 formal experiments, or 46 percent, failed to
claim successful outcomes. This rate of failure is much higher than
what might have been expected on the basis of the earlier claims by
Targ and Puthoff (1977), namely, that they had succeeded with every
subject they had tried.
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Even 15 successful outcomes out of 28 tries is impressive, especially
by parapsychological standards. An inspection of the listed studies,
however, suggests that the 28 formal experiments vary considerably
in their importance. Some of these "published formal experiments"
appeared as brief reports or abstracts of papers delivered at meetings
of the Parapsychological Association or similar organizations. Others
appeared in print only as brief or informal reports in book chapters
or letters to the editor. Altogether, 15 of the 28 were published
under conditions that fall short of scientific acceptability. Only 13,
or 46 percent, of the experiments were published under refereed
auspices. As in other sciences, only published reports that have
undergone peer review and are adequately documented can be con-
sidered seriously as part of the scientific data base.
Of the 13 scientifically reported experiments, 9 are classified as
successful in their outcomes by Hansen et al. (Targ and Harary,
1984). Seven of these nine experiments were conducted by Targ and
Puthoff at SRI International, the remaining two at other labora-
tories. This relatively small harvest of nine "successful" experiments
suffers from the fact that each is seriously flawed. A variety of
problems afflicts the published reports on remote viewing. The
documentation, even according to many parapsychologists, is seriously
inadequate. Attempts by both neutral and skeptical investigators to
gain access to the raw data have typically been thwarted or strongly
resisted. Because the essence of scientific justification is public
accessibility to the data, this relative inaccessibility suggests that
much of the remote viewing data base is not part of science.
Most of the reasons for questioning the acceptability of the evi-
dence for remote viewing lie in a methodological flaw that char-
acterizes all but one of the experiments deemed successful: the
successive trials are not independent of one another. This lack
of independence has unfortunate consequences for any attempt to
draw conclusions about ESP based on the outcomes of such experiments.
The concept of independence is technical and somewhat difficult to
explain simply, but, since it is critical to understanding why the remote
viewing experiments fail to make their case, we supply an intuitive
explanation.
Assume that we are considering a remote viewing experiment in
which the subject participates in only two trials. In other words, we
deal with two randomly chosen target sites. For the first trial, the
target team goes to the first target site and remains there while the
subject produces his or her first description. Immediately after this
trial, the target team returns to the laboratory and takes the subject
to the actual target site so that he or she and the others can gain a
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subjective impression of how closely the description corresponds with
the target. For the second trial, the target team visits a second
randomly chosen site. While they are visiting this site, the subject
produces a second description.
When the experiment is over, the list of target sites (in random
order) and the transcripts of the subject's descriptions are given to
a judge, who also visits each site. While at a given site, the judge
reads the two transcripts and ranks them in terms of how well each
one corresponds with the particular site. In our example, one of the
Ntranscripts will be ranked 1 and the other will be ranked 2 (with 1
Bindicating the better correspondence between that target and the
transcript). After visiting one site and doing this ranking, the judge
then visits the second site and repeats the ranking procedure. The
raw data can be set out in a matrix with the target sites as the
columns and the transcripts as the rows.
A perfect outcome would be indicated if the transcript produced
bat the time the team was visiting site A was ranked 1 against that
site, and the transcript produced when the team was visiting site B
was ranked 1 for that site. (Of course, two trials would be too few
to make an adequate statistical assessment of the success of the
matching-successful matching would occur too frequently just by
.chance. The principles we want to illustrate, however, remain the
same for two as for many trials.)
If the successive trials in the experiment were independent of one
another, and we were interested only in direct hits (that is, outcomes
for which the intended transcript was rated 1 against the target
site), then we could expect the subject to make between zero and
two direct hits. Indeed, if chance alone were operating, there would
be four, equally likely, possibilities: (1) no hits, (2) a hit on the first
trial and a miss on the second, (3) a miss on the first trial and a hit
on the second, and (4) two hits. By this reckoning, the subject could
be expected to get two direct hits just by chance in one of every four
experiments.
But, as we indicated, the successive trials are not independent.
This is because the judge is almost certainly not going to rank a
-transcript as 1 for more than one target site. This means, in our
example, that if he or she ranks the first transcript 1 for target A,
then he or she will probably rank the second transcript 1 for target
B. In effect, this lack of independence between trials means that,
instead of four equally likely possible outcomes there are only two:
no hits or two hits. The dependence between trials has created a
situation in which the chance probability of two hits is now 50 percent
rather than 25 percent.
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In this situation, if an experimenter uses a statistical test that
assumes independence, he or she will come out with the wrong
probabilities. In fact, the statistical test will exaggerate the signif-
icance of many outcomes. The failure of the experimenters to realize
this problem resulted in exaggerated levels of significance for the
early remote viewing experiments. Kennedy (1979), who originally
pointed to this problem, recalculated the probabilities for some of
these experiments. Puthoff and Targ (1976) reported that five of
their first six remote viewing experiments were significant at the .05
level. With Kennedy's corrections for lack of independence, only
two remained significant. According to Kennedy, only one of the
two successful replications by Bisaha and Dunne (1979) remained
significant with the more appropriate test.
One reason for the optimistic initial beliefs in the scientific reality
of remote viewing was the fact that the lack of independence between
trials produced exaggerated odds against chance results. But even
with conservative corrections for lack of independence, approxi-
mately one-third of the early experiments still yielded successful
outcomes.
One easy way to avoid this problem of dependence is to use a
separate target pool of possible sites for each trial. For example, for
the first trial one could designate a pool of four possible sites, one
of which is randomly chosen to be the actual target site. A second
pool of four different possible sites would be used for the second
trial. When the trials are completed, the judge is given the list of
the four sites for the first trial along with the subject's description
for that trial. The judge then ranks each site in terms of its
correspondence to the description. The four possible sites for the
second trial are then ranked in terms of their correspondence to the
subject's description for the second trial. In this illustration, the
subject has a probability of 1 in 4 of having the actual target site
ranked 1 on each trial, or a probability of 1 in 16 of being correct
on both trials.
This second procedure, which is typically used in most free-response
parapsychological experiments (such as the Ganzfeld experiments
discussed below), not only guarantees independence between succes-
sive trials, but also avoids other serious problems, which we discuss
next. The fact that the subject is given feedback by being taken to
the target site immediately after each trial creates an additional
form of dependence between trials. For this reason, other possibilities
exist for obtaining "successful" results artifactually. The tran-
scripts can contain clues that provide nonparanormal reasons for
judges to associate descriptions with targets correctly. Some of these
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clues can be quite overt, such as when a subject mentions in the
description how the current target apparently differs from a previous
target site. When such a clue appears in the description, it provides
the judge with information that the current description does not
belong with the previous site. This increases the probability that the
description will be matched with its appropriate target.
Marks and Kammann (1978) initiated a controversy, still not fully
resolved, by claiming that such overt clues were sufficient to account
foS'the striking results of the very first SRI remote viewing with
Pa& Price. Targ and Puthoff did not deny the existence of such clues
in The Price series but argued that they were not sufficient to have
accounted for the results. This dispute still has not been settled
(Tæt, Puthoff, and Targ, 1980; Scott, 1982; Marks and Scott, 1986).
Possibly this controversy over the role of the more overt clues
hag deflected attention from a much more fundamental and fatally
daglaging criticism first made by Hyman (1979) and independently by
Kenedy (1979). Hyman and Kennedy pointed out that the combination
of@immediate feedback and lack of independence between successive
trias makes it virtually impossible to prevent sensory cueing in the
trafscripts. As long as both the subject and the experimenter who is
closeted with the subject are not blind to the preceding target sites,
there is no way to prevent the transcript from being affected in a
variety of possible and perhaps subtle ways by the knowledge of the
preseding targets.
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Ryman (1984-1985) provides an illustration of how such implicit sensory
cueing might occur (pp. 131-132):
Saythat the target for the first session was the Hoover Tower at Stanford. This
willalmost certainly influence what both the viewer and the interviewer say
durthg the second and subsequent sessions in the same series. Almost certainly
theSiewer, during the second session, will not supply an exact description of the
Hoover Tower. So, whatever the viewer says during the second session, a judge
should find it to be a closer match to the second target site than to the first one.
Now, assume that the second target site happened to be the Palo Alto train
station. The viewer's descriptions during the third session will avoid describing
either the Hoover Tower or the Palo Alto train station. We do not need to
hypothesize something as mysterious as psi to predict that a judge should find
this Third description a better match to the third target site than either of the first
two. As we add sessions, this effect of immediate feedback should continue to
make the correlation between the viewer's descriptions and the target sites better
and better.
No amount of editing for overt clues can overcome this defect of
remote viewing experiments that follow the SRI pattern of dependent
trials and immediate feedback. The mechanism described by Hyman
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PARANORMAL PHENOMENA
should result in some dramatic correspondences. These dramatic corre-
spondences, in conjunction with subjective validation, are a highly potent
recipe for creating the illusion (for both experimenters and subjects) that
ESP has occurred.
Palmer (1985), a major parapsychologist who otherwise carefully
considers the criticisms of parapsychology, misses the seriousness of this
flaw. In mentioning Hyman's criticism, he writes (p. 50):
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.
Perhaps such complacency has enabled experimenters to continue con-
ducting remote viewing experiments with this fatal flaw. In fact, the size
of the target pool, no matter how large, does not affect the validity of
Hyman and Kennedy's criticism. Nor does the claim that the pool
contained sufficient redundancy make much difference. Each geographical
site is unique and contains a combination of specific characteristics that
distinguishes it from the other sites in a given series. Indeed, as the
parapsychologists themselves have asserted, unless this were so, there
would be no possibility of the transcripts' being uniquely associated with
a given target site. In every one of the remote viewing experiments that
allows the possibility of subtle cueing, the possibility of the judges' being
able to make completely successful matchings because of this artifact is
highly plausible; and as long as a highly plausible, normal alternative to
ESP can account for the apparent success of the outcomes the parapsy-
chologists, by their own standards, cannot claim evidence for paranormal
transmission of information.
As it turns out, all but one of the nine scientifically reported studies of
remote viewing (at the time of the Targ and Harary survey) suffer from
the flaw of sensory cueing. The one experiment that cannot be faulted
for this reason is the long-distance remote viewing experiment of Schlitz
and Gruber (1980). However, as Hyman (1984-1985) has pointed out,
this experiment suffers from another very serious flaw. Gruber, who was
a member of the target team and thus was familiar with the targets,
translated the subject's target descriptions into Italian for the judging
process. Why the experimenters allowed such potential sources of biased
experimental procedures is not known, but the violation obviously negates
the results as evidence for psi.
Since the Targ and Harary survey, we have learned of two attempts
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ENHANCING HUMAN PERFORMANCE
to replicate the Schlitz and Gruber experiment without the flaw mentioned.
One, still unpublished, produced negative results. The second, by Schlitz
and Haight (1984), produced marginally significant results. Indeed, if the
more acceptable two-tailed test of significance had been used, the results
would not have been considered significant by customary standards.
Although the report of this study lacks sufficient documentation with
respect to certain aspects of procedure, both Palmer (1985) and Alcock
agree that this is the best controlled and most methodologically sound of
albthe remote viewing experiments so far.
an summary, after approximately 15 years of claims and sometimes
tier controversy, the literature on remote viewing has managed to
produce only one possibly successful experiment that is not seriously
flawed in its methodology-and that one experiment provides only
marginal evidence for the existence of ESP. By both scientific and
parapsychological standards, then, the case for remote viewing is not
just very weak, but virtually nonexistent. It seems that the preeminent
position that remote viewing occupies in the minds of many proponents
results from the highly exaggerated claims made for the early experiments,
aswell as the subjectively compelling, but illusory, correspondences that
experimenters and participants find between components of the descrip-
tions and the target sites.
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RESEARCH ON RANDOM NUMBER GENERATORS
8
The Basic Paradigm
The use of random number (or random event) generators for
pamapsychological research began in the 1960s and became relatively
standard during the 1970s as the technology became widely available.
A Random number generator (RNG) is simply an electronic device
that uses either radioactive decay or electronic noise to generate a
sequence of random symbols. Originally such devices were used to
test ESP, usually clairvoyance or precognition, but the most wide-
spread and widely known work focuses on what is called micropsy-
chokinesis, or micro-PK. In such research a subject, or operator,
attempts to mentally bias the output of the random number generator,
so mat it produces a nonrandom sequence.
Most of the work with RNGs has used binary generators, or what
Schmidt calls "electronic coin flippers." The output on each trial
is either 0 or 1, that is, heads or tails. If the RNG is unbiased and
truly random, then it should produce, on control runs, sequences
of Os and Is that are independent of each other and that, in the long
run, will yield 1s 50 percent of the time.
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PARANORMAL PHENOMENA
In a typical experiment, a subject (either a person who claims to be
a psychic or a person chosen for availability who does not make such
claims) is placed in the vicinity of the RNG and attempts to bias the
output either toward more or fewer 1s. When an animal is used as
the subject, the RNG output is usually coupled to an outcome whose
frequency the animal presumably would like to either increase or
decrease. In an experiment carried out with cockroaches, for example,
one outcome was electric shock. If, during the time the output of
the RNG was coupled with the shock apparatus, the proportion of
shocks decreased below 50 percent, this would be taken as evidence
of a psychokinetic effect of the cockroach on the output of the RNG.
The RNG experiments have been of interest to some military and
governmental personnel because of the possibility, if such micro-PK
is demonstrable, of psychically affecting equipment and computers
that depend on the output of electronic symbols.
Results of the Experiments
In a recent survey 56 reports published between 1969 and 1984 and
dealing with research on possible psychokinetic perturbations of
binary RNGs (Radin, May, and Thomson, 1985), the reviewers counted
332 separate experiments. Of the 332 experiments, 188 were reported
in refereed journals or conference proceedings, and of these 188
experiments with some claim to scientific status, 58 reported statis-
tically significant results (compared with the 9 or 10 experiments
that would be expected by chance). The other 144 experiments were
produced by the Engineering Anomalies Research Laboratory at
Princeton University; none of them had been published in a refereed
journal at the time of the survey. Of these 144 experiments, 13 were
classified as yielding statistically significant results. So, in the total
sample of 332 experiments, 71 yielded ostensibly significant results
at the traditional .05 level. This amounts to a success rate of
approximately 21 percent, compared with the rate of 5 percent that
would be expected by chance.
Palmer (1985) and Alcock agree that such results cannot be
accounted for by chance. In other words, both the parapsychologist
and the skeptic, in their respective reviews of the RNG research,
agree that something other than accidental fluctuation is producing
these results. Palmer calls this something an anomaly, which, while
it may or may not be paranormal, cannot be explained by current
scientific theories. Alcock points to various defects in the experimen-
tal protocols and concludes that no conclusions about the origins
of these departures from randomness are justified until successful
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ENHANCING HUMAN PERFORMANCE
outcomes can be more or less consistently produced with adequately
designed and executed experiments.
Both Palmer and Alcock focus their reviews on the two most
influential research programs on RNGs. One is the program of Helmut
Schmidt, a quantum physicist who began working on psi and RNGs in
1969. The other is the program begun by Robert Jahn in the late
1970s, when he was dean of the School of Engineering and Applied
Science at Princeton University (see Jahn, 1982). These two programs
Lave accounted for almost 60 percent of all known experiments on
ENGs. They have also been the most consistently successful in
&hieving statistically significant outcomes.
SAlthough the results suggest that on each experimental group of
Wals the number of Is is greater or less than the 50 percent baseline
Bepending on the intended direction), the actual degree of deviation
from chance is quite small. As Palmer (1985) indicates, Schmidt's
Abjects have averaged approximately 50.5 percent hits over the years,
Ompared with the expected baseline of 50 percent. This amounts to
producing one extra 1 every 100 trials. The reason such a small
departure from chance is statistically significant is that an enormous
Rimber of trials is conducted with each subject.
Jahn and his colleagues at Princeton have, in a much shorter time,
produced on the order of 200 times the number of trials that Schmidt
did in 17 years. The Princeton researchers have also produced a
significantly lower success rate than Schmidt. In their formal series
§ 78 million trials, the percentage of hits in the intended direction
was only 50.02 percent, or an average of 2 extra hits every 2,500
Bals. Again, such an extremely weak effect is statistically signifi-
ant only when one is dealing with very large numbers of trials.
Scientific Assessment of the RNG Experiments
Palmer (1985) carefully reviews the major criticisms of the work
f Schmidt and Jahn. He addresses questions about security, because
abjects often are left alone with the apparatus during the data
ollection. In the Princeton experiments, the data are always col-
lected when the subject is alone with the apparatus. Although the
Linceton experiments now contain a number of features that would
make it extremely difficult for a naive subject to bias the results, it
is not clear that this has always been so. It would make good scientific
sense to conduct some trials during which the subject is carefully
monitored to see if successful outcomes are still obtained.
The major reservations about the RNG experiments concern the
adequacy of the randomization of the outputs. Schmidt applied only
limited tests for the randomness of his machines, and most of the
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PARANORMAL PHENOMENA
control trials were gathered by allowing the machine to run for
long periods, usually overnight. Although these controls usually
produced results in line with the chance baseline, critics have pointed
out that the controls are unsatisfactory because they were not
conducted for shorter runs and at the same time as the data from
the experimental sessions.
Palmer grants that the critics are correct in pointing out some of
the shortcomings in Schmidt's methods for testing and controlling
for the randomization of his machines. Palmer also correctly points
out that such criticism is somewhat blunted by the fact that the
critics have not specified any plausible mechanisms that would account
for the obtained differences between the experimental and control
trials. He is correct in pointing out that the Princeton experiments
provide more adequate controls; however, he has probably assumed
that the baseline controls in the Princeton experiments were run at
the same time as the two experimental conditions of hitting and
missing. It is easy to interpret the somewhat ambiguous description of
the procedure in this manner. The relevant part of the authors'
methodological description is as follows (Nelson, Dunne, and Jahn,
1984:9):
The primary variable in these experiments is the operator's pre-recorded
intention to shift the trial counts to higher or lower numbers. This direc-
tional intention may be the operator's choice-the so-called "volitional"
mode-or it may be assigned by a specified random process-the "instructed"
mode. In either mode, data are collected in a "tri-polar" protocol, wherein
trials taken under an intention to achieve high numbers (PK +), trials taken
under an intention to achieve low numbers (PK-), and trials taken as
baseline, i.e. under null intention (BL), are interspersed in some reasonable
fashion, with all other operating conditions held identical. For all three
streams of data, effect size is measured relative to the theoretical chance
mean. This tri-polar protocol is the ultimate safeguard in precluding any
artifacts such as residual electronic biases or transient environmental
influences from systematically distorting the data.
At first glance it might appear as if the tripolar protocol requires
that the two types of experimental groups of trials and the baseline
group of trials always be taken at the same session. This would be
consistent with the claim that "any artifacts such as residual
electronic biases or transient environmental influences" were thereby
precluded "from systematically distorting the data." Such a claim
would be justified if, in fact, at each session one group of trials of
each of the three types was obtained, provided that each group of
trials was of the same length and that the order of the three types
of trials was independently randomized for each session.
The description provided by Nelson and his colleagues says nothing
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at all about the order in which the three conditions were conducted,
and a careful reading indicates that the baseline data may not always
have been obtained at the same sessions and under the same conditions
as the experimental groups of trials. It is not clear what the authors
mean by stating that the three trials "are interspersed in some
reasonable fashion." In fact, an examination of the data reported
for each subject makes it clear that the strict tripolar protocol
could not possibly have been followed with much of the data
cection, because in many cases the baseline data are entirely
algent or occur with many fewer trials than the experimental data.
Indeed, it is not even clear that PK + and PK - trials were always
o Rained at the same sessions, because for some subjects the total
n&nbers of these trials are not equal.
&Ve suspect that, over the six years or so during which the Princeton
grup was accumulating its data base, it made many changes in both
the hardware and the experimental protocol. The sophisticated
pRcedures currently in use and the requirement that the three types
oftrials be of equal length and that one of each be conducted at
eash session are the most recent variations in the paradigm. Unfor-
tuffately, the data are not presented in such a way that it is possible
todetermine whether the successful results are due to the earlier
of the later experiments.
105/17 :
Such issues become especially important when we consider the
extremely small size of the effect being claimed and when we further
r@lize, as Palmer has pointed out, that the bulk of the significance
insthe formal series was due to just one subject, who contributed 23
porcent of the total data. This one subject achieved a hit rate of
5005 percent. When her data are eliminated, the remaining data
yigld a hit rate of 50.01 percent, which is no longer significantly
different from chance.
"In other words, it looks as if almost all the success of Jahn's huge
daa base can be attributed to the results from one individual, who,
over the years, produced almost 25 percent of the data. This one
ingividual was not only the most experienced subject, but also,
presumably, familiar with the equipment. When combined with the
fast, as Palmer points out, that the Princeton experiments provide
inadequate documentation on precautions to prevent tampering by
subjects, it becomes even more important to see if the same degree of
success can be achieved when the sessions are adequately monitored.
Alcock, in his review of the same RNG studies surveyed by Palmer,
points to a number of weaknesses in both the Schmidt and the Princeton
experiments. For example, he faults Schmidt's experiments for such
things as inadequate controls, failure to examine the target se-
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PARANORMAL PHENOMENA
quences, overcomplicated experimental setups, inadequate tests of
randomness, and lack of methodological rigor. Alcock faults the
Princeton experiments for such things as failing to randomize the
sequence of groups of trials at each session, inadequate documentation
on precautions against data tampering, and possibilities of data
selection.
Palmer and Alcock do not really differ in their assessments of the
shortcomings of the Schmidt and Princeton RNG experiments. They
do differ, however, on what conclusions can be drawn from such
imperfect experiments. Palmer emphasizes the fact that the critics
have not provided plausible explanations as to how the admitted
flaws could have caused the observed results. His position seems to
be that, unless the critics can provide such plausible alternatives,
the results should be accepted as demonstrating an anomaly. Alcock
focuses on the fact that the successful results have been obtained
under conditions that fall short of the experimental ideals that
parapsychologists themselves profess. He emphasizes that the para-
psychologists have no right to claim to have demonstrated psi from
experiments that have been conducted with "dirty test tubes." Such
a revolutionary conclusion as the existence of psi demands justifi-
cation from experiments that have clearly used "clean test tubes."
What would it take to conduct an adequate RNG experiment?
May, Humphrey, and Hubbard (1980) set out to do just that. After
reviewing all available RNG experiments from 1970 through 1979
and taking into account the various deficiencies in these experiments,
they gathered together and meticulously tested the components
necessary to provide adequately randomized trials. They also devised
a careful experimental protocol and set out in advance the precise
criteria that would have to be fulfilled before they could call their
results successful. Going further, after they completed the experi-
ment with results that met their criteria for success, they subjected
their equipment to all sorts of physical extremes to see if they could
obtain such a degree of success by a possible artifact.
They report that this singularly well controlled RNG experiment in
fact met their criteria for success. It is unfortunate, therefore, that this
carefully thought-out experiment was conducted only once. After the one
successful series, using seven subjects, the equipment was dismantled,
and the authors have no intention of trying to replicate it (personal
communication, August 1986). It is unfortunate because this appears to.
be the only near-flawless RNG experiment known to us, and the results
were just barely significant. Only two of the seven subjects produced
significant results, and the test of overall significance for the total formal
series yielded a probability of 0.029.
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The experiment, while nearly flawless, still had some problems as
evidence for psi. For one thing, it was reported only in a technical report
in 1980 and has never been published in a refereed scientific journal.
Despite the admirable attention to details, all the control trials were taken
when no human being was present. One might argue that this was not an
ideal control for the experimental session, in which a subject was
physically present in the room. The authors have assured us that their
various attempts to bias the machine by physical means almost certainly
nge out the possibility that the mere presence of a human being could
h&e affected the output. However, a physicist who claims to have
seral years of experience in constructing and testing random number
devices tells us that it is quite possible, under some circumstances, for
tig human body to act as an antenna and, as a result, possibly bias the
ofput.
May and his colleagues at SRI, in the same technical report in which
they claim successful results for their single experiment, surveyed all the
ROIG experiments known to them through the year 1979 and found that
their combined significance was astronomically high. They add (May,
Humphrey, and Hubbard, 1980:8):
This impressive statistic must, however, be evaluated with respect to experimental
equipment and protocols. All the studies surveyed could be considered incomplete
in at least one of the following four areas: (1) No control tests were reported in
more than 44 percent of the references. Of those that did, most did not check
fos temporal stability of the random sources during the course of the experiment.
(There were insufficient details about the physics and constructed parameters
ogthe experimental apparatus to assess the possibility of environmental influences.
( The raw data was not saved for later and independent analysis in virtually
any of the experiments. (4) None of the experiments reported controlled and
lingited access to the experimental apparatus.
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@As far as we can tell, the same four points can be made with respect
t& the RNG experiments that have been conducted since 1980. The
situation for the RNG experiments thus seems to be the same as that for
remote viewing: over a period of approximately 15 years of research,
ofly one successful experiment can be found that appears to meet most
ofthe minimal criteria of scientific acceptability, and that one successful
eSperiment yielded results that are just marginally significant.
RESEARCH ON THE GANZFELD
The Ganzfeld Experiments
The Ganzfeld psi experiments are named after the term used by
Gestalt psychologists to designate the entire visual field. For
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PARANORMAL PHENOMENA
theoretical purposes, the Gestalt psychologists wanted to create a
situation in which the subject or observer could view a homogeneous
visual field, one with no imperfections or boundaries. Psychologists
later discovered that when individuals are put into a Ganzfeld
situation they tend quickly to experience what they described as an
altered state of mind.
In the early 1970s, some parapsychologists decided that the use of
the Ganzfeld would provide a relatively safe and easy way to create
an altered state in their experimental subjects. They believed that
such a state was more conducive to picking up the elusive psi signals.
In a typical psi Ganzfeld experiment, the subject, or percipient, has
halved ping-pong balls taped over the eyes. The subject then reclines
in a comfortable chair while white noise plays through earphones
attached to his or her head. A bright light shines in front of the
subject's face. When seen through the translucent ping-pong balls,
the light is experienced as a homogeneous, foglike field. When so
prepared, almost all subjects report experiencing a pleasant, altered
state within 15 minutes.
While one experimenter is preparing the subject for the Ganzfeld
state, a second experimenter randomly selects a target pool from a
large set. The target pool typically consists of four possible targets,
usually reproductions of paintings or pictures of travel scenes. One
of the four is chosen at random to be the target for that trial. The
target is given to an agent, or sender, who tries to communicate its
substance psychically to the subject in the Ganzfeld state. After a
designated period, the subject is removed from the Ganzfeld state
and presented with the four candidates from the target pool. The
subject then ranks the four candidates in terms of how well each
matched the experience of the Ganzfeld period. If the actual target
is ranked first, the trial is designated a hit. An actual experiment
consists of several trials. In the example, the probability is that one
of every four trials will produce a hit. If the number of hits
significantly exceeds the expected 25 percent, then the result is
considered to be evidence for the existence of psi.
Critique of the Ganzfeld Experiments
In a careful and systematic review of the Ganzfeld experiments
undertaken in 1981 and published in the March 1985 issue of the
Journal of Parapsychology, Hyman concluded that the data base
exhibited flaws involving multiple testing, inadequate controls for
sensory leakage, inadequate randomization, statistical errors, and
inadequate documentation. These flaws, in his opinion, were sufficient
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to disqualify the Ganzfeld data base as evidence for psi. Of the 42
experiments, 39 (93 percent) used multiple analyses, which artificially
inflated the chances of obtaining significant outcomes. Only 11 (26
percent) clearly indicated that they had adequately randomized the
target selections. As many as 15 (36 percent) used inferior randomi-
zation, such as hand shuffling, or no randomization at all. The
remaining 16 experiments did not supply sufficient information on how
they had chosen the targets. As many as 23 of the experiments (55
pecent) used only one target pool, which means that the subject
was handed for judging not a copy of the target but the very same
tagget that the percipient had handled, permitting the possibility of
sessory cueing. Although the argument for psi is mainly a statistical
08, the reports of 12 experiments (29 percent) revealed statistical
effors. A number of other departures from optimal practice were also
fAnd.
