THE ANOMALY CALLED PSI: RECENT RESEARCH AND CRITICISM

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The anomaly called psi:
Recent research and criticism
K. Ramakrishna Rao and John Palmer
Institute for Parapsychology, Box 6847, College Station,
Durham, N. C. 27708
Abstract: Over the past hundred years, a number of scientific investigators claim to have adduced experimental evidence for "psi"
phenomena - that is, the apparent ability to receive information shielded from the senses (ESP) and to influence systems outside the
sphere of motor activity (PK). A report of one series of highly significant psi experiments and the objections of critics are discussed in
some depth. It is concluded that the possibility of sensory cues, machine bias, cheating by subjects, and experimenter error or
incompetence cannot reasonably account for the significant results. In addition, less detailed reviews of the experimental results in
several broad areas of psi research indicate that psi results are statistically replicable and that significant patterns exist across a large
body of experimental data. For example, a wide range of research seems to converge on the idea that, because ESP "information"
seems to behave like a weak signal that has to compete for the information-processing resources of the organism, a reduction of
ongoing sensorimotor activity may facilitate ESP detection. Such a meaningful convergence of results suggests that psi phenomena
-ay represent a unitary, coherent process whose nature and compatibility with current physical theory have yet to be determined.
The theoretical implications and potential practical applications of psi could be significant, irrespective of the small magnitude of psi
effects in laboratory settings.
Keywords: clairvoyance; extrasensory perception (ESP); methodology; parapsychology; psi; psychokinesis (PK); replication; scien-
tific method; telepathy
There is a large and growing body of experimental liter-
ature devoted to the study of certain anomalous interac-
tions that seem to involve psychologically meaningful
exchanges of information between living organisms and
their environment. We call these interactions anomalous
because they appear to exceed somehow the capacities of
the sensory and motor systems as these are presently
understood. These interactions are collectively desig-
nated by the term psi. Parapsychology is that branch of
science that makes a systematic study of psi anomalies. In
other words, it is the business of parapsychology to find
explanations of psi anomalies through scientific inquiry.
Psi is traditionally divided into various subcategories,
each of which has been the subject of experimental
research. For example, parapsychologists have been test-
ing whether subjects can acquire information that is
shielded from their senses (extrasensory perception, or
ESP) and whether subjects can directly influence exter-
nal systems that are outside the sphere of their motor
activity (psychokinesis, or PK). Experimenters have also
sought to differentiate forms of ESP, such as "telepathy"
(ESP for another's thoughts) and "clairvoyance" (ESP for
external objects and events). ESP is sometimes reported
to be time-displaced, in that the information may relate to
a past event ("retrocognition") or a future event ("precog-
nition"). In practice, it has often proved difficult to isolate
these forms of psi experimentally, and nowadays they
tend to be defined operationally rather than theoretically
(e.g., it is clairvoyance when you. do not have someone
c'69@ii'Jfiig'S the target)..
Somewhat contrary to common usage, we are not using
the term psi to imply that the anomalous interactions are
necessarily "paranormal," but rather that no adequate
conventional explanation of the interactions has yet been
offered. Phrases stating or implying the "existence" of psi
will be used somewhat informally to indicate that certain
interactions have achieved this status.
The term paranormal has been a source of some
confusion both within and outside parapsychology, and
thus we feel that a few comments on the term are in order.
Paranormal was first discussed in relation to psi by the
philosopher C. D. Broad (1953; 1962; see also Braude
1979b), who defined psychical research (the earlier term
for parapsychology) as "the scientific investigation of
ostensibly paranormal phenomena" (Broad 1962, p. 3).
Broad was careful to use the term "ostensibly paranor-
mal," by which he meant phenomena that seem prima
facie to conflict with one or more of what he referred to as
the "basic limiting principles" of nature. These are not
the same as the laws of nature, but rather a more funda-
mental set of assumptions that "we unhesitatingly take for
granted as the framework within which all our practical
activities and our scientific theories are confined" (Broad
1953, p. 7). For example, the assumption that "it is
impossible for a person to perceive a physical event or a
material thing except by means of sensations which that
event or thing produces in his mind" (Broad 1953, p. 10) is
a basic limiting principle that governs our way of acquir-
ing knowledge. A case of ESP, therefore, would be
ostensibly paranormal; it would be genuinely paranormal
only when and if it could be shown to really conflict with
one or more of the basic limiting principles. It is the task
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of parapsychology, according to Broad, "to investigate
ostensibly paranormal phenomena, with a view to dis-
covering whether they are or are not genuinely paranor-
mal phenomena" (Broad 1962, p. 5).
Although Broad's reasoning is sound, the term para-
normal has led to some difficulties in practice. For exam-
ple, as noted above, it is commonplace to find the terms
psi and paranormal phenomena being used interchange-
ably, implying that parapsychology has no subject matter
unless the paranormality of the phenomena is accepted in
advance! A second and subtler difficulty is more directly
related to the term itself. By stressing the conflict be-
tween potential "paranormal" explanations of psi and
"normal" science, and at the same time failing to acknowl-
edge that what constitutes normal science is historically
relative (i.e., it can change from one historical period to
the next), the term paranormal leaves the connotation
that explanations that violate the basic limiting principles
are unscientific in some fundamental sense. This, of
course, is not true. If a "paranormal" theory of psi were
someday to be confirmed, the practical consequence
would be a redefinition of "normal" science to accommo-
date the new theory. In other words, the "paranormal"
would become "normal," and the distinction would break
down. A similar objection to the term has recently been
raised by Paul Kurtz (1981), a well-known critic of
parapsychology.
It is our view that potential explanations of psi that
violate the basic limiting principles of nature are scien-
tifically legitimate and, along with conventional explana-
tions, should be entertained from the outset in our efforts
to explain psi anomalies. Such explanations, unorthodox
as they may be, are nonetheless worthy of consideration
for the simple reason that psi anomalies seem to violate
the basic limiting principles prima facie. Things are not
always what they seem, but the possibility that they are
should certainly be considered. Thus, the distinction to
which paranormal refers is a valid one, even though the
term itself is problematic. Recently, Palmer (1986b) has
proposed a neutral term, omega, to identify potential
explanations of psi that go beyond the basic limiting
principles. Thus, "paranormal" explanations would be
labeled "omegic." Despite our reluctance to introduce
neologisms, we think in this case an exception may be
justified.
2. Background
Like conventional psychology, experimental parapsy-
chology grew out of a need to account for people's
experiences in the "real world." The first major survey of
such experiences was conducted under the auspices of
the British Society for Psychical Research in the last
century (Gurney et al. 1886/1970). More recently, a
survey conducted by the National Opinion Research
Center of the University of Chicago revealed that a
majority of Americans thought they had experienced one
or more psychic events in their lives (Greeley & Mc-
Cready 1975). Similar results have been obtained in other
surveys in the United States (e.g., Palmer 1979), Europe
(e.g., Green 1960; Sannwald 1963; Haraldsson et al.
1977), and Asia (e.g., Prasad & Stevenson 1968). Palmer's
survey further revealed that for many of those who
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reported psychic experiences, these significantly influ-
enced their feelings, attitudes, and decisions in other
areas of their lives. Whatever the explanation of psychic
experiences, they happen, they are common, and they
are often important to people. For these reasons alone,
they deserve serious attention from scientists involved in
the study of human behavior and cognition.
Although some parapsychological research has di-
rectly examined the evidential value and characteriza-
tion of these spontaneous psychic experiences (e.g.,
Hart 1954; Rhine, L. E. 1962; Schouten 1982), the bulk
of the research has been experimental, and we will limit
ourselves to the latter in this target article. The first
major experimental investigation of psi was conducted at
Stanford University by John Coover (1917). Sustained
research, however, did not begin until 1927, when J. B.
Rhine arrived at Duke University to work with William
McDougall. With the publication of J. B. Rhine's
(1934/1973) monograph Extrasensory Perception, a sci-
entific claim for the existence of ESP was made. It gave
the field "a shared language, methods, and problems"
(McVaugh & Mauskopf 1976), and it provided "radical
innovation and a high potential for elaboration" (Allison
1973, p. 39).
Rhine's procedure was to have subjects guess the
randomized order of the cards in a deck containing five
examples of each of five geometric symbols: a star, circle,
cross, square, and wavy lines. By chance, the subject
should get 5 correct out of the 25. Standard statistical
techniques were used to determine the likelihood that
any given number of hits was statistically significant. If
the average number of correct guesses per run of 25
exceeded 5 to a significant degree, and acquisition of
information by artifactual means such as sensory cueing
and logical inference was ruled out, ESP was considered
to have been demonstrated.
