REPLICATION AND META-ANALYSIS IN PARAPSYCHOLOGY (JESSICA UTTS)

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Statistical Science
1991, Vol. 6, No. 4, 363-403
Replication and Meta-Analysis in
Parapsychology
Jessica Utts
Abstract. Parapsychology, the laboratory study of psychic phenomena,
has had its history interwoven with that of statistics. Many of the
controversies in parapsychology have focused on statistical issues, and
statistical models have played an integral role in the experimental
work. Recently, parapsychologists have been using meta-analysis as a
tool for synthesizing large bodies of work. This paper presents an
overview of the use of statistics in parapsychology and offers a summary
of the meta-analyses that have been conducted. It begins with some
anecdotal information about the involvement of statistics and statisti-
cians with the early history of parapsychology. Next, it is argued that
most nonstatisticians do not appreciate the connection between power
and "successful" replication of experimental effects. Returning to para-
psychology, a particular experimental regime is examined by summariz-
ing an extended debate over the interpretation of the results. A new set
of experiments designed to resolve the debate is then reviewed. Finally,
meta-analyses from several areas of parapsychology are summarized. It
is concluded that the overall evidence indicates that there is an anoma-
lous effect in need of an explanation.
Key words and phrases: Effect size, psychic research, statistical contro-
versies, randomness, vote-counting.
1. INTRODUCTION Parapsychology, as this field is called, has been a
In a June 1990 Gallup Poll, 49% of the 1236 source of controversy throughout its history. Strong
beliefs tend to be resistant to change even in the
respondents claimed to believe in extrasensory per- face of data, and many people, scientists included,
ception (ESP), and one in four claimed to have had seem to have made up their minds on the question
a personal experience involving telepathy (Gallup without examining any empirical data at all. A
and Newport, 1991). Other surveys have shown critic of parapsychology recently acknowledged that
even higher percentages; the University of "The level of the debate during the past 130 years
Chicago's National Opinion Research Center re- has been an embarrassment for anyone who would
Gently surveyed 1473 adults, of which 67% claimed like to believe that scholars and scientists adhere
that they had experienced ESP (Greeley, 1987). to standards of rationality and fair play" (Hyman,
Public opinion is a poor arbiter of science, how- 1985a, page 89). While much of the controversy has
ever, and experience is a poor substitute for the focused on poor experimental design and potential
scientific method. For more than a century, small fraud, there have been attacks and defenses of the
numbers of scientists have been conducting labora- statistical methods as well, sometimes calling into
tort' experiments to study phenomena such as question the very foundations of probability and
telepathy, clairvoyance and precognition, collet- statistical inference.
tively known as "psi" abilities. This paper will Most of the criticisms have been leveled b
examine some of that work, as well as some of the by psy
statistical controversies it has generated. chologists. For example, a 1988 report of the U.S.
National Academy of Sciences concluded that "The
committee finds no scientific justification from
research conducted over a period of 130 years for
Jessica Utts is Associate Professor, Division of the existence of parapsychological phenomena"
Statistics, University of California at Davis, 469 (Druckman and Swets, 1988, page 22). The chapter
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chaired by a psychologist who had published a
similar conclusion prior to his appointment to the
committee (Hyman, 1985a, page 7). There were no
parapsychologists involved with the writing of the
report. Resulting accusations of bias (Palmer, Hon-
orton and Utts, 1989) led U.S. Senator Claiborne
Pell to request that the Congressional Office of
Technology Assessment (OTA) conduct an investi-
gation with a more balanced group. A one-day
workshop was held on September 30, 1988, bring-
ing together parapsychologists, critics and experts
in some related fields (including the author of this
paper). The report concluded that parapsychology
needs "a fairer hearing across a broader spectrum
of the scientific community, so that emotionality
does not impede objective assessment of experimen-
tal results" (Office of Technology Assessment,
1989).
It is in the spirit of the OTA report that this
article is written. After Section 2, which offers an
anecdotal account of the role of statisticians and
statistics in parapsychology, the discussion turns to
the more general question of replication of experi-
mental results. Section 3 illustrates how replica-
tion has been (mis)interpreted by scientists in many
fields. Returning to parapsychology in Section 4, a
particular experimental regime called the "ganz-
feld" is described, and an extended debate about
the interpretation of the experimental results is
discussed. Section 5 examines a meta-analysis of
recent ganzfeld experiments designed to resolve the
debate. Finally, Section 6 contains a brief account
of meta-analyses that have been conducted in other
areas of parapsychology, and conclusions are given
in Section 7.
ments, offered one of the earliest treatises on the
statistical evaluation of forced-choice experiments
in two articles published in the Proceedings of the
Society for Psychical Research (Edgeworth, 1885,
1886). Unfortunately, as noted by Mauskopf and
McVaugh (1979) in their historical account of the
period, Edgeworth's papers were "perhaps too diffi-
cult for their immediate audience" (page 105).
Edgeworth began his analysis by using Bayes'
theorem to derive the formula for the posterior
probability that chance was operating, given the
data. He then continued with an argument
"savouring more of Bernoulli than Bayes" in which
"it is consonant, I submit, to experience, to put, 1 /2
both for a and a," that is, for both the prior proba-
bility that chance alone was operating, and the
prior probability that "there should have been some
additional agency." He then reasoned (using a
Taylor series expansion of the posterior prob-
ability formula) that if there were a large prob-
ability of observing the data given that some
additional agency was ail work, and a small objec-
tive probability of the data under chance, then the
latter (binomial) probability "may be taken as a
rough measure of the sought a posteriori probabil-
ity in favour of mere chance" (page 195). Edge-
worth concluded his article by applying his method
to some data published: previously in the same
journal. He found the probability against chance to
be 0.99996, which he said "may fairly be regarded
as physical certainty" (page 199). He concluded:
Such is the evidence which the calculus of
probabilities affords as to the existence of an
agency other than mere: chance. The calculus is
silent as to the nature of that agency-whether
it is more likely to be vulgar illusion or ex-
2. STATISTICS AND PARAPSYCHOLOGY traordinary law. That is a question to be
Parapsychology had its beginnings in the investi- decided, not by formulae and figures, but by
general philosophy and common sense [page
gation of purported mediums and other anecdotal
1991.
claims in the late 19th century. The Society for
Psychical Research was founded in Britain in 1882,
Both the statistical arguments and the experi-
and its American counterpart was founded in
mental controls in these: early experiments were
Boston in 1884. While these organizations and their
somewhat loose. For example, Edgeworth treated
members were primarily involved with investigat-
as binomial an experiment in which one person
anecdotal material, a few of the early re-
ing chose a string of eight letters and another at-
searchers were already conducting "forced-choice"
tempted to guess the string. Since it has long been
such as card-guessing. (Forced-choice
experiments understood that people are poor random number (or
are like multiple choice tests; on each
experiments letter) generators, there is no statistical basis for
trial the subject must guess from a small, known
analyzing such an experiment. Nonetheless, Edge-
set of possibilities.) Notable among these was
worth and his contemporaries set the stage for the
Nobel Laureate Charles Richet, who is generally
use of controlled experiments with statistical evalu-
credited with being the first to recognize that prob-
ation in laboratory parapsychology. An interesting
ability theory could be applied to card-guessing
historical account of Edgeworth's involvement and
experiments (Rhine, 1977, page 26; Richet, 1884).
the role telepathy experiments played in the early
F. Y. Edgeworth, partly in response to what he
history of randomization and experimental design
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REPLICATION IN PARAPSYCHOLOGY 365
One of the first American researchers to
use statistical methods in parapsychology was
John Edgar Coover, who was the Thomas Welton
Stanford Psychical Research Fellow in the Psychol-
ogy Department at Stanford University from 1912
to 1937 (Dommeyer, 1975). In 1917, Coover pub-
lished a large volume summarizing his work
(Coover, 1917). Coover believed that his results
were consistent with chance, but others have ar-
gued that Coover's definition of significance was
too strict (Dommeyer, 1975). For example, in one
evaluation of his telepathy experiments, Coover
found a two-tailed p-value of 0.0062. He concluded,
"Since this value, then, lies within the field of
chance deviation, although the probability of its
occurrence by chance is fairly low, it cannot be
accepted as a decisive indication of some cause
beyond chance which operated in favor of success in
guessing" (Coover, 1917, page 82). On the next
page, he made it explicit that he would require a
p-value of 0.0000221 to declare that something
other than chance was operating.