The same issue of the Journal of Parapsychology contained a
lengthy rebuttal by parapsychologist Charles Honorton, one of the
poneers of the Ganzfeld psi technique. Honorton disputed many of
ISman's opinions as to what constituted flaws; provided a reanalysis
of the data base to overcome many of the statistical weaknesses of
original experiments; and argued that the flaws he agreed existed
were not sufficient to have accounted for the findings. In this respect
his analysis is consistent with Palmer's approach. He does not deny
that the experiments depart from optimal design, but he argues that
sath departures are insufficient to account for the results.
05/57 & GTA-RDE96-00
SHonorton and Hyman had the opportunity to discuss their differ-
aces about psi in general at the Parapsychological Association
meetings in 1986; as a result, they agreed to draft a joint communiqué
to emphasize those points on which they agree. That communiqué
ampeared in the December issue of the Journal of Parapsychology
(Hyman and Honorton, 1986). They agree that the current data base
is insufficient to support either the conclusion that psi exists or the
conclusion that the results are due to artifacts. They further agree
that the issue can be settled only by future experiments conducted
agcording to the stated standards of parapsychology, which are also
A
accepted standards of psychological research.
Another important input to the committee's judgment on the
Ganzfeld research was the systematic evaluation of the contemporary
parapsychological literature by Charles Akers (1984), a former
parapsychologist. Akers's critique used a methodological strategy
different from that used by Hyman. Hyman undertook to evaluate
the entire data base of a single research paradigm (Ganzfeld),
including both successful and unsuccessful outcomes. Akers surveyed
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contemporary ESP experiments broadly, but confined his evaluation
to those that had produced significant results with unselected
subjects. Hyman assigned flaws to experiments without regard to
whether each flaw, by itself, could have caused the observed outcome.
Akers charged a flaw to a study only if he thought the flaw could
have been sufficient to produce the observed result. He chose a
sample of 54 parapsychological experiments from areas of research
that had been previously reviewed by Honorton or Palmer; his intent
was to choose experiments that could be viewed as the best current
evidence for the existence of psi. As a result of this exercise, he
concluded (Akers, 1984:160-161):
Results from the 54-experiment survey have demonstrated that there are
many alternative explanations for ESP phenomena; the choice is not simply
between psi and experimenter fraud. ... The numbers of experiments ...
flawed on various grounds were as follows: randomization failures (13),
sensory leakage (22), subject cheating (12), recording errors (10), classification
or scoring errors (9), statistical errors (12), reporting failures (10). ... All
told, 85% of the experiments were considered flawed (46/54).
This leaves eight experiments where no flaws were assigned. ... Although
none of these experiments has a glaring weakness, this does not mean that
they are especially strong in either their methods or their results. . . .
In conclusion, eight experiments were conducted with reasonable care,
but none of these could be considered as methodologically ideal. When all
54 experiments are considered, it can be stated that the research methods
are too weak to establish the existence of a paranormal phenomenon.
RESEARCH ON ELECTRICAL ACTIVITY AND EMOTIONAL STATES
The Backster Laboratory
In addition to examining parapsychological research in areas that
have produced large literatures, the committee witnessed an example
of experimental work at a far less developed stage. On February 10,
1986, committee members visited the Backster Research Foundation
in San Diego and saw a demonstration of experimental procedures
for detecting a correlation between the electrical activity of oral
leukocytes and the emotional states of the donor.
Cleve Backster is a polygraph specialist who had at one time helped
develop interrogation techniques for the Central Intelligence Agency
and now runs his own polygraph school in San Diego. The school is
housed in the same rooms that constitute the Backster Research
Foundation, which is devoted to the study of what Backster refers
to as primary perception. Backster's research on paranormal matters
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began in February 1966, when he recorded, from a philodendron plant
that he had hooked up to a polygraph, a response he recognized as
similar to that of human beings in emotional states. Backster believed
he had demonstrated that the plant showed such emotional response
when brine shrimp or other living organisms were either threatened
or actually killed in an adjoining room. The notion of primary
perception in plants became both a popular subject for research and
a Bighly controversial concept during the late 1960s and early 1970s.
SVe were told that Backster has quietly continued his researches
info this and related matters. He has now devised a technique for
recording electrical activity in leukocytes taken from a donor's
mouth. The advantage of this technique, we were told, is that the
leskocytes respond mostly to emotional states of the donor.
One committee member volunteered to be the demonstration subject.
ARother member accompanied him to observe the techniques for
ogaining the leukocytes and preparing them for recording. The
sample was obtained by having the subject "chew" on a 1.2 percent
saline solution and then spit it back into a centrifuge tube. Ten such
samples were obtained in this way. The samples were then spun in a
centrifuge for six minutes, and the particulate matter at the bottom
PRDE9
ofeach tube was pipetted into the preparation tube. The preparation
tube contained about one centimeter of particulate matter and was
filed almost to the top with 1.2 percent saline solution. Two
ugnsulated wire electrodes were inserted into the bottom of the
tube, which was then placed within a shielded cage and connected
bo leads to an EEG-type recording apparatus.
During the demonstration, the subject sat approximately two meters
from the preparation. We were told that subjects usually sit about
file meters from the preparation. A split-screen projection video
display was provided: the lower portion of the screen recorded the
migvements of the polygraph paper and pen as they produced a record
of the electrical activity presumably taking place in the leukocyte
preparation. The upper portion of the screen recorded the behavior
ofthe seated subject.
an his previous research using this arrangement, Backster reported
that, when the subject revealed an emotional reaction, the electrical
action of the leukocytes showed a corresponding reaction. During
our demonstration, the polygraph record produced several strong
deflections in both the control and the experimental series, but they
did not obviously correlate with any corresponding thoughts or
emotional states of the subject as various stimuli were presented.
Backster suggested that this was probably because so many people
were crowded into the laboratory that the leukocytes were respond-
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PARANORMAL PHENOMENA
ing to thoughts and feelings of other individuals in the room. Thus,
a demonstration of results, as opposed to techniques, was not, after
all, going to be possible during our visit.
Backster then showed us videotapes of the split-screen results he
had obtained in his "formal" experiments. The results consisted of
12 examples of apparent correlations between an emotional response
and a deflection of the polygraph record. The 12 examples came from
7 sessions with 7 different subjects. Although the information is not
given in his written report, it appears that each session lasted for
approximately half an hour. During this time, the donor is engaged
in conversation or watches videotapes of television programs. The
sessions are not standardized or planned. Backster's intent, appar-
ently, is to elicit spontaneous emotional responses from a subject
during the session. He believes that a stimulus that evokes an
emotional response in one subject will not necessarily do so in
another subject.
In one example, the subject was a young man who was looking at
an issue of Playboy magazine. The polygraph tracing began to display
large deflections soon after he encountered a nude photograph of
an attractive young woman. The large deflections continued for
approximately two minutes; the tracing slowly settled down to
normal activity after the magazine was closed. Soon after, the young
man reached for the closed magazine, and the record reveals a single
deflection at that point. In another example, the subject was a
retired police lieutenant. When discussing his approaching retirement,
he was asked a question about his wife's attitude toward having him
"underfoot." A large deflection of the polygraph tracing occurred
soon after this question was asked. When asked, the donor confirmed
that he was emotionally aroused at that moment in the session (see
Backster and White, 1985).
Cleve Backster and his supporters apparently believe that he has
successfully demonstrated that detached oral leukocytes respond
to the emotions of their donor even when separated by as much as
several miles. They also believe that these results are reliable and
replicable.
Critique of the Backster Experiment
What we have read and observed about Backster's procedures does
not justify the claim he is making. His answers to our questions made it
clear that he has not considered using the appropriate controls needed
to ensure that the obtained "correlations" are real and due to the causes
he has assumed. To make adequate physiological recordings from a
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preparation of in vitro leukocytes and to demonstrate the correlation
between emotional response and leukocyte activity requires experimental
arrangements and procedures at a level of sophistication well beyond
those we observed.
Committee members who are knowledgeable about the procedures and
instrumentation of psychophysiological experiments expressed doubts
about the adequacy of the setup to perform the tasks Backster has
undertaken. Serious doubts were expressed about the possibility that the
leul@cytes were alive at the time of recording. Further doubts were
expressed about the setup's ability to avoid contamination of the recording
2000-±
progdures by stray influences of various sorts. We do not discuss these
dra@backs in detail here. We confine our discussion to Backster's method
for Establishing a correlation between the alleged activity of the detached
leukocytes and the emotional state of the donor. When we consider how
thedexistence of such correlations was established, we again see how
inappropriate methodology can lead to very misleading conclusions.
Many problems exist with regard to Backster's procedures for detecting
corRelations. In trying to demonstrate a pattern of covariation between
tworecords of behavior over time, one record is the tracing of amplified
electrical activity coming from the electrodes and through the leads.
Although this tracing can be quantified, Backster has apparently made
no attempt to do so. Instead, he has relied on visual inspection of the
polygraph record to pick out points at which the deflections of the pen
from the baseline are noticeable. Although such subjective judgment is
scientifically unacceptable, the deflections that he uses in his examples
see sufficiently marked that they probably can be considered to be real
de @ations from the baseline. At any rate, let us assume that responses
on The polygraph record can be visually pinpointed with reasonable
objectivity.
The deflections on the polygraph record are then compared with
happenings on the concurrent videotaping of the conversation with the
subiect. Here we encounter very serious problems as to what constitutes
an
emotional response on this behavioral record. Backster believes he
ca
identify categories of potentially emotionally arousing stimuli in the
nogstandardized, qualitative, ongoing record of conversation. He then
campdetermine if the subject was experiencing an emotional reaction to
such a stimulus by simply replaying the record, pointing to the segment
that corresponds to a place where the polygraph showed a deflection,
and asking the subject if he or she recalls what was taking place at that
moment as an emotionally arousing experience. If the subject agrees,
this is said to confirm a "correlation" between the emotional state and
the corresponding activity of the tracing.
Such a purely subjective determination of an emotional response opens
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PARANORMAL PHENOMENA
the process to a variety of known biases, many of them discussed in the
paper prepared for the committee by Griffin (Appendix B). The literature
on "illusory correlation" (Alloy and Tabachnik, 1984; Griffin paper)
makes it clear how subjective expectations and cognitive biases can lead
to false impressions of correlation. Backster's method of searching for
correlations compounds these inevitable biases: he does not independently
determine moments of emotional response in the subject's behavioral
record and moments of polygraph deflections and then look for a match
between the two. Instead, he apparently looks for polygraph deflections
and then tries to determine if an emotional response can be found that
occurred in the vicinity of the polygraph activity. In other words, the
determination of the emotional response is done with full knowledge of
the fact that a polygraph deflection has occurred.
Under such circumstances, we would expect processes of subjective
validation to operate. In addition, the method of verifying the emotional
response, by asking the subject to acknowledge that he or she was in
fact experiencing such a state at the moment the polygraph record
indicated a leukocyte response, is itself suspect. This is the sort of
circumstance in which demand characteristics (i.e., responses determined
by the presumed intent of the experimenters) are known to operate.
Good science dictates that the moments of emotional response should
be determined independently of the moments of polygraph response.
Both the experimenter and the subject must be blind to the polygraph
record when determining the moments of emotional response. Only when
the determination of events on the two records has been made independ-
ently of each other can the records be compared to determine if the
emotional responses and the polygraph activity are correlated.
Illusory correlations occur because our subjective judgments of cov-
ariation tend to use only a portion of the relevant information and because
we tend to bias observed events in terms of our expectations. In particular,
intuitive judgments of covariation tend to focus only on the co-occurrence
of treatment of interest and successful outcomes, ignoring times when
the treatment co-occurred with unsuccessful outcomes. Backster uses
only those examples from his records in which an emotional response
co-occurs with a polygraph deflection; the 12 such examples from the 7
experimental series represent a very small fraction of the total data
collected.
Not only is a sample of just 12 co-occurrences probably too small for
estimating whether a true correlation exists, but it is also impossible from
this information alone to estimate whether any correlation exists. All the
data are needed for this purpose. Almost certainly, more than 12 polygraph
deflections must have appeared in the total record. In the brief demon-
stration for the committee, both the control and the experimental series
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yielded several deflections, so it is reasonable to assume that many more
than 12 deflections were obtained in the complete record. It is likely that
these unreported deflections were not preceded by any emotional re-
sponses.
Almost certainly, more than 12 emotional responses must have appeared
in the total record. The point of conducting the sessions was to expose
the subjects to a variety of emotional stimuli; therefore, it is essential to
know the number of times that emotional responses occurred without the
cgresponding occurrence of polygraph responses. Finally, to determine
c@relation, it is essential to know the frequency of co-occurrence of the
agence of emotional responses and the absence of polygraph responses.
All this information is needed to determine whether the claimed
cgrelation exists. All the data must be used. From these data, one can
compare the proportion of times that an emotional response is followed
by a polygraph response with the proportion of times that the absence
of an emotional response is followed by a polygraph response. Only if
these two proportions are significantly different from one another can we
assume that the data provide evidence for a correlation between emotional
6-00791R000200320001 1
response and leukocyte activity. The fact that Backster was able to find
12 examples of the co-occurrence between emotional response and
polygraph deflection, even if these correspondences had come from
double-blind matching, provides us with absolutely no information about
whether a correlation exists.
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The stronger claim would be, of course, not that a correlation exists,
bot that a causal connection exists between the subject's emotional states
agd the responses of the detached leukocytes. As Chapter 3 on evaluation
iflicates, such a causal explanation requires much more than the
demonstration of correlation between two series. Because Backster did
not use double-blind procedures to determine emotional responses, and
because the procedures he did use are known to be just those that
facilitate the occurrence of a variety of subjective biases, he may well
hove obtained a correlation between his two series. However, his
procedures for finding such correlations are sufficiently flawed that we
do not know if in fact the suspected (and presumably biased) correlation
actually does exist in his data. The Backster experiment indicates that
ti@ best intentions combined with scientific instrumentation and poly-
graphic records cannot, in themselves, guarantee data of scientific quality.
DISCUSSION OF THE SCIENTIFIC EVIDENCE
Both the parapsychologists cited in this report and the critics of
parapsychology believe that the best contemporary experiments in para-
psychology fall short of acceptable methodological standards. The critics
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conclude that such data, based on methodologically flawed procedures,
cannot justify any conclusions about psi. The parapsychologists argue
that, while each experiment is individually flawed, when taken together
they justify the conclusion that psi exists.
Palmer's conclusion in this regard is unique. Although he agrees that
the data do not justify the conclusion that a paranormal phenomenon has
been demonstrated, he argues that the data, with all their drawbacks, do
justify the conclusion that an anomaly of some sort has been demonstrated.
It is this purported demonstration of an anomaly that, according to
Palmer, further justifies the claim that parapsychologists do have a subject
matter. The awkward aspect of Palmer's position is that, without an
adequate theory, there is no way to know that the anomaly "demon-
strated" in one experiment is the same anomaly "demonstrated" in
another; indeed, there is no limit to the possible causes of the anomaly
in a given experiment. Without an adequate theory, there is no reason
to assume that the various anomalies constitute a coherent or intelligibly
related class of phenomena.
The committee distinguishes among three types of criticism that can
be leveled at a given parapsychological finding. The first is what we might
refer to as the smoking gun. This type of criticism asserts or strongly
implies that the observed findings were due not to psi but to factor X.
Such a claim puts the burden of proof on the critic. To back up such a
claim, the critic must provide evidence that the results were in fact caused
by X. Many of the bitterly contested feuds between critics and proponents
have often been the result of the proponent's assuming, correctly or
incorrectly, that this type of criticism was being made.
The second type of criticism can be referred to as the plausible
alternative. In this case, the critic does not assert that the result was due
to factor X, but instead asserts that the result could have been due to
factor X. Such a stance also places a burden on the critic, but one not
so stringent as the smoking gun assertion. The critic now has to make a
plausible case for the possibility that factor X was sufficient to have
caused the result. For example, optional stopping of an experiment on
the part of a subject can bias the results, but the bias is a small one; it
would be a mistake to assert that an outcome was due to optional stopping
if the probability of the outcome is extremely low. Akers's critique,
which was previously discussed, is an example based on the plausible
alternative.
The third type of criticism is what we have called the dirty test tube.
In this case, the critic does not claim that the results have been produced
by some artifact, but instead points out that the results have been obtained
under conditions that fail to meet generally accepted standards. The gist
of this type of criticism is that test tubes should be clean when doing
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careful and important scientific research. To the extent that the test tubes
were dirty, it is suggested that the experiment was not carried out
according to acceptable standards. Consequently, the results remain
suspect even though the critic cannot demonstrate that the dirt in the
test tubes was sufficient to have produced the outcome. Hyman's critique
of the Ganzfeld psi research and Alcock's paper on remote viewing and
random number generator research are examples of this type of criticism.
In the committee's view, it is in this latter sense, the dirty test tube
søse, that the best parapsychological experiments fall short. We do not
h&e a smoking gun, nor have we demonstrated a plausible alternative;
b& we imagine that even the parapsychological community must be
concerned that their best experiments still fall far short of the methodo-
logical adequacy that they themselves profess.
Ronorton and Hyman differ on whether to assign a flaw in randomization
tagja particular series of experiments. With Honorton's assignment, the
studies with adequate randomization do not differ in significance of
ofcome from those with inadequate randomization. With Hyman's
assignment, the experiments with inadequate randomization have signif-
icantly more successful outcomes than do those with adequate random-
ization. A simple disagreement on one experiment can thus make a huge
difference as to whether we conclude that this flaw contributed or did
no contribute to the observed outcomes. Several similar examples could
be cited to illustrate the extreme sensitivity of this data base to slight
changes in flaw assignments.
Even if Palmer is correct in asserting that in a particular case an
ammaly has been demonstrated, serious problems remain. In astronomy
and other sciences, an anomaly is a very precise and specifiable departure
from a well-defined theoretical expectation. Neptune was discovered, for
example, when Leverrier was able to specify not only that the orbit of
Umanus departed from that expected by Newtonian theory, but also
precisely in what way it departed from expectation. Nothing approaching
such a specifiable anomaly has been claimed for parapsychology. A vague
and unspecifiable departure from chance is a far cry from a well-described
arfi systematic departure from a precise, theoretical equation. Leverrier's
ammaly was consistent with only a very narrow range of possibilities.
TE sort of anomaly claimed for parapsychology is currently consistent
with an almost infinite variety of possibilities, including artifacts of various
kinds.
THE PROBLEM OF QUALITATIVE EVIDENCE
The committee continually encountered the distinction between qual-
itative and quantitative evidence for the existence of paranormal phe-
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nomena. Many proponents of the paranormal acknowledge such a differ-
ence in one way or another. Some realize that it is only quantitative
evidence that will convince the scientific community. Although they
themselves have relied on qualitative evidence for their own beliefs, they
refer us to the RNG experiments of Robert Jahn or the remote viewing
experiments at SRI as examples of supporting quantitative data.
Most proponents seem impatient with the request for scientific evidence.
They have been convinced through their own experiences or the vivid
testimonies of individuals whom they trust. Many argue that qualitative
evidence can be as good as quantitative; indeed, they claim that in some
circumstances it can be better.
The arguments for the superiority of qualitative evidence are based in
many cases on such factors as ecological validity, conducive atmosphere,
and holism. The ecological validity argument asserts that the artificial
conditions required for laboratory experiments are so different from the
natural settings in which paranormal phenomena typically occur that
findings from such controlled studies are irrelevant. By removing the
psychic from his or her natural domain or by arranging conditions to suit
the needs of scientific observation, it is claimed, the scientist destroys
the very phenomenon under question. The ecological validity argument
is closely related to the other arguments. Proponents who emphasize the
conducive atmosphere assert that the austere conditions of strict labo-
ratory procedure create an atmosphere that is numbing or inimical to
psychic functioning. Those who emphasize holism point out that the
experimental procedures necessarily dissect and focus on restricted
portions of a system. Such compartmentalization, it is claimed, makes it
impossible to study the sorts of paranormal phenomena that operate only
as a total system in a naturalistic context.
QUALITATIVE EVIDENCE AND SUBJECTIVE BIASES
What is meant by qualitative evidence? Roughly, it means any sort of
nonscientific evidence that proponents find personally convincing. Typ-
ically, it involves personally experiencing or witnessing the phenomenon.
Less compelling, but still effective, is the testimony of friends or trusted
acquaintances who have personally experienced it. Even individuals who
are intellectually aware of the pitfalls of personal observation and
testimony find it difficult, even impossible, to disregard the compelling
quality of such evidence in the formation of their own beliefs.
A major parapsychologist admitted to one committee member that the
scientific evidence did not justify concluding that psi exists. "As a trained
scientist," he said, "I know quite well that by scientific criteria there is
no evidence for the existence of psi. In fact, I have always argued with
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my parapsychological colleagues that they are making a serious mistake
in trying to get the scientific community to take their current evidence
seriously. Before they do this, they first have to be able to collect the
sort of repeatable and lawful data that constitute scientific evidence."
This same parapsychologist then explained why, despite the current lack
of evidence, he remained a parapsychologist. "When I was 16 I had some
personal experiences of a psychic nature that were so compelling that I
have no doubt that they were real. Yet, as a trained scientist, I know
tha my personal experiences and subjective convictions cannot and
should not be the basis for asking others to believe me." This parapsy-
ch
Bogist is unusual in that he makes the distinction within himself
between beliefs that are subjectively compelling and beliefs that are
scientifically justifiable. More typical is the proponent who, as a result
of compelling personal experience, not only has no doubt about the reality
of anderlying paranormal cause, but also has no patience with the refusal
of others to support that belief.
We see two problems regarding qualitative evidence. First, personal
observation and testimony are subject to a variety of strong biases of
winch most of us are unaware. When such observations and testimony
erfferge from circumstances that are emotional and personal, the biases
and distortions are greatly enhanced. Psychologists and others have found
that the circumstances under which such evidence is obtained are just
those that foster a variety of human biases and erroneous beliefs. Second,
beijefs formed under such circumstances tend to carry a high degree of
subjective certainty and often resist alteration by later, more reliable
digconfirming data. Such beliefs become self-sealing, in that when new
information comes along that would ordinarily contradict them, the
befevers find ways to turn the apparent contradictions into additional
confirmation.
The committee asked Dale Griffin to describe many of the ways in
which cognitive and social psychologists have documented that human
subjective judgment can lead us astray. Griffin's paper emphasizes the
cognitive biases termed availability and representativeness, but he also
discusses motivational biases. Although most of these biases have been
created under laboratory conditions, they are nonetheless quite powerful,
ar evidence has been mounting that, if anything, they are much more
powerful in natural settings. Griffin points out that one vivid, concrete
experience is usually sufficient to outweigh conclusions based on hundreds
or thousands of cases based on abstract summary statistics. These and
the other biases discussed by Griffin should make us wary of conclusions
based on qualitative evidence.
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EXAMPLES OF PROBLEMATIC BELIEFS
In this section we discuss some examples of beliefs about paranormal
phenomena that have been formed under conditions known to generate
cognitive illusions and strong delusional beliefs. We attempt to make
clear why we are skeptical of any evidence offered in support of the
paranormal that does not strictly fulfill scientific criteria. We believe it is
important to realize the power of such conditions to create strong but
false beliefs.
In 1974 a group of distinguished physicists at the University of London
observed renowned psychic Uri Geller apparently bend metallic objects
and cause part of a crystal, encapsulated in a container, to disappear.
Impressed with what they saw, in 1975 these scientists contributed an
article to Nature outlining their ideas about how to conduct successful
parapsychological research (reprinted in Hasted et al., 1976). In their
discussion they note that successful results depend on the relation among
the participants and that phenomena are more likely to occur when all
participants are in a relaxed state, all sincerely want the psychic to
succeed, and "the experimental arrangement is aesthetically or imagi-
natively appealing to the person with apparent psychokinetic powers."
Hasted and his colleagues describe further desiderata. The psychic
should be treated as one of the experimental team, contributing to an
attitude of mutual trust and confidence that facilitates successful appear-
ance of the allegedly paranormal effects. The slightest hint of suspicion
on the part of the observers can stifle the occurrence of any phenomena.
Observers should avoid looking for any particular outcome that interferes
with the required relaxed state of mind and impedes paranormal powers.
To help avoid the inhibiting effects of concentrated attention, participants
should talk and think about matters irrelevant to the experiment at hand.
Acknowledging that these desiderata make it difficult to preclude
trickery, Hasted and his colleagues express confidence that they can both
create psi-conducive conditions and eliminate the possibility of being
tricked (Hasted et al., 1976:194):
It should be possible to design experimental arrangements which are beyond any
reasonable possibility of trickery, and which magicians will generally acknowledge
to be so. In the first stages of our work we did in fact present Mr. Geller with
several such arrangements, but these proved aesthetically unappealing to him.
Although we may sympathize with the British physicists' desire to
create conditions conducive to the appearance of genuine psychic powers,
if such powers exist, we cannot fail to note the quandary that their efforts
produce. In their quest for psi-conducive conditions, they have created
guidelines that play into the hands of anyone intent on deceiving them.
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The very conditions that are specified as being conducive to the appearance
of paranormal phenomena are almost always precisely those that are
conducive to the successful performance of conjuring tricks. One of the
first rules the aspiring conjuror learns is never to announce in advance
the specific outcome that he or she is going to produce. In this way
onlookers will not know where and on what they should focus their
attention and consequently will be less apt to detect the method by which
the trick was accomplished. The authors' advice to avoid focusing on a
poedetermined outcome greatly facilitates the conjuror's task.
The insistence that the arrangements meet with the psychic's approval
Sby far the most devastating of these conditions. Geller will perform
bly if the conditions are "aesthetically pleasing." This amounts to giving
alleged psychic complete veto power over any situation in which he
she feels that success is not ensured. This in turn means that the
Rychic being tested, not the experimenters, is controlling the experiment.
Brely the British physicists ought to realize the irony of their admission
at all their experimental arrangements designed to preclude trickery
tmirned out to be aesthetically unacceptable to Uri Geller.
Another example of beliefs generated in circumstances that are known
¿ create cognitive illustions is macro-PK, which is practiced at spoon-
bonding, or PK, parties. The 15 or more participants in a PK party, who
¡sually pay a fee to attend and bring their own silverware, are guided
through various rituals and encouraged to believe that, by cooperating
Sth the leader, they can achieve a mental state in which their spoons
ad forks will apparently soften and bend through the agency of their
Rinds.
@Since 1981, although thousands of participants have apparently bent
metal objects successfully, not one scientifically documented case of
franormal metal bending has been presented to the scientific community.
Wet participants in the PK parties are convinced that they have both
Fitnessed and personally produced paranormal metal bending. Over and
over again we have been told by participants that they know that metal
became paranormally deformed in their presence. This situation gives
the distinct impression that proponents of macro-PK, having consistently
failed to produce scientific evidence, have forsaken the scientific method
and undertaken a campaign to convince themselves and others on the
basis of clearly nonscientific data based on personal experience and
testimony obtained under emotionally charged conditions.
Consider the conditions that leaders and participants agree facilitate
spoon bending. Efforts are made to exclude critics because, it is asserted,
skepticism and attempts to make objective observations can hinder or
prevent the phenomena from appearing. As Houck, the originator of the
PK party, describes it, the objective is to create in the participants a
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peak emotional experience (Houck, 1984). To this end, various exercises
involving relaxation, guided imagery, concentration, and chanting are
performed. The participants are encouraged to shout at the silverware
and to "disconnect" by deliberately avoiding looking at what their hands
are doing. They are encouraged to shout Bend! throughout the party.