Using this methodology, Rhine (1934/1973) reported
highly significant results, especially with five selected
subjects who were tested repeatedly over a number of
years. Prior to August 1, 1933, all subjects in the program
had completed a grand total of 85,724 trials, with an
average score of 7.1 hits per run.
The reaction of the scientific community to Rhine's
claim was understandably cautious and critical. Subse-
quent to the publication of the monograph, there were 35
criticisms contained in 56 published reports. Some of
these criticisms were specific and others were merely
speculative. The specific criticisms had to do with Rhine's
methods of data collection and statistical analysis. These
criticisms and Rhine's responses are fully documented in
the book Extrasensory Perception After Sixty Years
(Rhine et al. 1930).
'he first line of criticism dealt with the experimental
conditions. One essenti requirement ent or an acceptable
Eexperiment was that data should be collected under
conditions that provide no reasonable opportunity for
sensory leakage of information or inferential knowledge of
the targets. Skinner (1937), Wolfle (1938), and J. L.
Kennedy (1938), among others, pointed out that under
certain lighting conditions the commercially produced
ESP cards could be read through their reverse sides.
Rhine responded that the original experiments were
conducted with hand-printed ESP cards that were free
from such defects and that in his more formal experiments
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 Liao Or Palmer: Parapsychology review
the use of scree Yac 8i~ f08/@Y S1~bPWrNMO WZ28Gns1tOQQr1jo5 a
from obtaining a xl cuesm flie car s. I Inne y respectable rate of replication; (3) the experimental ob-
Kello
(1)38)
(1936)
d L
b
,
gg
, an
eu
a (1938) argued that an
increase in the experimental rigor of ESP research had
resulted in a corresponding decline in ESP results, sug-
gesting that extrachance ESP scores were due to loose
experimental conditions. To this Rhine responded that
his most rigorously controlled experiment, the Pearce-
Pratt series, did give highly significant results (Rhine et
al. 1940). Although this experiment was later challenged
by critic C. E. M. Hansel (1966) - with questionable
success (Hansel 1980; Rhine & Pratt 1961; Stevenson
1967) - as being susceptible to fraud on the part of the
subject, it was still more rigorously controlled than the
other experiments in the original data base and thus
d
Ri
servations in parapsychology are not unrelated, and sig-
nificant patterns involving large bodies of experimental
data are apparent; (4) a wide range of process-oriented
research has focused on a single cognitive process that
may be seen to give coherence and even a degree of
consistency to a diverse array of experimental results; and
(5) the small magnitude of most current psi effects is
irrelevant to both their theoretical importance and their
potential applicability.
3. The question of the "conclusive" experiment
supporte
me s point. Referring to parapsychology, Phillip H. Abelson (1978),
- The second line of criticism related to data analysis.," Editor of Science, is quoted in U. S. News and World
Will ou i~L935) -K ll
1
Y ogg (
936), Heinlein and
Heinlein (1938), Herr (1938), and Lemmon (1939) crit-
icized various features of the statistical analysis used by
Rhine and his colleagues. In particular, the criticism
focused on Rhine's assumption that the binomial theorem
is applicable to "closed decks," decks in which the
number of times each type of card appears is not free to
vary. This aspect of the methodological debate essentially
ceased in 1937, when Burton Camp, President of the
Institute of Mathematical Statistics, stated that Rhine's
"statistical analysis is essentially valid. If the Rhine inves-
tigation is to be fairly attacked it must be on other than
mathematical grounds" (Camp 1937). For further details,
see Burdick and Kelly (1977).
It would be wrong to conclude from this, however, that
Rhine's experiments were perfect and that they had
conclusively eliminated every alternative explanation. In
retrospect, one could suggest improvements in the ex-
perimental conditions of his experiments. But for his
time, Rhine's best experiments were ahead of others in
the behavioral sciences. The experimental precautions he
took, including two-experimenter controls and double-
blind procedures, were rare in other disciplines at that
time. Nonetheless, much of the early criticism of Rhine's
experiments was helpful in progressively raising the stan-
dards of ESP research and reducing the possibility of
experimental errors and artifacts.
Since the publication of Rhine's monograph over fifty
years ago, there have been hundreds of experimental
reports of evidence for psi. Yet skepticism has not de-
creased. Psi results are generally ignored in,mainstream
science, and when called to the attention of scientists they
are apt to arouse suspicion. When specific criticisms are
voiced, they generally include the following: (1) There is
no "conclusive" experiment in parapsychology's long
history; (2) there is no repeatable psi experiment; (3) the
so-called significant psi results are disparate, incoherent,
and isolated one-shot observations that do not merit
scientific attention; (4) the results themselves are nonsen-
sical in that they do not suggest any lawful relationships or
progressive research programs; and (5) even if psi is real,
it is too weak to be of any practical importance. If such
perceptions were strongly supported by all the available
data, it would be right to ignore parapsychology's claims.
But the fact (as we hope to show in the following pages) is
that (1) there are good experiments that seem to provide
evidence for the existence of psi by reasonable standards
Report as saying that "extraordinary claims require ex-
traordinary evidence." This statement implies that the
strength of evidence required to establish a new phe-
nomenon is directly proportional to how incongruent the
phenomenon is with our prior notions. Our prior notions,
however, are not always self-evident truisms. They are
derived from, among other things, prevailing religious
and cultural beliefs, personal experiences and observa-
tions, and our general world view. They are translated
into subjective probability estimates and determine the
evidential demands we make for a given claim. If the
subjective probability of a disputed claim is zero, then no
amount of empirical evidence will be sufficient to estab-
lish that claim. In serious scientific discourse, however,
few would be expected to take a zero-probability stance
because such a stance could be seen to be sheer dog-
matism and the very antithesis of the basic assumption of
science's open-endedness.
Nevertheless, the demand for extraordinary evidence
of psi often seems to be derived from an implicit notion of
its a priori impossibility. For example, some critics of psi
research have demanded a "foolproof' experiment that
would control for all conceivable kinds of error, including
fraud by the experimenter(s). They have argued that if a
claim is made for the existence of a phenomenon that
conflicts with "established laws," it is much more par-
simonious to assume error or even fraud on the part of the
claimant than it is to assume the reality of that phe-
nomenon (Price 1955; Hansel 1966). This argument is
often identified with David Hume's (1825) maxim that
"no testimony is sufficient to establish a miracle, unless
the testimony be of such a kind, that its falsehood would
be more miraculous than the fact which it endeavours to
establish" (p. 115). Hume's maxim is a metaphysical
statement, and it is inappropriate to use it when one
speaks of empirical evidence. Moreover, his definition of
a miracle as a universally nonexistent event is self-contra-
dictory inasmuch as any claimed evidence in support of a
miracle is also evidence against the universality of its
nonexistence (Rao 1981a). As Saint Augustine remarked,
"Miracles occur in contradiction not to nature, but to
what is known to us of nature." It should also be kept in
mind that Hume might not have regarded psi phenomena
as miraculous or as anything more than extraordinary
events.
The call for a totally "foolproof' study assumes that at a
given time one can identify all possible sources of error
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and how to control against them. Such a methodological
stance is comparable to the epistemological position that
one can determine for all time to come what is and is not
possible. Again, the demand for experimental controls
against experimenter fraud is unique to discussions of
evidence for what are perceived to be extraordinary
claims. Pushed to its extreme, the hypothesis of experi-
menter fraud becomes nonfalsifiable, in that it is impossi-
ble to be certain that fraud is completely eliminated in
any given experiment.
The concept of a "conclusive" experiment, totally free
of any possible error or fraud and immune to all skeptical
doubt, is a practical impossibility for empirical phe-
nomena. In reality, evidence in science-is-,A, matter of
degree; the` of"cT tfiat one can concoct alternative explana-
f indin--n-
lionsoa ~doa s ot automatically render that
finding evidentially worthless. Evidentiality must be -as-
sessedon a continuum and in relation to the plausibility of
and the empirical support for the competing hypotheses.
These considerations demand that a "conclusive" experi-
ment be defined more modestly as one in which it is
highly improbable that the result is artifactual. In this
sense, we think a case can be made for "conclusive"
experiments in parapsychology.
During a test, the subject sits in front of a small panel
with four pushbuttons and four corresponding colored
lamps. Each of the pushbuttons simultaneously acti-
vates a recorder switch and a trigger switch. The
recorder switch serves to register which of the buttons
has been pressed. The four trigger switches are con-
nected in parallel such that pressing any one of the
buttons closes a circuit, in turn triggering the random
lighting of one of the four lamps. The system is de-
signed so that on repeated pressing of the buttons the
lamps light in random sequence, i.e., each lamp lights
with the same average frequency, and there is no
correlation between successively lit lamps or between
the buttons pushed and the lamps lit. (p. 101)
Random lighting of the lamps was achieved, following
the subject's response, by a sophisticated electronic ran-
dom event generator that used a radioactive source,
strontium 90. (See Schmidt [1970b] for a more complete
account of the hardware design and methods of statistical
evaluation.) The REG was extensively tested in control
trials and found not to deviate significantly from chance.