It 'was during the summer of 1930, with the
card-guessing experiments of J. B. Rhine at Duke
University, that parapsychology began to take hold
as a laboratory science. Rhine's laboratory still
exists under the name of the Foundation for Re-
search on the Nature of Man, housed at the edge of
the Duke University campus.
It wasn't long after Rhine published his first
book, Extrasensory Perception in 1934, that the
attacks on his methodology began. Since his claims
were wholly based on statistical analyses of his
experiments, the statistical methods were closely
scrutinized by critics anxious to find a conventional
explanation for Rhine's positive results.
The most persistent critic was a psychologist
from McGill University named Chester Kellogg
(Mauskopf and McVaugh, 1979). Kellogg's main
argument was that Rhine was using the binomial
distribution (and normal approximation) on a se-
ries of trials that were not independent. The experi-
ments in question consisted of having a subject
guess the order of a deck of 25 cards, with five each
of five symbols, so technically Kellogg was correct.
By 1937, several mathematicians and statis-
ticians had come to Rhine's aid. Mauskopf and
McVaugh (1979) speculated that since statistics was
itself a young discipline, "a number of statisticians
were equally outraged by Kellogg, whose argu-
ments they saw as discrediting their profession"
(page 258). The major technical work, which ac-
knowledged that Kellogg's criticisms were accurate
but did little to change the significance of the
results, was conducted by Charles Stuart and
Joseph AAf3~1Lq6J P
l*IWAha
Mof the Journal of arapsychology ( tuar
and Greenwood, 1937). Stuart, who had been an
undergraduate in mathematics at Duke, was one of
Rhine's early subjects and continued to work with
him as a researcher until Stuart's death in 1947.
Greenwood was a Duke mathematician, who appar-
ently converted to a statistician at the urging of
Rhine.
Another prominent figure who was distressed
with Kellogg's attack was E. V. Huntington, a
mathematician at Harvard. After corresponding
with Rhine, Huntington decided that, rather than
further confuse the public with a technical reply to
Kellogg's arguments, a simple statement should be
made to the effect that the mathematical issues in
Rhine's work had been resolved. Huntington must
have successfully convinced his former student,
Burton Camp of Wesleyan, that this was a wise
approach. Camp was the 1937 President of IMS.
When the annual meetings were held in December
of 1937 (jointly with AMS and AAAS), Camp
released a statement to the press that read:
Dr. Rhine's investigations have two aspects:
experimental and statistical. On the exper-
imental side mathematicians, of course,
have nothing to say. On the statistical side,
however, recent mathematical work has
established the fact that, assuming that the
experiments have been properly performed,
the statistical analysis is essentially valid. If
the Rhine investigation is to be fairly attacked,
it must be on other than mathematical grounds
[Camp, 1937].
One statistician who did emerge as a critic was
William Feller. In a talk at the Duke Mathemati-
cal Seminar on April 24, 1940, Feller raised three
criticisms to Rhine's work (Feller, 1940). They had
been raised before by others (and continue to be
raised even today). The first was that inadequate
shuffling of the cards resulted in additional infor-
mation from one series to the next. The second was
what is now known as the "file-drawer effect,"
namely, that if one combines the results of pub-
lished studies only, there is sure to be a bias in
favor of successful studies. The third was that the
results were enhanced by the use of optional stop-
ping, that is, by not specifying the number of trials
in advance. All three of these criticisms were ad-
dressed in a rejoinder by Greenwood and Stuart
(1940), but Feller was never convinced. Even in its
third edition published in 1968, his book An Intro-
duction to Probability Theory and Its Applications
still contains his conclusion about Greenwood and
Stuart: "Both their arithmetic and their experi-
s have a distinct tinge of the supernatural"
ment
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Feller was confused ... he seemed to have decided
the opposition was wrong and that was that."
Several statisticians have contributed to the
literature in parapsychology to greater or lesser
degrees. T. N. E. Greville developed applicable
statistical methods for many of the experiments in
parapsychology and was Statistical Editor of the
Journal of Parapsychology (with J. A. Greenwood)
from its start in 1937 through Volume 31 in 1967;
Fisher (1924, 1929) addressed some specific prob-
lems in card-guessing experiments; Wilks (1965a, b)
described various statistical methods for parapsy-
chology; Lindley (1957) presented a Bayesian anal-
ysis of some parapsychology data; and Diaconis
(1978) pointed out some problems with certain ex-
periments and presented a method for analyzing
experiments when feedback is given.
Occasionally, attacks on parapsychology have
taken the form of attacks on statistical inference in
general, at least as it is applied to real data.
Spencer-Brown (1957) attempted to show that true
randomness is impossible, at least in finite se-
quences, and that this could be the explanation for
the results in parapsychology. That argument re-
emerged in a recent debate on the role of random-
ness in parapsychology, initiated by psychologist J.
Barnard Gilmore (Gilmore, 1989, 1990; Utts, 1989;
Palmer, 1989, 1990). Gilmore stated that "The ag-
nostic statistician, advising on research in psi,
should take account of the possible inappropriate-
ness of classical inferential statistics" (1989, page
338). In his second paper, Gilmore reviewed several
non-psi studies showing purportedly random sys-
tems that do not behave as they should under
randomness (e.g., Iversen, Longcor, Mosteller,
Gilbert and Youtz, 1971; Spencer-Brown, 1957).
Gilmore concluded that "Anomalous data ...
should not be found nearly so often if classical
statistics offers a valid model of reality" (1990,
page 54), thus rejecting the use of classical statisti-
cal inference for real-world applicationsin general.
diverse views among parapsychologists on the na-
ture of the problem. Ilonorton (1985a) and. Rao
(1985), for example, both argued that strict replica-
tion is uncommon in most branches of science and
that parapsychology should not be singled out as
unique in this regard. Other authors expressed
disappointment in the lack of a single repeatable
experiment in parapsychology, with titles such
as "Unrepeatability: Parapsychology's Only Find-
ing" (Blackmore, 1985),; and "Research Strategies
for Dealing with Unstable Phenomena" (Beloff,
1985).
It has never been clear, however, just exactly
what would constitute acceptable evidence of a re-
peatable experiment. In the early days of investiga-
tion, the major critics `insisted that it would be
sufficient for Rhine and Soal to convince them of
ESP if a parapsychologist could perform success-
fully a single 'fraud-proof' xperiment" (Hyman,
1985a, page 71). However, as soon as well-designed
experiments showing statistical significance
emerged, the critics realized that a single experi-
ment could be statistically significant just by
chance. British psychologist C. E. M. Hansel quan-
tified the new expectation, that the experiment
should be repeated a few; times, as follows:
If a result is significant at the .01 level and
this result is not due to chance but to informa-
tion reaching the subject, it may be expected
that by making two further sets of trials the
antichance odds of one, hundred to one will be
increased to around a million to one, thus en-
abling the effects of ESP-or whatever is re-
sponsible for the original result-to manifest
itself to such an extent: that there will be little
doubt that the result; is not due to chance
[Hansel, 1980, page 29$].
In other words, three consecutive experiments at
p s 0.01 would convince Hansel that something
other than chance was at! work.
This argument implies that if a particular experi-
ment produces a statistically significant result, but
subsequent replications fail to attain significance,
Implicit and explicit in the literature on parapsy- then the original result was probably due to chance,
chology is the assumption that, in order to truly or at least remains unconvincing. The problem with
establish itself, the field needs to find a repeat- this line of reasoning is that there is no consid-
able experiment. For example, Diaconis (1978) eration given to sample, size or power. Only an
started the summary of his article in Science with experiment with extremely high power should
the words "In search of repeatable ESP experi- be expected to be "successful" three times in
ments, modern investigators. .. " (page 131). On succession.