"To help with the release of that initial concentration, people are
encouraged to jump up or scream that theirs is bending, so that others
can observe." Houck makes it clear that the objective is to create a state
of emotional chaos. "Shouting at the silverware has also been added as
a means of helping to enhance the emotional level in a group. This
procedure adds to the intensity of the command to bend and helps create
pandemonium throughout the party."
A PK party obviously is not the ideal situation for obtaining reliable
observations. The conditions are just those which psychologists and
others have described as creating states of heightened suggestibility and
implanting compelling beliefs that may be unrelated to reality. It is beliefs
acquired in this fashion that seem to motivate persons who urge us to
take macro-PK seriously. Complete absence of any scientific evidence
does not discourage the proponents; they have acquired their beliefs
under circumstances that instill zeal and subjective certainty. Unfortu-
nately, it is just these circumstances that foster false beliefs.
DISCUSSION OF QUALITATIVE EVIDENCE
Our analysis of the evidence put before us indicates that even the most
solidly based arguments for the existence of paranormal phenomena fall
short of the currently accepted parapsychological standards. Even if the
best evidence had been collected according to acceptable scientific
standards, most proponents would have in fact remained convinced by
personal experiences and data that clearly fall far short of scientific
acceptability. We have looked at two examples to make clear why and
in what ways such failures to meet acceptable standards render the
corresponding arguments useless as evidence for the paranormal, even
though they have created compelling and strongly held beliefs in those
who have been exposed to them.
The examples illustrate how different ways of attempting to acquire
evidence for paranormal phenomena can depart from adequate standards.
These inadequacies become especially critical when we note that the
conditions under which the alleged paranormal phenomena are supposed
to occur are just those known to foster biases and false beliefs. The PK
parties, while creating powerful beliefs in paranormal metal bending,
clearly violate almost every principle for obtaining trustworthy data.
These parties offer no standardization, no objective records, and no
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controls against self-deception or the deliberate deception of others. All
participants, including the leader, are encouraged to achieve a peak
emotional state, and general chaos is encouraged.
The suggestions of a group of British physicists for testing alleged
psychics are aimed at somehow combining the desire to keep the psychic
from feeling inhibited with the desire to obtain evidence of acceptable
scientific quality. The observers' zeal for making the psychic feel trusted
produces conditions that make scientific observation impossible: observ-
er& are instructed to refrain from focusing attention on any expected
result, and the experimental arrangement must be aesthetically acceptable
toShe psychic, a condition that in effect puts the psychic in control of
theexperiment.
R000200320091
The search for psi-conducive conditions is understandable. Parapsy-
chological research, even at its best, has been continually frustrated by
thelack of robust, lawful, and repeatable outcomes, yet parapsychologists
h&e experienced phenomena or have encountered data that have con-
vinced them of the reality of the paranormal. When they try to put such
evidence before their critics, however, the phenomena have a habit of
disappearing. If one fervently believes that the phenomena are real, then
it becomes easy to imagine a variety of reasons why they are elusive and
hard to produce on demand.
"When proponents encounter a new phenomenon or psychic, they are
strongly motivated to create conditions that will not drive the phenomenon
atgay. The special atmosphere of PK parties and the suggestions of the
British physicists are just two examples of attempts to generate psi-
conducive conditions that also seem to be deception-conducive and bias-
conducive.
CONCLUSIONS
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In drawing conclusions from our review of evidence and other consid-
erAtions related to psychic phenomena, we note that the large body of
research completed to date does not present a clear picture. Overall, the
experimental designs are of insufficient quality to arbitrate between the
claims made for and against the existence of the phenomena. While the
best research is of higher quality than many critics assume, the bulk of
the work does not meet the standards necessary to contribute to the
knowledge base of science. Definitive conclusions must depend on
evidence derived from stronger research designs. The points below
summarize key arguments in this chapter.
1. Although proponents of ESP have made sweeping claims, not only
for its existence but also for its potential applications, an evaluation of
the best available evidence does not justify such optimism. The strongest
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claims have been made for remote viewing and the Ganzfeld experiments.
The scientific case for remote viewing is based on a relatively small
number of experiments, almost all of which have serious methodological
defects. Although the first experiments of this type were begun in 1972,
the existence of remote viewing still has not been established. Further-
more, although success rates varying from 30 to 60 percent have been
claimed for the Ganzfeld experiments, the evidence remains problematic
because all the experiments deviate in one or more respects from accepted
scientific procedures. In the committee's view, the best scientific evidence
does not justify the conclusion that ESP-that is, gathering information
about objects or thoughts without the intervention of known sensory
mechanisms-exists.
2. Nor does scientific evidence offer support for the existence of
psychokinesis-that is, the influence of thoughts upon objects without
the intervention of known physical processes. In the experiments using
random number generators, the reported size of effects is very small, a
hit rate of no more than 50.5 percent compared with the chance expectancy
of 50 percent. Although analysis indicates that overall significance for
the experiments, with their unusually large number of trials, is probably
not due to a statistical fluke, virtually all the studies depart from good
scientific practice in a variety of ways; furthermore, it is not clear that
the pattern of results is consistent across laboratories. In the committee's
view, any conclusions favoring the existence of an effect so small must
at least await the results of experiments conducted according to more
adequate protocols.
3. Should the Army be interested in evaluating further experiments,
the following procedures are recommended: first, the Army and outside
scientists should arrive at a common protocol; second, the research
should be conducted according to that protocol by both proponents and
skeptics; and third, attention should be given to the manipulability and
practical application of any effects found. Even if psi phenomena are
determined to exist in some sense, this does not guarantee that they will
have any practical utility, let alone military applications. For this to be
possible, the phenomena would have to obey causal laws and be
manipulable.
4. The committee is aware of the discrepancy between the lack of
scientific evidence and the strength of many individuals' beliefs in
paranormal phenomena. This is a cause for concern. Historically, many
of the the world's most prominent scientists have concluded that such
phenomena exist and that they have been scientifically verified. Yet in
just about all these cases, subsequent information has revealed that their
convictions were misguided. We also are aware that many proponents
believe that the scientific method may not be the only, or the most
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208
ENHANCING HUMAN PERFORMANCE
appropriate, method for establishing the reality of paranormal phenomena.
Unfortunately, the alternative methods that have been used to demonstrate
the existence of the paranormal create just those conditions that psy-
chologists have found enhance human tendencies toward self-deception
and suggestibility. Concerns about making the experimental situation
comfortable for the alleged psychic or conducive to paranormal phenom-
ena frequently result in practices that also increase opportunities for
deception and error.
R000200320001-18
SOURCES OF INFORMATION
wo of the military officers who briefed us during our first meeting
unged the committee to give serious consideration to paranormal phe-
n@nena and related parapsychological techniques. They described a
v&iety of such phenomena that they felt had military potential, either as
threats to security or as aids to defense. Site visits to leading laboratories
and a paper prepared for the committee also contributed to the bases for
the committee's work. Briefings were given to committee members by
Robert Jahn, Cleve Backster, Helmut Schmidt, members of the staff of
the Stanford Research Institute, and the U.S. Army Laboratory Command
ingAdelphi, Maryland. The paper prepared by James Alcock provided
detailed reviews of the available evidence on random event generators
andremote viewing. In addition, the committee benefited from a thorough
review conducted for the Army Research Institute by John Palmer and
from its own review of recent articles in the Journal of Parapsychology
andother relevant periodicals and handbooks.
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206
ENHANCING HUMAN PERFORMANCE
controls against self-deception or the deliberate deception of others. All
participants, including the leader, are encouraged to achieve a peak
emotional state, and general chaos is encouraged.
The suggestions of a group of British physicists for testing alleged
psychics are aimed at somehow combining the desire to keep the psychic
from feeling inhibited with the desire to obtain evidence of acceptable
scientific quality. The observers' zeal for making the psychic feel trusted
produces conditions that make scientific observation impossible: observ-
ergare instructed to refrain from focusing attention on any expected
realt, and the experimental arrangement must be aesthetically acceptable
to ge psychic, a condition that in effect puts the psychic in control of
theexperiment.
The search for psi-conducive conditions is understandable. Parapsy-
ch@logical research, even at its best, has been continually frustrated by
thelack of robust, lawful, and repeatable outcomes, yet parapsychologists
have experienced phenomena or have encountered data that have con-
vinged them of the reality of the paranormal. When they try to put such
evidence before their critics, however, the phenomena have a habit of
disappearing. If one fervently believes that the phenomena are real, then
it becomes easy to imagine a variety of reasons why they are elusive and
hard to produce on demand.
When proponents encounter a new phenomenon or psychic, they are
strongly motivated to create conditions that will not drive the phenomenon
away. The special atmosphere of PK parties and the suggestions of the
Brish physicists are just two examples of attempts to generate psi-
cducive conditions that also seem to be deception-conducive and bias-
conducive.
CONCLUSIONS
Approved For Release 2002/851
gh drawing conclusions from our review of evidence and other consid-
erations related to psychic phenomena, we note that the large body of
research completed to date does not present a clear picture. Overall, the
experimental designs are of insufficient quality to arbitrate between the
claims made for and against the existence of the phenomena. While the
best research is of higher quality than many critics assume, the bulk of
the work does not meet the standards necessary to contribute to the
knowledge base of science. Definitive conclusions must depend on
evidence derived from stronger research designs. The points below
summarize key arguments in this chapter.
1. Although proponents of ESP have made sweeping claims, not only
for its existence but also for its potential applications, an evaluation of
the best available evidence does not justify such optimism. The strongest
207
PARANORMAL PHENOMENA
claims have been made for remote viewing and the Ganzfeld experiments.
The scientific case for remote viewing is based on a relatively small
number of experiments, almost all of which have serious methodological
defects. Although the first experiments of this type were begun in 1972,
the existence of remote viewing still has not been established. Further-
more, although success rates varying from 30 to 60 percent have been
claimed for the Ganzfeld experiments, the evidence remains problematic
because all the experiments deviate in one or more respects from accepted
scientific procedures. In the committee's view, the best scientific evidence
does not justify the conclusion that ESP-that is, gathering information
about objects or thoughts without the intervention of known sensory
mechanisms-exists.
2. Nor does scientific evidence offer support for the existence of
psychokinesis-that is, the influence of thoughts upon objects without
the intervention of known physical processes. In the experiments using
random number generators, the reported size of effects is very small, a
hit rate of no more than 50.5 percent compared with the chance expectancy
of 50 percent. Although analysis indicates that overall significance for
the experiments, with their unusually large number of trials, is probably
not due to a statistical fluke, virtually all the studies depart from good
scientific practice in a variety of ways; furthermore, it is not clear that
the pattern of results is consistent across laboratories. In the committee's
view, any conclusions favoring the existence of an effect so small must
at least await the results of experiments conducted according to more
adequate protocols.
3. Should the Army be interested in evaluating further experiments,
the following procedures are recommended: first, the Army and outside
scientists should arrive at a common protocol; second, the research
should be conducted according to that protocol by both proponents and
skeptics; and third, attention should be given to the manipulability and
practical application of any effects found. Even if psi phenomena are
determined to exist in some sense, this does not guarantee that they will
have any practical utility, let alone military applications. For this to be
possible, the phenomena would have to obey causal laws and be
manipulable.
4. The committee is aware of the discrepancy between the lack of
scientific evidence and the strength of many individuals' beliefs in
paranormal phenomena. This is a cause for concern. Historically, many
of the the world's most prominent scientists have concluded that such
phenomena exist and that they have been scientifically verified. Yet in
just about all these cases, subsequent information has revealed that their
convictions were misguided. We also are aware that many proponents
believe that the scientific method may not be the only, or the most
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208
ENHANCING HUMAN PERFORMANCE
appropriate, method for establishing the reality of paranormal phenomena.
Unfortunately, the alternative methods that have been used to demonstrate
the existence of the paranormal create just those conditions that psy-
chologists have found enhance human tendencies toward self-deception
and suggestibility. Concerns about making the experimental situation
comfortable for the alleged psychic or conducive to paranormal phenom-
ena frequently result in practices that also increase opportunities for
deception and error.
79IR808280320001-1
SOURCES OF INFORMATION
wo of the military officers who briefed us during our first meeting
U
ena and related parapsychological techniques. They described a
ty of such phenomena that they felt had military potential, either as
od the committee to give serious consideration to paranormal phe-
nor
va
thr
Pats to security or as aids to defense. Site visits to leading laboratories
anPa paper prepared for the committee also contributed to the bases for
theCommittee's work. Briefings were given to committee members by
Robert Jahn, Cleve Backster, Helmut Schmidt, members of the staff of
the stanford Research Institute, and the U.S. Army Laboratory Command
in @delphi, Maryland. The paper prepared by James Alcock provided
detailed reviews of the available evidence on random event generators
and remote viewing. In addition, the committee benefited from a thorough
review conducted for the Army Research Institute by John Palmer and
from its own review of recent articles in the Journal of Parapsychology
and other relevant periodicals and handbooks.
Approved For Release 2002/05/47 €1.
.
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NATIONAL ACADEMY PRESS . 2101 Constitution Avenue, NW . Washington, DC 20418
NOTICE: The project that is the subject of this report was approved by the Governing
Board of the National Research Council, whose members are drawn from the councils of
the National Academy of Sciences, the National Academy of Engineering, and the Institute
of Medicine. The members of the committee responsible for the report were chosen for
their special competences and with regard for appropriate balance.
This report has been reviewed by a group other than the authors according to procedures
approved by a Report Review Committee consisting of members of the National Academy
of Sciences, the National Academy of Engineering, and the Institute of Medicine.
The National Academy of Sciences is a private, nonprofit, self-perpetuating society of
distinguished scholars engaged in scientific and engineering research, dedicated to the
furtherance of science and technology and to their use for the general welfare. Upon the
auth ty of the charter granted to it by the Congress in 1863, the Academy has a mandate
that requires it to advise the federal government on scientific and technical matters. Dr.
Fran&Press is president of the National Academy of Sciences.
TheNational Academy of Engineering was established in 1964, under the charter of the
National Academy of Sciences, as a parallel organization of outstanding engineers. It is
auto@mous in its administration and in the selection of its members, sharing with the
National Academy of Sciences the responsibility for advising the federal government. The
National Academy of Engineering also sponsors engineering programs aimed at meeting
national needs, encourages education and research, and recognizes the superior achieve-
menof engineers. Dr. Robert M. White is president of the National Academy of
Enginbering.
The Institute of Medicine was established in 1970 by the National Academy of Sciences
to secure the services of eminent members of appropriate professions in the examination
of percy matters pertaining to the health of the public. The Institute acts under the
responsibility given to the National Academy of Sciences by its congressional charter to
be an adviser to the federal government and, upon its own initiative, to identify issues of
medical care, research, and education. Dr. Samuel O. Thier is president of the Institute of
Medicine.
The National Research Council was organized by the National Academy of Sciences in
191640 associate the broad community of science and technology with the Academy's
purposes of furthering knowledge and advising the federal government. Functioning in
accordance with general policies determined by the Academy, the Council has become the
princ al operating agency of both the National Academy of Sciences and the National
Academy of Engineering in providing services to the government, the public, and the
scientific and engineering communities. The Council is administered jointly by both
Acadeinies and the Institute of Medicine. Dr. Frank Press and Dr. Robert M. White are
chairman and vice chairman, respectively, of the National Research Council.
Library of Congress Cataloging-in-Publication Data
EnhaRing human performance : issues, theories, and techniques
1
Dalliel Druckman and John A. Swets, editors.
b.
cm.
Committee on Techniques for the Enhancement of Human Performance,
Commission on Behavioral and Social Sciences and Education, National
Research Council."
Beliography: p.
Includes index.
ISBN 0-309-03792-1.
ISBN 0-309-03787-5 (soft)
1. Self-realization-Congresses. 2. Performance-Psychological
aspects-Congresses. I. Druckman, Daniel, 1939-
II. Swets,
John Arthur, 1928-
III. National Research Council (U.S.).
Committee on Techniques for the Enhancement of Human Performance.
BF637.S4E56 1987
158-dc19
87-31233
CIP
Copyright @ 1988 by the National Academy of Sciences
Printed in the United States of America
COMMITTEE ON TECHNIQUES FOR THE
ENHANCEMENT OF HUMAN PERFORMANCE
JOHN A. SWETS, Chair, Bolt Beranek and Newman Inc., Cambridge,
Mass.
ROBERT A. BJORK, Department of Psychology, University of
California, Los Angeles
THOMAS D. COOK, Department of Psychology, Northwestern
University
GERALD C. DAVISON, Department of Psychology, University of
Southern California
LLOYD G. HUMPHREYS, Department of Psychology, University of
Illinois
RAY HYMAN, Department of Psychology, University of Oregon
DANIEL M. LANDERS, Department of Physical Education, Arizona
State University
SANDRA A. MOBLEY, Director of Training and Development, The
Wyatt Company, Washington, D.C.
LYMAN W. PORTER, Graduate School of Management, University of
California, Irvine
MICHAEL I. POSNER, Department of Neurology, Washington
University
WALTER SCHNEIDER, Department of Psychology, University of
Pittsburgh
JEROME E. SINGER, Department of Medical Psychology, Uniformed
Services University of Health Sciences, Bethesda, Md.
SALLY P. SPRINGER, Department of Psychology, State University of
New York, Stony Brook
RICHARD F. THOMPSON, Department of Psychology, Stanford
University
DANIEL DRUCKMAN, Study Director
JULIE A. KRAMAN, Administrative Secretary
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iit

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Contents
PREFACE
vii
Į
OVERVIEW
1
Introduction
3
1
2
Findings and Conclusions
15
3
Evaluation Issues
24
II
PSYCHOLOGICAL TECHNIQUES
37
4
Learning
39
5
Improving Motor Skills
61
6
Altering Mental States
102
7
Stress Management
115
8
Social Processes
133
III PARAPSYCHOLOGICAL TECHNIQUES
167
9 Paranormal Phenomena
169
REFERENCES
209
APPENDIXES
233
A Summary of Techniques: Theory, Research, and
Applications
235
B Background Papers
246
C Committee Activities
248
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V

vi
CONTENTS
D
Key Terms
252
E
Military Applications of Scientific Information
262
F
Biographical Sketches
282
INDEX
289
.
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Preface
The Army Research Institute in 1984 asked the National Academy of
Sciences to form a committee to examine the potential value of certain
techniques that had been proposed to enhance human performance. As
a class, these techniques were viewed as extraordinary, in that they were
developed outside the mainstream of the human sciences and were
presented with strong claims for high effectiveness. The committee was
also to recommend general policy and criteria for future evaluation of
enhancement techniques by the Army.
The Committee on Techniques for the Enhancement of Human Per-
formance first met in June 1985. The 14 members of the committee were
appointed for their expertise in areas related to the techniques examined.
The disciplines they represent include experimental, physiological, clin-
ical, social, and industrial psychology and cognitive neuroscience; one
member is a training program director from the private sector. During
the next two years, the committee gathered six times, met in toto or in
part on several occasions with various representatives of the Army,
conducted interviews and site visits and sent subcommittees on several
others, and commissioned 10 analytical and survey papers. The committee
also examined a variety of materials, including state-of-the-art reviews
of relevant literature, reports commissioned by the Army Research
Institute, and unpublished documents provided by institutes, practition-
ers, and researchers. The report that follows describes the committee's
activities, findings, and conclusions. Though cast largely in terms of the
sponsor's setting, this report is relevant to other settings, for example,
industry. The next few paragraphs present some background.
vii
1
.
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ix
viii
PREFACE
That the United States Army should be concerned to enhance the
performance of its personnel is self-evident. We know that young
volunteers must become not only soldiers who do well in battle but also
technicians who skillfully operate and maintain complex equipment in
peace and war. We are aware, moreover, that personal skills are not
enough: individuals are heavily dependent on each other within small
groups, and groups of various sizes must work very effectively together
to permit survival and ensure success. And, of course, all must be ready
to-give peak performances in situations of great hardship, uncertainty,
ard stress. In the face of these staggering requirements, one must realize
that turnover of personnel is high and that the training time available-
toompart the necessary cognitive, physical, and social skills-is brief.
RDP96-06791R090200320601-1
do it comes as no surprise that the Army is on the lookout for techniques
that can help enhance human performance. The Army Research Institute
ischarged with seeking out and developing such techniques: it does so
bygemploying researchers in the human sciences and by supporting
appropriate research in universities and other public and private organi-
zafons. It focuses largely on promising new techniques as they appear
ingthe mainstream of behavioral, physiological, and social research.
Havever, given the pressures and given a view of mainstream research
as low, narrow, and insufficiently targeted, it also comes as no surprise
that some influential officers and certain segments of the Army want to
cast a broader net to snare promising enhancement techniques. To do
this, they look beyond traditional research organizations and practices
towhat are viewed as extraordinary techniques. These techniques are
thought possibly to provide such unusual benefits as accelerated learning,
leagning during sleep, superior performance through altered mental states,
better management of behavior under stress, more effective ways of
infencing other people, and so on. There is also an initiative within the
ArBy to consider techniques based on paranormal phenomena, for
example, extrasensory perception to view remote sites and psychokinesis
to influence the operation of distant machines.
Along with these urgings to examine, to try, or to implement extraor-
dinary techniques come difficult new problems for those in the Army
responsible for evaluation, as well as for those in the Army responsible
for personnel and training practices. One issue is that proponents of such
techniques are usually not content with traditional evaluation procedures
or scientific standards of evidence, often giving more weight to personal
experience and testimony. Furthermore, a typical technique of this kind
does not arise from the usual research traditions of experiments published
in refereed journals and peer review of cumulated evidence, but rather
appears full-blown as a package promoted by a commercial vendor. What
does the Army Training and Doctrine Command or the base commander
PREFACE
do when the need is great, the package is ready, the claims are for
miracles, some senior officers are vocally supportive, and the evaluation
criteria are fluid? What do Army intelligence agencies do when the same
conditions apply and other nations are said to be active in investigating
paranormal effects?
The committee decided to assess a representative set of the techniques
in question and resolved to address the surrounding issues in an open-
minded and thorough way. We therefore divided ourselves into a number
of subcommittees organized according to the behavioral processes ad-
dressed by the several techniques: accelerated learning, sleep learning,
guided imagery, split-brain effects, stress management, biofeedback,
influence strategies, group cohesion, and parapsychology. In addition, a
subcommittee on evaluation issues was formed to examine practices and
standards relevant to all the techniques. Each chapter of the report was
prepared by the appropriate subcommittee, but interactions were frequent
and so the report represents a collaborative effort of all the members.
Chapter 1 provides a context for the committee's task and the Army's
interest in enhancing performance, characterizes some particular tech-
niques, and introduces some general issues in evaluating them. Chapter
2 presents the committee's findings about the techniques examined and
conclusions about appropriate evaluation procedures. Chapter 3 treats
the relevant evaluation issues more systematically and presents the
committee's philosophy of evaluation as it pertains to the matter at hand.
Chapters 4 through 8 deal with particular techniques but are organized
in terms of more general psychological processes. Chapter 9 considers
parapsychological techniques.
The report concludes with six appendixes. Appendix A briefly sum-
marizes the key elements of each enhancement technique. Appendix B
lists the ten papers commissioned by the committee and their authors.
Appendix C lists the members and activities of the subcommittees and
also the activities of the committee as a whole. Appendix D lists key
terms used in the research on particular techniques. Appendix E discusses
the application of scientific research by the military. Appendix F contains
biographical sketches of the committee members.
As committee chair, I am now in the pleasant position of recounting
the several contributors to the total committee process, a process that
went remarkably well. Definition and guidance for the committee's task
came primarily from Edgar M. Johnson, director of the Army Research
Institute. Administrative and technical liaison was ably provided by
project monitor George Lawrence, who worked closely with the com-
mittee in its various activities. They were supported well by several
senior Army officers, including Colonel William Darryl Henderson,
Commander of the Army Research Institute; Major General John Crosby,
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x
PREFACE
Assistant Deputy Chief of Staff for Personnel; and General Maxwell R.
Thurman, Vice Chief of Staff. The committee met with members of a
resource advisory group that included Lieutenant General Robert M.
Elton, chair, Deputy Chief of Staff for Personnel; Lieutenant General
Sidney T. Weinstein, Assistant Chief of Staff for Intelligence; Dr. Louis
M. Cameron, Director of Army Research and Technology; Major General
Maurice O. Edmunds, Commander of the Soldier Support Center; and
Major General Philip K. Russell, Commander of the Medical Research
and Development Command. Among the Army staff who were very
hapful to the committee are Colonel John Alexander and Mr. Robert
Klaus; the names of many others appear in Appendix C.
31809020032000
The committee's two consultants contributed special expertise: Paul
Førwitz (of Bolt Beranek and Newman Inc.) joined the site visits of the
soocommittee on parapsychology and advised on physical aspects of
experiments in that area; James Schroeder (of Southwest Research
Institute) attended the committee's meeting at Fort Benning, Georgia,
advised on the application of scientific research by the military (see
Appendix E). The committee also received special expertise by commis-
signing papers. These papers and their authors are listed in Appendix B.
At the National Research Council, David Goslin, executive director of
the Commission on Behavioral and Social Sciences and Education, once
again provided wise counsel and support. Ira Hirsh, commission chair,
and William Estes, also representing the commission, gave valuable
advice and encouragement. Thomas Landauer, a member of the NRC's
Committee on Human Factors, provided liaison in the areas of our
committees' mutual interests. The reviewers of this report gave us a good
measure of reinforcement along with helpful critiques. Eugenia Grohman,
associate director for reports, lent experience and wisdom to this report.
Special gratitude is extended to Christine McShane, the commission's
ed gor: her skillful editing of the entire manuscript contributed substantially
to #s readability, and the coherence of the volume owes much to her
suggestions for organizing the material. Julie Kraman, as administrative
secretary to the committee, earned its considerable appreciation for
setting up efficient meetings and for handling all manner of tasks graciously
and smoothly.
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Daniel Druckman, study director of the project, receives the commit-
teea great appreciation for his intellectual contributions across the broad
range of topics considered as well as for his logistic support. Working
closely with the authors of chapters and commissioned papers, he provided
an integration of the several contributions as well as much of the
introductory and interstitial material. He also served on two subcommit-
tees in areas of his expertise.
The ultimate debt of anyone who finds this report useful, and my large
xi
.
PREFACE
personal debt, is to the members of the committee. As individuals, their
capabilities are broad and deep. As a group, they gave generously and
productively of their time, were always engaged, responded to every
challenge, and, especially, showed an exceptional talent for reaching
consensus in a collegial, advised, and efficient way.
JOHN A. SWETS, Chair
Committee on Techniques for the
Enhancement of Human Performance
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--
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PART
I
Overview
PART I CONSISTS OF THREE CHAPTERS. Chapter 1 sets the stage for the
report. It describes the committee's task, provides background on
the Army's interest in enhancement techniques, characterizes specific
techniques examined by the committee, and identifies the main issues in
evaluating the relation between techniques and human performance .!
Chapter 2 presents the committee's findings and conclusions. We draw
general conclusions about the process of consideration given to any
technique and state specific findings and conclusions for each of the areas
of human performance examined.
Chapter 3 presents the committee's philosophy of evaluation as it
pertains to enhancement techniques. Some of the issues involved concern
the conduct of basic research; others concern the conduct of field tests.
With respect to basic research, issues include the plausibility of inferences
about novel concepts, causation, alternative explanations of causal
relations, and the generalizability of causal relations. With respect to
field tests, a number of questions are of interest: Does the enhancement
program meet genuine Army needs? Is the resulting program implement-
able, given program design and resources? Do unintended side effects
limit utility? Is the program more cost-effective than its alternatives?
These questions underscore the reality that evaluation research is largely
a pragmatic activity influenced by the organizational context in which it
occurs.
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1
Introduction
THE COMMITTEE'S TASK
At the request of the U.S. Army Research Institute, the National
Research Council formed a committee to assess the field of techniques
that are claimed to enhance human performance. The Institute asked the
Council to evaluate the claims made by proponents of selected existing
techniques and to address two general additional questions: (1) What are
the appropriate criteria for evaluating claims for such techniques in the
future? (2) What research is needed to advance our understanding of
performance enhancement in areas related to the proposed techniques?