The sequence of buttons pressed and lamps lit is
recorded automatically on paper punch tape. In the
research reported here, the two types of test (trying for
a high or low number of hits) were recorded in different
codes
such that the evaluating com
uter could dis-
,
p
3.1. Schmidt's REG experiments
tinguish between them. The number of trials made and
A defense of the existence of probabilistically conclusive hits obtained were displayed to the subject by elec-
parapsychological studies requires a detailed review and tromechanical reset-counters. These numbers were
discussion of any experiments that might qualify. Because also registered by nonreset counters, and the readings
such a treatment must be rather lengthy, we will limit of all counters were regularly recorded by hand. This
ourselves to a single group of experiments as an example. record agreed with the results obtained from the paper
Although they are somewhat dated, we have chosen tape. The equipment was fraud proof, so that one
Helmut Schmidt's (1969a; 1969b) reports on random could, in principle, let the subjects work alone. This
event generator (REG) experiments because (a) they was done, however, only in a small part of the tests with
represent one of the major experimental paradigms in subject OC in the first experiment and did not increase
contemporary parapsychology; (b) they are regarded by the scores. In all other tests the writer was present in
most parapsychologists as providing good evidence for the same room with the subject. (Schmidt 1969b, p.
psi; and (c) they have been subjected to detailed scrutiny 103)
by critics. In no sense do we imply that these are the only Schmidt's first report was based on two experiments.
good experiments the field has to offer. Nor do we The subjects in this study were preselected on the basis of
believe, for the reasons stated above, that there can be their performance in the preliminary tests. In the first
any crucial experiment or experimental program on experiment there were three subjects. All of them at-
which the case for psi does or could rest exclusively. tempted to obtain high scores. Together they did 63,066
At the time of conducting these experiments, Helmut trials and scored 16,458 hits, which was 691.5 more than
Schmidt was a physicist at Boeing Scientific Research mean chance expectation (MCE). The probability that
Laboratories. The studies were designed to test the such a result occurred by chance is smaller than 2 x
possibility of ESP and were carried out with the help of a 10'9.
specially built machine that seemed to rule out all ar- In the second experiment, two subjects from the first
tifacts arising from recording errors, sensory cues, and series and one new subject participated. One subject
subject cheating. The safety features of the Schmidt aimed for high scores and another for low scores. The
machine are actually superior to those of the VERITAC third aimed high in some trials and low in others. The
machine used earlier by Smith and his colleagues to test total number of trials was 20,000. Of these, 10,672 were
for ESP (Smith et at. 1963). Hansel (1966) had praised high-aim trials and 9,328 were low-aim. The combined
VERITAC as "admirably designed" and had suggested deviation of hits in the desired direction was 401 greater
that it -could be "standardized for testing subjects for than MCE, which has an associated probability smaller
extrasensory perception" (p. 172). than 10-10.
The Schmidt machine randomly selected targets with In the third experiment, Schmidt (1969a) tested six
equal probability and recorded both the target selections subjects, including two who had participated in the trials
and the subject's responses. The subject's task was to just described. The experiment was designed to test
guess which of four lamps would light and to press the primarily for clairvoyance; the targets were digits from a
corresponding button if he was aiming for high scores (or random number table further shuffled by a congruential
to avoid that button if aiming for low scores). As Schmidt generator and recorded on paper punch tape. The sub-
(1969b) described it: jects completed a total of 7,091 hi h-aim trials and 7,909
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w-aim trials, for a grand total of 15,000. The combined er could have artifactually produced the significant re-
;viation of hits in the desired direction was +260 (p = suits.
3 X 10-6).
2. Criticisms of Schmidt's REG experiments
ansel (1980) discussed the "weaknesses" in Schmidt's
(periments under three headings: (1) experimental de-
gn, (2) unsatisfactory features of the machine, and (3)
Lability to confirm the findings. He criticized the experi-
iental design (a) for its failure to specify in advance the
exact numbers and types of trials to be undertaken by
ach subject," (b) for its introduction of high-aim and low-
im conditions, and (c) for its lack of control of the
xperimenter.
Strictly speaking, criticism (a) is not relevant to the
lain purpose of the experiment, which was to determine
tot whether a given subject had ESP, but whether the
!xperiment as a whole provided evidence for ESP. It is
rue, however, that in Schmidt's first experiment the
lumber of total trials was also not specified precisely in
Ldvance. The high level of statistical significance ob-
ained, however, renders the possibility that this factor
-ould account for the results extremely unlikely. And, as
Hansel acknowledges, this problem was corrected in the
ater experiments.
Criticism (b) is not substantiated. Noting that high-aim
scores gave a positive deviation and low-aim scores a
negative deviation, Hansel argued, "The fact that when
positive and negative deviations are combined (maintain-
ing their sign) they invariably give a purely chance score
suggests that sampling from a common distribution may
have taken place" (p. 230). In the first place, this argu-
ment fails to account for Experiment I, which involved
only the high-aim condition and gave results that were
just as significant as in the other experiments. Second, it
is not clear how Hansel's criticism could apply to the
other experiments, since the high and low conditions
were assigned in advance and recorded automatically on
paper punch tape in different codes. It would seem, in
fact, that the introduction of high/low conditions has a
certain additional merit in that one condition could be
considered as a control for the other, as well as for
machine bias. It is of interest that in discussing a different
Schmidt experiment, Hansel (1981) himself criticized
Schmidt for not having a control condition and recom-
mended the introduction of a condition in which "the
subject would not be 'willing' the light to move, or he
would aim at moving the light in the opposite direction"
(p. 32, our italics).
Hansel went on to contend that two different ma-
chines, one for high aim and the other for low aim, should
have been used. But would not such a procedure have
been criticized on the grounds that any obtained dif-
ference between the scores could have been due to the
opposite bias of the two machines?
Criticism (c) is valid if by "control of the experimenter"
Hansel meant control against experimenter fraud. It
would have been entirely possible for Schmidt to fake the
results if he had wished to. In the extreme case, for
example, the whole experimental report could simply
have been fabricated. We cannot conceive, however,
Hansel's criticism (2) of the machine itself overlaps
criticism (1-b) above and was discussed under that
heading.
The final reason given by Hansel for his rejection of
Schmidt's results was that they have not been confirmed.
But this again seems erroneous, as will be shown in
Section 4.1.1 below. Hansel made no mention of several
experimental reports already in the literature that did in
fact claim to confirm Schmidt's results; he instead re-
ferred only to the 1963 report of Smith et al., which gave
null results when VERITAC was used to test for ESP. But
even this comparison is problematic. First, the machines,
experimental procedures, and manipulation of the psy-
chological conditions differed markedly between the two
studies. Second, Schmidt's subjects were carefully
screened through pretesting procedures, whereas those
who participated in the VERITAC experiment were not.
In a more recent publication, Hansel (1981) proposed a
scenario that permits the possibility of trickery without
providing any evidence that fraud had indeed occurred.
Referring to one of Schmidt's -experiments testing PK
(Schmidt 1970a), he claimed that the subject could have
shorted "either the + 1 or the -1 input in the display
panel to the earth line according to whether he wished to
produce a high or a low score" (p. 30), which would
account for the significant results. This argument seems
fallacious. Because the REG and electronic counters
were sealed in a metal box and the REG outputs were
completely buffered, there was no way the subject could
have tampered with the apparatus in the way Hansel
suggests. Second, the data were independently recorded
on punch tape. Had the subject shorted the tape ma-
chine, the total number of punches would have differed
from the 128 specified for each run. Inspection of the
tapes revealed no such discrepancies (Schmidt, personal
communication).
Hansel went on to argue that the experimenter himself
could have easily affected the punched record. This is
debatable, but the possibility that Schmidt could have
faked his data somehow has already been acknowledged.
Recently, however, Schmidt has published a PK experi-
ment designed to rule out the possibility of his (or his two
co-experimenters) falsifying the data without collabora-
tion from at least one of the others (Schmidt et al. 1986).
Briefly, Schmidt, located at his lab in San Antonio, Texas,
prepared lists of paired six-digit random numbers, called
seed numbers, which were to be used to generate se-
quences of quasirandom binary digits by means of a
complex mathematical algorithm known only to Schmidt.
These seed numbers were mailed to the private address
of Professor Luther Rudolph (L. R.) of Syracuse Univer-
sity. Robert Morris (R. M.) of the same university inde-
pendently obtained a list of random target directions
(high and low), one for each binary sequence, by using his
laboratory's own REG. R. M. and L. R. exchanged their
copies of the target-direction sequences and the seed
numbers and then made the former available to Schmidt.