October 28-29, 1983, the 32nd International Con- It is perhaps a failure! of the way statistics is
ference of the Parapsychology Foundation was held taught that many scientists do not understand the
in San Antonio, Texas, to address "The Repeatabil- importance of power in defining successful replica-
ity Problem in Parapsychology." The Conference tion. To illustrate this point, psychologists Tversky
Proceedings (Shapin and Coly, 1985) reflect the and Kahnemann (1982) distributed a questionnaire
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REPLICATION IN PARAPSYCHOLOGY
to their colleagues at a professional meeting, with
the question:
An investigator has reported a result that you
consider implausible. He ran 15 subjects, and
reported a significant value, t = 2.46. Another
investigator has attempted to duplicate his pro-
cedure, and he obtained a nonsignificant value
of t with the same number of subjects. The
direction was the same in both sets of data.
You are reviewing the literature. What is the
highest value of t in the second set of data that
you would describe as a failure to replicate?
[1982, page 281.
In reporting their results, Tversky and Kahne-
mann stated:
The majority of our respondents regarded t =
1.70 as a failure to replicate. If the data of two
such studies (t = 2.46 and t = 1.70) are pooled,
the value of t for the combined data is about
3.00 (assuming equal variances). Thus, we are
faced with a paradoxical state of affairs, in
which the same data that would increase our
confidence in the finding when viewed as part
of the original study, shake our confidence
when viewed as an independent study [1982,
page 281.
At a recent presentation to the History and Phi-
losophy of Science Seminar at the University of
California at Davis, I asked the following question.
Two scientists, Professors A and B, each have a
theory they would like to demonstrate. Each plans
to run a fixed number of Bernoulli trials and then
test Ho: p = 0.25 versus Ha: p > 0.25. Professor A
has access to large numbers of students each
semester to use as subjects. In his first experiment,
he runs 100 subjects, and there are 33 successes
(p = 0.04, one-tailed). Knowing the importance of
replication, Professor A runs an additional 100 sub-
jects as a second experiment. He finds 36 successes
(p = 0.009, one-tailed).
Professor B only teaches small classes. Each
quarter, she runs an experiment on her students to
test her theory. She carries out ten studies this
way, with the results in Table 1.
I asked the audience by a show of hands to
indicate whether or not they felt the scientists had
successfully demonstrated their theories. Professor
A's theory received overwhelming support, with
approximately 20 votes, while Professor B's theory
received only one vote.
If you aggregate the results of the experiments
for each professor, you will notice that each con-
ducted 200 trials, and Professor B actually demon-
strated a higher level of success than Professor A
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with 71 as opposed to 69 successful trials. The
one-tailed p-values for the combined trials are
0.0017 for Professor A and 0.0006 for Professor B.
To address the question of replication more ex-
plicitly, I also posed the following scenario. In
December of 1987, it was decided to prematurely
terminate a study on the effects of aspirin in reduc-
ing heart attacks because the data were so convinc-
ing (see, e.g., Greenhouse and Greenhouse, 1988;
Rosenthal, 1990a). The physician-subjects had been
randomly assigned to take aspirin or a placebo.
There were 104 heart attacks among the 11,037
subjects in the aspirin group, and 189 heart attacks
among the 11,034 subjects in the placebo group
(chi-square = 25.01, p < 0.00001).
After showing the results of that study, I pre-
sented the audience with two hypothetical experi-
ments conducted to try to replicate the original
result, with outcomes in Table 2.
I asked the audience to indicate which one they
thought was a more successful replication. The au-
dience chose the second one, as would most journal
editors, because of the "significant p-value." In
fact, the first replication has almost exactly the
same proportion of heart attacks in the two groups
as the original study and is thus a very close repli-
cation of that result. The second replication has
TABLE 1
Attempted replciations for professor B
10
4
0.22
15
6
0.15
17
6
0.23
25
8
0.17
30
10
0.20
40
13
0.18
18
7
0.14
10
5
0.08
15
5
0.31
20
7
0.21
TABLE 2
Hypothetical replications of the aspirin / heart
attack study
Replication #1
Heart attack
Replication #2
Heart attack
Aspirin
11
1156
20
2314
Placebo
19
1090
48
2170
Chi-square
2.596, p =
0.11
13.206, p =
0.0003
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very different proportions, and in fact the relative
risk from the second study is not even contained in
a 95% confidence interval for relative risk from the
original study. The magnitude of the effect has
been much more closely matched by the "nonsig-
nificant" replication.
Fortunately, psychologists are beginning to no-
tice that replication is not as straightforward as
they were originally led to believe. A special issue
of the Journal of Social Behavior and Personality
was entirely devoted to the question of replication
(Neuliep, 1990). In one of the articles, Rosenthal
cautioned his colleagues: "Given the levels of sta-
tistical power at which we normally operate, we
have no right to expect the proportion of significant
results that we typically do expect, even if in na-
ture there is a very real and very important effect"
(Rosenthal, 1990b, page 16).
Jacob Cohen, in his insightful article titled
"Things I Have Learned (So Far)," identified an-
other misconception common among social scien-
tists: "Despite widespread misconceptions to the
contrary, the rejection of a given null hypothesis
gives us no basis for estimating the probability that
a replication of the research will again result in
rejecting that null hypothesis" (Cohen, 1990, page
1307).
Cohen and Rosenthal both advocate the use of
effect sizes as opposed to significance levels when
defining the strength of an experimental effect. In
general, effect sizes measure the amount by which
the data deviate from the null hypothesis in terms
of standardized units. For instance, the effect size
for a two-sample t-test is usually defined to be the
difference in the two means, divided by the stan-
dard deviation for the control group. This measure
can be compared across studies without the depen-
dence on sample size inherent in significance lev-
els. (Of course there will still be variability in the
sample effect sizes, decreasing as a function of sam-
ple size.) Comparison of effect sizes across studies is
one of the major components of meta-analysis.
Similar arguments have recently been made in
the medical literature. For example, Gardner and
Altman (1986) stated that the use of p-values "to
define two alternative outcomes-significant and
not significant-is not helpful and encourages lazy
thinking" (page 746). They advocated the use of
confidence intervals instead.
As discussed in the next section, the arguments
used to conclude that parapsychology has failed to
demonstrate a replicable effect hinge on these mis-
conceptions of replication and failure to examine
power. A more appropriate analysis would compare
the effect sizes for similar experiments across ex-
perimenters and across time to see if there have
been consistent effects of the same magnitude.
Rosenthal also advocates this view of replication:
The traditional view; of replication focuses on
significance level as the relevant summary
statistic of a study and evaluates the success of
a replication in a dichotomous fashion. The
newer, more useful view of replication focuses
on effect size as the more important summary
statistic of a study and evaluates the success of
a replication not in a dichotomous but in a
continuous fashion [Rosenthal, 1990b, page 28].
The dichotomous view of replication has been
used throughout the history of parapsychology, by
both parapsychologists and critics (Utts, 1988). For
example, the National Academy of Sciences report
critically evaluated "significant" experiments, but
entirely ignored "nonsignificant" experiments.
In the next three sections, we will examine, some
of the results in parapsychology using the broader,
more appropriate definition of replication. In doing
so, we will show that the results are far more
interesting than the critics would have us believe.
4. THE GANZFELD DEBATE IN
PARAPSYCHOLOGY
An extensive debate took place in the mid-1980s
between a parapsychologist and critic, questioning
whether or not a particular body of parapsychologi-
cal data had demonstrated psi abilities. The experi-
ments in question were all conducted using the
ganzfeld setting (described below). Several authors
were invited to write commentaries on the debate.
As a result, this data base has been more thor-
oughly analyzed by both critics and proponents
than any other and provides a good source for
studying replication in parapsychology.
The debate concluded; with a detailed series of
recommendations for further experiments, and left
open the question of whether or not psi abilities
had been demonstrated. A new series of experi-
ments that followed the recommendations were
conducted over the next few years. The results of
the new experiments will be presented in Section 5.