The objectives of the committee's study are to provide an authoritative
assessment of these questions for policymakers in research and devel-
opment who are consumers of the techniques, as well as to consider their
possible applications to Army training.
Many of the techniques under consideration grew out of the human
potential movement of the 1960s, including guided imagery, meditation,
biofeedback, neurolinguistic programming, sleep learning, accelerated
learning, split-brain learning, and various techniques to reduce stress and
increase concentration. Many of these techniques have gained popularity
over the past two decades, promoted by persons eager to provide answers
to problems of human performance or to prosper from them. While often
using the language of science to justify their approach, these promoters
are for the most part not trained professionals in the social and behavioral
sciences. Nonetheless, they do appeal to basic needs for human perform-
ance, and the Army, like many other institutions, is attracted to the
prospect of cost-effective procedures that can improve performance.
3
.
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4
ENHANCING HUMAN PERFORMANCE
These institutions must evaluate the effects of such procedures, however.
Issues include the appropriateness of a quick-fix approach, the distinction
between the impact of an experience and actual change, and the plausibility
of evidence indicating that something is happening even if the effects are
not reproducible or the benefits uncertain.
A more conservative atmosphere in the 1980s is reflected in the way
techniques are advanced. Motivation in the 1980s may be primarily
entrepreneurial, not ideological, as it was in the 1960s. Advocates focus
onrelating the techniques to specific tasks, such as marksmanship, foreign
laguage acquisition, fine motor skills, sleep inducement, and even combat
effectiveness. Some techniques are in fact rooted in a scientific literature.
Fof these reasons the various techniques have attracted the interest of
ingitutions that have rejected, and would probably continue to reject,
contercultural trends in society. Indeed, much attention has been given
toThese techniques by industrial, government, and military policymakers,
as well as by the general public. For this reason especially, it is important
to address the issues surrounding the claims made for effectiveness.
elaborate training programs have grown, nourished by their developers'
erffhusiasm and salesmanship in a social context receptive to quick cures.
For many of these programs, success in the marketplace is used to justify
th@approaches. For others, more esoteric concepts, including the role
of neurotransmitters, the physics of neuromuscular programming, brain
wave patterns, hemispheric laterality, high-access memory storage, pre-
ferred sensory modalities, and low-gain innervation of muscles, are used
to Attempt to provide scientific justification for the claims. The chapters
thefollow evaluate the evidence and theories used to support the claims
of Several popular techniques. Before turning to these evaluations,
hoRever, we provide some background on the Army's interest in these
techniques, as well as a discussion of issues surrounding enhanced
performance and issues in evaluating the relation between techniques
andoperformance.
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THE ARMY'S NEEDS
The Army motto, "Be all that you can be," symbolizes the current
eth@ of the institution, an army of excellence. Emphasis is placed on
attaging certain ideals, such as fearlessness, cunning, courage, one-shot
effectiveness, fatigue reversal, and nighttime fighting capabilities. These
ideals are assumed to be realizable through training, even if the most
effective techniques have not as yet been identified. The culture of
improvement is further reinforced by the dilemma created by an all-
volunteer Army and the demands of complex new computer technologies.
Many civilians enter military service with only the required minimum of
5
INTRODUCTION
formal education; most of these volunteers enlist in the Army. For this
reason, the Army's emphasis on skill training is well founded.
The importance of the human element in combat is recognized in the
Army Science Board's 1983 report "Emerging Concepts in Human
Technology," which phrases the issue in terms of high yield at relatively
low investment. Human capital is considered to be the best potential
source for growth in Army effectiveness, both in terms of return on
investment and as a moral imperative "if we are to commit our soldiers
to fight outnumbered and win." The technologies singled out in the report
are those that can improve creativity and innovation, learning and training,
motivation and cohesion, leadership and management, individual, crew,
and unit fitness, soldier-machine interface, and the general productivity
of the Army's human resources.
The Board's report largely bypasses issues of systematic evaluation of
enhancement techniques within the Army context, while addressing
mechanisms for integrating them with Army activities. Little concern is
shown for adducing relevant criteria to determine whether implementation
is feasible. The Army's ambitious goals, combined with a reluctance to
deal with the complexities surrounding issues of human performance,
make this institution potentially susceptible to a variety of claims made
by technique developers. It would therefore seem prudent to devise
criteria for evaluating those claims.
A SELLER'S MARKET
Techniques for enhancement of human performance have received
much attention in the popular press. They have been actively promoted
by entrepreneurs who sense a profitable market in self-improvement. The
American Society for Training and Development "estimates that com-
panies are spending an astounding $30 billion a year on formal courses
and training programs for workers. And that's only the tip of the iceberg"
(Wall Street Journal, August 5, 1986). They are also taken seriously by
the U.S. military, who are at times accused of losing the "mind race"
to the Soviets (see, for example, Anderson and Van Atta, Washington
Post, July 17, 1985). The Army has shown particular interest in techniques
that help people acquire, maintain, or improve such skills as classroom
learning, communication and influence, creativity, and accuracy in the
execution of tasks requiring motor skills. Those that are cost-effective
and produce relatively rapid results are likely to receive the most attention,
along with research breakthroughs that could be a basis for new training
programs. What are these techniques? What claims are being made for
them? Is there evidence that substantiates these claims?
Examples of techniques include biofeedback (information about internal
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ENHANCING HUMAN PERFORMANCE
processes), Suggestive Accelerative Learning and Teaching Techniques
(a package of methods geared primarily toward classroom learning),
hemispheric synchronization (a machine-aided process based on assump-
tions about right brain-left brain activities), neurolinguistic programming
(procedures for influencing another person), and Concentrix (a procedure
used to improve concentration on specific targets). Also of interest to
the Army are such processes as group cohesion and stress reduction, as
well as the claims for sleep learning, peak performance, and parapsy-
chology. Together, these techniques and processes cover the major types
o
skills-motor, cognitive, and social. Several of them are described
hexe briefly, along with illustrative claims found in brochures and course
material.
CIA RDP36 007918000200320008-1
Suggestive Accelerative Learning and Teaching Techniques (SALTT)
isoan approach to training that employs a combination of physical
relaxation, mental concentration, guided imagery, suggestive principles,
add baroque music with the intent of improving classroom performance.
Some applications have included language training, typing instruction,
and high school science courses. Attempts have been made to evaluate
the applications, and many of these evaluations are published in the
Jaurnal of the Society for Accelerative Learning and Teaching (Psy-
chology Department, Iowa State University). The following is a sampling
of claims made in brochures and convention announcements: "A proven
method which has broad potential application in U.S. Army training";
It will significantly reduce training time, improve memory of material
learned and introduce behavioral changes that positively affect soldier
performance-self-esteem, self-confidence, and mental discipline"; and
Slost students will prove to themselves that they have learned a far
greater amount of material per unit of time with a greater amount of
pleasure than they have ever previously done."
"Approved ForRelease 2002208/17
Neurolinguistic programming (NLP) refers to a set of procedures
developed to influence and change the behaviors and beliefs of a target
person. Its goals are mostly therapeutic, but its proponents also advocate
the use of the techniques in advertising, management, education, and
interpersonal activities. A small research literature, published primarily
in the Journal of Counseling Psychology, has developed. Practitioners
can be trained and certified at various institutes, and the National
Association for Neurolinguistic Programming distributes a newsletter to
its membership, currently about 500 persons. Illustrative claims and
testimonials found in advertising materials include: "[NLP] has evolved
a unique technology which encompasses a set of specific techniques
enabling you to produce well-defined results" and "NLP ... is clear,
easy to learn, and brilliant." A typical slogan is that found in a brochure
from the Potomac Institutes, Silver Spring, Maryland: "The difference
7
INTRODUCTION
that makes the difference, for education, management, psychotherapy,
psychiatry, business, law, health care, and the arts."
Hemi-Synco), which is short for hemispheric synchronization, is a
technique that consists of presenting two tones slightly differing in
frequency to separate ears with stereo headphones to produce binaural
beats. The long-known result is a tone that waxes and wanes at a
frequency equal to the difference between the original tones. Pioneered
as an enhancement technique by Robert Monroe of the Monroe Institute
of Applied Science in Faber, Virginia, the technique is based on the
assumption of a frequency following response (FFR) in the human brain.
The FFR refers to a correspondence between sound signals heard by the
ear and electrical signals recorded by an electroencephalograph (EEG).
It is claimed that, by altering sound patterns, it is possible to alter states
. of awareness. Stated applications are in the areas of language learning,
stress management, reading skills, and creativity and problem solving.
Claims of effectiveness stated in the Monroe Institute's brochure are
wide-ranging, covering education (e.g., "77.8 percent of a class reported
improvement in mental-motor skills"), health (early recuperation, lower
blood pressure), psychotherapy (stress reduction, working with terminally
ill patients, teaching autistic children), and sleep restorative training (e.g.,
"forty of forty-five insomniacs reported that one-month use of Hemi-
Sync@ tapes was at least as effective as medication, without the drug
side effects").
SyberVision® is a scripted videotape that presents an expert (e.g., a
world-class athlete) repeatedly performing fundamental skills of his or
her activity (e.g., golf) without verbal instructions. It is based loosely on
principles of vicarious learning, guided imagery, and mental rehearsal.
Developed and marketed by SyberVision Systems Inc., San Leandro,
California, the package includes a cassette and instruction manual with
an appendix on the "simple physics of neuro-muscular programming."
The appendix presents a scientific rationale for the technique, for example,
"the more you see and hear pure movement, the deeper it becomes
imprinted in your nervous system ... and the more likely you are to
perform it as a conditioned reflex," and "The decomposition of what is
seen and sensorily experienced into an electromagnetic wave form is
accomplished by a complex mathematical operation (Fourier Transform)
by the brain" (Instruction Manual on Golf with Patty Sheehan). Support
for enhanced performance is, however, based on testimonials rather than
experiments, for example, Killy on skiing, a Stanford tennis coach on
tennis, Professional Golf Association members on golf, Peters (In Search
of Excellence) on achievement, Salk on leadership, and a variety of
corporate executives and educators on self-improvement. Claims range
from sweeping statements (e.g., "We owe these two men a large debt of
.
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8
ENHANCING HUMAN PERFORMANCE
gratitude") to rather precise statements (e.g., "In 47 days I have lost 25
pounds [191 to 166], yet I look like I lost 40") (in the United Airlines
magazine, Discoveries). This technique involves a significant marketing
effort that builds on users' willingness to be quoted and the use of
acknowledged academic experts (e.g., Stanford neuropsychologist Karl
Pribram), whose role in the program is advertised as being central.
Stress management techniques are procedures designed to alleviate
anxiety or tension. Catering to an age of anxiety, self-help books, groups,
ad clinics on managing stress proliferate. A good example of the approach
igthe recent book by Charlesworth and Nathan (1982), which emphasizes
@;ness, nutrition, managing time, general life-styles and life-cycles, as
Sell as strategies such as progressive relaxation, autogenic training, and
ilage rehearsal. Appendixes provide the reader with home practice
Harts, a guide to self-help groups, and suggested books and recordings.
The groups offer their members information, emotional support, and a
@nse of belonging. Often stress management procedures are combined
gth a number of other techniques into a single package. The promoters
often emphasize the total package rather than particular techniques; the
ackages usually combine several processes that, when acting together,
thought to produce significant effects.
Be-2002705/17 &CIA-RDF96.00791R
The Army's needs for techniques that can improve performance make
issubject to the sorts of claims illustrated above. While they and other
consumers can avoid the more obvious pitfalls, the proliferation of choices
and products and the lack of scientific evidence allow marketplace criteria
to become the bases for decisions. But there are exceptions. Some
techniques have received the attention of the scientific community, and
Sidence is available to be used as criteria in such areas as biofeedback,
guided imagery, sleep learning, cohesion, and even for some aspects of
poychic phenomena and neurolinguistic programming.
@The literature has alerted us, for example, to the distinction between
the effects of biofeedback on fine motor skills and on stress, to the
different effects of mental and physical rehearsal, to placebo and Haw-
thorne effects in stress research, to the priming and repetition effects of
nigaterial presented during sleep, to some dysfunctions of group cohesion,
te the difficulties of replicating experiments on extrasensory perception,
agd to the implausibility of specialized sensory modalities as postulated
b& NLP (see Appendix D for key terms). These findings make evident a
complex relation between technique and performance.
IMPROVED PERFORMANCE:
COMPLEX ISSUES, SIMPLE SOLUTIONS
The research literature in such traditional areas of experimental psy-
chology as learning, perception, sensation, and motivation suggests
INTRODUCTION
complex relations between interventions and improved performance.
Many technique promoters appear to pay little attention to this literature,
preferring an alternative route to invention: rather than derive a procedure
from appropriate scientific literature, they create techniques from personal
experiences, sudden insights, or informal observation of "what works."
Science may enter the process after the technique is developed and used,
for example, to legitimize its use or to endorse methods for evaluation.
Research follows rather than precedes the invention. This sequence,'
increases the likelihood that important considerations will be missed. We
highlight some of these considerations in this section.
The lack of easy avenues to improved performance may well be due
to the complexity of the behavior in question. One definition of skills
emphasizes the importance of the coordination of behavior: "A skilled
response ... means one in which receptor-effector-feedback processes
are highly organized, both spatially and temporally. The central problem
for the study of skill learning is how such organizations or patterning
comes about" (Fitts, 1964:244). This definition implies that skill learning
involves an orchestration of diverse processes, making the topic an
interesting one to various subfields of psychology. It also makes evident
a, number of unresolved issues, including whether different skills are
learned and retained in different ways. The research findings obtained in
this literature contribute to our understanding of the necessary, if not
sufficient, conditions for improved performance.
Research on skill acquisition addresses such basic questions as What
are the stages of learning? and What is learned? Distinctions made
between short-term and long-term memory storage and between schemas
and details have contributed to our understanding of basic processes (see
Welford, 1976). Other questions have more direct consequences for
application: for example, what contributes to the acquisition and main-
tenance of skills? How can the adverse effects of stress, fatigue, and
monotony be avoided? These questions are the basis for programs of
research that can be divided into several parts, each defined in terms of
empirical issues (Irion, 1969; see also the other chapters in Bilodeau and
Bilodeau, 1969). Some examples of empirical issues are practice effects
(differences due to distributed versus massed practice, long versus short
rest periods, short versus long sessions), the whole-part problem (differ-
ences due to learning a task as a whole versus learning it by its constituent
elements), feedback (differences due to delays in receiving knowledge of
results and to type of information during the delay period), retention
(differences due to whether the the task is motor or verbal), and transfer
of training.
These and related considerations suggest that skill learning is an
incremental process likely to differ from one type of skill to another.
Whether intending to enhance motor, verbal, problem-solving, or social
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ENHANCING HUMAN PERFORMANCE
performances, technique designers can ill afford to ignore these lessons
from the experimental literature on skill acquisition and maintenance. It
is also the case, however, that the agenda of unexplored issues is much
larger than the accomplishments to date, and this is recognized particularly
in the rapidly growing field of cognitive psychology, in which the
"information-processing revolution" is just beginning.
6-00791R000200320001-1
Practical applications are, however, not automatic. Many excellent
applications do not spring from basic science; some are the result of craft
End experience. More important perhaps are the indirect contributions
Made in both directions-from basic to applied and vice versa. A
Systematic approach taken in both domains serves to vitalize each, as
Chen applied investigations reveal new phenomena that need explanation
when a new package incorporates basic principles discovered originally
the laboratory. Such an approach is likely to facilitate the design of
Appropriate techniques for skill acquisition. At issue is whether a particular
technique can produce and sustain desired changes.
One conclusion from the research accumulated to date is that effective
Aterventions are those that are continuous and self-regulating and take
Account of both context and person (see, for example, Lerner, 1984).
Particularly relevant is the difference between short-term and long-term
changes. Effects obtained by many techniques for performance enhance-
@ent may be short-term in their effects. This distinction is made by Back
([973, 1987) in his evaluation of the sensitivity training movement. The
changes observed by sensitivity trainers and documented by evaluators
may well reflect the impact of the experience per se. Such situation
effects are unlikely to be sustained in different environments, an obser-
Ation supported by the literatures in both developmental and social
psychology (Druckman, 1971; Frederiksen, 1972). These literatures cau-
toon against hasty generalizations from observed, situation-specific effects;
jey also explain why long-term effects may be difficult to produce with
Grief exposures to "treatments." Like the sensitivity trainers of the 1960s
ad 1970s, many of the promoters (and consumers) of the 1980s pay little
attention to issues of causality and intrinsic motivation, preferring instead
t@ dwell on single dimensions of treatments or to offer a mixed package
constructed in arbitrary ways and producing diffuse effects that reflect
tBe experience.
<The issue of expected benefits from techniques provides a bridge
between research and application. Research can be designed to evaluate
techniques, as well as to discover possible unintended side effects.
Indeed, a research literature has developed in some of the areas examined
in this book, namely biofeedback, stress, and guided imagery. For many
other techniques, however, a relevant body of research does not exist;
this lack applies to some of the techniques examined by the committee,
11
INTRODUCTION
as well as to those yet to appear on the market. It is these techniques
that present a problem for us as evaluators. Evaluation without data is
difficult, but not impossible. Our approach is to place the techniques into
broader categories corresponding to the key processes being influenced,
for example, learning, motor skills, and influence. By so doing, the claims
can be evaluated within the frameworks of existing theories and metho-
dologies. They can also be judged against results obtained in related
areas. This approach serves as the organizing theme for the chapters that
follow.
EVALUATING THE TECHNIQUES
Evaluations properly hinge on answers to a standard set of questions
proposed in a paper entitled "Evaluating Human Technologies: What
Questions Should We Ask?" by Hegge, Tyner, and Genser (1983) at the
Walter Reed Army Institute for Research:
. What changes will the technique produce?
. What evidence supports the claims for the technique?
. What theories stand behind the technique?
. Who will be able to use the technique?
. What are the implications of the technique for Army operations?
. How does the technique fit with Army philosophy?
· What are the cost-benefit factors?
These questions served as guidelines for the committee's evaluations.
Appendix A is a summary description of each technique, organized along
the lines of the Hegge, Tyner, and Genser questions, covering theory,
research, and application. For many of the categories, however, the
desired information is either too limited to be useful or simply not
available; in such cases we have considered other strategies for evaluation.
The committee faced a number of difficulties in evaluation that stem
from recurrent problems posed by the technologies. One is the tendency
for some promoters (and consumers) to rely primarily on testimonials or
anecdotal evidence as a basis for application. Another is a general lack
of strong research designs to provide evidence of effects. These problems
are considered also in the context of specific techniques discussed in the
chapters of Parts II and III.
Practitioners of techniques often emphasize the value of personal or
clinical experience and marketplace popularity as bases for judging the
techniques. They are generally less inclined to seek research evidence
or to support research evaluation programs. These attitudes may be
related to the fact that few practitioners are trained as researchers. For
some it is sufficient to let others do the research. For others, research is
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ENHANCING HUMAN PERFORMANCE
viewed, in varying degrees, as a threat to their product. At one extreme,
research is regarded as a debunking enterprise, engaged in by scientists
who have little interest in providing human services. At another extreme,
the problem is one of educating the researchers in nuance, context, and
a clinical approach that emphasizes adapting techniques to changed
situations and client tastes. The result is a gap in communication
epitomized by two cultures-scientists searching for evidence and prac-
titioners seeking effects and cures. A step toward bridging the gap would
consist of mutual education through joint ventures. These ventures would
e Dose scientists to the goals (and motives) of practitioners and would
alb make practitioners aware of the general analytical approaches used
bgscientists.
@Experimentation is an appropriate vehicle for evaluating performance-
eDancing techniques; the problem is usually defined in terms of effects
oftechniques (procedures) on performance (behaviors). It is also appro-
patate at an earlier stage in the process, when products are being
deeloped. Products evolve in a kind of trial-and-error fashion similar in
many respects to scientific discoveries. One model for integrating research
00791R0002
with product development is engineering research and development
(R&D). A strenuous applied research effort accompanies the development
process in many firms, as does a quality-control program designed to
etluate products both during development and after they have been
placed on the market. With a few exceptions, this model has not been
adopted by firms or institutions in the field of performance enhancement.
Experimental evidence has accumulated in some areas related to
techniques. Although not linked specifically to product development in
the manner of an R&D operation, this work does address the question,
What evidence supports the claims for the technique? In fact, so strong
is the experimental tradition in some areas that a body of work has
developed programmatically within a generally accepted paradigm (e.g.,
gugled imagery). The benefits of a long research tradition can be seen in
these areas. Meta-analyses have been performed and can be used as a
basis for evaluation. For other areas, we are presented with the prospect
of Selying on scattered experiments or using other criteria as a basis for
evaluation, or both (see Appendix A for summaries of the state of the
scance in each of the areas).
However, the benefits of experimental evidence derive primarily from
the general approach rather than from the particular experiments. This
idea is captured by Kelman, who noted that "an experimental finding
. . . cannot very meaningfully stand by itself. Its contribution to knowledge
hinges on the conceptual thinking that has produced it and into which it
is subsequently fed back" (1968:161). We emphasize here the contribution
13
INTRODUCTION
of an analytical approach to thinking about behavior, as distinct from the
establishment of laws about psychological processes. It is the cumulation
of a series of experiments that winnows out the useful parts of treatments
or techniques. It is the self-correcting progression of new experiments
that refines treatments, saving those that work and discarding those that
do not (or that work only under very restricted conditions). This process
contributes equally well to the goals of theory development and product
development.
Other evaluation criteria elucidated by Hegge, Tyner, and Genser,
(1983) include theories, uses, and implications for Army operations and
philosophy. A problem with these criteria is that they tend to be vague
and somewhat idiosyncratic, making it difficult to propose general cate
gories on which most people would agree. Without precisely defined
categories for judging techniques, it is difficult to address issues of transfer
of performance from one situation to another or to evaluate newly
emerging techniques. A similar problem exists with respect to developing
taxonomies in broadly defined fields: there is little agreement on a set of
categories for the fields of human learning, performance, motivation,
perception, and social and organizational processes. More mature sub-
disciplines provide an empirical basis for taxonomies, allowing for more
tightly constructed systems of tasks and situations: for example, rote
learning, short-term memory, concept learning, problem solving, work
motivation, and team functions (see Fleishman and Quaintance, 1984).
An advantage of such systems is that they capture rather precise
relationships between task and performance.
This discussion serves only to introduce the issues and identifies several
themes that receive more detailed attention in the chapters to follow.
First, any evaluation must take into account the status of the available
evidence. Confidence placed in judgments about a technique should be
based on the quality of the evidence produced by researchers. Second,
the evaluator cannot afford to rely exclusively on a single criterion for
judging effectiveness. Theoretical and applied issues are also important,
as are considerations of values served or violated by use of the technique.
Third, technique development issues are not isolated from research or
analytical issues. Each step in the process of product design can be
regarded as an empirical issue; decisions made about procedures and
packaging can be the result of experimental outcomes. Fourth, the subject
of enhancing human performance is not new. It has been a topic of
interest for centuries and an area of scientific work for several decades.
The literatures on learning and skill acquisition should be consulted by
developers, and insights derived from these literatures should be used in
product design.
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These themes are woven throughout the discussions of specific tech-
niques. Each chapter discusses relevant literature, describes the specific
techniques, points to directions for further research when appropriate,
and notes possible applications in military and industrial settings. Despite
the common coverage, however, each chapter is also unique in that each
is tailored to the particular problems associated with its focus.
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·
2
Findings and Conclusions
The committee's first major task was to evaluate the existing scientific
evidence for a wide range of techniques that have been proposed to
enhance human performance. This evaluation was intended by our Army
sponsors to suggest guidelines for decision making on Army research and
training programs. In our evaluation we draw conclusions with respect
to whether more basic or applied research is warranted, whether training
programs could benefit from new findings or procedures, and what, in
particular, might be worth monitoring for potential breakthroughs of use
to the Army. In many of the areas examined it appears feasible to pursue
carefully designed programs that build on basic research; however, such
programs should be monitored closely.
The committee's second major task was to develop general guidelines
for evaluating newly proposed techniques and their potential application.
We are aware that the use of basic and applied research in decision
making is a complex issue. Although payoffs from basic research can
often be realized in the long run, the value of research findings to the
Army depends on developing a way of putting them into practice. With
regard to applied or evaluation research, further complexities are evident:
multiple, sometimes conflicting, criteria must be satisfied at each of
several stages in the evaluation process, from assessing a pilot program
to implementing the program in an appropriate setting. Another problem
is that of choosing among alternative techniques when none of them has
been subjected to a systematic evaluation. In the absence of evaluation
studies, the Army needs guidelines for selecting packages and vendors.
The committee's evaluation has produced several answers to questions
15
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ENHANCING HUMAN PERFORMANCE
of how best to improve performance in specific areas. On the positive
side, we learned about the possibilities of priming future learning by
presenting material during certain stages of sleep, of improving learning
by integrating certain instructional elements, of improving skilled per-
formance through certain combinations of mental and physical practice,
of reducing stress by providing information that increases the sense of
control, of exerting influence by employing certain communication strat-
egies, and of maximizing group performance by taking advantage of
organizational cultures to transmit values. On the negative side, we
@scovered a lack of supporting evidence for such techniques as visual
Chining exercises as enhancers of performance, hemispheric synchroniz-
gion, and neurolinguistic programming; a lack of scientific justification
gr the parapsychological phenomena considered; some potentially neg-
give effects of group cohesion; and ambiguous evidence for the effec-
Veness of the suggestive accelerative learning package.
Release 2002-05/17 : CIA REP96-0879150002003
»The remainder of this chapter presents the committee's findings and
onclusions, which are presented in two parts: general conclusions
¿garding the process of evaluating any technique being considered by
je Army and specific findings and conclusions for each of the areas of
Oman performance examined. Whenever appropriate, we make recom-
mendations for research, evaluation, and practice.
GENERAL CONCLUSIONS
The committee suggests that the Army move vigorously, yet carefully
od systematically, to implement techniques that can be shown to enhance
Erformance in military settings. Such an effort would be timely because
Nrecent developments in the relevant research areas. Moreover, the
payoff is likely to be very high if techniques are selected judiciously.
Although the desire for dramatic improvements in performance makes
some extraordinary techniques attractive, techniques drawn from main-
stream research in relevant areas of performance may be more effective.
The Army's concern for enhancing human performance and its substantial
resources for evaluating techniques place it in a favorable position to
take advantage of developments. The Army might also consider the
possibilities of transferring its findings to the civilian sector.
Collectively, the committee's conclusions call for the adoption of
scientifically sound evaluation procedures; however, these procedures
must be adapted to institutional needs and must take into account problems
of implementation. We summarize these considerations below.
SCIENTIFIC EVIDENCE
Techniques and commercial packages proposed for consideration by
the Army should be shown to be effective by adequate scientific evidence
17
FINDINGS AND CONCLUSIONS
or compelling theoretical argument, or both. A technique's utility should
be judged in relation to alternatives designed for similar purposes, and
the estimated utility should be of significant magnitude. Specific stages
of analysis can be incorporated in pilot or field testing, and such testing
should be carried out by investigators who are independent of the
technique's originators or promoters.
TESTIMONIALS AS EVIDENCE
Personal experiences and testimonials cited on behalf of a technique
are not regarded as an acceptable alternative to rigorous scientific
evidence. Even when they have high face validity, such personal beliefs
are not trustworthy as evidence. They often fail to consider the full range
of factors that may be responsible for an observed effect. Personal
'versions of reality, which are essentially private, are especially antithetical
to science, which is a fundamentally public enterprise. Of course, a
caution about testimonials should not be confused with a lack of openness
to new and unusual ideas. Such openness is consistent with the require-
ment that the evidential criteria of science be satisfied.