For the test proper, the subject in San Antonio entered
the seed numbers into a computer. The computer then
derived the binary sequences, which in turn governed
the display on a computer screen of a pendulum swinging
how a nonintentionPiprprcr pb.oet6i,2MD/08'1b'fi,-'9-=70P2bDi'~ih5
 Rao"& Paf it '1 &1 'se 2000/08/08
pendulum to swing with large amplitude on high-aim
trials and with small amplitude on low-aim trials.' At the
end of the run, which lasted for about a minute, the
display showed the average swing over the run; thus the
subject was given feedback about his rate of success.
Schmidt et al. reported significant results in support of
their hypothesis. The combined Z for all the ten sessions
was 2.71 (p < .005). Because (a) the seed numbers for the
binary sequences and (b) the target directions were inde-
pendently derived by Schmidt and Morris, respectively,
we know of no way Schmidt or Morris alone could have
artifactually obtained the results. Such security pro-
cedures involving experimenters working independently
in two different laboratories are seldom used in scientific
research; but it is understandable that Schmidt felt that
the validity of his results should not be based ultimately
on his honesty alone.
Of course, the possibility of fraud is still not eliminated
completely in this experiment. Even if we grant that
Schmidt alone could not have faked the results, it remains
possible, though less probable, that Schmidt and Morris,
or Morris and Rudolph, could have conspired to produce
them spuriously. Perhaps the logical next step is to have a
critic participate as a co-experimenter, using the design of
Schmidt et al. We would be curious to see how critics
would react if such an experiment succeeded.
Hansel's criticisms of Schmidt's experiments are rou-
tinely taken as valid by most writers skeptical of psi (e.g.,
Alcock 1981). One of the few critics of psi who questions
the basic premises of Hansel's reasoning on this point is
Hyman (1981). "There is no such thing as an experiment
immune from trickery," says Hyman. "Even if one as-
sembles all the world's magicians and scientists and puts
them to the task of designing a fraud-proof experiment, it
cannot be done" (p. 39). Hyman, however, agrees with
Hansel that Schmidt's PK experiments "do not provide
an adequate case for the existence of psi" (p. 34). His
principal reasons are twofold: (1) "Experience shows that
the most promising research programs in parapsychology
will most likely be passe within a generation or two" (p.
37); and (2) although Schmidt's randomization tests con-
trol against "long-term, or even temporary" machine
bias, they do not "control against possible short-run
biases in the generator output" (p. 38). He suggested, as
did Hansel, that matched experimental and control se-
quences would have been a superior procedure.
The first point is not really a substantive criticism but
merely counsels patience. The same thing can be said of
research in some other areas of psychology. Moreover,
"passe" does not necessarily mean "discredited," and
much of the older research in parapsychology has with-
stood criticism rather well. The second point, as Hyman
himself recognizes, "does not automatically provide an
alternative explanation for how Schmidt obtained his
results" (p. 38). Schmidt, who was aware of such a
possibility, notes that "many more randomness tests
were done than published to satisfy my own questions
about the possibility of temporary random generator
malfunctions" (Schmidt 1981, p. 41). Also, it is difficult to
see how such malfunctions could account for subjects'
ability to anticipate the timing and direction of the
hypothesized short-run biases in Schmidt's early PK
research, which used a l hga~ OTAtnW 6e/08
(Schmidt 197~Ap'i~IPd ii more
: CIA-RDP96-00789R002200110001-5
recent work, direct comparisons were made between
experimental and control sequences (e.g., Schmidt
1976).
4. 1
4. The question of replication
Even assuming that it was possible to determine con-
clusively the proper interpretation of a single experimen-
tal result, such an exercise would have little value in the
context of doing science. The way the scientist functions
is different from the way the historian does, for example.
Unique events and isolated facts, unless they lead to, or
are capable of leading to, some kind of general law,
ordinarily hold little interest for science. Unlike historical
facts, most phenomena of science are capable of being
repeated. The Battle of Gettysburg will not be fought !!!
again. But psi as a laboratory effect must be reasonably
capable of being observed repeatedly if one is to study it
effectively and to understand it. Thus, as even Hansel
(1980) concedes at one point, the importance of a fool-
proof experiment recedes into the background as the
phenomena become increasingly replicable.
Replicability does not necessarily mean that a finding
must be reproducible on demand. It is not strictly an
either-or situation, but a continuum (Rao 1981b). In this
sense of statistical replication, an experiment or an effect
may be considered replicated if a series of replication
attempts provides statistically significant evidence for the
original effect when analyzed as a series.
It may be argued that statistical replication is simply
imperfect replication, and that a real phenomenon is
something that is in principle repeatable. If a phe-
nomenon has occurred once, it will occur again, provided
the same set of circumstances arises. If one had perfect
understanding of the critical variables, one could invari-
ably predict its occurrence; if one had control over those
variables one could produce the phenomenon on de-
mand. The problem is that, in practice, perfect duplica-
tion of conditions is impossible to achieve. This is es-
pecially true in behavioral science experiments, where
the causes of an effect are likely to be complex and
difficult to pin down.
This does not mean that replicability cannot be im-
proved substantially if some understanding of these cru-
cial variables can be achieved. Indeed, such understand-
ing is a major goal of scientific investigation. The other
side of the coin, however, is that inquiry in such cases
begins without this understanding. It is therefore inap-
propriate to dem
d
b
l
an
a
so
ute or even strlibili
ong repcaty
of a phenomenon simply as a prerequisite for further
research.
4.1. Examples of replicablllty in parapsychology
Once we give up the notion of absolute replication, we
can see that parapsychological phenomena are replicated
in a significant statistical sense. For example, Palmer's
(1971) review of so-called sheep-goat studies reveals that
in 13 of the 17 experiments that used standard methods of
analysis, the "sheep" (the subjects who believed in the
possitbbiility of ESP) obtained higher scores than did the
6
of e 1 ac iev g statistical s g nific0 A8Q0-,fiit Sargent's
V_
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(1981) review of the reports published in English on the results significant at or beyond the 5% level (2-tailed), and
association between ESP and extraversion suggests that the combined binomial probability for all the studies was
significant confirmations of a positive relationship occur 5.4 x 10-43. The outcome was still significant, although
at over six times the chance rate. However, the most more modestly so, when the data from Schmidt and the
extensive evidence for the statistical replicability of psi Princeton group were removed (p < 4.25 x 10 - 7).
comes from the three data bases to be discussed in more
detail below. 4.1.2. Ganzfeld and ESP. A second major research para-
digm in which the replication rate over a relatively large
4.1.1. REGs and psi. Since the publication of the REG number of studies has been systematically evaluated
results discussed in Section 3.1 above, Schmidt has car- concerns ESP in the ganzfeld. The ganzfeld is a homoge-
ried out several other successful REG experiments, neous visual field produced, for example, by placing a
mostly involving PK. More to the point, a number of halved Ping-Pong ball over each eye with cotton filling
other experimenters have successfully used the same around the edges. While the subject relaxes in a comfort-
devices or similar ones to test for psi. able chair or bed, a uniform white or red light is focused
The most prominent of these replications comes from on his face from about two feet. Sometimes the subject
the laboratory of Robert Jahn at Princeton University also listens to "pink" noise through attached earphones.
(Jahn 1982; Nelson et al. 1984). Jahn and colleagues use Subjects typically report a pleasant sensation of being
an REG based on a commercial electronic noise source. immersed in a "sea of light", (Honorton 1977, p. 459).