4.1 Free-Response Experiments
Recent experiments in parapsychology tend to
use more complex target material than the cards
and dice used in the early investigations, partially
to alleviate boredom on the part of the subjects and
partially because they are thought to "more nearly
resemble the conditions of spontaneous psi occur-
rences" (Burdick and Kelly, 1977, page 109). These
experiments fall under: the general heading of
"free-response" experiments, because the subject is
asked to give a verbal or written description of the
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REPLICATION IN PARAPSYCHOLOGY 369
target, rather than being forced to make a choice
from a small discrete set of possibilities. Various
types of target material have been used, including
pictures, short segments of movies on video tapes,
actual locations and small objects.
Despite the more complex target material, the
statistical methods used to analyze these experi-
ments are similar to those for forced-choice experi-
ments. A typical experiment proceeds as follows.
Before conducting any trials, a large pool of poten-
tial targets is assembled, usually in packets of four.
Similarity of targets within a packet is kept to a
minimum, for reasons made clear below. At the
start of an experimental session, after the subject is
sequestered in an isolated room, a target is selected
at random from the pool. A sender is placed in
another room with the target. The subject is asked
to provide a verbal or written description of what
he or she thinks is in the target, knowing only that
it is a photograph, an object, etc.
After the subject's description has been recorded
and secured against the potential for later alter-
ation, a judge (who may or may not be the subject)
is given a copy of the subject's description and the
four possible targets that were in the packet with
the correct target. A properly conducted experi-
ment either uses video tapes or has two identical
sets of target material and uses the duplicate set
for this part of the process, to ensure that clues
such as fingerprints don't give away the answer.
Based on the subject's description, and of course on
a blind basis, the judge is asked to either rank the
four choices from most to least likely to have been
the target, or to select the one from the four that
seems to best match the subject's description. If
ranks are used, the statistical analysis proceeds by
summing the ranks over a series of trials and
comparing the sum to what would be expected by
chance. If the selection method is used, a "direct
hit" occurs if the correct target is chosen, and the
number of direct hits over a series of trials is
compared to the number expected in a binomial
experiment with p = 0.25.
Note that the subjects' responses cannot be con-
sidered to be "random" in any sense, so probability
assessments are based on the random selection of
the target and decoys. In a correctly designed ex-
periment, the probability of a direct hit by chance
is 0.25 on each trial, regardless of the response, and
the trials are independent. These and other issues
related to analyzing free-response experiments are
discussed by Utts (1991).
4.2 The Psi Ganzfeld Experiments
The ganzfeld procedure is a particular kind of
isolation technique originally developed by Gestalt
psychologists for other purposes. Evidence from
spontaneous case studies and experimental work
had led parapsychologists to a model proposing that
psychic functioning may be masked by sensory in-
put and by inattention to internal states (Honorton,
1977). The ganzfeld procedure was specifically de-
signed to test whether or not reduction of external
"noise" would enhance psi performance.
In these experiments, the subject is placed in a
comfortable reclining chair in an acoustically
shielded room. To create a mild form of sensory
deprivation, the subject wears headphones through
which white noise is played, and stares into a
constant field of red light. This is achieved by
taping halved translucent ping-pong balls over the
eyes and then illuminating the room with red light.
In the psi ganzfeld experiments, the subject speaks
into a microphone and attempts to describe the
target material being observed by the sender in a
distant room.
At the 1982 Annual Meeting of the Parapsycho-
logical Association, a debate took place over the
degree to which the results of the psi ganzfeld
experiments constituted evidence of psi abilities.
Psychologist and critic Ray Hyman and parapsy-
chologist Charles Honorton each analyzed the re-
sults of all known psi ganzfeld experiments to date,
and they reached strikingly different conclusions
(Honorton, 1985b; Hyman, 1985b). The debate con-
tinued with the publication of their arguments in
separate articles in the March 1985 issue of the
Journal of Parapsychology. Finally, in the Decem-
ber 1986 issue of the Journal of Parapsychology,
Hyman and Honorton (1986) wrote a joint article
in which they highlighted their agreements and
disagreements and outlined detailed criteria for
future experiments. That same issue contained
commentaries on the debate by 10 other authors.
The data base analyzed by Hyman and Honorton
(1986) consisted of results taken from 34 reports
written by a total of 47 authors. Honorton counted
42 separate experiments described in the reports, of
which 28 reported enough information to determine
the number of direct hits achieved. Twenty three of
the studies (55%) were classified by Honorton as
having achieved statistical significance at 0.05.
4.3 The Vote-Counting Debate
Vote-counting is the term commonly used for the
technique of drawing inferences about an experi-
mental effect by counting the number of significant
versus nonsignificant studies of the effect. Hedges
and Olkin (1985) give a detailed analysis of the
inadequacy of this method, showing that it is more
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number of studies increases. While Hyman ac-
knowledged that "vote-counting raises many prob-
lems" (Hyman, 1985b, page 8), he nonetheless spent
half of his critique of the ganzfeld studies showing
why Honorton's count of 55% was wrong.
Hyman's first complaint was that several of the
studies contained multiple conditions, each of which
should be considered as a separate study. Using
this definition he counted 80 studies (thus further
reducing the sample sizes of the individual studies),
of which 25 (31%) were "successful." Honorton's
response to this was to invite readers to examine
the studies and decide for themselves if the varying
conditions constituted separate experiments.
Hyman next postulated that there was selection
bias, so that significant studies were more likely to
be reported. He raised some important issues about
how pilot studies may be terminated and not re-
ported if they don't show significant results, or may
at least be subject to optional stopping, allowing
the experimenter to determine the number of tri-
als. He also presented a chi-square analysis that
"suggests a tendency to report studies with a small
sample only if they have significant results"
(Hyman, 1985b, page 14), but I have questioned his
analysis elsewhere (Utts, 1986, page 397).
Honorton refuted Hyman's argument with four
rejoinders (Honorton, 1985b, page 66). In addition
to reinterpreting Hyman's chi-square analysis,
Honorton pointed out that the Parapsychological
Association has an official policy encouraging the
publication of nonsignificant results in its journals
and proceedings, that a large number of reported
ganzfeld studies did not achieve statistical signifi-
cance and that there would have to be 15 studies in
the "file-drawer" for every one reported to cancel
out the observed significant results.
The remainder of Hyman's vote-counting analy-
sis consisted of showing that the effective error rate
for each study was actually much higher than the
nominal 5%. For example, each study could have
been analyzed using the direct hit measure, the
sum of ranks measure or one of two other measures
used for free-response analyses. Hyman carried out
a simulation study that showed the true error rate
that the number of significant studies (using his
definition of a study) only dropped from 55% to
45%. Next, he proposed that a uniform index of
success be applied to all studies. He used the num-
ber of direct hits, since it was by far the most
commonly reported measure and was the measure
used in the first published psi ganzfeld study. He
then conducted a detailed analysis of the 28 studies
reporting direct hits and found that 43% were sig-
nificant at 0.05 on that ;measure alone. Further, he
showed that significant effects were reported by six
of the 10 independent investigators and thus were
not due to just one or two investigators or laborato-
ries. He also noted that success rates were very
similar for reports pubished in refereed journals
and those published in unrefereed monographs and
abstracts.
While Hyman's arguments identified issues such
as selective reporting end optional stopping that
should be considered in any meta-analysis, the de-
pendence of significance 'levels on sample size makes
the vote-counting technique almost useless for as-
sessing the magnitude of the effect. Consider, for
example, the 24 studies where the direct hit meas-
ure was reported and the chance probability of a
direct hit was 0.25, the most common type of study
in the data base. (There, were four direct hit studies
with other chance probabilities and 14 that did not
report direct hits.) Of the 24 studies, 13 (54%) were
"nonsignificant" at a = 0.05, one-tailed. But if the
367 trials in these "failed replications" are com-
bined, there are 106 direct hits, z = 1.66, and p =
0.0485, one tailed. This is reminiscent of the
dilemma of Professor B ':in Section 3.
Power is typically very low for these studies. The
median sample size for the studies reporting direct
hits was 28. If there is a real effect and it increases
the success probability from the chance 0.25 to
an actual 0.33 (a value whose rationale will be
made clear below), the: power for a study with 28
trials is only 0.181 (Utts, 1986). It should be no
surprise that there is a "repeatability" problem in
parapsychology.