The subject of testimonials as evidence has received considerable
attention in recent research on how people arrive at their beliefs. These
studies indicate that many sources of bias operate and that they can lead
to personal knowledge that is invalid despite its often being associated
with high levels of conviction. The committee recommends that this
research be disseminated, as appropriate, in the Army. It may then be
applied whenever testimony is used as the primary evidence to promote
an enhancement technique.
CONDITIONS FOR IMPLEMENTATION
Two kinds of evidence should be sought to support decisions to
implement a technique: successful field tests and an analysis of imple-
mentability. It would also be useful to analyze the impact of the technique
or package on the larger system in which it is to be embedded. These
analyses would aid in explaining why the procedures are necessary and
why certain consequences are expected. In general, any description of
what a technique accomplishes should be accompanied by an explanation
of why it accomplishes what it does. Such an explanation would provide
a more fundamental understanding of processes affected by exposure to
the technique and permit optimal implementation.
RATIONAL DECISION MAKING
The considerations that must be entertained in selecting a technique
for practical use in a military setting are different from the considerations
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needed to verify the existence of an enhancement effect in a scientific
setting. For example, the benefits of correct decisions and the costs of
incorrect decisions, that is, the risk calculus, may differ in the two
settings! Furthermore, what is viewed as a timely decision will also differ.
The specific differences as they apply to particular decisions should be
made explicit.
MECHANISMS FOR ADVICE
It would be useful to provide valid information about useful techniques
Army commanders and other interested staff on a regular basis. Special
Ensideration should be given to ways in which technique-related infor-
Sation can be transferred from scientists to practitioners. The charac-
Bristics of a transfer agent could be defined, and such a position might
he established within an appropriate office.
The committee recommends that the Army Research Institute formalize
Be ways in which it receives and provides advice about specific tech-
biques. A committee to review experimental designs and statistical
analyses could be convened to improve the evaluation of techniques.
Special and standing committees could also be used to make program
recommendations and to review proposals for intramural and extramural
research.
BIDDING PROCEDURES
Purchase by the Army of a commercial enhancement package should
Bake place within the context of a set of well-defined procedures. The
committee recommends that an open-bid procedure be followed, based
On a full presentation of the Army's stated objectives. This would
encourage competitive evaluation of techniques. The following informa-
mon, presented in a standard format, should be required: the objectives
of the technique, a description of its procedures, evidence that it produces
Lthe claimed effects, and the vendor's record of past achievements in
Relevant areas.
Lack of professional training and research experience in human per-
formance by a designer or advocate should not preclude consideration
of the proposed package; it should, however, signal the need for a more
stringent analysis by the Army.
SPECIFIC FINDINGS AND CONCLUSIONS
We present below findings and conclusions for each of the areas
investigated. Some statements take the form of suggested actions based
19
FINDINGS AND CONCLUSIONS
on what we know; others consist of suggestions for more work or for
research that has not yet been done.
LEARNING DURING SLEEP
1. The committee finds no evidence to suggest that learning occurs
during verified sleep (confirmed as such by electrical recordings of brain
activity). However, waking perception and interpretation of verbal ma-
terial could well be altered by presenting that material during the lighter
stages of sleep. We conclude that the existence and degree of learning
and recall of materials presented during sleep should be examined again
as a basic research problem.
2. Pending further research results, the committee concludes that
possible Army applications of learning during sleep deserve a second
look. Findings that suggest the possibility of state-dependent learning
and retention (i.e., better recall of material when learned in the same
physiological and mental state) may be applicable to fatigued soldiers.
Furthermore, even presentations of material that disrupt normal sleep
may be cost-effective, as may presentations that coincide with stages of
light sleep.
ACCELERATED LEARNING
1. Many studies have found that effective instruction is the result of
such factors as the quality of instruction, practice or study time, motivation
of the learner, and the matching of the training regimen to the job
demands. Programs that integrate all these factors would be desirable.
We recommend that the Army examine the costs, effectiveness, and
longevity of training benefits to be derived from such programs and
compare them with established Army procedures.
2. The committee finds little scientific evidence that so-called super-
learning programs, such as Suggestive Accelerative Learning and Teach-
ing Techniques, derive their instructional benefits from elements outside
the mainstream of research and practice. We observe, however, that
these programs do integrate well-known instructional, motivational, and
practice elements in a manner that is generally not present in most
scientific studies.
3. We find that scientifically supported procedures for enhancing skills
are not being sufficiently used in training programs and make two
recommendations to remedy this problem. First, the basic research
literature should be monitored to identify procedures verified by laboratory
tests to increase instructional effectiveness. Second, additional basic
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research should be supported to expand the understanding of skill
acquisition for both noncombat and combat activities.
'4. We conclude that the Army training system provides a unique
opportunity for cohort testing of training regimens. The Army is in a
position to create laboratory classroom environments in which competing
training procedures can be scientifically evaluated.
5. The committee recommends that the Army investigate expert teacher
programs by identifying and evaluating particularly effective programs
within the Army. In addition, transferable elements of effective instruction
can be reported to the larger instructional community.
IMPROVING MOTOR SKILLS
1. The committee concludes that mental practice is effective in en-
hancing the performance of motor skills. This conclusion suggests further
work in two directions: (1) evaluation studies of motor skills used in the
Army and (2) research designed to determine the combination of mental
and physical practice that, on average, would best enhance skill acquisition
and maintenance, taking into account both time and cost.
2. The committee concludes that programs purporting to enhance
cognitive and behavioral skills by improving visual concentration have
not been shown to be effective to date. In our judgment, these programs
are not worth further evaluation at this time.
3. The committee concludes that existing data do not establish the
generality of observed effects from programs that train visual capabilities
to increase performance.
4. Similarly, the committee concludes that the effects of biofeedback
on skilled performance remain to be determined.
5. The committee recommends additional research to establish the
potential of these techniques in the domain of specific skilled perform-
ances.
ALTERING MENTAL STATES
1. Time did not allow the committee to explore the evidence for a
wide variety of specific methods for relating mental states to changes in
performance. Such methods include forms of self-induced hypnotic states
and peak performance resulting from high levels of focused concentration
and meditation. We recommend that reviews of the literature in these
areas be undertaken to ascertain whether any practical results might be
obtained by the use of such methods.
2. The committee finds that, while the study of mental computations
in language and imagery has progressed in recent years, the effort to
understand how such computations are modulated by energetic factors
21
FINDINGS AND CONCLUSIONS
such as arousal, stress, emotion, and high levels of sustained concentration
has not been fully developed. For example, the claims that certain mental
states produce general improvements in performance derive from the
idea, supported by research, that arousal affects mental computations
and that there ought to be an optimal level of arousal for the performance
of such computations. We recommend this as an important area for
investment of basic research funds.
3. The committee's review of the appropriate literature refutes claims
that link differential use of the brain hemispheres to performance. Further
evaluation of these claims depends on developing valid and reliable
measures of hemispheric involvement.
4. The committee finds no scientifically acceptable evidence to support
the claimed effects of techniques intended to integrate hemispheric
activity, for example, Hemi-Sync(@). Attempts to increase information-
processing capacity by presenting material separately to the two hemi-
spheres do not appear to be useful. We conclude that such techniques
should be considered further by the Army only if scientific evidence is
provided to and evaluated by the Army Research Institute.
STRESS MANAGEMENT
1. Existing data indicate that stress is reduced by giving an individual
as much knowledge and understanding as possible regarding future events.
In addition, giving the individual a sense of control is effective. On the
basis of these findings, the committee recommends a systematic program
of research and development that would address three questions: (1) How
relevant is this finding for stress reduction in the Army? (2) To what
extent does stress reduction realized in training transfer to combat
situations? (3) What are the limitations on providing knowledge and
understanding of future events and a sense of control in the Army setting?
Pending the outcome of this research, we suggest that consideration be
given to including the material in training programs for company grade,
field grade, command, and staff officers.
2. We find that, while biofeedback can achieve a reduction of muscle
tension, it does not reduce stress effectively. It is therefore not a promising
research topic in that respect. We recommend that funding be directed
toward investigation of more promising stress management procedures.
3. We recommend that information be gathered on the costs of stress
in terms of organ breakdown, loss of efficiency, and loss of time. This
information would have implications for training programs.
INFLUENCE STRATEGIES
1. The committee finds no scientific evidence to support the claim that
neurolinguistic programming is an effective strategy for exerting influence.
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We advise that further Army study of this aspect of NLP be made only
in comparison with other techniques.
2. There are no existing evaluations of NLP as a model of expert
performance. We conclude that further investigation of such models may
be worthwhile and suggest that NLP be examined in comparison with
several other techniques.
3. Concerning the process of technology transfer, we recommend that
studies be conducted to develop training regimens for those who train
others to wield social influence. The large literature on this topic in social
psychology would provide a basis for such packages.
GROUP COHESION
1. We find few scientific studies that address the possible relationship
between group cohesion and performance; however, such a relationship
may well be found with more extensive research. There is a need for
research to consider the possibility of negative effects from inducing
cohesion and methods of avoiding such effects. The committee recom-
mends continued study of cohesion and related group processes.
2. We are favorably impressed with the evaluation studies of the
Army's COHORT system. We endorse the investigators' plan to proceed
beyond measures of attitudes to measures of group performance.
3. We recommend that the Army, as well as independent investigators,
study the possible impacts of cohesion beyond the COHORT system, for
pexample, on intergroup performance.
PARAPSYCHOLOGY
1. The committee finds no scientific justification from research con-
@ducted over a period of 130 years for the existence of parapsychological
"phenomena. It therefore concludes that there is no reason for direct
involvement by the Army at this time. We do recommend, however, that
research in certain areas be monitored, including work by the Soviets
dand the best work in the United States. The latter includes that being
@one at Princeton University by Robert Jahn; at Maimonides Medical
Center in Brooklyn by Charles Honorton, now in Princeton; at San
Antonio by Helmut Schmidt; and at the Stanford Research Institute by
Edward May. Monitoring could be enhanced by site visits and by expert
advice from both proponents and skeptics. The research areas included
would be psychokinesis with random event generators and Ganzfeld
effects.
2. One possible result of the monitoring mentioned above is the proposal
23
FINDINGS AND CONCLUSIONS
of specific studies. In that situation the committee recommends the
following procedures: first, the Army and outside scientists should arrive
at a common protocol; second, the research should be conducted
according to that protocol by both proponents and skeptics; and third,
attention should be given in such research to the manipulability and
practical application of any effects found to exist.
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3
Evaluation Issues
.....
Implementation of an enhancement technique, in the committee's view,
should depend on two general kinds, or levels, of evaluation. The first
examines primarily the scientific justification for the effectiveness of the
technique and the potential of the technique for improving performance
· in practice. The second kind examines field tests of a pilot program
incorporating the technique to determine how feasible it is and to what
extent it brings about effects that Army officials consider useful.
Convincing scientific justification can come only from basic research,
that is, from carefully controlled studies that usually take place in
laboratory settings and that preferably are related to a body of theory.
Such research can provide evidence for the existence of the causal effect
on which a technique is based and can help explain, or indicate a
Ymechanism for, the effect. Analysis in connection with basic research
should go beyond scientific justification to operational potential and likely
cost-effectiveness. Only field tests can assess a program's actual opera-
tions and effects, however, and for such tests a broader array of evaluative
criteria are needed, related primarily to the technique's utility.
Because strong claims of support from basic research have been made
for some of the techniques the committee examined, we review here
what it takes to justify a scientific claim, specifically, we review some
standards for evaluating basic research. We then examine in more detail
some standards for evaluating field tests of pilot programs. In the third
section of this chapter, we set forth briefly some of our impressions of
how the Army now manages the solicitation and evaluation of new
performance-enhancing techniques. This chapter concludes with a note
24
.
EVALUATION ISSUES
on informal, qualitative approaches to evaluation, which are sometimes
suggested as alternatives to basic research and field tests.
This chapter does not aspire to a comprehensive treatment of evaluation
issues, and it barely touches on research methods. Articles, journals,
books, and handbooks testify to the scope and complexity of this
burgeoning field (e.g., Barber, 1976; Cook and Campbell, 1979). Our
objective here is to highlight the topics that have impressed us as most
germane. The various sources just mentioned would need to be consulted
for even a minimal elaboration of these topics, and other committees
would be required if recipes for evaluation of the Army's enhancement
programs were sought as extensions of our work. Still, we believe thisg
chapter will help the Army set general evaluation standards.
STANDARDS FOR EVALUATING BASIC RESEARCH
The purpose of basic research is to permit inferences to be drawn in
accordance with scientific standards, including inferences about novel
concepts, about causation, about alternative explanations of causal
relations, and about the generalizability of causal relations.
For novel concepts, evidence must be gathered that both the purported
enhancement technique and the relevant performance have been (1)
defined in a way to highlight their critical elements, (2) differentiated
from related variables that might bring about similar effects, and (3) put
into operation (manipulated or measured) in ways that include the critical
parts. The burden is on the evaluator to analyze how the components of
each new technique differ from concepts already in the literature. The
need for this standard is illustrated well by packages for accelerated
learning, as discussed in Chapter 4.
Evidence needs also to be adduced that supposed cause and effect
variables vary together in a systematic manner. Relevant procedures
include comparison of performance before and after introduction of the
technique, contrasts of experimental and control groups in an experimental
design, and calculation of statistical significance. Illusory covariation can
occur more easily in nonstatistical studies, which are used often to support
the existence of paranormal effects, as discussed in Chapter 9.
Especially demanding is the need for evidence that the performance
effect observed is due to the postulated cause and not to some other
variable. Ruling out alternative explanations or mechanisms requires
intimate knowledge of a research area. Historical findings and critical
commentary are needed to identify alternatives, determine their plausi-
bility, and judge how well they have been ruled out in particular sets of
experiments. Common threats to the validity of any presumed cause-
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ENHANCING HUMAN PERFORMANCE
effect relation include effects stemming from subject selection, unexpected
changes in organizational forces, the spontaneous maturation of subjects,
and the sensitizing effects of a pretest measurement on a posttest
assessment. Experiments with random assignment of subjects to treat-
ments' are preferred, but some of the better quasi-experimental designs
are also useful. Another class of threats to validity is associated with
subject reactions to such conceptual irrelevancies as experimenter ex-
pectations about how subjects should perform or subjects' performing
better merely because they are receiving attention. Procedures that have
Evolved to reduce this sort of threat include double-blind experiments,
placebo control groups, mechanical delivery of treatments, and the
Elimination of all communication between experimenters and subjects or
Among subjects. These safeguards, however, are not certain, and imple-
Inenting them is not a simple matter.
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Finally, for a technique to be of value, one must ascertain that a causal
elation observed in one setting is likely to be observed in other settings
n which the technique is to be employed. Replication of an experiment
By an independent investigator is a first step. Another step is to produce
The cause and effect with different samples of people, settings, and times.
Systematic reviews of the literature, perhaps aided by what is referred
Mo as meta-analysis of studies (as illustrated in Chapter 5), are also helpful.
Beyond these steps, a thorough theoretical understanding of causal
Processes, which is a fundamental goal of science, permits increased
practical control.
; Our point-perhaps seeming obvious to many but nonetheless needing
Emphasis here-is that a planned or existing program for implementing
ai enhancement technique is much more likely to bear fruit if evidence
far the technique's effectiveness is properly derived from basic research.
complex set of ground rules exists for conducting and drawing inferences
jom basic research, and waiving those rules greatly increases the chances
@ incorrect conclusions.
STANDARDS FOR EVALUATING
FIELD TESTS OF PROGRAMS
"An adequate appraisal of an actual enhancement program requires
agention to three general factors. First, the organizational (i.e., political,
administrative) context in which the program is embedded should be
described. That context strongly influences the choice of evaluation
criteria, the types of evaluations considered feasible, and the extent to
which evaluation results will be used. Second, the program's conse-
quences should be described and explained, including planned and
unplanned, short-term and long-term consequences. The way the program
27
EVALUATION ISSUES
is construed influences the claims resulting from an evaluation and the
degree of confidence that can be placed in what was learned. Third, value
or merit should be explicitly assigned to a program. Valuing relates an
enhancement technique to an Army need and to feasible alternatives. In
the following sections we comment on these three factors in turn.
THE ORGANIZATIONAL CONTEXT
A description of the broader context of an enhancement program would
include an assessment both of the various constituencies with a stake in
its implementation and of the priorities of the larger institution. We do
not discuss stakeholder interests in general at this point because we refer
to some specifically later in this chapter, in the section on the committee's
impressions of current Army evaluation practices. We do comment here
on the Army's institutional priorities as they may relate to scientific
standards.
We understand that the Army, like other organizations in society, may
have-and quite possibly should have-different standards for evaluating
knowledge claims, or technique effectiveness, than science has. The
scientific establishment is conservative in the tests it administers to
discipline its conjectures; in particular, its goal is to reduce uncertainty
as far as possible, no matter how long that takes. In the Army, by
contrast, the need for timely information and decisions may lead to an
acceptance of greater uncertainty and a higher risk of being wrong.
There is no Army doctrine of which we are aware concerning the
degree of risk that is acceptable in evaluations of pilot programs. Yet
surely one objective of evaluations of pilot programs should be to describe
the costs to the Army of drawing incorrect conclusions so that inferential
standards can be made commensurate with those costs. If the costs are
relatively low, the riskier approach of most commercial research (as, for
example, in management consulting or marketing) may be preferred to
the more conservative approach of basic science.
DESCRIBING A PROGRAM'S CONSEQUENCES
In evaluating a program, it is desirable to present an analysis and
defense of the questions probed and not probed, together with justification
for the priorities accorded to various issues. Primary issues usually
include the program's immediate effects and its organizational side effects.
Immediate Effects
A primary problem in evaluation is to decide on the criteria by which
a program is to be assessed. The major sources for identifying potential
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ENHANCING HUMAN PERFORMANCE
criteria include program goals, interviews with interested persons, con-
sideration of plausible consequences found in the literature, and insights
gained from preliminary field work.
Such criteria specify only potential effects, however. They do not
speak to the matter of whether the relation between a supposed cause
and effect is truly causal. In this respect, a fundamental issue of
methodology is the use of randomized experiments. Although logistic
reasons abound in any practical context for not going to the trouble to
se such research designs, one might nonetheless argue that the Army is
a better position to conduct randomized experiments than are organi-
00 1:15
gations in such fields as education, job training, and public health. The
Reason for going to such trouble is that randomized experiments give a
Ower risk of incorrect causal conclusions than the alternatives.
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Alternatives at the next level of confidence are quasi-experimental
fesigns that include pretest measures and comparison (control) groups.
Relatively little confidence can be placed either in before-after measure-
pients of a single group exposed to a technique without an external
Comparison, or in comparisons of nonequivalent intact groups for which
gretest measures are not available.
Side Effects
Unintended side effects include impacts on the broader organization,
End these should be monitored. For example, trainers from other (non-
experimental) units may copy what they think is going on, or they may
Amply be upset by the implementation of new instructional packages in
The experimental units. Units not treated in the same way as the
experimental units may be unwilling to cooperate when cooperation
Would seem to be in their best interest. They may also suffer by
Comparison, as is thought to be the case, for example, when COHORT
units are introduced into a division (see Chapter 8). Evaluators should
Istrive to see any program as fitting into a wider system of Army activities
En which it may have unintended positive or negative effects.
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ASSIGNING VALUE TO PILOT PROGRAMS
The described consequences of a program tell us what a program has
achieved but not how valuable it is. Three other factors are important in
inferring value: Does the new technique meet a demonstrable Army need
to the extent that without it the organization would be less effective?
How likely is it that the program can be transferred to other Army
settings, either as a total package or in part? How well does the new
EVALUATION ISSUES
program fare when compared with current practi
for bringing about the same results?
Meeting Needs
Representatives of the commercial world wh
products often confound wants with needs, enth
hope with reality. While it is axiomatic that all
meet genuine Army needs, it is not clear how
when the developers of new products
permission to do general research or fiek tests.
analysis should be part of the documentation abo
What should a needs analysis look like? At
document the current level of performance at so
is inadequate, what reason there is to believe
change, and what the Armywide impacts wou
performance in question were improved. &n addit
question why a particular program is needed fo
Such an analysis would describe the program,
justification in basic research, identify the financi
required to make the program work, relate the re
funds available, examine other ways of bringing a
results, and justify the program at hand in terms
effectiveness. To facilitate critical feedback, s
independent of the persons who sponsor@ progr
thorough, firsthand acquaintance with the progr
and sponsors.
As just described, needs analysis is a plann
mounting a pilot program. It is not a review of
relative to needs, for which a description of a pr
is required. At that later stage in evaluation a judg
whether the magnitude of a program's effeas is su
to a degree that makes a practical difference.
whether the program makes a statistically @eliable
ance. Size of effect relative to need is the cruci
magnitude of change required for practical significa
in advance, it is easy to use such a specification
need has been met. But the level of change requi
not usually predetermined, and there are political r
are not always eager to have their programs evalu
sizes they themselves have clearly promised or tl
them.
Needs can be specified only by Army officials,
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ENHANCING HUMAN PERFORMANCE
officials inspect the results a program has achieved, relating them to their
perception of need. Since the Army is heterogeneous, it would be naive
to believe that there are no significant differences within it about how
important various needs are and how far a particular effect goes in
meeting a particular need. Some theorists relate needs primarily to the
number of persons performing below a desired level, while others
emphasize the seriousness of consequences for unit performance, for
which deficiencies in only one or two persons may be crucial. Some
practitioners are likely to think a deficit in skill X is worse than a deficit
in skill Y, while others may believe the opposite. Evaluators who take
the concept of need seriously have to take cognizance of such hetero-
geneity, perhaps using group approaches like the Delphi technique to
bring about consensus on both the level of need and the extent to which
a particular pattern of evaluative results helps meet that need.
Likelihood of Transfer
Although some local commanders may sponsor field trials for the benefit
of their command alone, the more widely a successful new practice can
be implemented within the Army, the more important it is likely to be.
Consequently, evaluations of pilot programs should seek to draw conclu-
sions about the likelihood that findings will transfer to populations and
settings different from those studied.
In this regard, it is particularly important to probe the extent to which
any findings from a pilot study might depend on the special knowledge
and enthusiasm of those persons who deliver or sponsor the program.
Such persons are often strongly committed to a program, treating it with
a concern and intensity that most regular Army personnel could not be
expected to match. While it is sometimes possible to transfer such
committed persons from one Army site to another in order to implement
@ a program, in many instances this cannot be done. Transfer is partly a
question of the psychology of ownership; authorities who did not sponsor
a product will sometimes reject out of hand what others have developed,
including their immediate predecessors. Since Army leaders in any
position turn over with some regularity due to transfers, promotions, and
retirement, successors will probably not identify with a program as
strongly as the original sponsors and developers did.
The likelihood of transfer also affects the degree to which program
implementation is monitored. Pilot programs are likely to be more
obtrusively monitored than other programs. Not only is this obtrusiveness
due to developers' and evaluators' fussing over their charge, it is also
due to teams of experts brought in to inspect what is novel and to
responsible officers wanting to show others the unique programs they
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EVALUATION ISSUES
are leading (and on which the success of their careers may depend). For
at least these reasons pilot programs tend to stand out more than the
regular programs they may engender. Research suggests that the quality
with which programs are delivered may in fact increase when outside
personnel are obviously monitoring individual and group performance.
It is naive to believe that one can go confidently from a single pilot
program to full-blown Armywide implementation. Even if this were
feasible politically, it would not be technically advisable unless there
were compelling evidence from a great deal of prior research indicating
that the program was indeed built on valid substantive foundations. Given
a single pilot program, decisions about transfer are best made if the
program is tested again, at a larger but still restricted set of sites and
under conditions that more closely approximate those that would pertain
if the new enhancement technique were implemented as routine policy.
Only then might serious plans for Armywide implementation be feasible.
Contrast with Alternatives
Most of the evaluation we have discussed contrasts a novel program
with standard practices that are believed worth improving; yet rational
models of decision making are usually predicated on managers' having
to choose among several different options for performing a particular
task. One would hope that every sponsor of a novel performance
enhancement technique is conversant with the practical alternatives to it
and has cogent arguments for rejecting them.
Many novel techniques have some components that are already in
standard practice or can be clearly derived from established theories.
Upon close inspection, pilot programs often turn out to be less novel
than their developers and sponsors claim. Of course, the Army may often
find it convenient to order complete packages in the form offered and
may not have much latitude to interact with developers in order to modify
package contents to emphasize what is truly a novel alternative and to
downplay that which is merely standard practice.
Ultimately, alternatives have to do with costs. Although many forms
of cost are at issue-including those associated with how much a new
practice disrupts normal Army activities and how much stress it puts on
personnel-the major cost usually considered is financial. Cost analysis
is always difficult, nowhere more so than in the Army, which uses many
ways to calculate personnel costs. Nonetheless, in planning an evaluation,
some evidence about the total cost of a pilot program to the Army will
usually be available and can be critically scrutinized. It is also useful, as
far as possible, to ascribe accurate Army costs to each of the major
components of such an intervention. In our view, what is called cost-
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effectiveness analysis lends itself better than what is called cost-benefit
analysis to the comparison of different programs. The purpose of cost-
effectiveness research is to express the total cost for each program in
dollar terms and to relate this to the amount of effect as expressed in its
original metrics-unlike cost-benefit research, in which even the effects
have to be expressed in dollar terms. Sophisticated consumers of eval-
uation should want something akin to cost-effectiveness knowledge, for
it reflects decisions they should be making. Is it not useful to know, for
example, that the best available computer-assisted instruction packages
are much less cost-effective than peer tutoring?
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CURRENT STATUS OF ARMY EVALUATIONS
We set forth here some of our impressions of the way in which the
Army currently manages the solicitation and evaluation of novel tech-
niques to enhance performance. We must stress that these are only
impressions, gained through the limited investigative capabilities of a
committee such as ours, not hard conclusions based on systematic
research directed at the particular question. Furthermore, although the
opinions that follow are largely critical of Army procedures, they are not
accompanied by much detail. As noted earlier, the focus here is on the
identification of the various Army constituencies that have a stake in
enhancement programs and on the role they play in evaluation.
How the Army decides which among competing proposals should be
sponsored for development or for field tests is not clear. What is clear is
that decision making is diffuse both geographically and institutionally.
Sponsorship may come from senior managers in the Pentagon or from
local personnel of varying rank. While differences in the quality of
program design, implementation, or evaluation may be correlated with
the source of sponsorship, such a correlation is not clear at present in
the Army context.
A particular concern is that Army sponsors of pilot programs may base
their judgment about the value of a program either on their own ideas
about what is desirable or effective or on the persuasiveness of the
arguments presented to them by program developers, who stand to gain
financially if the Army adopts their program. Judgments of value should
depend on broader analysis of Army needs and resources, as well as on
realistic assessment of the quality of proposed ideas based on a thorough
and independent knowledge of the relevant research literatures. Sponsors
should examine what is being advocated at every stage: proposal, testing,
and implementation.
Also of concern when pilot programs are planned is how decisions are
reached about funding and about the quality of implementation expected
33
EVALUATION ISSUES
from them. Although systematic evidence is lacking, it seemed to
committee members that pilot programs are not generally implemented
well and, except for fiscal accountability, are not closely monitored by
their Army sponsors. Evaluations of pilot programs should try to char-
acterize resources required by the program and the resources actually
available.
We found little evidence that sponsors, advocates, or local implementers
had aspirations to evaluations that use state-of-the-art methods. We found!
no guidelines about the standards expected for evaluative work, whethe@
in the form of published minimal standards or published statements of
preferred practices. When it comes to field trials of novel ideas for
enhancing human performance, the monitoring of evaluation quality doe
not seem to be part of the organizational context. Given the absence of
formal expectations in these regards, it is not surprising that the pilot
programs we saw and the evaluation materials we read were usually.
disappointing in the technical quality of the research conducted. In
settings in which program sponsors or advocates control an evaluation,
weaker evaluations (e.g., based on testimony) will sometimes be preferredg
to stronger methods (e.g., experiments) because the latter are usually
more disruptive when implemented and are more likely to result in effectso
that are disappointing, however much more accurate they may be. Thes
weaker methods are easier to implement when few units are available,
are less disruptive of ongoing activities, are easier to manipulate for self-
interested ends, and need not be as expensive for data collection.