The hits are counted and displayed on the instrument In a typical ganzfeld-ESP trial, the subject receives
panel and are permanently recorded on a strip printer as approximately 30 minutes of ganzfeld stimulation. After a
well as a computer. The subject's task is to influence the period of adjustment and relaxation, the subject is asked
device mentally to produce an excess of hits on predesig- to report all images, impressions, and so on, that occur at
nated PK+ trials and an excess of misses on PK- trials. In the time. From another room, an experimenter blind to
a total of 195,100 PK+ trials, 22 subjects obtained a mean the target monitors the subject's mentation via a micro-
score of 100.043 (MCE = 100). The mean for the same phone link and a one-way mirror. In a room located some
number of PK- trials was 99.965. Although small in distance from the subject, another experimenter acts as
magnitude, both these means are significantly different the agent. Some time after the subject has been in the
from mean chance expectation. The combined proba- ganzfeld, the agent-experimenter opens an envelope
bility of the results is approximately 3 X 10-4. containing a target picture (randomly chosen from a pool
Each trial in Jahn's experiments incorporated alternate of four), views it for about 15 minutes, and then stays in
positive and negative counting on successive samples to the room for an additional 10 minutes. After the comple-
provide an on-line internal control against any systematic tion of the ganzfeld period, the first experimenter gives
bias in the noise source (i.e., positive and negative noise the subject four pictures and asks him to assign them
pulses alternated as hits). Also, baseline trials were re- ranks of 1 through 4 for their correspondence to his
corded "under a variety of conditions before, during, and mentation. At this time neither the subject nor the first
after the active PK trials" (Jahn 1982, p. 148) in a manner experimenter knows which of the four pictures is the
resembling that recommended by critics. The mean score target. The agent-experimenter is then called in and
for these 179,250 baseline trials was 100.005, which does reveals the target picture.
not differ significantly from chance. The first ganzfeld experiment in parapsychology was
Radin et al. (1985) conducted a preliminary survey of all reported by Honorton and Harper (1974). The results of
binary (two-choice) REG experiments published from this experiment were subsequently replicated by Terry
1969 (the year of Schmidt's first published REG expert- and Honorton (1976), Braud et al. (1975), and Sargent
ment) to 1984. The sources sampled were the five major (1980), among others. According to a recent count
refereed parapsychological journals, the bound Proceed- adopted both by Honorton (1985) and critic Ray Hyman
ings of refereed papers presented at the annual Para- (1985b), there are 42 published ESP experiments that
psychological Association Conventions, and a report of have used the ganzfeld procedure. After correcting for
the Princeton data by Nelson et al. (1984), cited above. multiple analyses, if any, Honorton concluded that 19 of
The reviewers defined an "experiment" as the "largest the experiments (45%) gave significant evidence for psi at
possible accumulation of data compatible with a single or beyond the 5% level. Moreover, 26 of the 36 studies for
'direction of effort' assigned to the subjects" (p. 205). In which the direction of the effect could be clearly deter-
other words, data from all trials in which subjects aimed mined (72%) gave deviations, in the positive direction, as
for the same binary outcome were pooled, ignoring other compared to the 50% expected by chance. Hyman
experimental conditions or classifications that may have (1985b) dissented, concluding that the "rate of 'suc-
pertained. cessful' replication is probably very close to what should
The reviewers uncovered 56 reports from approx- be expected by chance given the various options for
imately 30 principal investigators describing a total of 332 multiple testing exhibited in the data base" (p. 25). Later,
individual experiments. For 30 of the nonsignificant ex- however, he came to agree with Honorton that "there is
periments, the authors of the reports provided insuffi- an overall significant effect in this data base which cannot
cient data to allow the outcome (deviation of the hit total reasonably be explained by selective reporting or multi-
from chance) to be expressed quantitatively. In each of ple analysis" (Hyman & Honorton 1986).
these cases, the reviewers randomly selected a Z-score
from a normal (null) distribution of Z-scores to represent 4.1.3. The differential effect. Another area of psi research
the outcome. ~2 r~1 with a large number of studies spanning a long period of
Seventy-one ofA~~l"IIVi~p~Iffa~~~~OB/~}~e1~1R~7ZS~'F7~'~1J~s
 Rao & Palmerpp: Parapsychology review
~g I {~ n p 7 n n''n ~1
the tendency"o7ifidi0XuasuFJjects fob scooreedi r18 'h~r! r~athl~a~ 3 b~1~~(c ~`tStatt]i~1~t~ G~ topic
in successive ESP tests when these consist of two con- (animal learning: 73%), the percentages ranged from 22%
trasting conditions, such as two different sets of targets or to 44%, which is very similar to what we find in para-
two different modes of response. In other words, subjects psychology.
score above chance in one condition and below chance in
the other. The first author's (K. R. R.'s) initial encounter
with differential scoring occurred when he attempted to
test subjects using both ESP cards and cards consisting of
symbols to which the subjects were emotionally attached.
In the first experiment, he found not only that the
subjects obtained more hits than expected by chance with
the cards of their chosen symbols, but also that their
scores on cards with ESP symbols were lower than MCE.
The scoring pattern with one set of cards was the mirror
image of the pattern with the other (Rao 1962). Since then
Rao has carried out a large number of tests under a variety
of conditions and has found a rather consistent tendency
on the part of subjects to show a bimodal response pattern
when the ESP test consists of two contrasting conditions
(Rao 1965).
It is interesting to note that evidence for the differential
effect can be found in a number of studies carried out
before and after Rao's studies, even when the experi-
menters themselves were not looking for it. For example,
Rao and Krishna (in press) examined 72 independent
comparisons between ESP scores obtained by the same
subjects responding to two different classes of targets
where interactions with other variables had not been
predicted. Their sources were the five major refereed
parapsychological journals and reports of refereed papers
presented at Parapsychological Association conventions.
They found that 45 of the 72 comparisons (63%) showed
differential scoring, where we would expect 36 (50%) by
chance (p < .05). In 19 of the experiments (26%), the
scoring rate between the two conditions was significantly
different at or beyond the .05 level, though one would
expect only 3.6 experiments (5%) to show significant
differences by chance.
The meaning of the differential effect is not yet clear. It
was not derived from a theory or model and provides no
explanatory construct that might help us to understand
psi. Rather, it reflects a characteristic of psi in a certain
type of design, a characteristic that any adequate theory
of psi must ultimately account for. One may call it a
descriptive construct as distinct from an explanatory
construct. Descriptive constructs are important in the
early stages of scientific inquiry because, by defining
what it is that a theory must explain, they serve to channel
the process of theory development. Much of the research
in modern parapsychology is directed toward identifying
such descriptive constructs or "effects," with the objec-
tive of bringing closer to attainment the ultimate goal of a
credible theory of psi.
4.1.4. Overview. The proportions of statistically significant
studies in the three areas we have reviewed are as follows:
REGs (21%); ganzfeld (45%); differential effect (26%).
Given the expected success rate of 5%, these values are
not trivial, and they compare favorably with comparable
examples from psychology, such as the placebo effect
(Moerman 1981) and the experimenter expectancy effect
(Rosenthal & Rubin 1978). The latter authors, for exam-
ple, reviewed evidence on the experimenter expectancy
effect in eight types of experiments . The median replica-
4.2. Some criticisms
A number of objections can be raised to the kind of
procedure we have used in obtaining these replication
rates, objections similar to those that have been raised in
discussing experimenter expectancy effects (Barber 1969;
1973). Some of these objections will now be discussed in
relation to the data under consideration.
4.2.1. Comparability of studies. One objection to such
analyses is that the studies included are often not directly
comparable. This objection has merit, but only to a point.
We should not insist, for example, that all experiments be
strict replications of one another. So long as they con-
stitute conceptual replications, methodological differ-
ences can often be treated as random variables that
actually serve to increase the generality of any conclu-
sions that might be drawn from the analysis. On the other
hand, it is usually desirable that the outcomes of the
studies be represented by, or reduced to, some common
metric. One of Hyman's (1985b) criticisms of the ganzfeld
data base, for example, was that the studies used diver-
gent -
and sometimes multiple measures of the dependent
variable, and that the primary measure was sometimes
not specified in advance. In response to this objection,
Honorton (1985) computed a new analysis, using as a
single, uniform measure Z-scores representing the pro-
portion of trials in the experiment in which the subject
correctly picked out the target during the judging (i.e.,
direct hits). This was the measure used in the original
ganzfeld experiment by Honorton and Harper (1974), and
it was the measure most frequently reported in the data
base as a whole. Sufficient information for this analysis
was provided for 28 of the 42 experiments in the data
base. These experiments came from ten different labora-
tories. Twenty-three of the 28 experiments (82%) yielded
positive Z-scores, 12 of which were individually signifi-
cant at the .05 level on a one-tailed test. The cumulative
Z-score for all 28 studies, computed by the Stouffer
method (Rosenthal 1984), was 6.60 (p < 10-9).
Both Radin et al. (1985) and Rao and Krishna (in press)
dealt with the uniformity issue in their analyses of the
REG and differential effect experiments (discussed
above) by using as a common metric Z-statistics. In the
former case, these represented the proportion of trials
that were hits; in the latter case, they represented the
difference between the proportions of hits in the two
conditions.
4.2.2. Publication bias. A second criticism concerns
whether these analyses may suffer from biased selection
and so-called publication artifact; that is, nonsignificant
results may systematically go unreported, and therefore
our sample of studies may not reflect the "true state of S %s
afairsf"Close scrutiny of the field suggests that pu ica-
tion bias cannot explain away the significant number of
replications in parapsychology. Parapsychologists are
sensitive to the possible impact of unreported negative
results, more so than most other scientists. Our profes-
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Tonal society, the Parapsychological Association (PA),
as advocated a policy of publishing the results of all
nethodologically sound experiments, irrespective of out-
:ome. Since 1976, this policy has been reflected in the
publications of all the journals affiliated with the PA and
in the papers accepted for presentation at the annual PA
conventions.