4.4 Flaw Analysis and Future Recommendations
would be 0.22 if "significance" was defined by re- The second half of Hy' man's paper consisted of a
quiring at least one of these four measures to "Meta-Analysis of Flaws and Successful Outcomes"
achieve the 0.05 level. He suggested several other (1985b, page 30), designed to explore whether or
ways in which multiple testing could occur and not various measures of success were related to
concluded that the effective error rate in each ex- specific flaws in the experiments. While many crit-
periment was not the nominal 0.05, but rather was ics have argued that the results in parapsychology
probably close to the 31% he had determined to be can be explained by experimental flaws, Hyman's
the actual success rate in his vote-count. analysis was the first to attempt to quantify the
Honorton acknowledged that there was a multi- relationship between flaws and significant results.
ple testing problem, but he had a two-fold response. Hyman identified 12 potential flaws in the
First, he a lied a Bo f ro c rectio zf~1 eriments such as inadequate random-
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ization, multiple tests used without adjusting the
significance level (thus inflating the significance
level from the nominal 5%) and failure to use a
duplicate set of targets for the judging process (thus
allowing possible clues such as fingerprints). Using
cluster and factor analyses, the 12 binary flaw
variables were combined into three new variables,
which Hyman named General Security, Statistics
and Controls.
Several analyses were then conducted. The one
reported with the most detail is a factor analysis
utilizing 17 variables for each of 36 studies. Four
factors emerged from the analysis. From these,
Hyman concluded that security had increased over
the years, that the significance level tended to be
inflated the most for the most complex studies and
that both effect size and level of significance were
correlated with the existence of flaws.
Following his factor analysis, Hyman picked the
three flaws that seemed to be most highly corre-
lated with success, which were inadequate atten-
tion to both randomization and documentation and
the potential for ordinary communication between
the sender and receiver. A regression equation was
then computed using each of the three flaws as
dummy variables, and the effect size for the experi-
ment as the dependent variable. From this equa-
tion, Hyman concluded that a study without these
three :flaws would be predicted to have a hit rate of
27%. He concluded that this is "well within the
statistical neighborhood of the 25% chance rate"
(1985b, page 37), and thus "the ganzfeld psi data
base, despite initial impressions, is inadequate ei-
ther to support the contention of a repeatable study
or to demonstrate the reality of psi" (page 38).
Honorton discounted both Hyman's flaw classifi-
cation and his analysis. He did not deny that flaws
existed, but he objected that Hyman's analysis was
faulty and impossible to interpret. Honorton asked
psychometrician David Saunders to write an Ap-
pendix to his article, evaluating Hyman's analysis.
Saunders first criticized Hyman's use of a factor
analysis with 17 variables (many of which were
dichotomous) and only 36 cases and concluded that
"the entire analysis is meaningless" (Saunders,
1985, page 87). He then noted that Hyman's choice
of the three flaws to include in his regression anal-
ysis constituted a clear case of multiple analysis,
since there were 84 possible sets of three that could
have been selected (out of nine potential flaws), and
Hyman chose the set most highly correlated with
effect size. Again, Saunders concluded that "any
interpretation drawn from [the regression analysis]
must be regarded as meaningless" (1985, page 88).
Hyman's results were also contradicted by Harris
Hyman in his capacity as Chair of the National
Academy of Sciences' Subcommittee on Parapsy-
chology. Using Hyman's flaw classifications and a
multivariate analysis, Harris and Rosenthal con-
cluded that "Our analysis of the effects of flaws on
study outcome lends no support to the hypothesis
that ganzfeld research results are a significant
function of the set of flaw variables" (1988b,
page 3).
Hyman and Honorton were in the process of
preparing papers for a second round of debate when
they were invited to lunch together at the 1986
Meeting of the Parapsychological Association. They
discovered that they were in general agreement on
several major issues, and they decided to coauthor
a "Joint Communique" (Hyman and Honorton,
1986). It is clear from their paper that they both
thought it was more important to set the stage for
future experimentation than to continue the techni-
cal arguments over the current data base. In the
abstract to their paper, they wrote:
We agree that there is an overall significant
effect in this data base that cannot reasonably
be explained by selective reporting or multiple
analysis. We continue to differ over the degree
to which the effect constitutes evidence for psi,
but we agree that the final verdict awaits the
outcome of future experiments conducted by a
broader range of investigators and according to
more stringent standards [page 351].
The paper then outlined what these standards
should be. They included controls against any kind
of sensory leakage, thorough testing and documen-
tation of randomization methods used, better re-
porting of judging and feedback protocols, control
for multiple analyses and advance specification of
number of trials and type of experiment. Indeed,
any area of research could benefit from such a
careful list of procedural recommendations.
4.5 Rosenthal's Meta-Analysis
The same issue of the Journal of Parapsychology
in which the Joint Communique appeared also car-
ried commentaries on the debate by 10 separate
authors. In his commentary, psychologist Robert
Rosenthal, one of the pioneers of meta-analysis in
psychology, summarized the aspects of Hyman's
and Honorton's work that would typically be in-
cluded in a meta-analysis (Rosenthal, 1986). It is
worth reviewing Rosenthal's results so that they
can be used as a basis of comparison for the more
recent psi ganzfeld studies reported in Section 5.
Rosenthal, like Hyman and Honorton, focused
only on the 28 studies for which direct hits were
and Rosenthal (1988b) in an analysis requested b known. He chose to use an effect size measure
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called Cohen's h, which is the difference between
the arcsin transformed proportions of direct hits
that were observed and expected:
h = 2(arcsin - arcsin \).
One advantage of this measure over the difference
in raw proportions is that it can be used to compare
experiments with different chance hit rates.
If the observed and expected numbers of hits
were identical, the effect size would be zero. Of the
28 studies, 23 (82%) had effect sizes greater than
zero, with a median effect size of 0.32 and a mean
of 0.28. These correspond to direct hit rates of 0.40
and 0.38 respectively, when 0.25 is expected by
chance. A 95% confidence interval for the true
effect size is from 0.11 to 0.45, corresponding to
direct hit rates of from 0.30 to 0.46 when chance is
0.25.
A common technique in meta-analysis is to calcu-
late a "combined z," found by summing the indi-
vidual z scores and dividing by the square root of
the number of studies. The result should have a
standard normal distribution if each z score has a
standard normal distribution. For the ganzfeld
studies, Rosenthal reported a combined z of 6.60
with a p-value of 3.37 x 10- ri. He also reiterated
Honorton's file-drawer assessment by calculating
that there would have to be 423 studies unreported
to negate the significant effect in the 28 direct hit
studies.
Finally, Rosenthal acknowledged that, because of
the flaws in the data base and the potential for at
least a small file-drawer effect, the true average
effect size was probably closer to 0.18 than 0.28. He
concluded, "Thus, when the accuracy rate expected
under the null is 1/4, we might estimate the ob-
tained accuracy rate to be about 1/3" (1986, page
333). This is the value used for the earlier power
calculation.
It is worth mentioning that Rosenthal was com-
missioned by the National Academy of Sciences to
prepare a background paper to accompany its 1988
report on parapsychology. That paper (Harris and
Rosenthal, 1988a) contained much of the same
analysis as his commentary summarized above.
Ironically, the discussion of the ganzfeld work in
the National Academy Report focused on Hyman's
1985 analysis, but never mentioned the work it had
commissioned Rosenthal to perform, which contra-
dicted the final conclusion in the report.
5. A META-ANALYSIS OF RECENT GANZFELD
EXPERIMENTS
After the initial exchange with Hyman at
the 1982 Parapsychological Association Meeting,
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Honorton and his colleagues developed an auto-
mated ganzfeld experiment that was designed to
eliminate the methodo)ogical flaws identified by
Hyman. The execution and reporting of the experi-
ments followed the deta.led guidelines agreed upon
by Hyman and Honorton.
Using this "autoganzfeld" experiment, 11 experi-
mental series were conducted by eight experi-
menters between February 1983 and September
1989, when the equipment had to be dismantled
due to lack of funding. In this section, the results
of these experiments are summarized and com-
pared to the earlier ganzfeld studies. Much of the
information is derived from Honorton et al. (1990).