We saw little evidence that the Army requires evaluations by persons
independent of the pilot program under review. Moreover, the noninde-
pendent evaluations we saw did not seem to have been subjected to any
of the peer review procedures to which research results (and plans) are
subjected not only in academic sciences, but also in much of the corporate
world, as with, say, pharmaceutical testing. While in-house evaluation is
highly valuable for gaining feedback for program improvement, many
experienced evaluators contend that it is inadequate for assigning overall
value because in-house evaluators cannot divorce themselves from their
own stake in the program under examination. Although it is not easy to
specify organizational standards adequate for a high-quality field test of
some novel technique, it is also not difficult to detect the inadequacies
associated with local program sponsors' having few clear expectations
about the desirable qualities of program operations or evaluative practices.
In the absence of such expectations, program developers and evaluators
may believe that few officials care about the small-scale field tests of
techniques on which the developers'-and, all too often, the evaluators' --
own welfare depends.
Since the organizational climate we have just described is not optimal
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for gaining trustworthy information about program value, future evaluators
of Army field trials might do well to characterize: (1) what program
managers expect in terms of the quality of the program and its evaluation;
(2) who is paying attention to the trials; and (3) for what purposes they
want to use any information provided by the evaluation. This kind of
information, as mentioned above, contributes to a description of the
organizational context of a program, which is a major part of an adequate
evaluation.
QUALITATIVE APPROACHES
Alternatives to experimentation are the largely qualitative traditions,
which rely mostly on direct observation, sometimes supplemented by
archival data. Investigative journalists operate in this mode; so do many
cultural anthropologists, political scientists, and historians. These profes-
sions use clues to suggest hypotheses about possible causes and investigate
the empirical evidence in ever-greater detail in an attempt to rule out
hypotheses until they are left with just one. A critical aspect of their
work is the use of substantive theories and ad hoc findings from the past
to help in ruling out alternative explanations. Also working in this tradition
are committees of psychologists who seek to make statements about the
causes of enhanced human performance. Rarely conducting studies
themselves, they instead sift through historical evidence provided by
· reviews of the literature and make on-site observations in the manner of
detectives, pathologists, investigative journalists, and cultural anthropol-
ogists.
These traditions rely strongly on personal testimony. Respondents'
reports are taken seriously and, indeed, should be. Any method can, in
principle, generate strong causal evidence, provided that plausible alter-
natives to a preferred hypothesis have been ruled out. The general issues
are: Can personal testimony usually rule out all the plausible alternative
interpretations? Does use of it engender the very threats to validity that
militate against strong inferences? Dale Griffin, in a paper prepared for
the committee (see Appendix B), suggests "no" to the first question and
"yes" to the second. His analysis of biases that operate when people
attempt to explain how and why they changed after an experience reveals
many of the shortcomings associated with relying on testimony as a major
means of testing causal hypotheses.
While testimony can be regarded as a form of confirmatory evidence,
it does not provide any of the disconfirming evidence needed to reduce
uncertainty. Rarely are there the kinds of comprehensive probes needed
to discover why respondents believe that the effects are due to a treatment
rather than to maturation, statistical regression, or the pleasant feelings
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EVALUATION ISSUES
aroused by the experiences. People are typically weak at identifying the
range of such alternatives, however simply they may be described, and
at distinguishing the different ways in which the causal forces might
operate. How can people know how they would have matured over time
in the absence of an intervention (technique) that is being assessed? How
can people disentangle effects due to a pleasant experience, a dynamic
leader, or a sense of doing something important from effects due to the
critical components of the treatment per se? Much research has shown
that individuals are poor intuitive scientists and that they recreate a set
of known cognitive biases (Nisbett and Ross, 1980; Griffin). These include
belief perseverance, selective memory, errors of attribution, and over-
confidence. These biases influence experts and nonexperts alike, usually
without one's awareness of them. Scientists hold these biases in partial
check by using random assignment instead of testimony and by the
tradition of public scrutiny to identify and analyze alternative interpre-
tations for observed events. Such methodological traditions can be
transmitted to consumers and producers of enhancement techniques
through courses on statistical inference and formal decision making.
These courses would have the salutary effect of calling attention to the
shortcomings of testimony as evidence.
We submit that experimental methods facilitate causal inferences better
than the alternatives. They reduce more uncertainty by ruling out more
of the contending interpretations for observed effects. However, we refer
here to the relative superiority of experimentation; such superiority
should not be confused with either the perfection or even the adequacy
of experimentation. Its problems include the facts that experiments
cannot be implemented under all conditions and that experimentation has
its own set of unintended side effects. Thus, experimental methods do
not guarantee causal inferences and so cannot obviate the need for critical
analysis that, on a case-by-case basis, is sensitive to the contexts and
traditions of particular institutions or communities, such as the Army,
on one hand, and the various promoters of new enhancement techniques,
on the other. Moreover, well-conceived research is costly: it requires
specially trained investigators, equipped facilities, and programs that may
need extensive collaborations and review panels. It is also a demanding
craft that requires sensitivity to detail and precision in order to ensure
results that are interpretable.
On balance, the benefits derived from careful experimentation outweigh
the costs just mentioned. All other things being equal, experimentation
is much the preferred strategy for judging the efficacy of techniques that
purport to enhance performance, and it should be used whenever possible.
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PART
III
Parapsychological Techniques
O
F ALL THE SUBJECTS TREATED in this volume, none is more contro-
versial than parapsychology. While the flavor of the debates is
captured to some extent in this chapter, the subject is treated in the same
manner as the other techniques reviewed: we address the question of
whether the evidence warrants further consideration of parapsychological
techniques for research or application or both.
Emphasized here is information gathering by remote viewing and mind-
over-matter effects in controlling machine behavior, particularly machines
that generate series of random numbers, which are often used in para-
psychology experiments. Although scattered results are said to be statis-
tically significant, an evaluation of a large body of the best available
evidence does not support the contention that these phenomena exist.
If, however, future experiments, conducted according to the best possible
methodological standards, are more generally viewed as producing sig-
nificant results, it would be appropriate to consider a systematic program
of research. Such a program should include a concern for the need to
proceed from small effects to practical applications.
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Paranormal Phenomena
BACKGROUND
The primary purpose of this chapter is to evaluate the scientific evidence
on parapsychological techniques in selected areas. A more complete
understanding of the topic, however, requires that we provide background
on the military's interest in these phenomena and treat the conceptual
issue of how people come to believe as they do. This background section
includes a discussion of the phenomena and the military's interest in
them as well as an overview of the committee's focus. A brief examination
of the different kinds of justifications for the claims is followed by a more
detailed treatment of the evidence in areas that have produced large
literatures: remote viewing, random number generators, and what are
called Ganzfeld (whole visual field) experiments. In addition, we describe
experimental work that the committee actually witnessed by visiting a
parapsychological laboratory. Despite the growing scientific tradition in
some of these areas, many people continue to rely on qualitative or
experiential evidence to support their beliefs; we discuss the problems
associated with qualitative evidence in conjunction with the research on
cognitive and emotional biases, which is reviewed in the paper by Dale
Griffin (Appendix B). Finally, the chapter summarizes the committee's
major conclusions.
THE NATURE OF THE PHENOMENA
Parapsychologists divide psi-the term applied to all psychic phenom-
ena-into two broad categories: extrasensory perception (ESP) and
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psychokinesis (PK). Included in ESP are telepathy, precognition, and
clairvoyance, all of which refer to methods of gathering information about
objects or thoughts without the intervention of known sensory mecha-
nisms. Popularly called mind over matter, PK refers to the influence of
thoughts upon objects without the intervention of known physical proc-
esses.
A presentation to the committee by several military officers described
Tin some detail the results of experiments in remote viewing carried out
bat both SRI International and the Engineering Anomalies Research
SLaboratory at Princeton University. In these experiments subjects are
said to have more or less accurately described a geographical location
Sbeing visited by a target team. Although the human subjects have no way
Sof normally knowing the target location, the examples recounted appear
Sto indicate, at first glance, some striking correspondences between their
descriptions and the actual sites. These studies have been related by
"some persons to reported out-of-body experiences.
The presentation included discussion of psychic mind-altering tech-
oniques, the levitation claims of transcendental meditation groups, psy-
Lchotronic weapons, psychic metal bending, dowsing, thought photogra-
¿phy, and bioenergy transfer. It was indicated that the Soviet Union is far
rahead of the United States in developing potential applications of such
Oparanormal phenomena, in particular psychically controlling and influ-
'encing minds at a distance. At the presentation, personal accounts were
given of spoon-bending parties, in which participants believe they have
caused cutlery to bend with the power of their minds, as well as instances
of self-hypnosis to control pain and cure illness, walking barefoot on fire
and handling hot coals without being burned, leaving one's body at will,
wand bursting clouds by psychic means.
The media and popular publications, especially in recent years, have
discussed various aspects of psychic warfare. Three recent books, by
ŽEbon (1983), McRae (1984), and Targ and Harary (1984), have attempted
to document Soviet and American efforts to develop military and intel-
ligence applications of alleged paranormal phenomena. These accounts
whave been augmented by newspaper stories, magazine articles, and
otelevision programs. Many of these sources acknowledge the speculative
Enature of the proposed applications, but others report that some of the
techniques already exist and work.
The claimed phenomena and applications range from the incredible to
the outrageously incredible. The "antimissile time warp," for example,
is supposed to somehow deflect attack by nuclear warheads so that they
will transcend time and explode among the ancient dinosaurs, thereby
leaving us unharmed but destroying many dinosaurs (and, presumably,
some of our evolutionary ancestors). Other psychotronic weapons, such
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PARANORMAL PHENOMENA
as the "hyperspatial nuclear howitzer," are claimed to have equally
bizarre capabilities. Many of the sources cite the claim that Soviet
psychotronic weapons were responsible for the 1976 outbreak of Legion-
naires' disease, as well as the 1963 sinking of the nuclear submarine
Thresher.
POTENTIAL MILITARY APPLICATIONS
Some people, including some military decision makers, can imagine
potential military applications of the two broad categories of psychic
phenomena. In their view, ESP, if real and controllable, could be used
for intelligence gathering and, because it includes "precognition," ESP
could also be used to anticipate the actions of an enemy. It is believed
that PK, if realizable, might be used to jam enemy computers. prematurely
trigger nuclear weapons, and incapacitate weapons and vehicles. More
specific applications envisioned involve behavior modification; inducing
sickness, disorientation, or even death in a distant enemy; communicating
with submarines; planting thoughts in individuals without their knowledge;
hypnotizing individuals at a distance; psychotronic weapons of various
kinds; psychic shields to protect sensitive information or military instal-
lations; and the like. One suggested application is a conception of the
"First Earth Battalion," made up of "warrior monks," who will have
mastered almost all the techniques under consideration by the committee,
including the use of ESP, leaving their bodies at will, levitating, psychic
healing, and walking through walls.
THE COMMITTEE'S FOCUS
Although such colorful examples provide the context for our agenda,
the cumulative body of data in the discipline of parapsychology enables
us to judge the degree to which paranormal claims should be taken
seriously. Since 1882 reports of both naturally occurring incidents and
phenomena in laboratory settings have been accumulated in journals,
monographs, and books. Just to survey the reports in the refereed journals
of parapsychology would be an enormous undertaking. As scientists, our
inclination is, of course, to restrict ourselves to the evidence that purports
to be scientific. But the alleged phenomena that have apparently gained
most attention and that have apparently convinced many proponents do
not come from the parapsychological laboratory. Nothing approaching a
scientific literature supports the claims for psychotronic weaponry,
psychic metal bending, out-of-body experiences, and other potential
applications supported by many proponents.
The phenomena are real and important in the minds of proponents, so
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we attempt to evaluate them fairly. Although we cannot rely solely on a
scientific data base to evaluate the claims, their credibility ultimately
must stand or fall on the basis of data from scientific research that is
subject to adequate control and is potentially replicable.
We divided the task into two parts. First, we looked at the best scientific
arguments for the reality of psychic phenomena. Our sponsors, as well
as our own appraisal of the current status of parapsychology, indicated
that the two most influential scientific programs were the experiments on
&mote viewing and the experiments on psychokinesis using random
went generators. In addition, we looked at the research on the Ganzfeld
Bvhole visual field) because this, in the opinion of many parapsychologists,
" the most likely candidate for a replicable experiment. We also report
on a parapsychological experiment that the committee itself witnessed.
Second, we considered the arguments of proponents who rely on what
They call qualitative as opposed to quantitative evidence for the paranor-
Bal. Such evidence depends on personal experience or the testimony of
others who have had such experience. Most, if not all, of this evidence
cannot be evaluated by scientific standards, yet it has created compelling
Beliefs among many who have encountered it. Witnessing or having an
Anomalous experience can be more powerful than large accumulations of
Quantitative, scientific data as a method of creating and reinforcing beliefs.
Because personal experience rather than scientific data has been the
rsource of most beliefs in the paranormal, we have devoted some of our
resources to considering this sort of cognitive method as a tool for
Achieving knowledge.
STANDARDS OF EVIDENCE
Diverse justifications have been offered for pursuing paranormal claims.
Dne argument asserts that paranormal phenomena may no longer be
anomalous, given the implications of contemporary quantum mechanics.
Indeed, a few physicists have supported some parapsychologists in
maintaining that certain forms of precognition and psychokinesis are
Sonsistent with some interpretations of quantum theory. The other major
argument is that we have no choice but to get involved because the
Soviet Union already has a program to develop military applications of
Psychic phenomena.
Several proponents, including some scientists, firmly believe that
paranormal phenomena have been scientifically demonstrated several
times over. At the same time, most scientists do not believe that psi
exists. Many persons on both sides believe this paradox to be the result
of irrational and dogmatic belief systems. The proponents accuse the
critics of being closed-minded and bigoted. The critics imply that the
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PARANORMAL PHENOMENA
proponents have allowed wishful thinking to bias their judgment and that
they are incompetent scientists and are self-deceived. Both sides can
point to examples to back their positions.
One essential question confronts the committee: What does an impartial
examination of the scientific evidence reveal about the existence of psi?
Such an examination assumes that clear standards exist for judging the
adequacy of the evidence, which, in turn, raises the issue of what
constitutes sufficient evidence. That issue involves many difficult philo-
sophical, theoretical, and methodological matters. For example, Palmer,
in his "An Evaluative Report on the Current Status of Parapsychology"
(1985), denies that current parapsychological experiments can provide
any evidence for the existence of psi. This is because psi implies
paranormality and, according to Palmer, we cannot argue that a given
effect has a paranormal cause until we have an adequate theory of
paranormality. He further argues, however, that parapsychological ex-
periments can and do provide evidence for the existence of anomalies.
By an anomaly, Palmer means a statistically significant deviation from
chance expectation that cannot readily be explained by existing scientific
theories. The burden of Palmer's paper is that just such anomalies have
been demonstrated.
Because parapsychologists other than Palmer do not make this distinc-
tion between demonstrating an anomaly and testing a theory of paranor-
mality, we do not carry on this distinction in our own assessment of the
evidence. We tend to agree with Palmer on this matter, however. When
we talk about evidence for psi in the remainder of this chapter, we are
using psi in the neutral sense of an apparent anomaly rather than in the
stronger sense of a paranormal phenomenon.
MINIMAL CRITERIA
Fortunately, critics and parapsychologists appear to agree on the
general requirements necessary to demonstrate psi in a parapsychological
experiment. Both Palmer (1985) and James E. Alcock (Appendix B)
discuss such criteria in their respective papers. As Palmer points out, psi
is defined negatively as a statistical departure from a chance baseline
that cannot be accounted for by chance, sensory cues, or known artifacts.
Such a negative definition implies the minimal criteria required to justify
a conclusion that psi has been demonstrated.
Given the statistical aspect, it is imperative that the data be collected
in such a way that the underlying probability model and assumptions of
the statistical test are fulfilled. This means that targets must be adequately
randomized and that each trial in the experiment must be independent of
the preceding ones-and, of course, the statistical procedures must be
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applied and interpreted correctly. Given that all ordinary explanations
must be ruled out, the experimenter must take special precautions to
ensure that sensory cues, recording errors, subject fraud, and other
alternatives have been prevented. Although it is impossible to rule out
completely every possible contaminant or to anticipate every alternative,
there are reasonable standards that most parapsychologists would agree
should be followed.
Because different research paradigms have their own special require-
ments, no single set of standards can be specified in advance for all
parapsychological experiments. Experiments with electronic number
generators, for example, rarely have problems with data recording, but
they do require special methods such as tests of randomness and attention
t&the immediate physical environment that are unnecessary with more
traditional parapsychological experiments. One requirement for assessing
the adequacy of a given experiment is that its procedures and methods
analysis be adequately documented. Unless we know how the targets
MR00020032000
være selected, how the results were analyzed, how the possibility of
sahsory leakage was prevented, and how other such aspects of the study
votre carried out, we have no basis for evaluating the quality of the
formation provided by the experiment.
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GLOBAL CRITERIA
The criteria mentioned in the preceding paragraphs apply to the
ilividual experiment. More global criteria come into play when one
ants to evaluate an entire research program or set of experiments. Here
e look for such things as replicability, robustness, lawfulness, manip-
uability, and coherent theory. These criteria deal with the coherence
afd intelligibility of the alleged phenomena. It is in terms of such global
cfteria that parapsychological research has been especially vulnerable.
@Much of the objectivity involved in assessing the adequacy of research
applies to judging individual experiments. But science is cumulative and
depends not so much on the outcome of a single experiment as on
consistent and lawful patterns of results across many experiments carried
oft in a variety of independent settings. Lawful consistency in this sense,
according to both parapsychologists and their critics, has never been
found in parapsychological investigations in the history of psychic
research. Recently a few parapsychologists have expressed the hope that
the experiments on remote viewing, random number generators, and the
Ganzfeld (the very ones we have chosen to examine in detail in this
report) may actually yield the long-sought replicability. The type of
replicability that has been claimed so far is the possibility of obtaining
significant departures from the chance baseline in only a proportion of
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PARANORMAL PHENOMENA
the experiments, which is a kind of replicability quite different from the
consistent and lawful patterns of covariation found in other areas of
inquiry.
Despite the fact that scientific progress in a given area depends on the
accumulation of lawful and consistent patterns across many experiments,
the methods for deciding that such consistency exists are still quite
primitive in comparison with the standards for judging the adequacy of
a single experiment. Indeed, it is only within the past few years that
serious attention has been devoted to developing objective and standard-
ized procedures for evaluating the consistencies across a body of inde-
pendent studies. For the most part, judgment about what a body of
investigations demonstrates is still a surprisingly intuitive and haphazard
process. This probably has not been a serious drawback in those areas
of inquiry in which the basic phenomena are robust and experiments can
be conducted with high confidence that the predicted relations will be
obtained; but such impressionistic means for aggregating the outcomes
of several experiments in the domain of parapsychology open the door
to all the motivational and cognitive biases discussed in the paper prepared
for the committee by Griffin. Not only are the data and alleged correlations
erratic and elusive in this field, but their very existence is open to
question.
EVALUATION OF THE SCIENTIFIC EVIDENCE
To evaluate the best scientific evidence on the existence of psi, and
with the advice of proponents and our sponsors, we conducted site visits
to some of the most notable parapsychological laboratories. The para-
psychology subcommittee (see Appendix C) visited Robert Jahn's Engi-
neering Anomalies Research Laboratory at Princeton University, where
it witnessed presentations and demonstrations regarding psychokinetic
experiments on random number generators. Jahn and his associates also
briefed the subcommittee on the current status of their work in remote
viewing.
The subcommittee also visited Helmut Schmidt's laboratory at the
Mind Science Foundation, San Antonio, Texas. Schmidt pioneered the
use of random number generators in parapsychology experiments in 1969.
His is considered one of the two major research programs on psychokinesis
(the second is Jahn's).
As an additional posssible input, the committee agreed to participate
in a psychokinetic experiment of new design with Helmut Schmidt.
Specifically, Schmidt accepted the suggestion that the committee's con-
sultant, Paul Horwitz, be included in the conduct of the experiment. The
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work has not yet begun, however, and it now appears that we will not
have any results to report before our terms expire.
The chair of the parapsychology subcommittee also visited SRI Inter-
national, another major laboratory studying psychic effects on random
number generators. (This latter research group argues that the observed
effects are not due to psychokinesis but rather represent a special form
of precognition.) The subcommittee chair also attended the meetings of
the Parapsychological Association held at Sonoma State College in
California. The entire committee made a site visit to Cleve Backster's
Biboratory in San Diego (arranged to coincide with the committee's
Sheeting in La Jolla, California).
These site visits enabled the committee to observe firsthand the
Experimental arrangements and equipment used by some of the major
Contributors to parapsychological research. They also provided us an
Opportunity to discuss results, interpretations, and problems with a few
important investigators. We were impressed with the sincerity and
gledication of these investigators and believe that they are trying to
Gonduct their research in the best scientific tradition. We also got the
Impression that this type of research involves many unresolved problems
And still has a long way to go before it develops standardized, easily
Teplicable procedures. The information obtained from these site visits
does not provide an adequate basis for making scientific judgments. For
this we rely, as we would in other fields of science, on a careful survey
of the literature.
RESEARCH ON REMOTE VIEWING
The SRI Remote Viewing Program
Since the early 1970s, probably the best known research program
Ih parapsychology has been the experiments in remote viewing initiated
dy physicists Harold Puthoff and Russell Targ when they were at
SRI International. In a typical remote viewing experiment a subject,
Lor percipient, remains in a room or laboratory with an experimenter,
While a target team visits a randomly selected geographical site
Be.g., a shopping mall, an outdoor arena, the Palo Alto airport, the
Sloover tower). Neither the experimenter nor the subject has been
given any information about the target. Once the experimenter and
the subject are closeted in the laboratory, they wait for 30 minutes
before the subject begins to describe his or her impressions of the
target site.
Meanwhile the target team, consisting of two to four members of
the SRI staff, obtains instructions for going to a randomly chosen
target site from another SRI staff member. They then drive to the
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PARANORMAL PHENOMENA
designated target site and remain there for an agreed-on 15-minute
period (after allowing approximately 30 minutes to reach the site).
During the time that the target team remains at the target site, the
subject describes his or her impressions into a tape recorder and also
makes any drawings that would help to clarify those impressions.
When the target team returns to the laboratory, all the participants
listen to the tape recording of the subject's impressions. Then all
the participants go to the target site, where the subject is allowed
to see how closely his or her impressions agreed with the actual
target.
The first subject to participate in such a formal series of trials was
the late Pat Price. In the first series, consisting of nine sessions, the
duration of each session was 30 minutes. The transcript for each
session is rich in detail; the one published transcript in Targ and
Puthoff's first book runs to almost six printed pages (Targ and
Puthoff, 1977).
Given such data, how does one decide if the experiment was a
success? Did Price's descriptions, for example, convey correct knowl-
edge of the different target sites? In fact, two methods have been
used to demonstrate the effectiveness of remote viewing. One method
is simply to compare the description with the target and make a
judgment as to whether the correspondence is sufficient to claim a
"hit." The second method uses an independent judge to rank the
degree to which each description matches each site and then applies
statistical tests to decide if the association is greater than chance.
Unprecedented success was claimed for the early remote viewing
experiments in terms of both methods (Targ and Puthoff, 1974, 1977;
Puthoff and Targ, 1976). Many examples were supplied of dramatic
correspondences between impressions of the percipient and the physical
details of the actual target. Such correspondences, no matter how
dramatic and compelling, do not carry scientific weight, because it
is impossible to assess their probabilities. In addition, much psycholog-
ical research indicates how such subjective validation can create
strong, but false, illusions of matching (see below).
The more formal evidence from the rankings of independent judges
was also impressive. The first formal series of nine trials resulted in
seven of the transcripts being ranked 1 against their intended target
sites by the independent judge. Only one such ranking would be
expected by chance. Puthoff and Targ reported the probability of
such an outcome being due to chance as only 0.0000029. The second
formal series, using Hella Hammid, was equally impressive, producing
five first places and four second places in the rankings of transcripts
against target sites.
Although subsequent series by Targ and Puthoff, as well as by
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other investigators, have not always yielded such overwhelmingly
impressive results, most of them have continued to display highly
significant outcomes (Targ and Harary, 1984). On the surface, at
least, this is a reliable, simple, and highly effective recipe for
producing paranormal communication. Especially appealing is the
claim that remote viewing works with just about everyone. Targ and
Harary, for example, provide exercises for anyone who wants to
develop and improve his or her ability to pick up information at remote
Bes. Neither space nor time, its proponents assert, is a barrier. The
jercipient can pick up information from the surface of Jupiter as well
3 from target sites that can be visited at some future time.
Scientific Assessment of Remote Viewing
"After the first remote viewing experiments were conducted in the
Brly 1970s, many investigators throughout the world tried to follow
kait. Most of them believed that their findings supported the claims
f the SRI International researchers. The majority of these experi-
gents, however, consisted of informal demonstrations rather than
formal scientific experiments and relied solely on subjective matching.
[ the past 15 years, the number of formal experimental replications
f the SRI remote viewing experiments has been surprisingly few.
Targ and Harary (1984) include as an appendix in their book a
Sport by Hansen, Schlitz, and Tart that evaluates all the known
imote viewing experiments conducted from 1973 through 1982. "In
m examination of the twenty-eight formal published reports of
aftempted replications of remote viewing," write Targ and Harary,
Hansen, Schlitz, and Tart at the Institute for Parapsychology
@und that more than half of the papers reported successful out-
Momes." They concluded: "We have found that more than half
fifteen out of twenty-eight) of the published formal experiments
Have been successful, where only one in twenty would be expected
By chance."
Two comments may be in order with respect to the foregoing
conclusion. First, given the enormous publicity and the unusually
Trong claims, 28 formal experiments in 10 years seems surprisingly
few. In comparison, the Ganzfeld psi experiments produced approxi-
mately twice as many formal experiments during the same interval.
Second, 13 of the 28 formal experiments, or 46 percent, failed to
claim successful outcomes. This rate of failure is much higher than
what might have been expected on the basis of the earlier claims by
Targ and Puthoff (1977), namely, that they had succeeded with every
subject they had tried.
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Even 15 successful outcomes out of 28 tries is impressive, especially
by parapsychological standards. An inspection of the listed studies,
however, suggests that the 28 formal experiments vary considerably
in their importance. Some of these "published formal experiments"
appeared as brief reports or abstracts of papers delivered at meetings
of the Parapsychological Association or similar organizations. Others
appeared in print only as brief or informal reports in book chapters
or letters to the editor. Altogether, 15 of the 28 were published
under conditions that fall short of scientific acceptability. Only 13,
or 46 percent, of the experiments were published under refereed
auspices. As in other sciences, only published reports that have
undergone peer review and are adequately documented can be con-
sidered seriously as part of the scientific data base.
Of the 13 scientifically reported experiments, 9 are classified as
successful in their outcomes by Hansen et al. (Targ and Harary,
1984). Seven of these nine experiments were conducted by Targ and
Puthoff at SRI International, the remaining two at other labora-
tories. This relatively small harvest of nine "successful" experiments
suffers from the fact that each is seriously flawed. A variety of
problems afflicts the published reports on remote viewing. The
documentation, even according to many parapsychologists, is seriously
inadequate. Attempts by both neutral and skeptical investigators to
gain access to the raw data have typically been thwarted or strongly
resisted. Because the essence of scientific justification is public
accessibility to the data, this relative inaccessibility suggests that
much of the remote viewing data base is not part of science.