This policy, however, cannot guarantee that re-
searchers will submit negative findings for publication.
Fortunately; thanks to a technique developed by Rosen-
thal (1979), we are able to estimate the number of un-
published and nonsignificant experiments that would be
necessary to reduce an entire data base to nonsignifi-
cance. Honorton (1985), for example, used Rosenthal's
technique to estimate that 423 nonsignificant ganzfeld
studies would be needed to reduce the direct-hit studies
in this data base to a nonsignificant level. Given the
complex and time-consuming nature of the ganzfeld pro-
cedure, it is unreasonable to suppose that so many experi-
ments exist in the "file drawer." As noted earlier, Hyman
now agrees that selective reporting cannot account for the
aggregate findings in the ganzfeld data base (Hyman &
Honorton 1986).
A particularly ingenious way of estimating the extent of
the file-drawer problem was implemented by Radin et al.
k1985) in their analysis of the REG data base. By inspect-
ing a graph of the distribution of outcomes, they noted a
marked discontinuity at the Z-value associated with sta-
tistical significance: There were too many studies at the
tail to make a smooth curve. They determined that the
curve could be smoothed by adding 95 nonsignificant
experiments to the data base. Doing this reduced the
combined binomial probability of all the studies from 5.4
X 10-43 to 3.9 x 10` 18, still an impressive value. Using
the Stouffer method, Radin et al. then estimated that ten
parapsychology laboratories would each have needed to
produce nonsignificant studies at the rate of 2.6 per
month over the 15 years surveyed to cancel out the effect.
Finally, there are some areas in parapsychology where
we can be reasonably certain we have access to all the
experiments done. One such area concerns the rela-
tionship between ESP performance and the ratings ob-
tained on the Defense Mechanism Test (DMT) devel-
oped in Sweden by Ulf Kragh and associates (Kragh &
Smith 1970). Because the administration and scoring of
this test requires specialized training available to only a
few individuals, it has been possible for Dr. Martin
Johnson of the University of Utrecht, the leading authori-
ty on the DMT and a man very sensitive to the issue of
publication bias, to keep track of the number of relevant
experiments conducted by qualified persons. In all ten of
these studies the less defensive subjects scored higher on
the ESP test. In seven of them, this effect was significant
at the .05 level, one-tailed (Johnson & Haraldsson 1984).
4.2.3. Controls and flaws. A third line of criticism relates
to experimental controls. It is argued, for example, that
the replication of an experimental result by other experi-
menters "does not assure that experimental artifacts were
not responsible for the results in the replication as well as
in the original experiment" (Alcock 1981, p. 134).
It is true, of course, that the replication of an effect
implies nothing directly about its cause. But it is also a
basic premise of experimental science that replication
reduces the probability of some causal explanations, par-
ticularly those related to the honesty or competence of
individual experimenters. As Alcock (1981) himself states
in another context, "It is not enough for a researcher to
report his observations with regard to a phenomenon; he
could be mistaken, or even dishonest. But if other peo-
ple, using his methodology, can independently produce
the same results, it is much more likely that error and
dishonesty are not responsible for them" (p. 133).
A more specific set of criticisms has been offered by
Hyman (1985b) with reference to the ganzfeld-ESP data
base. He concluded that the case for replication in this
area is unconvincing because of the presence of meth-
odoligical flaws such as potential sensory cues (e.g.,
including the target handled by the sender in the set
given to the subject for judging), suboptimal randomiza-
tion of targets (e.g., hand-shuffling), and multiple statis-
tical analyses of the data. Honorton (1985) replied that
Hyman made several unsupported assumptions in his
analysis and interpretation of the ganzfeld-ESP data,
and, in particular, that he often did not assign flaws
properly with respect to his own criteria. Honorton
presented his own analyses, arguing that the replication
rate is not significantly influenced by the presence or
absence of potential flaws in these studies. Although
continuing to disagree on the seriousness of the "flaws,"
the reviewers have agreed that "the present data base
does not support any firm conclusion about the rela-
tionship between `flaws' and study outcome (Hyman &
Honorton 1986). (Flaw analyses have yet to be reported
on the REG and differential effect data bases.)
The Hyman-Honorton ganzfeld debate is continuing
in the Journal of Parapsychology. Whatever its final
outcome, the discussion will lead to a more accurate
interpretation of the data and better research in the
future. In the final analysis, the case for psi cannot be won
or lost by arguments over past experiments, but only by
systematic and sustained new research that will survive
the test of time. Honorton has recently reported con-
tinued success using an automated testing protocol that
would appear to answer Hyman's methodological objec-
tions to the earlier ganzfeld research (Berger & Honorton
1985; Honorton & Schechter 1986).
4.2.4. "Disbelievers" as repllcators. Several critics of psi
research (Alcock 1981; Kurtz 1981; Moss & Butler 1978)
have argued that the replication work must be done by
investigators who are unsympathetic to psi, a category
that would exclude most (but not all) parapsychologists.
Moss and Butler, for example, argue that "replication by
a qualified nonsympathetic observer is the only guard
against results which may have been contaminated by a
conscious or unconscious bias" (p. 1068).
We are now aware of its being common practice in
other sciences to disqualify positive results from experi-
ments conducted by researchers who are favorably dis-
posed to the hypothesis they are testing. The personal
beliefs of researchers are rarely reported and may often
be difficult to determine reliably. We suspect, however,
that if such a standard could be applied retrospectively to
published research in psychology, for example, there
would not be much left. The fact that parapsychologists
are singled out for this treatment is symptomatic of the
often ad hominem nature of the psi controversy. We have
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-yet to hear a critic suggest that negative results from
clI -RDP96-R0 w89?0192e 2t001 de4~c~- uch an
"disbelievers" in psi be rejected on this basis. experiment.
Although it is reasonable to assume that experimenters
who obtained strong positive results in the first few psi
experiments they conducted were converted to a "belief'
in psi by these results (if they were not "believers"
already), we have far too few data to draw any conclusions
about the distribution of attitudes of investigators at the
time they undertook their first psi experiments. Thus we
really do not know how many "disbelievers" have ob-
tained positive psi results.
Finally, one cannot assume that confirmatory evi-
dence, even from hardened "disbelievers," will neces-
sarily be acknowledged as such. BBS readers might find it
instructive in this connection to study what happened
when certain members of the Committee for Scientific
Investigation of Claims of the Paranormal quite unexpect-
edly confirmed Michel Gauquelin's astrological "Mars
Effect." (See Zetetic Scholar 1982a; 1982b; 1983; and
references contained therein.)
On the other hand, the fact that the outcomes of psi
experiments seem to be sensitive at least to e, to
th tity of the experimenter or principal investigator
is a legitimate cause for concern: 17his-experimenter
e$ecE' in ra apra apsychology has long been recognized and
extensively discussed within the field (e.g., Kennedy, J.
E. & Taddonio 1976; White 1976a; 1976b); even some
strong proponents of psi have had trouble obtaining
positive results in their experiments. The jury is still out
as to why this state of affairs exists. Until more is known, it
is unwarranted and unfair to jump to the conclusion that
the experimenter effect is due to fraud, negligence, or
incompetence on the part of the successful experiment-
ers, especially in the absence of supporting empirical
evidence. The number of trained scientists who have
obtained positive results in psi experiments is by no
means inconsiderable, and many of these scientists have
published in orthodox areas. More important, other plau-
sible explanations of the experimenter effect can be
proposed. For example, it is not implausible from a
psychological point of view that an experimenter who
does not expect positive results could convey this attitude
to his subjects by nonverbal cues, thereby adversely
affecting their confidence or motivation and thus their
performance on the psi task. There is evidence from
psychology for just such a process (Rosenthal & Rubin
1978). In addition, several studies within parapsychology
that compared experimenters who had different attitudes
or expectations about psi, or who behaved differently
toward their subjects, have provided more direct support
for this hypothesis (e.g., Honorton et al. 1975; Parker
1975; Taddonio 1976).