5.1 The Automated Ganzfeld Procedure
Like earlier ganzfeld studies, the "autoganzfeld"
experiments require fogy participants. The first is
the Receiver (R), who attempts to identify the tar-
get material being observed by the Sender (S). The
Experimenter (E) prepares R for the task, elicits
the response from R and supervises R's judging of
the response against the four potential targets.
(Judging is double blind; E does not know which is
the correct target.) The fourth participant is the lab
assistant (LA) whose only task is to instruct the
computer to randomly select the target. No one
involved in the experiment knows the identity of
the target.
Both R and S are sequestered in sound-isolated,
electrically shielded rooms. R is prepared as in
earlier ganzfeld studies, with white noise and a
field of red light. In a nonadjacent room, S watches
the target material on atelevision and can hear R's
target description ("mentation") as it is being
given. The mentation is also tape recorded.
The judging process takes place immediately af-
ter the 30-minute sending period. On a TV monitor
in the isolated room, R views the four choices from
the target pack that contains the actual target. R is
asked to rate each one according to how closely it
matches the ganzfeld mentation. The ratings are
converted to ranks and, if the correct target is
ranked first, a direct hit is scored. The entire proc-
ess is automatically recorded by the computer. The
computer then displays the correct choice to R as
feedback.
There were 160 preselected targets, used with
replacement, in 10 of the 11 series. They were
arranged in packets of four, and the decoys for a
given target were always the remaining three in
the same set. Thus, even if a particular target in a
set were consistently favored by Rs, the probability
of a direct hit under the null hypothesis would
remain at 1/4. Popular targets should be no more
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likely to be selected by the computer's random
number generator than any of the others in the set.
The selection of the target by the computer is the
only source of randomness in these experiments.
This is an important point, and one that is often
misunderstood. (See Utts, 1991, for elucidation.)
Eighty of the targets were "dynamic," consisting
of scenes from movies, documentaries and cartoons;
80 were "static," consisting of photographs, art
prints and advertisements. The four targets within
each set were all of the same type. Earlier studies
indicated that dynamic targets were more likely to
produce successful results, and one of the goals of
the new experiments was to test that theory.
The randomization procedure used to select the
taf,get and the order of presentation for judging was
thoroughly tested before and during the experi-
ments. A detailed description is given by Honorton
et al. (1990, pages 118-120).
Three of the 11 series were pilot series, five were
formal series with novice receivers, and three were
formal series with experienced receivers. The last
series with experienced receivers was the only one
that did not use the 160 targets. Instead, it used
only one set of four dynamic targets in which one
target had previously received several first place
ranks and one had never received a first place
rank. The receivers, none of whom had had prior
exposure to that target pack, were not aware that
only one target pack was being used. They each
contributed one session only to the series. This will
be called the "special series" in what follows.
Except for two of the pilot series, numbers of
trials were planned in advance for each series.
Unfortunately, three of the formal series were not
yet completed when the funding ran out, including
the special series, and one pilot study with advance
planning was terminated early when the experi-
menter relocated. There were no unreported trials
during the 6-year period under review, so there was
no "file drawer."
Overall, there were 183 Rs who contributed only
one trial and 58 who contributed more than one, for
a total of 241 participants and 355 trials. Only 23
Rs had previously participated in ganzfeld experi-
ments, and 194 Rs (81%) had never participated in
any parapsychological research.
While acknowledging that no probabilistic con-
clusions can be drawn from qualitative data, Hon-
orton et al. (1990) included several examples of
session excerpts that Rs identified as providing the
basis for their target rating. To give a flavor for the
dream-like quality of the mentation and the amount
rank, the first example is reproduced here. The
target was a painting by. Salvador Dali called
"Christ Crucified." The correct target received a
first place rank. The part of the mentation R used
to make this assessment read:
... I think of guides, like spirit guides, leading
me and I come into a court with a king. It's
quiet .... It's like heaven. The king is some-
thing like Jesus. Woman. Now I'm just sort of
summersaulting through heaven ... .
Brooding .... Aztecs, the Sun God .... High
priest ....Fear . . . . Graves. Woman.
Prayer . . . . Funeral . . . . Dark.
Death .... Souls .... Ten Commandments.
Moses .... [Honorton et al., 19901.
Over all 11 series, there were 122 direct hits in
the 355 trials, for a hit rate of 34.4% (exact bino-
mial p-value = 0.00005) when 25% were expected
by chance. Cohen's h is 0.20, and a 95% confidence
interval for the overall hit rate is from 0.30 to 0.39.
This calculation assumes, of course, that the proba-
bility of a direct hit is constant and independent
across trials, an assumption that may be question-
able except under the null hypothesis of no psi
abilities.
Honorton et al. (1990) also calculated effect sizes
for each of the 11 series and each of the eight
experimenters. All but one of the series (the first
novice series) had positive effect sizes, as did all of
the experimenters.
The special series with experienced Rs had an
exceptionally high effect size with h = 0.81, corre-
sponding to 16 direct hits out of 25 trials (64%), but
the remaining series and the experimenters had
relatively homogeneous effect sizes given the
amount of variability expected by chance. If the
special series is removed, the overall hit rate is
32.1%, h = 0.16. Thus, the positive effects are not
due to just one series or one experimenter.
Of the 218 trials contributed by novices, 71 were
direct hits (32.5%, h = 0.17), compared with 51
hits in the 137 trials by those with prior ganzfeld
experience (37%, h = 0.26). The hit rates and effect
sizes were 31% (h = 0.14) for the combined pilot
series, 32.5% (h = 0.17) for the combined formal
novice series, and 41.5% (h = 0.35) for the com-
bined experienced series. The last figure drops to
31.6% if the outlier series is removed. Finally,
without the outlier series the hit rate for the com-
bined series where all of the planned trials were
completed was 31.2% (h = 0.14), while it was 35%
(h = 0.22) for the combined series that were termi-
nated early. Thus, optional stopping cannot
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There were two interesting comparisons that had
been suggested by earlier work and were pre-
planned in these experiments. The first was to
compare results for trials with dynamic targets
with those for static targets. In the 190 dynamic
target sessions there were 77 direct hits (40%, h =
0.32) and for the static targets there were 45 hits
in 165 trials (27%, h = 0.05), thus indicating
that dynamic targets produced far more successful
results.
The second comparison of interest was whether
or not the sender was a friend of the receiver. This
was a choice the receiver could make. If he or she
did not bring a friend, a lab member acted as
sender. There were 211 trials with friends as
senders (some of whom were also lab staff), result-
ing in 76 direct hits (36%, h = 0.24). Four trials
used no sender. The remaining 140 trials used
nonfriend lab staff as senders and resulted in 46
direct hits (33%, h = 0.18). Thus, trials with friends
as senders were slightly more successful than those
without.
Consonant with the definition of replication based
on consistent effect sizes, it is informative to com-
pare the autoganzfeld experiments with the direct
hit studies in the previous data base. The overall
success rates are extremely similar. The overall
direct hit rate was 34.4% for the autoganzfeld stud-
ies and was 38% for the comparable direct hit
studies in the earlier meta-analysis. Rosenthal's
(1986) adjustment for flaws had placed a more con-
servative estimate at 33%, very close to the
observed 34.4% in the new studies.
One limitation of this work is that the auto-
ganzfeld studies, while conducted by eight experi-
menters, all used the same equipment in the same
laboratory. Unfortunately, the level of fund-
ing available in parapsychology and the cost in
time and equipment to conduct proper experiments
make it difficult to amass large amounts of data
across laboratories. Another autoganzfeld labora-
tory is currently being constructed at the Univer-
sity of Edinburgh in Scotland, so interlaboratory
comparisons may be possible in the near future.
Based on the effect size observed to date, large
samples are needed to achieve reasonable power. If
there is a constant effect across all trials, resulting
in 33% direct hits when 25% are expected by chance,
to achieve a one-tailed significance level of 0.05
with 95% probability would require 345 sessions.