Most of the reasons for questioning the acceptability of the evi-
dence for remote viewing lie in a methodological flaw that char-
acterizes all but one of the experiments deemed successful: the
successive trials are not independent of one another. This lack
of independence has unfortunate consequences for any attempt to
draw conclusions about ESP based on the outcomes of such experiments.
The concept of independence is technical and somewhat difficult to
explain simply, but, since it is critical to understanding why the remote
viewing experiments fail to make their case, we supply an intuitive
explanation.
Assume that we are considering a remote viewing experiment in
which the subject participates in only two trials. In other words, we
deal with two randomly chosen target sites. For the first trial, the
target team goes to the first target site and remains there while the
subject produces his or her first description. Immediately after this
trial, the target team returns to the laboratory and takes the subject
to the actual target site so that he or she and the others can gain a
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subjective impression of how closely the description corresponds with
the target. For the second trial, the target team visits a second
randomly chosen site. While they are visiting this site, the subject
produces a second description.
When the experiment is over, the list of target sites (in random
order) and the transcripts of the subject's descriptions are given to
a judge, who also visits each site. While at a given site, the judge
reads the two transcripts and ranks them in terms of how well each
one corresponds with the particular site. In our example, one of the
transcripts will be ranked 1 and the other will be ranked 2 (with 1
indicating the better correspondence between that target and the
transcript). After visiting one site and doing this ranking, the judge
then visits the second site and repeats the ranking procedure. The
raw data can be set out in a matrix with the target sites as the
columns and the transcripts as the rows.
A perfect outcome would be indicated if the transcript produced
at the time the team was visiting site A was ranked 1 against that
site, and the transcript produced when the team was visiting site B
was ranked 1 for that site. (Of course, two trials would be too few
" to make an adequate statistical assessment of the success of the
matching-successful matching would occur too frequently just by
chance. The principles we want to illustrate, however, remain the
same for two as for many trials.)
If the successive trials in the experiment were independent of one
another, and we were interested only in direct hits (that is, outcomes
for which the intended transcript was rated 1 against the target
site), then we could expect the subject to make between zero and
two direct hits. Indeed, if chance alone were operating, there would
be four, equally likely, possibilities: (1) no hits, (2) a hit on the first
trial and a miss on the second, (3) a miss on the first trial and a hit
on the second, and (4) two hits. By this reckoning, the subject could
be expected to get two direct hits just by chance in one of every four
experiments.
But, as we indicated, the successive trials are not independent.
This is because the judge is almost certainly not going to rank a
transcript as 1 for more than one target site. This means, in our
example, that if he or she ranks the first transcript 1 for target A,
then he or she will probably rank the second transcript 1 for target
B. In effect, this lack of independence between trials means that,
instead of four equally likely possible outcomes there are only two:
no hits or two hits. The dependence between trials has created a
situation in which the chance probability of two hits is now 50 percent
rather than 25 percent.
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In this situation, if an experimenter uses a statistical test that
assumes independence, he or she will come out with the wrong
probabilities. In fact, the statistical test will exaggerate the signif-
icance of many outcomes. The failure of the experimenters to realize
this problem resulted in exaggerated levels of significance for the
early remote viewing experiments. Kennedy (1979), who originally
pointed to this problem, recalculated the probabilities for some of
these experiments. Puthoff and Targ (1976) reported that five of
their first six remote viewing experiments were significant at the .05
level. With Kennedy's corrections for lack of independence, only
two remained significant. According to Kennedy, only one of the
two successful replications by Bisaha and Dunne (1979) remained
significant with the more appropriate test.
One reason for the optimistic initial beliefs in the scientific reality
of remote viewing was the fact that the lack of independence between
trials produced exaggerated odds against chance results. But even
with conservative corrections for lack of independence, approxi-
mately one-third of the early experiments still yielded successful
outcomes.
One easy way to avoid this problem of dependence is to use a
separate target pool of possible sites for each trial. For example, for
the first trial one could designate a pool of four possible sites, one
of which is randomly chosen to be the actual target site. A second
pool of four different possible sites would be used for the second
trial. When the trials are completed, the judge is given the list of
the four sites for the first trial along with the subject's description
for that trial. The judge then ranks each site in terms of its
correspondence to the description. The four possible sites for the
second trial are then ranked in terms of their correspondence to the
subject's description for the second trial. In this illustration, the
subject has a probability of 1 in 4 of having the actual target site
ranked 1 on each trial, or a probability of 1 in 16 of being correct
on both trials.
This second procedure, which is typically used in most free-response
parapsychological experiments (such as the Ganzfeld experiments
discussed below), not only guarantees independence between succes-
sive trials, but also avoids other serious problems, which we discuss
next. The fact that the subject is given feedback by being taken to
the target site immediately after each trial creates an additional
form of dependence between trials. For this reason, other possibilities
exist for obtaining "successful" results artifactually. The tran-
scripts can contain clues that provide nonparanormal reasons for
judges to associate descriptions with targets correctly. Some of these
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clues can be quite overt, such as when a subject mentions in the
description how the current target apparently differs from a previous
target site. When such a clue appears in the description, it provides
the judge with information that the current description does not
belong with the previous site. This increases the probability that the
description will be matched with its appropriate target.
Marks and Kammann (1978) initiated a controversy, still not fully
resolved, by claiming that such overt clues were sufficient to account
forgthe striking results of the very first SRI remote viewing with
PagPrice. Targ and Puthoff did not deny the existence of such clues
in The Price series but argued that they were not sufficient to have
ac@unted for the results. This dispute still has not been settled
(T&t, Puthoff, and Targ, 1980; Scott, 1982; Marks and Scott, 1986).
DP96-80791R90020032000.161
Possibly this controversy over the role of the more overt clues
has deflected attention from a much more fundamental and fatally
damaging criticism first made by Hyman (1979) and independently by
Kennedy (1979). Hyman and Kennedy pointed out that the combination
of gnmediate feedback and lack of independence between successive
trials makes it virtually impossible to prevent sensory cueing in the
transcripts. As long as both the subject and the experimenter who is
clogeted with the subject are not blind to the preceding target sites,
there is no way to prevent the transcript from being affected in a
variety of possible and perhaps subtle ways by the knowledge of the
preceding targets.
Byman (1984-1985) provides an illustration of how such implicit sensory
cuang might occur (pp. 131-132):
Say that the target for the first session was the Hoover Tower at Stanford. This
willyalmost certainly influence what both the viewer and the interviewer say
durgig the second and subsequent sessions in the same series. Almost certainly
theviewer, during the second session, will not supply an exact description of the
Houver Tower. So, whatever the viewer says during the second session, a judge
should find it to be a closer match to the second target site than to the first one.
Now, assume that the second target site happened to be the Palo Alto train
station. The viewer's descriptions during the third session will avoid describing
either the Hoover Tower or the Palo Alto train station. We do not need to
hypothesize something as mysterious as psi to predict that a judge should find
thisThird description a better match to the third target site than either of the first
two. As we add sessions, this effect of immediate feedback should continue to
make the correlation between the viewer's descriptions and the target sites better
and better.
No amount of editing for overt clues can overcome this defect of
remote viewing experiments that follow the SRI pattern of dependent
trials and immediate feedback. The mechanism described by Hyman
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should result in some dramatic correspondences. These dramatic corre-
spondences, in conjunction with subjective validation, are a highly potent
recipe for creating the illusion (for both experimenters and subjects) that
ESP has occurred.
Palmer (1985), a major parapsychologist who otherwise carefully
considers the criticisms of parapsychology, misses the seriousness of this
flaw. In mentioning Hyman's criticism, he writes (p. 50):
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.
Perhaps such complacency has enabled experimenters to continue con-
ducting remote viewing experiments with this fatal flaw. In fact, the size
of the target pool, no matter how large, does not affect the validity of
Hyman and Kennedy's criticism. Nor does the claim that the pool
contained sufficient redundancy make much difference. Each geographical
site is unique and contains a combination of specific characteristics that
distinguishes it from the other sites in a given series. Indeed, as the
parapsychologists themselves have asserted, unless this were so, there
would be no possibility of the transcripts' being uniquely associated with
a given target site. In every one of the remote viewing experiments that
allows the possibility of subtle cueing, the possibility of the judges' being
able to make completely successful matchings because of this artifact is
highly plausible; and as long as a highly plausible, normal alternative to
ESP can account for the apparent success of the outcomes the parapsy-
chologists, by their own standards, cannot claim evidence for paranormal
transmission of information.
As it turns out, all but one of the nine scientifically reported studies of
remote viewing (at the time of the Targ and Harary survey) suffer from
the flaw of sensory cueing. The one experiment that cannot be faulted
for this reason is the long-distance remote viewing experiment of Schlitz
and Gruber (1980). However, as Hyman (1984-1985) has pointed out,
this experiment suffers from another very serious flaw. Gruber, who was
a member of the target team and thus was familiar with the targets,
translated the subject's target descriptions into Italian for the judging
process. Why the experimenters allowed such potential sources of biased
experimental procedures is not known, but the violation obviously negates
the results as evidence for psi.
Since the Targ and Harary survey, we have learned of two attempts
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to replicate the Schlitz and Gruber experiment without the flaw mentioned.
One, still unpublished, produced negative results. The second, by Schlitz
and Haight (1984), produced marginally significant results. Indeed, if the
more acceptable two-tailed test of significance had been used, the results
would not have been considered significant by customary standards.
Although the report of this study lacks sufficient documentation with
respect to certain aspects of procedure, both Palmer (1985) and Alcock
agree that this is the best controlled and most methodologically sound of
alltthe remote viewing experiments so far.
summary, after approximately 15 years of claims and sometimes
bißer controversy, the literature on remote viewing has managed to
produce only one possibly successful experiment that is not seriously
flæed in its methodology-and that one experiment provides only
m&ginal evidence for the existence of ESP. By both scientific and
paapsychological standards, then, the case for remote viewing is not
just very weak, but virtually nonexistent. It seems that the preeminent
position that remote viewing occupies in the minds of many proponents
results from the highly exaggerated claims made for the early experiments,
as vell as the subjectively compelling, but illusory, correspondences that
experimenters and participants find between components of the descrip-
tims and the target sites.
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RESEARCH ON RANDOM NUMBER GENERATORS
The Basic Paradigm
The use of random number (or random event) generators for
parapsychological research began in the 1960s and became relatively
standard during the 1970s as the technology became widely available.
A Random number generator (RNG) is simply an electronic device
thas uses either radioactive decay or electronic noise to generate a
sequence of random symbols. Originally such devices were used to
tes? ESP, usually clairvoyance or precognition, but the most wide-
sprgad and widely known work focuses on what is called micropsy-
ch&kinesis, or micro-PK. In such research a subject, or operator,
attempts to mentally bias the output of the random number generator,
so ghat it produces a nonrandom sequence.
Most of the work with RNGs has used binary generators, or what
Schmidt calls "electronic coin flippers." The output on each trial
is either 0 or 1, that is, heads or tails. If the RNG is unbiased and
truly random, then it should produce, on control runs, sequences
of Os and Is that are independent of each other and that, in the long
run, will yield 1s 50 percent of the time.
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In a typical experiment, a subject (either a person who claims to be
a psychic or a person chosen for availability who does not make such
claims) is placed in the vicinity of the RNG and attempts to bias the
output either toward more or fewer 1s. When an animal is used as
the subject, the RNG output is usually coupled to an outcome whose
frequency the animal presumably would like to either increase or
decrease. In an experiment carried out with cockroaches, for example,
one outcome was electric shock. If, during the time the output of
the RNG was coupled with the shock apparatus, the proportion of
shocks decreased below 50 percent, this would be taken as evidence
of a psychokinetic effect of the cockroach on the output of the RNG.
The RNG experiments have been of interest to some military and
governmental personnel because of the possibility, if such micro-PK
is demonstrable, of psychically affecting equipment and computers
that depend on the output of electronic symbols.
Results of the Experiments
In a recent survey 56 reports published between 1969 and 1984 and
dealing with research on possible psychokinetic perturbations of
binary RNGs (Radin, May, and Thomson, 1985), the reviewers counted
332 separate experiments. Of the 332 experiments, 188 were reported
in refereed journals or conference proceedings, and of these 188
experiments with some claim to scientific status, 58 reported statis-
tically significant results (compared with the 9 or 10 experiments
that would be expected by chance). The other 144 experiments were
produced by the Engineering Anomalies Research Laboratory at
Princeton University; none of them had been published in a refereed
journal at the time of the survey. Of these 144 experiments, 13 were
classified as yielding statistically significant results. So, in the total
sample of 332 experiments, 71 yielded ostensibly significant results
at the traditional .05 level. This amounts to a success rate of
approximately 21 percent, compared with the rate of 5 percent that
would be expected by chance.
Palmer (1985) and Alcock agree that such results cannot be
accounted for by chance. In other words, both the parapsychologist
and the skeptic, in their respective reviews of the RNG research,
agree that something other than accidental fluctuation is producing
these results. Palmer calls this something an anomaly, which, while
it may or may not be paranormal, cannot be explained by current
scientific theories. Alcock points to various defects in the experimen-
tal protocols and concludes that no conclusions about the origins
of these departures from randomness are justified until successful
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outcomes can be more or less consistently produced with adequately
designed and executed experiments.
Both Palmer and Alcock focus their reviews on the two most
influential research programs on RNGs. One is the program of Helmut
Schmidt, a quantum physicist who began working on psi and RNGs in
1969. The other is the program begun by Robert Jahn in the late
1970s, when he was dean of the School of Engineering and Applied
Science at Princeton University (see Jahn, 1982). These two programs
have accounted for almost 60 percent of all known experiments on
INGs. They have also been the most consistently successful in
Phieving statistically significant outcomes.
00999 R00020032000131
3Although the results suggest that on each experimental group of
Rals the number of Is is greater or less than the 50 percent baseline
Depending on the intended direction), the actual degree of deviation
Fom chance is quite small. As Palmer (1985) indicates, Schmidt's
objects have averaged approximately 50.5 percent hits over the years,
compared with the expected baseline of 50 percent. This amounts to
producing one extra 1 every 100 trials. The reason such a small
Sparture from chance is statistically significant is that an enormous
Pumber of trials is conducted with each subject.
Jahn and his colleagues at Princeton have, in a much shorter time,
produced on the order of 200 times the number of trials that Schmidt
&d in 17 years. The Princeton researchers have also produced a
significantly lower success rate than Schmidt. In their formal series
& 78 million trials, the percentage of hits in the intended direction
was only 50.02 percent, or an average of 2 extra hits every 2,500
@als. Again, such an extremely weak effect is statistically signifi-
ant only when one is dealing with very large numbers of trials.
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Scientific Assessment of the RNG Experiments
&Palmer (1985) carefully reviews the major criticisms of the work
Schmidt and Jahn. He addresses questions about security, because
subjects often are left alone with the apparatus during the data
collection. In the Princeton experiments, the data are always col-
l@ted when the subject is alone with the apparatus. Although the
PSinceton experiments now contain a number of features that would
make it extremely difficult for a naive subject to bias the results, it
is not clear that this has always been so. It would make good scientific
sense to conduct some trials during which the subject is carefully
monitored to see if successful outcomes are still obtained.
The major reservations about the RNG experiments concern the
adequacy of the randomization of the outputs. Schmidt applied only
limited tests for the randomness of his machines, and most of the
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control trials were gathered by allowing the machine to run for
long periods, usually overnight. Although these controls usually
produced results in line with the chance baseline, critics have pointed
out that the controls are unsatisfactory because they were not
conducted for shorter runs and at the same time as the data from
the experimental sessions.
Palmer grants that the critics are correct in pointing out some of
the shortcomings in Schmidt's methods for testing and controlling
for the randomization of his machines. Palmer also correctly points
out that such criticism is somewhat blunted by the fact that the
critics have not specified any plausible mechanisms that would account
for the obtained differences between the experimental and control
trials. He is correct in pointing out that the Princeton experiments
provide more adequate controls; however, he has probably assumed
that the baseline controls in the Princeton experiments were run at
the same time as the two experimental conditions of hitting and
missing. It is easy to interpret the somewhat ambiguous description of
the procedure in this manner. The relevant part of the authors'
methodological description is as follows (Nelson, Dunne, and Jahn,
1984:9):
The primary variable in these experiments is the operator's pre-recorded
intention to shift the trial counts to higher or lower numbers. This direc-
tional intention may be the operator's choice-the so-called "volitional"
mode-or it may be assigned by a specified random process-the "instructed"
mode. In either mode, data are collected in a "tri-polar" protocol, wherein
trials taken under an intention to achieve high numbers (PK +), trials taken
under an intention to achieve low numbers (PK-), and trials taken as
baseline, i.e. under null intention (BL), are interspersed in some reasonable
fashion, with all other operating conditions held identical. For all three
streams of data, effect size is measured relative to the theoretical chance
mean. This tri-polar protocol is the ultimate safeguard in precluding any
artifacts such as residual electronic biases or transient environmental
influences from systematically distorting the data.
At first glance it might appear as if the tripolar protocol requires
that the two types of experimental groups of trials and the baseline
group of trials always be taken at the same session. This would be
consistent with the claim that "any artifacts such as residual
electronic biases or transient environmental influences" were thereby
precluded "from systematically distorting the data." Such a claim
would be justified if, in fact, at each session one group of trials of
each of the three types was obtained, provided that each group of
trials was of the same length and that the order of the three types
of trials was independently randomized for each session.
The description provided by Nelson and his colleagues says nothing
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at all about the order in which the three conditions were conducted,
and a careful reading indicates that the baseline data may not always
have been obtained at the same sessions and under the same conditions
as the experimental groups of trials. It is not clear what the authors
mean by stating that the three trials "are interspersed in some
reasonable fashion." In fact, an examination of the data reported
for each subject makes it clear that the strict tripolar protocol
could not possibly have been followed with much of the data
confection, because in many cases the baseline data are entirely
abEnt or occur with many fewer trials than the experimental data.
Inated, it is not even clear that PK + and PK - trials were always
obRined at the same sessions, because for some subjects the total
numbers of these trials are not equal.
Se suspect that, over the six years or so during which the Princeton
group was accumulating its data base, it made many changes in both
the hardware and the experimental protocol. The sophisticated
procedures currently in use and the requirement that the three types
of drials be of equal length and that one of each be conducted at
eagh session are the most recent variations in the paradigm. Unfor-
tu@tely, the data are not presented in such a way that it is possible
todetermine whether the successful results are due to the earlier
The later experiments.
Such issues become especially important when we consider the
extremely small size of the effect being claimed and when we further
reggize, as Palmer has pointed out, that the bulk of the significance
ingthe formal series was due to just one subject, who contributed 23
pegcent of the total data. This one subject achieved a hit rate of
50.05 percent. When her data are eliminated, the remaining data
yield a hit rate of 50.01 percent, which is no longer significantly
different from chance.
&h other words, it looks as if almost all the success of Jahn's huge
data base can be attributed to the results from one individual, who,
over the years, produced almost 25 percent of the data. This one
in@vidual was not only the most experienced subject, but also,
presumably, familiar with the equipment. When combined with the
fact, as Palmer points out, that the Princeton experiments provide
ingequate documentation on precautions to prevent tampering by
subjects, it becomes even more important to see if the same degree of
success can be achieved when the sessions are adequately monitored.
Alcock, in his review of the same RNG studies surveyed by Palmer,
points to a number of weaknesses in both the Schmidt and the Princeton
experiments. For example, he faults Schmidt's experiments for such
things as inadequate controls, failure to examine the target se-
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PARANORMAL PHENOMENA
quences, overcomplicated experimental setups, inadequate tests of
randomness, and lack of methodological rigor. Alcock faults the
Princeton experiments for such things as failing to randomize the
sequence of groups of trials at each session, inadequate documentation
on precautions against data tampering, and possibilities of data
selection.
Palmer and Alcock do not really differ in their assessments of the
shortcomings of the Schmidt and Princeton RNG experiments. They
do differ, however, on what conclusions can be drawn from such
imperfect experiments. Palmer emphasizes the fact that the critics
have not provided plausible explanations as to how the admitted
flaws could have caused the observed results. His position seems to
be that, unless the critics can provide such plausible alternatives,
the results should be accepted as demonstrating an anomaly. Alcock
focuses on the fact that the successful results have been obtained
under conditions that fall short of the experimental ideals that
parapsychologists themselves profess. He emphasizes that the para-
psychologists have no right to claim to have demonstrated psi from
experiments that have been conducted with "dirty test tubes." Such
a revolutionary conclusion as the existence of psi demands justifi-
cation from experiments that have clearly used "clean test tubes."
What would it take to conduct an adequate RNG experiment?
May, Humphrey, and Hubbard (1980) set out to do just that. After
reviewing all available RNG experiments from 1970 through 1979
and taking into account the various deficiencies in these experiments,
they gathered together and meticulously tested the components
necessary to provide adequately randomized trials. They also devised
a careful experimental protocol and set out in advance the precise
criteria that would have to be fulfilled before they could call their
results successful. Going further, after they completed the experi-
ment with results that met their criteria for success, they subjected
their equipment to all sorts of physical extremes to see if they could
obtain such a degree of success by a possible artifact.
They report that this singularly well controlled RNG experiment in
fact met their criteria for success. It is unfortunate, therefore, that this
carefully thought-out experiment was conducted only once. After the one
successful series, using seven subjects, the equipment was dismantled,
and the authors have no intention of trying to replicate it (personal
communication, August 1986). It is unfortunate because this appears to
be the only near-flawless RNG experiment known to us, and the results
were just barely significant. Only two of the seven subjects produced
significant results, and the test of overall significance for the total formal
series yielded a probability of 0.029.
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The experiment, while nearly flawless, still had some problems as
evidence for psi. For one thing, it was reported only in a technical report
in 1980 and has never been published in a refereed scientific journal.
Despite the admirable attention to details, all the control trials were taken
when no human being was present. One might argue that this was not an
ideal control for the experimental session, in which a subject was
physically present in the room. The authors have assured us that their
various attempts to bias the machine by physical means almost certainly
ruis out the possibility that the mere presence of a human being could
h&e affected the output. However, a physicist who claims to have
several years of experience in constructing and testing random number
deices tells us that it is quite possible, under some circumstances, for
the human body to act as an antenna and, as a result, possibly bias the
owput.
May and his colleagues at SRI, in the same technical report in which
they claim successful results for their single experiment, surveyed all the
RSG experiments known to them through the year 1979 and found that
thoir combined significance was astronomically high. They add (May,
Humphrey, and Hubbard, 1980:8):
TMis impressive statistic must, however, be evaluated with respect to experimental
equipment and protocols. All the studies surveyed could be considered incomplete
in at least one of the following four areas: (1) No control tests were reported in
more than 44 percent of the references. Of those that did, most did not check
for temporal stability of the random sources during the course of the experiment.
(There were insufficient details about the physics and constructed parameters
ofthe experimental apparatus to assess the possibility of environmental influences.
(The raw data was not saved for later and independent analysis in virtually
afty of the experiments. (4) None of the experiments reported controlled and
limited access to the experimental apparatus.
"As far as we can tell, the same four points can be made with respect
t& the RNG experiments that have been conducted since 1980. The
sigulation for the RNG experiments thus seems to be the same as that for
r
mote viewing: over a period of approximately 15 years of research,
only one successful experiment can be found that appears to meet most
o
Sthe minimal criteria of scientific acceptability, and that one successful
e
periment yielded results that are just marginally significant.
RESEARCH ON THE GANZFELD
The Ganzfeld Experiments
The Ganzfeld psi experiments are named after the term used by
Gestalt psychologists to designate the entire visual field. For
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PARANORMAL PHENOMENA
theoretical purposes, the Gestalt psychologists wanted to create a
situation in which the subject or observer could view a homogeneous
visual field, one with no imperfections or boundaries. Psychologists
later discovered that when individuals are put into a Ganzfeld
situation they tend quickly to experience what they described as an
altered state of mind.
In the early 1970s, some parapsychologists decided that the use of
the Ganzfeld would provide a relatively safe and easy way to create
an altered state in their experimental subjects. They believed that
such a state was more conducive to picking up the elusive psi signals.
In a typical psi Ganzfeld experiment, the subject, or percipient, has
halved ping-pong balls taped over the eyes. The subject then reclines
in a comfortable chair while white noise plays through earphones
attached to his or her head. A bright light shines in front of the
subject's face. When seen through the translucent ping-pong balls,
the light is experienced as a homogeneous, foglike field. When so
prepared, almost all subjects report experiencing a pleasant, altered
state within 15 minutes.
While one experimenter is preparing the subject for the Ganzfeld
state, a second experimenter randomly selects a target pool from a
large set. The target pool typically consists of four possible targets,
usually reproductions of paintings or pictures of travel scenes. One
of the four is chosen at random to be the target for that trial. The
target is given to an agent, or sender, who tries to communicate its
substance psychically to the subject in the Ganzfeld state. After a
designated period, the subject is removed from the Ganzfeld state
and presented with the four candidates from the target pool. The
subject then ranks the four candidates in terms of how well each
matched the experience of the Ganzfeld period. If the actual target
is ranked first, the trial is designated a hit. An actual experiment
consists of several trials. In the example, the probability is that one
of every four trials will produce a hit. If the number of hits
significantly exceeds the expected 25 percent, then the result is
considered to be evidence for the existence of psi.
Critique of the Ganzfeld Experiments
In a careful and systematic review of the Ganzfeld experiments
undertaken in 1981 and published in the March 1985 issue of the
Journal of Parapsychology, Hyman concluded that the data base
exhibited flaws involving multiple testing, inadequate controls for
sensory leakage, inadequate randomization, statistical errors, and
inadequate documentation. These flaws, in his opinion, were sufficient
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to disqualify the Ganzfeld data base as evidence for psi. Of the 42
experiments, 39 (93 percent) used multiple analyses, which artificially
inflated the chances of obtaining significant outcomes. Only 11 (26
percent) 'clearly indicated that they had adequately randomized the
target selections. As many as 15 (36 percent) used inferior randomi-
zation, such as hand shuffling, or no randomization at all. The
remaining 16 experiments did not supply sufficient information on how
they had chosen the targets. As many as 23 of the experiments (55
pegent) used only one target pool, which means that the subject
w& handed for judging not a copy of the target but the very same
taget that the percipient had handled, permitting the possibility of
sensory cueing. Although the argument for psi is mainly a statistical
org, the reports of 12 experiments (29 percent) revealed statistical
erfors. A number of other departures from optimal practice were also
found.
The same issue of the Journal of Parapsychology contained a
lengthy rebuttal by parapsychologist Charles Honorton, one of the
pioneers of the Ganzfeld psi technique. Honorton disputed many of
Haman's opinions as to what constituted flaws; provided a reanalysis
offthe data base to overcome many of the statistical weaknesses of
the original experiments; and argued that the flaws he agreed existed
were not sufficient to have accounted for the findings. In this respect
his analysis is consistent with Palmer's approach. He does not deny
that the experiments depart from optimal design, but he argues that
suh departures are insufficient to account for the results.
Honorton and Hyman had the opportunity to discuss their differ-
ences about psi in general at the Parapsychological Association
meetings in 1986; as a result, they agreed to draft a joint communiqué
tog emphasize those points on which they agree. That communiqué
appeared in the December issue of the Journal of Parapsychology
(Hyman and Honorton, 1986). They agree that the current data base
isPinsufficient to support either the conclusion that psi exists or the
conclusion that the results are due to artifacts. They further agree
that the issue can be settled only by future experiments conducted
according to the stated standards of parapsychology, which are also
the accepted standards of psychological research.
Another important input to the committee's judgment on the
Ganzfeld research was the systematic evaluation of the contemporary
parapsychological literature by Charles Akers (1984), a former
parapsychologist. Akers's critique used a methodological strategy
different from that used by Hyman. Hyman undertook to evaluate
the entire data base of a single research paradigm (Ganzfeld),
including both successful and unsuccessful outcomes. Akers surveyed
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PARANORMAL PHENOMENA
contemporary ESP experiments broadly, but confined his evaluation
to those that had produced significant results with unselected
subjects. Hyman assigned flaws to experiments without regard to
whether each flaw, by itself, could have caused the observed outcome.