The correct explanation(s) of the experimenter effect
can come only from more research. This will come sooner
if more scientists outside the parapsychological commu-
nity - "believers," "disbelievers," and neutrals - can be
persuaded to undertake psi experiments of their own, and
to publish their results irrespective of outcome. Despite
our remarks earlier in this section, we think that the
involvement of a wider range of investigators in psi
research is important and we wish to encourage such
involvement. Indeed, that was one of our objectives in
writing this BBS target article. We and other para-
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5. Patterns, order,-and sense in parapsychology
Has parapsychology gone any further than merely sug-
gesting that anomalies exist? We think it has. Although
some work in the field is still concerned with demonstrat-
ing the integrity of the anomalies, emphasis in recent
years has shifted strongly to so-called process-oriented
research designed to uncover lawful regularities between
psi and other psychological or physical variables. For
example, there have been successful attempts to relate
psi to subjects' beliefs and attitudes (Schmeidler & Mc-
Connell 1958), personality and motivation (Eysenck
1967; Honorton & Schechter 1986), and to cognitive
variables such as memory (Rao et al. 1977), visual imagery
(Kelly et al. 1975), and stereotypy of responses to ESP
target sequences (Stanford 1975). We would like to focus
here, however, on one hypothesis that appears to bring
together a large and diverse body of experimental results:
the idea that psi may be facilitated by procedures that
result in the reduction of meaningful sensory and pro-
prioceptive input to the organism, and the concomitant
redirection of attention to internally generated imagery.
This hypothesis is known in parapsychology as the noise
reduction model.
Whatever its "real" mechanism, ESP may usefully be
thought of as behaving like a weak signal that must
compete for the information-processing resources of the
organism. It follows that the reduction of ongoing sen-
sorimotor activity may facilitate ESP detection by the
organism. As illustrated in a book by the psychologist
Harvey Irwin (1979), the noise reduction model fits in
well with concepts that are widely accepted in cognitive
psychology and information-processing theory. The
model is particularly relevant to the notion of limits in the
information-processing capacity of the organism (Kahne-
man 1973); namely, the more internal and external
"noise" the system must process, the less is available to
process possible psi information.
It is interesting that most of the traditional techniques
of "psychic" development seem to involve some form of
reduced vigilance or "noise reduction." For example, the
practice of yoga, which is believed among other things to
help develop ESP ability, appears to involve procedures
that control habitual sensory, autonomic, and cognitive
processes (Rao et al. 1978). The first five of the eight
stages in Patanjali's yoga, for example, are preparatory
and are aimed at achieving voluntary control of internal
processes. The ability of yogins to exercise unusual con-
trol over heartbeat and EEG activity, to cause sweat on
certain parts of the body, and become physiologically
nonresponsive to external stimuli has been satisfactorily
documented (Anand et al. 1961; Wallace 1970; Wallace et
al. 1971). The final three stages of yoga are dharana
(concentration), dhyana (meditation), and samadhi (a
state of stillness of the mind). If the introspective accounts
of the yogins are any guide, the dharana state seems to
involve intense focusing of attention on a single object,
whereas meditation (dhyana) enables the practitioner to
hold that focus over an extended period of time, which is
believed to result in a stand-still state of mind (samadhi).
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his state is also described as an expansion of con-
:iousness that goes beyond the object of perceptual
:tension (Dasgupta 1930). There is voluminous phe-
omenological information on this, along with a modicum
f physiological data (see, e.g., Das & Gastaut 1955).
Historically, many of those who have claimed suc-
essful psi receptivity have also claimed that they did
heir best when they were physically relaxed and when
he mind was in a "blank" state. Rhea White (1964), who
eviewed the early literature on this topic, concluded that
ttempts "to still the body and mind" are common among
he techniques used by successful psi subjects. Mary
;inclair, whom her husband, Upton Sinclair, found to be
in excellent psi subject, recommended for a successful
)Si outcome that "you first give yourself a 'suggestion' to
he effect that you will relax your mind and your body,
:raking the body insensitive and the mind a blank"
'Sinclair 1930, p. 180). White (1964) further elaborated
this technique and classified it into four stages: (1) relaxa-
tion; (2) engaging the conscious mind by keeping it blank
or focusing on a single mental image or feeling, perhaps
following this by a "demand" that the psychic impression
come; (3) waiting patiently for the impression to appear;
and (4) assessing rationally if the impression is psychic.
There is also a large body of experimental evidence that
procedures enabling a subject to limit extraneous sensory
and proprioceptive input are conducive to the manifesta-
tion of psi. Much of this evidence has been comprehen-
sively reviewed by Honorton (1977), so we will limit
ourselves to a brief discussion of work in five areas -
ganzfeld stimulation, hypnosis, relaxation, meditation,
and dreams.
The research on ESP in the ganzfeld has already been
discussed at some length. One additional point may be
added that is particularly relevant to the present discus-
sion: Those studies that assessed the self-reported effects
of the ganzfeld on subjects' state of consciousness have
generally found that the largest mean deviation scores
from chance on the ESP test occurred among those
subjects who claimed the greatest psychological effect
from the manipulation (Palmer 1978; Sargent 1980).
5.2. Hypnosis and ESP
There is an extensive experimental literature on ESP and
hypnosis. Fabler and Cadoret (1958), for example, tested
college students in two formal experiments using a clair-
voyance type of card-guessing task. In half of the trials the
subjects were "under hypnosis" as they attempted to
guess ESP cards screened from their view, and in the
other half they guessed the targets while in a waking
state. The order of testing was counterbalanced. In both
experiments the subjects did significantly better in the
hypnotic condition than in the waking condition.
In a careful review, Ephraim Schechter (1984) evalu-
ated data from 25 experiments in which ESP performance
was compared in hypnotic and control conditions. The
results of 5 of these experiments are uninterpretable for a
variety of reasons. Of the remaining 20 studies, 16 show
higher scores for the hypnotic condition, with 7 of them
showing statistical significance. None of the four reversals
are significant.
The most extensive work in this area has been carried out
by William Braud. In one of the best designed of these
studies (Brand & Brand 1974), 20 volunteer subjects were
assigned randomly to "relaxation" or "tension" condi-
tions. Those in the relaxation condition went through a
taped, progressive-relaxation procedure (an adaptation of
Jacobson's) before taking an ESP test, which was to guess
the picture being "transmitted" by an agent in another
room. The subjects in the other group were given taped,
tension-inducing instructions before they did the same
ESP test. Each subject's level of physical tension was
assessed through electromyographic recordings and self-
ratings. Both measures revealed a significant decrease in
tension among the subjects in the relaxation group and a
significant increase among those in the tension group; as
predicted, the ESP scores of the subjects in the relaxation
group were significantly above chance and significantly
higher than those of the subjects in the tension group.
Although no formal meta-analyses have been con-
ducted on this data base, our own informal survey un-
covered 13 series from six researchers that have reported
significant effects (two-tailed) favoring the facilitative ef-
fect of relaxation, and only one significant reversal using
the same criteria.
5.4. Meditation and ESP
Studies investigating meditation and psi suggest a
positive relationship between these two variables. Rao et
al. (1978) reported three series of experiments with a
total of 59 subjects who had various degrees of proficien-
cy in yoga and meditation. The subjects were given two
ESP tests both before and after they meditated for at
least half an hour. In one test the subjects "blind
matched" cards with ESP symbols against target cards
concealed in opaque black envelopes, and in the other
test they attempted to describe concealed pictures. The
results of both tests yielded independently significant
premeditation-to-postmeditation differences when the
three series were pooled. The card-testing results were
also significant for each of the three series separately.
Again, no formal meta-analyses have been conducted
on this data base. However, our own informal survey
uncovered 12 series from six researchers that have re-
ported significant effects (two-tailed) favoring the facili-
tative effect of meditation, and only one significant rever-
sal, using the same criteria.
5.5. ESP In dreams
Finally, mention should be made of a successful series of
experiments on ESP in dreams conducted at Maimonides
Medical Center (Ullman et al. 1973). In a typical experi-
ment, a sender attempted to transmit the content of a
randomly selected art print to a subject sleeping in an
isolated room. When physiological monitoring indicated
that the subject was dreaming, an experimenter blind to
the target awakened the subject and elicited a dream
report. The following morning, a tape of the dream
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BEHAVIORAL AND BRAIN SCIENCES (1987) 10:4 549
 .A "I tp ycnoiogy review
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reports was plad back to the subject, w io MEN cSi i t-~?x~?n ~i > lc -QQi i~~Jtidies be
an character
d d
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"
Subse-
ciational material and a "guess for the night.
quently, outside judges and/or the subject attempted to
match the randomly ordered targets and dream tran-
scripts from a series of sessions on a blind basis.
In an article that appeared recently in American Psy-
chologist, Irvin Child (1985) reviewed 15 separate series
from the Maimonides program. After eliminating data
from analyses that may have been compromised by non-
independence of the judgings, he concluded that the
remaining data were collectively significant both for the
independent judges and for the subjects as judges.
Child's article also documents several instances of gross
misrepresentation of the Maimonides experiments in
commentaries by critics.
In contrast to the other research considered in this
section, there have been no independent replications of
the Maimonides research that have provided significant
results. Two major failures to replicate have been re-
ported (Belvedere & Foulkes 1971; Foulkes et al. 1972),
and one other is equivocal (Globus et al. 1968).