We end this section by returning to the aspirin
and heart attack example in Section 3 and expand-
ing a comparison noted by Atkinson, Atkinson,
Smith and Bem (1990, page 237). Computing the
equivalent of Cohen's h for comparing obser-
ved heart90A1rbv"ett rt reaig 2M01b8Yi_
groups results in h = 0.068. Thus, the effect size
observed in the ganzfeld data base is triple the
much publicized effect of aspirin on heart attacks.
6. OTHER META-ANALYSES IN
PARAPSYCHOLOGY
Four additional meta-analyses have been con-
ducted in various areas of parapsychology since the
original ganzfeld me~a-analyses were reported.
Three of the four analyses focused on evidence of
psi abilities, while the fourth examined the rela-
tionship between extroversion and psychic func-
tioning. In this section, each of the four analyses
will be briefly summarized.
There are only a handful of English-language
journals and proceedings in parapsychology, so
retrieval of the relevant studies in each of the
four cases was simple to accomplish by searching
those sources in detail and by searching other
bibliographic data bases for keywords.
Each analysis included an overall summary, an
analysis of the quality of the studies versus the size
of the effect and a "file-drawer" analysis to deter-
mine the possible number of unreported studies.
Three of the four also contained comparisons across
various conditions.
6.1 Forced-Choice Pre9ognition Experiments
Honorton and Ferrari (1989) analyzed forced-
choice experiments conducted from 1935 to 1987, in
which the target material was randomly selected
after the subject had attempted to predict what it
would be. The time delay in selecting the target
ranged from under a !second to one year. Target
material included iterris as diverse as ESP cards
and automated random number generators. Two
investigators, S. G. Soal and Walter J. Levy, were
not included because gome of their work has been
suspected to be fraudulent.
Overall Results. There were 309 studies re-
ported by 62 senior atthors, including more than
50,000 subjects and nearly two million individual
trials. Honorton and Ferrari used z/,,I-n as the
measure of effect size (ES) for each study, where n
was the number of Bernoulli trials in the study.
They reported a mean ES of 0.020, and a mean
z-score of 0.65 over all studies. They also reported a
combined z of 11.41, p = 6.3 x 10 - 25. Some 30%
(92) of the studies were statistically significant at
a = 0.05. The mean ES per investigator was 0.033,
and the significant results were not due to just a
few investigators.
Quality. Eight dichotomous quality measures
CfAlp1 ig possible
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scores from zero for the lowest quality, to eight for
the highest. They included features such as ade-
quate randomization, preplanned analysis and au-
tomated recording of the results. The correlation
between study quality and effect size was 0.081,
indicating a slight tendency for higher quality
studies to be more successful, contrary to claims by
critics that the opposite would be true. There was
a clear relationship between quality and year of
publication, presumably because over the years
experimenters in parapsychology have responded
to suggestions from critics for improving their
methodology.
File Drawer. Following Rosenthal (1984), the
authors calculated the "fail-safe N" indicating the
number of unreported studies that would have to be
sitting in file drawers in order to negate the signifi-
cant effect. They found N = 14,268, or a ratio of 46
unreported studies for each one reported. They also
followed a suggestion by Dawes, Landman and
Williams (1984) and computed the mean z for all
studies with z > 1.65. If such studies were a ran-
dom sample from the upper 5% tail of a N(0,1)
distribution, the mean z would be 2.06. In this case
it was 3.61. They concluded that selective reporting
could not explain these results.
Comparisons. Four variables were identified
that appeared to have a systematic relationship to
study outcome. The first was that the 25 studies
using subjects selected on the basis of good past
performance were more successful than the 223
using unselected subjects, with mean effect sizes of
0.051 and 0.008, respectively. Second, the 97 stud-
ies testing subjects individually were more success-
ful than the 105 studies that used group testing;
mean effect sizes were 0.021 and 0.004, respec-
tively. Timing of feedback was the third moderat-
ing variable, but information was only available for
104 studies. The 15 studies that never told the
subjects what the targets were had a mean effect
size of -0.001. Feedback after each trial produced
the best results, the mean ES for the 47 studies
was 0.035. Feedback after each set of trials re-
sulted in mean ES of 0.023 (21 studies), while
delayed feedback (also 21 studies) yielded a mean
ES of only 0.009. There is a clear ordering; as the
gap between time of feedback and time of the
actual guesses decreased, effect sizes increased.
The fourth variable was the time interval be-
tween the subject's guess and the actual target
selection, available for 144 studies. The best results
were for the 31 studies that generated targets less
than a second after the guess (mean ES = 0.045),
while the worst were for the seven studies that
delayed target selection by at least a month (mean
trend, decreasing in order as the time interval
increased from minutes to hours to days to weeks to
months.
6.2 Attempts to Influence Random Physical
Systems
Radin and Nelson (1989) examined studies de-
signed to test the hypothesis that "The statistical
output of an electronic RNG [random number gen-
erator] is correlated with observer intention in ac-
cordance with prespecified instructions" (page
1502). These experiments typically involve RNGs
based on radioactive decay, electronic noise or pseu-
dorandom number sequences seeded with true ran-
dom sources. Usually the subject is instructed to
try to influence the results of a string of binary
trials by mental intention alone. A typical protocol
would ask a subject to press a button (thus starting
the collection of a fixed-length sequence of bits),
and then try to influence the random source to
produce more zeroes or more ones. A run might
consist of three successive button presses, one each
in which the desired result was more zeroes or
more ones, and one as a control with no conscious
intention. A z score would then be computed for
each button press.
The 832 studies in the analysis were conducted
from 1959 to 1987 and included 235 "control" stud-
ies, in which the output of the RNGs were recorded
but there was no conscious intention involved.
These were usually conducted before and during
the experimental series, as tests of the RNGs.
Results. The effect size measure used was again
z / Y W , where z was positive if more bits of the
specified type were achieved. The mean effect size
for control studies was not significantly different
from zero (-1.0 x 10-5). The mean effect size
for the experimental studies was also very small,
3.2 x 10-', but it was significantly higher than the
mean ES for the control studies (z = 4.1).
Quality. Sixteen quality measures were defined
and assigned to each study, under the four general
categories of procedures, statistics, data and the
RNG device. A score of 16 reflected the highest
quality. The authors regressed mean effect size on
mean quality for each investigator and found a
slope of 2.5 x 10-5 with standard error of 3.2 x
10 - 5, indicating little relationship between quality
and outcome. They also calculated a weighted mean
effect size, using quality scores as weights, and
found that it was very similar to the unweighted
mean ES. They concluded that "differences
in methodological quality are not significant
predictors of effect size" (page 1507).
File Drawer. Radin and Nelson used several
Cl e;khgc] JUU e ~ti tul Orlyp~ UU1-unreported
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studies (pages 1508-1510). Their estimates ranged
from 200 to 1000 based on models assuming
that all significant studies were reported. They
calculated the fail-safe N to be 54,000.
6.3 Attempts to Influence Dice
Radin and Ferrari (1991) examined 148 studies,
published from 1935 to 1987, designed to test
whether or not consciousness can influence the
results of tossing dice. They also found 31 "con-
trol" studies in which no conscious intention was
involved.
Results. The effect size measure used was
z / V, where z was based on the number of throws
in which the die landed with the desired face (or
faces) up, in n throws. The weighted mean ES for
the experimental studies was 0.0122 with a stan-
dard error of 0.00062; for the control studies the
mean and standard error were 0.00093 and 0.00255,
respectively. Weights for each study were de-
termined by quality, giving more weight to high-
quality studies. Combined z scores for the exper-
imental and control studies were reported by Radin
and Ferrari to be 18.2 and 0.18, respectively.
Quality. Eleven dichotomous quality measures
were assigned, ranging from automated recording
to whether or not control studies were interspersed
with the experimental studies. The final quality
score for each study combined these with informa-
tion on method of tossing the dice, and with source
of subject (defined below). A regression of quality
score versus effect size resulted in a slope of - 0.002,
with a standard error of 0.0011. However, when
effect sizes were weighted by sample size, there was
a significant relationship between quality and ef-
fect size, leading Radin and Ferrari to conclude
that higher-quality studies produced lower weighted
effect sizes.