Akers charged a flaw to a study only if he thought the flaw could
have been sufficient to produce the observed result. He chose a
sample of 54 parapsychological experiments from areas of research
that had been previously reviewed by Honorton or Palmer; his intent
was to choose experiments that could be viewed as the best current
evidence for the existence of psi. As a result of this exercise, he
concluded (Akers, 1984:160-161):
Results from the 54-experiment survey have demonstrated that there are
many alternative explanations for ESP phenomena; the choice is not simply
between psi and experimenter fraud. ... The numbers of experiments ...
flawed on various grounds were as follows: randomization failures (13),
sensory leakage (22), subject cheating (12), recording errors (10), classification
or scoring errors (9), statistical errors (12), reporting failures (10). ... All
told, 85% of the experiments were considered flawed (46/54).
This leaves eight experiments where no flaws were assigned. . .. Although
none of, these experiments has a glaring weakness, this does not mean that
they are especially strong in either their methods or their results. . . .
In conclusion, eight experiments were conducted with reasonable care,
but none of these could be considered as methodologically ideal. When all
54 experiments are considered, it can be stated that the research methods
are too weak to establish the existence of a paranormal phenomenon.
RESEARCH ON ELECTRICAL ACTIVITY AND EMOTIONAL STATES
The Backster Laboratory
In addition to examining parapsychological research in areas that
have produced large literatures, the committee witnessed an example
of experimental work at a far less developed stage. On February 10,
1986, committee members visited the Backster Research Foundation
in San Diego and saw a demonstration of experimental procedures
for detecting a correlation between the electrical activity of oral
leukocytes and the emotional states of the donor.
Cleve Backster is a polygraph specialist who had at one time helped
develop interrogation techniques for the Central Intelligence Agency
and now runs his own polygraph school in San Diego. The school is
housed in the same rooms that constitute the Backster Research
Foundation, which is devoted to the study of what Backster refers
to as primary perception. Backster's research on paranormal matters
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began in February 1966, when he recorded, from a philodendron plant
that he had hooked up to a polygraph, a response he recognized as
similar to that of human beings in emotional states. Backster believed
he had demonstrated that the plant showed such emotional response
when brine shrimp or other living organisms were either threatened
or actually killed in an adjoining room. The notion of primary
perception in plants became both a popular subject for research and
a highly controversial concept during the late 1960s and early 1970s.
De were told that Backster has quietly continued his researches
in this and related matters. He has now devised a technique for
reOrding electrical activity in leukocytes taken from a donor's
math. The advantage of this technique, we were told, is that the
legocytes respond mostly to emotional states of the donor.
One committee member volunteered to be the demonstration subject.
Another member accompanied him to observe the techniques for
obtaining the leukocytes and preparing them for recording. The
sample was obtained by having the subject "chew" on a 1.2 percent
sabine solution and then spit it back into a centrifuge tube. Ten such
samples were obtained in this way. The samples were then spun in a
centrifuge for six minutes, and the particulate matter at the bottom
ofseach tube was pipetted into the preparation tube. The preparation
tube contained about one centimeter of particulate matter and was
filled almost to the top with 1.2 percent saline solution. Two
uninsulated wire electrodes were inserted into the bottom of the
tuse, which was then placed within a shielded cage and connected
byBeads to an EEG-type recording apparatus.
During the demonstration, the subject sat approximately two meters
frogn the preparation. We were told that subjects usually sit about
fivg meters from the preparation. A split-screen projection video
display was provided: the lower portion of the screen recorded the
movements of the polygraph paper and pen as they produced a record
of Athe electrical activity presumably taking place in the leukocyte
preparation. The upper portion of the screen recorded the behavior
of The seated subject.
& his previous research using this arrangement, Backster reported
tha, when the subject revealed an emotional reaction, the electrical
action of the leukocytes showed a corresponding reaction. During
our demonstration, the polygraph record produced several strong
deflections in both the control and the experimental series, but they
did not obviously correlate with any corresponding thoughts or
emotional states of the subject as various stimuli were presented.
Backster suggested that this was probably because so many people
were crowded into the laboratory that the leukocytes were respond-
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ing to thoughts and feelings of other individuals in the room. Thus,
a demonstration of results, as opposed to techniques, was not, after
all, going to be possible during our visit.
Backster then showed us videotapes of the split-screen results he
had obtained in his "formal" experiments. The results consisted of
12 examples of apparent correlations between an emotional response
and a deflection of the polygraph record. The 12 examples came from
7 sessions with 7 different subjects. Although the information is not
given in his written report, it appears that each session lasted for
approximately half an hour. During this time, the donor is engaged
in conversation or watches videotapes of television programs. The
sessions are not standardized or planned. Backster's intent, appar-
ently, is to elicit spontaneous emotional responses from a subject
during the session. He believes that a stimulus that evokes an
emotional response in one subject will not necessarily do so in
another subject.
In one example, the subject was a young man who was looking at
an issue of Playboy magazine. The polygraph tracing began to display
large deflections soon after he encountered a nude photograph of
an attractive young woman. The large deflections continued for
approximately two minutes; the tracing slowly settled down to
normal activity after the magazine was closed. Soon after, the young
man reached for the closed magazine, and the record reveals a single
deflection at that point. In another example, the subject was a
retired police lieutenant. When discussing his approaching retirement,
he was asked a question about his wife's attitude toward having him
"underfoot." A large deflection of the polygraph tracing occurred
soon after this question was asked. When asked, the donor confirmed
that he was emotionally aroused at that moment in the session (see
Backster and White, 1985).
Cleve Backster and his supporters apparently believe that he has
successfully demonstrated that detached oral leukocytes respond
to the emotions of their donor even when separated by as much as
several miles. They also believe that these results are reliable and
replicable.
Critique of the Backster Experiment
What we have read and observed about Backster's procedures does
not justify the claim he is making. His answers to our questions made it
clear that he has not considered using the appropriate controls needed
to ensure that the obtained "correlations" are real and due to the causes
he has assumed. To make adequate physiological recordings from a
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preparation of in vitro leukocytes and to demonstrate the correlation
between emotional response and leukocyte activity requires experimental
arrangements and procedures at a level of sophistication well beyond
those we observed.
Committee members who are knowledgeable about the procedures and
instrumentation of psychophysiological experiments expressed doubts
about the adequacy of the setup to perform the tasks Backster has
undertaken. Serious doubts were expressed about the possibility that the
leukocytes were alive at the time of recording. Further doubts were
expressed about the setup's ability to avoid contamination of the recording
progedures by stray influences of various sorts. We do not discuss these
dra@backs in detail here. We confine our discussion to Backster's method
for Establishing a correlation between the alleged activity of the detached
leukocytes and the emotional state of the donor. When we consider how
the existence of such correlations was established, we again see how
inappropriate methodology can lead to very misleading conclusions.
Many problems exist with regard to Backster's procedures for detecting
congelations. In trying to demonstrate a pattern of covariation between
tworecords of behavior over time, one record is the tracing of amplified
electrical activity coming from the electrodes and through the leads.
Although this tracing can be quantified, Backster has apparently made
no attempt to do so. Instead, he has relied on visual inspection of the
polygraph record to pick out points at which the deflections of the pen
from the baseline are noticeable. Although such subjective judgment is
scientifically unacceptable, the deflections that he uses in his examples
seea sufficiently marked that they probably can be considered to be real
2002/05
de ations from the baseline. At any rate, let us assume that responses
on che polygraph record can be visually pinpointed with reasonable
objectivity.
The deflections on the polygraph record are then compared with
happenings on the concurrent videotaping of the conversation with the
sub@ct. Here we encounter very serious problems as to what constitutes
an Emotional response on this behavioral record. Backster believes he
candidentify categories of potentially emotionally arousing stimuli in the
nonstandardized, qualitative, ongoing record of conversation. He then
can determine if the subject was experiencing an emotional reaction to
suck a stimulus by simply replaying the record, pointing to the segment
that corresponds to a place where the polygraph showed a deflection,
and asking the subject if he or she recalls what was taking place at that
moment as an emotionally arousing experience. If the subject agrees,
this is said to confirm a "correlation" between the emotional state and
the corresponding activity of the tracing.
Such a purely subjective determination of an emotional response opens
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the process to a variety of known biases, many of them discussed in the
paper prepared for the committee by Griffin (Appendix B). The literature
on "illusory correlation" (Alloy and Tabachnik, 1984; Griffin paper)
makes it clear how subjective expectations and cognitive biases can lead
to false impressions of correlation. Backster's method of searching for
correlations compounds these inevitable biases: he does not independently
determine moments of emotional response in the subject's behavioral
record and moments of polygraph deflections and then look for a match
between the two. Instead, he apparently looks for polygraph deflections
and then tries to determine if an emotional response can be found that
occurred in the vicinity of the polygraph activity. In other words, the
determination of the emotional response is done with full knowledge of
the fact that a polygraph deflection has occurred.
Under such circumstances, we would expect processes of subjective
validation to operate. In addition, the method of verifying the emotional
response, by asking the subject to acknowledge that he or she was in
fact experiencing such a state at the moment the polygraph record
indicated a leukocyte response, is itself suspect. This is the sort of
circumstance in which demand characteristics (i.e., responses determined
by the presumed intent of the experimenters) are known to operate.
Good' science dictates that the moments of emotional response should
be determined independently of the moments of polygraph response.
Both the experimenter and the subject must be blind to the polygraph
record when determining the moments of emotional response. Only when
the determination of events on the two records has been made independ-
ently of each other can the records be compared to determine if the
emotional responses and the polygraph activity are correlated.
Illusory correlations occur because our subjective judgments of cov-
ariation tend to use only a portion of the relevant information and because
we tend to bias observed events in terms of our expectations. In particular,
intuitive judgments of covariation tend to focus only on the co-occurrence
of treatment of interest and successful outcomes, ignoring times when
the treatment co-occurred with unsuccessful outcomes. Backster uses
only those examples from his records in which an emotional response
co-occurs with a polygraph deflection; the 12 such examples from the 7
experimental series represent a very small fraction of the total data
collected.
Not only is a sample of just 12 co-occurrences probably too small for
estimating whether a true correlation exists, but it is also impossible from
this information alone to estimate whether any correlation exists. All the
data are needed for this purpose. Almost certainly, more than 12 polygraph
deflections must have appeared in the total record. In the brief demon-
stration for the committee, both the control and the experimental series
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yielded several deflections, so it is reasonable to assume that many more
than 12 deflections were obtained in the complete record. It is likely that
these unreported deflections were not preceded by any emotional re-
sponses.
Almost certainly, more than 12 emotional responses must have appeared
in the total record. The point of conducting the sessions was to expose
the subjects to a variety of emotional stimuli; therefore, it is essential to
know the number of times that emotional responses occurred without the
colresponding occurrence of polygraph responses. Finally, to determine
corelation, it is essential to know the frequency of co-occurrence of the
alence of emotional responses and the absence of polygraph responses.
1R080200320
All this information is needed to determine whether the claimed
courelation exists. All the data must be used. From these data, one can
compare the proportion of times that an emotional response is followed
bra polygraph response with the proportion of times that the absence
ofan emotional response is followed by a polygraph response. Only if
these two proportions are significantly different from one another can we
assume that the data provide evidence for a correlation between emotional
response and leukocyte activity. The fact that Backster was able to find
12examples of the co-occurrence between emotional response and
p&fygraph deflection, even if these correspondences had come from
double-blind matching, provides us with absolutely no information about
whether a correlation exists.
The stronger claim would be, of course, not that a correlation exists,
but that a causal connection exists between the subject's emotional states
and the responses of the detached leukocytes. As Chapter 3 on evaluation
indicates, such a causal explanation requires much more than the
demonstration of correlation between two series. Because Backster did
no, use double-blind procedures to determine emotional responses, and
because the procedures he did use are known to be just those that
faglitate the occurrence of a variety of subjective biases, he may well
have obtained a correlation between his two series. However, his
procedures for finding such correlations are sufficiently flawed that we
degnot know if in fact the suspected (and presumably biased) correlation
acgially does exist in his data. The Backster experiment indicates that
the best intentions combined with scientific instrumentation and poly-
graphic records cannot, in themselves, guarantee data of scientific quality.
DISCUSSION OF THE SCIENTIFIC EVIDENCE
Both the parapsychologists cited in this report and the critics of
parapsychology believe that the best contemporary experiments in para-
psychology fall short of acceptable methodological standards. The critics
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conclude that such data, based on methodologically flawed procedures,
cannot justify any conclusions about psi. The parapsychologists argue
that, while each experiment is individually flawed, when taken together
they justify the conclusion that psi exists.
Palmer's conclusion in this regard is unique. Although he agrees that
the data do not justify the conclusion that a paranormal phenomenon has
been demonstrated, he argues that the data, with all their drawbacks, do
justify the conclusion that an anomaly of some sort has been demonstrated.
It is this purported demonstration of an anomaly that, according to
Palmer, further justifies the claim that parapsychologists do have a subject
matter. The awkward aspect of Palmer's position is that, without an
adequate theory, there is no way to know that the anomaly "demon-
strated" in one experiment is the same anomaly "demonstrated" in
another; indeed, there is no limit to the possible causes of the anomaly
in a given experiment. Without an adequate theory, there is no reason
to assume that the various anomalies constitute a coherent or intelligibly
related class of phenomena.
The committee distinguishes among three types of criticism that can
be leveled at a given parapsychological finding. The first is what we might
refer to as the smoking gun. This type of criticism asserts or strongly
implies that the observed findings were due not to psi but to factor X.
Such a claim puts the burden of proof on the critic. To back up such a
claim, the critic must provide evidence that the results were in fact caused
by X. Many of the bitterly contested feuds between critics and proponents
have often been the result of the proponent's assuming, correctly or
incorrectly, that this type of criticism was being made.
The second type of criticism can be referred to as the plausible
alternative. In this case, the critic does not assert that the result was due
to factor X, but instead asserts that the result could have been due to
factor X. Such a stance also places a burden on the critic, but one not
so stringent as the smoking gun assertion. The critic now has to make a
plausible case for the possibility that factor X was sufficient to have
caused the result. For example, optional stopping of an experiment on
the part of a subject can bias the results, but the bias is a small one; it
would be a mistake to assert that an outcome was due to optional stopping
if the probability of the outcome is extremely low. Akers's critique,
which was previously discussed, is an example based on the plausible
alternative.
The third type of criticism is what we have called the dirty test tube.
In this case, the critic does not claim that the results have been produced
by some artifact, but instead points out that the results have been obtained
under conditions that fail to meet generally accepted standards. The gist
of this type of criticism is that test tubes should be clean when doing
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careful and important scientific research. To the extent that the test tubes
were dirty, it is suggested that the experiment was not carried out
according to acceptable standards. Consequently, the results remain
suspect even though the critic cannot demonstrate that the dirt in the
test tubes was sufficient to have produced the outcome. Hyman's critique
of the Ganzfeld psi research and Alcock's paper on remote viewing and
random number generator research are examples of this type of criticism.
In the committee's view, it is in this latter sense, the dirty test tube
seyse, that the best parapsychological experiments fall short. We do not
hage a smoking gun, nor have we demonstrated a plausible alternative;
buy we imagine that even the parapsychological community must be
concerned that their best experiments still fall far short of the methodo-
local adequacy that they themselves profess.
gonorton and Hyman differ on whether to assign a flaw in randomization
toda particular series of experiments. With Honorton's assignment, the
stødlies with adequate randomization do not differ in significance of
outcome from those with inadequate randomization. With Hyman's
assignment, the experiments with inadequate randomization have signif-
icantly more successful outcomes than do those with adequate random-
izion. A simple disagreement on one experiment can thus make a huge
difference as to whether we conclude that this flaw contributed or did
Econtribute to the observed outcomes. Several similar examples could
be.cited to illustrate the extreme sensitivity of this data base to slight
changes in flaw assignments.
Even if Palmer is correct in asserting that in a particular case an
am maly has been demonstrated, serious problems remain. In astronomy
angother sciences, an anomaly is a very precise and specifiable departure
froth a well-defined theoretical expectation. Neptune was discovered, for
example, when Leverrier was able to specify not only that the orbit of
Uranus departed from that expected by Newtonian theory, but also
precisely in what way it departed from expectation. Nothing approaching
such a specifiable anomaly has been claimed for parapsychology. A vague
andLunspecifiable departure from chance is a far cry from a well-described
an@systematic departure from a precise, theoretical equation. Leverrier's
anemaly was consistent with only a very narrow range of possibilities.
The sort of anomaly claimed for parapsychology is currently consistent
with an almost infinite variety of possibilities, including artifacts of various
kinds.
THE PROBLEM OF QUALITATIVE EVIDENCE
The committee continually encountered the distinction between qual-
itative and quantitative evidence for the existence of paranormal phe-
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nomena. Many proponents of the paranormal acknowledge such a differ-
ence in one way or another. Some realize that it is only quantitative
evidence that will convince the scientific community. Although they
themselves have relied on qualitative evidence for their own beliefs, they
refer us to the RNG experiments of Robert Jahn or the remote viewing
experiments at SRI as examples of supporting quantitative data.
Most proponents seem impatient with the request for scientific evidence.
They have been convinced through their own experiences or the vivid
testimonies of individuals whom they trust. Many argue that qualitative
evidence can be as good as quantitative; indeed, they claim that in some
circumstances it can be better.
The arguments for the superiority of qualitative evidence are based in
many cases on such factors as ecological validity, conducive atmosphere,
and holism. The ecological validity argument asserts that the artificial
conditions required for laboratory experiments are so different from the
natural settings in which paranormal phenomena typically occur that
findings from such controlled studies are irrelevant. By removing the
psychic from his or her natural domain or by arranging conditions to suit
the needs of scientific observation, it is claimed, the scientist destroys
the very phenomenon under question. The ecological validity argument
is closely related to the other arguments. Proponents who emphasize the
conducive atmosphere assert that the austere conditions of strict labo-
ratory procedure create an atmosphere that is numbing or inimical to
psychic functioning. Those who emphasize holism point out that the
experimental procedures necessarily dissect and focus on restricted
portions of a system. Such compartmentalization, it is claimed, makes it
impossible to study the sorts of paranormal phenomena that operate only
as a total system in a naturalistic context.
QUALITATIVE EVIDENCE AND SUBJECTIVE BIASES
What is meant by qualitative evidence? Roughly, it means any sort of
nonscientific evidence that proponents find personally convincing. Typ-
ically, it involves personally experiencing or witnessing the phenomenon.
Less compelling, but still effective, is the testimony of friends or trusted
acquaintances who have personally experienced it. Even individuals who
are intellectually aware of the pitfalls of personal observation and
testimony find it difficult, even impossible, to disregard the compelling
quality of such evidence in the formation of their own beliefs.
A major parapsychologist admitted to one committee member that the
scientific evidence did not justify concluding that psi exists. "As a trained
scientist," he said, "I know quite well that by scientific criteria there is
no evidence for the existence of psi. In fact, I have always argued with
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my parapsychological colleagues that they are making a serious mistake
in trying to get the scientific community to take their current evidence
seriously. Before they do this, they first have to be able to collect the
sort of repeatable and lawful data that constitute scientific evidence."
This same parapsychologist then explained why, despite the current lack
of evidence, he remained a parapsychologist. "When I was 16 I had some
personal experiences of a psychic nature that were so compelling that I
have no doubt that they were real. Yet, as a trained scientist, I know
thatmy personal experiences and subjective convictions cannot and
shogd not be the basis for asking others to believe me." This parapsy-
chologist is unusual in that he makes the distinction within himself
bet geen beliefs that are subjectively compelling and beliefs that are
scientifically justifiable. More typical is the proponent who, as a result
of compelling personal experience, not only has no doubt about the reality
of underlying paranormal cause, but also has no patience with the refusal
of @hers to support that belief.
Vge see two problems regarding qualitative evidence. First, personal
observation and testimony are subject to a variety of strong biases of
which most of us are unaware. When such observations and testimony
emAge from circumstances that are emotional and personal, the biases
and Distortions are greatly enhanced. Psychologists and others have found
thatthe circumstances under which such evidence is obtained are just
those that foster a variety of human biases and erroneous beliefs. Second,
beliefs formed under such circumstances tend to carry a high degree of
sub@ctive certainty and often resist alteration by later, more reliable
disconfirming data. Such beliefs become self-sealing, in that when new
information comes along that would ordinarily contradict them, the
believers find ways to turn the apparent contradictions into additional
congrmation.
The committee asked Dale Griffin to describe many of the ways in
which cognitive and social psychologists have documented that human
subactive judgment can lead us astray. Griffin's paper emphasizes the
cognitive biases termed availability and representativeness, but he also
discasses motivational biases. Although most of these biases have been
creged under laboratory conditions, they are nonetheless quite powerful,
andæevidence has been mounting that, if anything, they are much more
powerful in natural settings. Griffin points out that one vivid, concrete
experience is usually sufficient to outweigh conclusions based on hundreds
or thousands of cases based on abstract summary statistics. These and
the other biases discussed by Griffin should make us wary of conclusions
based on qualitative evidence.
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EXAMPLES OF PROBLEMATIC BELIEFS
In this section we discuss some examples of beliefs about paranormal
phenomena that have been formed under conditions known to generate
cognitive illusions and strong delusional beliefs. We attempt to make
clear why we are skeptical of any evidence offered in support of the
paranormal that does not strictly fulfill scientific criteria. We believe it is
important to realize the power of such conditions to create strong but
false beliefs.
In 1974 a group of distinguished physicists at the University of London
observed renowned psychic Uri Geller apparently bend metallic objects
and cause part of a crystal, encapsulated in a container, to disappear.
Impressed with what they saw, in 1975 these scientists contributed an
article to Nature outlining their ideas about how to conduct successful
parapsychological research (reprinted in Hasted et al., 1976). In their
discussion they note that successful results depend on the relation among
the participants and that phenomena are more likely to occur when all
participants are in a relaxed state, all sincerely want the psychic to
succeed, and "the experimental arrangement is aesthetically or imagi-
natively appealing to the person with apparent psychokinetic powers."
Hasted and his colleagues describe further desiderata. The psychic
should be treated as one of the experimental team, contributing to an
attitude of mutual trust and confidence that facilitates successful appear-
ance of the allegedly paranormal effects. The slightest hint of suspicion
on the part of the observers can stifle the occurrence of any phenomena.
Observers should avoid looking for any particular outcome that interferes
with the required relaxed state of mind and impedes paranormal powers.
To help avoid the inhibiting effects of concentrated attention, participants
should talk and think about matters irrelevant to the experiment at hand.
Acknowledging that these desiderata make it difficult to preclude
trickery, Hasted and his colleagues express confidence that they can both
create psi-conducive conditions and eliminate the possibility of being
tricked (Hasted et al., 1976:194):
It should be possible to design experimental arrangements which are beyond any
reasonable possibility of trickery, and which magicians will generally acknowledge
to be so. In the first stages of our work we did in fact present Mr. Geller with
several such arrangements, but these proved aesthetically unappealing to him.
Although we may sympathize with the British physicists' desire to
create conditions conducive to the appearance of genuine psychic powers,
if such powers exist, we cannot fail to note the quandary that their efforts
produce. In their quest for psi-conducive conditions, they have created
guidelines that play into the hands of anyone intent on deceiving them.
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204
ENHANCING HUMAN PERFORMANCE
The very conditions that are specified as being conducive to the appearance
of paranormal phenomena are almost always precisely those that are
conducive to the successful performance of conjuring tricks. One of the
first rules the aspiring conjuror learns is never to announce in advance
the specific outcome that he or she is going to produce. In this way
onlookers will not know where and on what they should focus their
attention and consequently will be less apt to detect the method by which
the trick was accomplished. The authors' advice to avoid focusing on a
predetermined outcome greatly facilitates the conjuror's task.
ECIA-RDP96-00791R000200320901-1:
@The insistence that the arrangements meet with the psychic's approval
is by far the most devastating of these conditions. Geller will perform
if the conditions are "aesthetically pleasing." This amounts to giving
th
alleged psychic complete veto power over any situation in which he
ontshe feels that success is not ensured. This in turn means that the
pspchic being tested, not the experimenters, is controlling the experiment.
Sively the British physicists ought to realize the irony of their admission
that all their experimental arrangements designed to preclude trickery
tugned out to be aesthetically unacceptable to Uri Geller.
Another example of beliefs generated in circumstances that are known
to create cognitive illustions is macro-PK, which is practiced at spoon-
beading, or PK, parties. The 15 or more participants in a PK party, who
usually pay a fee to attend and bring their own silverware, are guided
through various rituals and encouraged to believe that, by cooperating
wish the leader, they can achieve a mental state in which their spoons
and forks will apparently soften and bend through the agency of their
mids.
Since 1981, although thousands of participants have apparently bent
metal objects successfully, not one scientifically documented case of
paranormal metal bending has been presented to the scientific community.
Y&t participants in the PK parties are convinced that they have both
witnessed and personally produced paranormal metal bending. Over and
omer again we have been told by participants that they know that metal
bgame paranormally deformed in their presence. This situation gives
the distinct impression that proponents of macro-PK, having consistently
fayed to produce scientific evidence, have forsaken the scientific method
angl undertaken a campaign to convince themselves and others on the
basis of clearly nonscientific data based on personal experience and
testimony obtained under emotionally charged conditions.
Consider the conditions that leaders and participants agree facilitate
spoon bending. Efforts are made to exclude critics because, it is asserted,
skepticism and attempts to make objective observations can hinder or
prevent the phenomena from appearing. As Houck, the originator of the
PK party, describes it, the objective is to create in the participants a
205
PARANORMAL PHENOMENA
peak emotional experience (Houck, 1984). To this end, various exercises
involving relaxation, guided imagery, concentration, and chanting are
performed. The participants are encouraged to shout at the silverware
and to "disconnect" by deliberately avoiding looking at what their hands
are doing. They are encouraged to shout Bend! throughout the party.
"To help with the release of that initial concentration, people are
encouraged to jump up or scream that theirs is bending, so that others
can observe." Houck makes it clear that the objective is to create a state
of emotional chaos. "Shouting at the silverware has also been added as
a means of helping to enhance the emotional level in a group. This
procedure adds to the intensity of the command to bend and helps create
pandemonium throughout the party."
A PK party obviously is not the ideal situation for obtaining reliable
observations. The conditions are just those which psychologists and
others have described as creating states of heightened suggestibility and
implanting compelling beliefs that may be unrelated to reality. It is beliefs
acquired in this fashion that seem to motivate persons who urge us to
take macro-PK seriously. Complete absence of any scientific evidence
does not discourage the proponents; they have acquired their beliefs
under circumstances that instill zeal and subjective certainty. Unfortu-
nately, it is just these circumstances that foster false beliefs.
DISCUSSION OF QUALITATIVE EVIDENCE
Our analysis of the evidence put before us indicates that even the most
solidly based arguments for the existence of paranormal phenomena fall
short of the currently accepted parapsychological standards. Even if the
best evidence had been collected according to acceptable scientific
standards, most proponents would have in fact remained convinced by
personal experiences and data that clearly fall far short of scientific
acceptability. We have looked at two examples to make clear why and
in what ways such failures to meet acceptable standards render the
corresponding arguments useless as evidence for the paranormal, even
though they have created compelling and strongly held beliefs in those
who have been exposed to them.
The examples illustrate how different ways of attempting to acquire
evidence for paranormal phenomena can depart from adequate standards.
These inadequacies become especially critical when we note that the
conditions under which the alleged paranormal phenomena are supposed
to occur are just those known to foster biases and false beliefs. The PK
parties, while creating powerful beliefs in paranormal metal bending,
clearly violate almost every principle for obtaining trustworthy data.
These parties offer no standardization, no objective records, and no
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