5.6. Some criticisms
Considering the legendary elusiveness of psi, the rate of
reported success in the psi studies involving sensory
noise reduction, although far from perfect, is impressive,
even more so because the results appear to make sense in
the context of both traditional psychic training practices
and theories from orthodox psychology. One could of
course point out that studies such as the so-called remote-
viewing experiments (Targ & Puthoff 1977), which do not
involve any explicit procedures for reducing sensory
noise, have also recorded success rates of about 50%,
arguing that our rationale is unsupported by these stud-
ies. However, such an argument does not take into
account the fact that most of the successful remote view-
ing experiments, unlike the experiments discussed
above, used subjects that were preselected for psychic
talent and thus less likely than ordinary volunteers to
need a supportive cognitive state to perform successfully.
Second, there is reason to believe that at least some of
these subjects attempted to reduce noise on their own.
Marilyn Schlitz, a highly successful remote viewing sub-
ject, put herself in a "calm state throughout," even
though she used no formal relaxation procedure (Schlitz
& Gruber 1980). Dunne and Bisaha (1978) asked their
remote viewing subjects to "relax and clear their minds"
prior to the remote viewing test.
Even if one were to concede that successful remote
viewers are generally in an ordinary state of conscious-
ness during the psi task, it does not follow that they might
not have performed even better had they been in an
altered state of the type we have been discussing. This
observation, however, brings to light another criticism of
the studies supporting the noise reduction model. Many
of these studies, in particular most of the ganzfeld and
relaxation experiments, failed to use control groups or
other means of assessing whether the induction pro-
cedure was actually responsible for the positive scoring.
Among those studies that did use such controls, the
designs still did always preclude other interpretations of
the results (see, e.g., }SStanford 1987). Especially in the
experimenipprovea `i oriRelea eS2000/08/08
-
em
ec
s or
attributable to expectancy e
istics.
More research will be needed before the status of the
noise reduction model can be cbnclusively determined. A
large body of empirical data from diverse sources is
nevertheless consistent with this hypothesis. This fact is
sufficient to support the more modest point we are trying
to make: Psi data fall into patterns that make psycho-
logical sense and encourage a systematic program of re-
search.
6. Practical significance
The remaining criticism that needs to be addressed con-
cerns practical significance. Even if one concedes that the
preceding criticisms have been addressed satisfactorily, it
can be argued that the results of psi experiments are
trivial and of no practical or clinical importance. It is
certainly true that the effect sizes in most psi experiments
are small. For example, the effects reported by Schmidt
in his REG experiments rarely exceed chance expectation
by more than a few percent. Such outcomes hardly seem
to be practically useful.
There are fallacies in this line of criticism, however.
First, it fails to acknowledge the distinction between
basic and applied research. Practical significance is in-
deed important if the objective is to determine whether a
process can be applied to solve "real-world" problems.
Parapsychology, however, is devoted almost exclusively
to basic research, where the objective is to address
theoretical issues. Psi results seem to violate expectations
derived from generally accepted physical theory, and this
makes them of theoretical interest irrespective of their
magnitude. For example, many of the most important
experiments in physics deal with effects of very small
magnitude.
The above criticism is problematic even from the
applied perspective, however, because techniques from
information theory can be implemented to amplify a weak
effect of the type commonly found in psi experiments. In
one experiment, for example, Ryzl (1966) had the subject
Stepanek guess whether the green or white sides of 30
cards placed inside opaque envelopes were uppermost.
The cards were rerandomized and Stepanek guessed the
order again. This process was repeated until Stepanek's
distribution of guesses on each of 10 principal cards
favored either green or white to a prespecified degree.
Other criteria involving the other. 20 cards also had to be
met. The result was a single "majority vote" on each of the
10 principal cards. In each of five experiments, Step-
anek's majority votes duplicated the target order of the 10
principal cards perfectly (100%), although his success rate
on individual guesses was only 62%. Other examples of
this approach have also been documented (e. g., Car-
penter 1975; Puthoff 1985).
The reason that psi has not yet been applied on a broad
scale has to do not with the size of the effects but with
their unreliability, which (as discussed above) probably
reflects our lack of understanding of the factors that affect
performance on psi tasks. Uncovering these factors is a
prime objective of modern parapsychological research.
If si anomalies do in fact turn out to represent some
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~retbfore unrecognized and far-reaching ability to ac-
Lute information and manipulate the environment, and
this ability could be brought under conscious control,
ie practical applications and potential benefits to man-
ind seem almost limitless. It is easy to put para-
sychologists on the defensive by citing the slow progress
at has been made to date in coming to grips with the
nomalies. What such an approach overlooks is the im-
ortance of solving the admittedly unsolved puzzle that
he anomalies represent. It seems to us that too many
ommentators on both sides of the psi controversy place
xcessive faith in what amounts to little more than spec-
ulations about the true nature of the anomalies. Only by
ontinued research, preferably supported in a mean-
ngful way by the scientific community at large, will the
peculations turn into knowledge.
We find that the frequency of replications, especially with
regard to the noise reduction hypothesis, indicates that
we are indeed on the trail of something interesting. At the
same time, we cannot totally rule out the possibility that
we may yet discover a hidden artifact or set of artifacts
that would provide a satisfactory conventional explana-
tion of the results (and which might, in their own way,
likewise prove interesting). Such an open approach,
which is widely shared within the parapsychological com-
munity (Parapsychological Association 1986), is dictated
by the anomalous nature of psi and the fact that there is
still no verified theory of the mechanism(s) involved in psi
interactions. Scientists working in this area must accord-
ingly approach all hypotheses with an attitude of skep-
ticism and must show a readiness to look at various
alternatives (Palmer 1986a). Critics with a great deal of a
priori skepticism about psi have reasonable grounds for
not accepting omegic hypotheses - that is, that the
anomalies represent a new principle of nature. At the
same time, they have little justification for choosing to
close their minds to the alternative possibility - namely,
that the anomalies might reveal a currently unrecognized
human capacity of great potential importance. If they do
close their minds, they make the same mistake as those
"believers in the paranormal" who refuse to study evi-
dence and arguments contrary to their beliefs.
At the least, there is now an excellent prima facie case
for the statistical repeatability of the anomalies under
certain conditions. There appears to be a common thread
running through these studies, diverse though they may
be, in the techniques of eliciting and measuring psi. This
commonality appears, at least in a crude and preliminary
way, to make some theoretical sense and is leading to
work now in progress at various laboratories to refine and
consolidate the methods and concepts.
We have discussed here some experimental evidence
for the reality of psi, as well as the objections of critics to
such evidence. We have also considered the idea that
sensory noise reduction may be favorable to psi, sketch-
ing the experimental results that bear on this hypothesis.
The following conclusions seem to emerge:
(1) Schmidt's results and many other parapsychological
findings would be taken seriously if they related to a
conventional area in science, for standard methodological
and statistical criticisms have been answered.
(2) No single experiment, no matter how carefully
designed and executed, can be expected to settle a
controversial claim. The results of one good experiment
do no more than make a claim. The significance of that
claim is proportional to the degree that experiments
supporting it are successfully replicated, and the degree
of research and hypothesis-testing it generates. Also
important is its potential for contributing to a theoretical
understanding of the natural world and for practical
application.
(3) The issue of replication and the meaning of experi-
mental results in psi research have been a primary con-
cern of parapsychologists. The discussion of the studies
bearing on psi and sensory noise reduction and the
rationale behind them show (a) a moderately significant
rate of replication (in a statistical sense) and (b) the
possibility of finding conditions that favor or inhibit psi.
Together, these studies make a strong prima facie case for
a genuine scientific anomaly and provide a viable re-
search program.
(4) Further clarity and precision in the concepts and
hypotheses are needed. Noise reduction, for example,
needs to be defined more precisely. Some improvements
in experimental design may have to be introduced to deal
with the central issue of how psi operates. No mechanism
or theory that would adequately explain psi has been
validated. Those who accord an extremely low subjective
probability to omegic hypotheses may therefore justifia-
bly demand more and better evidence. But demanding
such evidence is not the same as questioning the cred-
ibility of past research.
(5) The final settlement of the question of the status of
psi will have to depend on further research. The scientific
legitimacy of psi cannot be denied by personal innuendos
and ad hominem arguments, just as it cannot be estab-
lished by preaching. One can only hope that the climate
of scientific opinion will be sufficiently tolerant to permit
free and open inquiry by those who have the necessary
skills and interest.
NOTE
1. The theoretical rationale of the study was that the subject
could psychokinetically influence the selection of the random
seed numbers retroactively. We will not elaborate this hypoth-
esis further, as it is not directly relevant to the control features of
the experiment.
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