File Drawer. Radin and Ferrari calculated
Rosenthal's fail-safe, N for this analysis to be
17,974. Using the assumption that all significant
studies were reported, they estimated the number
of unreported studies to be 1152. As a final assess-
ment, they compared studies published before and
after 1975, when the Journal of Parapsychology
adopted an official policy of publishing nonsigni-
ficant results. They concluded, based on that an-
alysis, that more nonsignificant studies were
published after 1975, and thus "We must consi-
der the overall (1935-1987) data base as suspect
with respect to the filedrawer problem."
Comparisons. Radin and Ferrari noted that
there was bias in both the experimental and control
studies across die face. Six was the face most likely
to come up, consistent with the observation that it
has the leas` V vdT&e 4sR4MSVa10'@6910'~/08
sults for the set of 69 studies in which targets
were evenly balanced among the six faces. They
still found a significant ;effect, with mean and stan-
dard error for effect size of 8.6 x 10 - 3 and 1.1 x
10-3, respectively. The combined z was 7.617 for
these studies.
They also compared effect sizes across types of
subjects used in the studies, categorizing them as
unselected, experimenter and other subjects, exper-
imenter as sole subject, and specially selected sub-
jects. Like Honorton and Ferrari (1989), they found
the highest mean ES for studies with selected
subjects; it was approxinpately 0.02, more than twice
that for unselected subjects.
6.4 Extroversion and ESP Performance
Honorton, Ferrari and Bem (1991) conducted a
meta-analysis to examine the relationship between
scores on tests of extroversion and scores on
psi-related tasks. They found 60 studies by 17
investigators, conducted! from 1945 to 1983.
Results. The effect size measure used for this
analysis was the correlation between each subject's
extroversion score and ESP score. A variety of
measures had been usedfor both scores across stud-
ies, so various correlation coefficients were used.
Nonetheless, a stem and leaf diagram of the corre-
lations showed an approximate bell shape with
mean and standard deviation of 0.19 and 0.26,
respectively, and with an additional outlier at r =
0.91. Honorton et al. reported that when weighted
by degrees of freedom, the weighted mean r was
0.14, with a 95% confidence interval covering 0.10
to 0.19.
Forced-Choice versus Free-Response Re-
sults. Because forced-choice and free-response tests
differ qualitatively, Honorton et al. chose to exam-
ine their relationship to extroversion separately.
They found that for free-response studies there was
a significant correlation, between extroversion and
ESP scores, with mean r = 0.20 and z = 4.46. Fur-
ther, this effect was homogeneous across both
investigators and extroversion scales.
For forced-choice studies, there was a significant
correlation between ESP; and extroversion, but only
for those studies that reported the ESP results
to the subjects before: measuring extroversion.
Honorton et al. speculated that the relationship
was an artifact, in which extroversion scores
were temporarily inflated as a result of positive
feedback on ESP performance.
Confirmation with New Data Following the
extroversion /ESP meta-analysis, Honorton et al.
attempted to confirm the relationship using
the autoganzfeld data base. Extroversion scores
based on the Myers-Briggs Type Indicator were
ClAlObP F-6678JFf0?ibceo jeo@1'o had
participated in autoganzfeld studies.
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The correlation between extroversion scores and
ganzfeld rating scores was r = 0.18, with a 95%
confidence interval from 0.05 to 0.30. This is con-
sistent with the mean correlation of r = 0.20 for
free-response experiments, determined from the
meta.-analysis. These correlations indicate that ex-
troverted subjects can produce higher scores in
free-response ESP tests.
much to be gained by discovering how to enhance
and apply these abilities to important world
problems.
I would like to thank Deborah Delanoy, Charles
Honorton, Wesley Johnson, Scott Plous and an
anonymous reviewer for their helpful comments on
an earlier draft of this paper, and Robert Rosenthal
and Charles Honorton for discussions that helped
clarify details.
Parapsychologists often make a distinction be-
tween "proof-oriented research" and "process-
oriented research." The former is typically con-
ducted to test the hypothesis that psi abilities exist,
while the latter is designed to answer questions
about; how psychic functioning works. Proof-
oriented research has dominated the literature
in parapsychology. Unfortunately, many of the
studies used small samples and would thus be
nonsignificant even if a moderate-sized effect
exists.
The recent focus on meta-analysis in parapsy-
chology has revealed that there are small but
consistently nonzero effects across studies, experi-
menters and laboratories. The sizes of the effects in
forced-choice studies appear to be comparable to
those reported in some medical studies that had
been heralded as breakthroughs. (See Section 5;
also Honorton and Ferrari, 1989, page 301.) Free-
response studies show effect sizes of far greater
magnitude.
A promising direction for future process-oriented
research is to examine the causes of individual
differences in psychic functioning. The ESP/ex-
troversion meta-analysis is a step in that direction.
In keeping with the idea of individual differ-
ences, Bayes and empirical Bayes methods would
appear to make more sense than the classical infer-
ence methods commonly used, since they would
allow individual abilities and beliefs to be modeled.
Jeffreys (1990) reported a Bayesian analysis of some
of the RNG experiments and showed that conclu-
sions were closely tied to prior beliefs even though
hundreds of thousands of trials were available.
It may be that the nonzero effects observed in the
meta-analyses can be explained by something other
than ESP, such as shortcomings in our understand-
ing of randomness and independence. Nonetheless,
there is an anomaly that needs an explanation. As
I have argued elsewhere (Utts, 1987), research in
parapsychology should receive more support from
the scientific community. If ESP does not exist,
there is little to be lost by erring in the direction of
further research, which may in fact uncover other
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Comment
M. J. Bayarri and James Berger
There are many fascinating issues discussed in
this paper. Several concern parapsychology itself
and the interpretation of statistical methodology
therein. We are not experts in parapsychology, and
so have only one comment concerning such mat-
ters: In Section 3 we briefly discuss the need to
switch from P-values to Bayes factors in discussing
evidence concerning parapsychology.
A more general issue raised in the paper is that
of replication. It is quite illuminating to consider
the issue of replication from a Bayesian perspec-
tive, and this is done in Section 2 of our discussion.
Many insightful observations concerning replica-
tion are given in the article, and these spurred us
to determine if they could be quantified within
Bayesian reasoning. Quantification requires clear
delineation of the possible purposes of replication,
and at least two are obvious. The first is simple
reduction of random error, achieved by obtaining
more observations from the replication. The second
purpose is to search for possible bias in the original
experiment. We use "bias" in a loose sense here, to
refer to any of the huge number of ways in which
the effects being measured by the experiment can
differ from the actual effects of interest. Thus a
clinical trial without a placebo can suffer a placebo
"bias"; a survey can suffer a "bias" due to the
sampling frame being unrepresentative of the
actual population; and possible sources of bias
in parapsychological experiments have been
extensively discussed.
Replication to Reduce Random Error
If the sole goal of replication of an experiment is
to reduce random error, matters are very straight-
forward. Reviewing the Bayesian way of studying
this issue is, however, useful and will be done
through the following simple example.
EXAMPLE 1. Consider the example from Tversky
and Kahnemann (1982), in which an experiment
results in a standardized test statistic of zl = 2.46.
(We will assume normality to keep computations
trivial.) The question is: What is the highest value
of z2 in a second set of data that would be consid-
ered a failure to replicate? Two possible precise
versions of this question are: Question 1: What is
the probability of observing z2 for which the null
hypothesis would be rejected in the replicated ex-
periment? Question 2: What value of z2 would
leave one's overall opinion about the null hypothe-
sis unchanged?
Consider the simple case where Zl - N(zl 0, 1)
and (independently) Z2 - N(z2 101 1), where 0 is
the mean and 1 is the standard deviation of the
normal distribution. Note that we are considering
the case in which no experimental bias is suspected
and so the means for each experiment are assumed
to be the same.
Suppose that it is desired to test Ho: 0 0 versus
Hl: 0 > 0, and suppose that initial prior opinion
about 0 can be described by the noninformative
prior a(0) = 1. We consider the one-sided testing
problem with a constant prior in this section, be-
cause it is known that then the posterior probabil-
ity of H0, to be denoted by P(Ho I data), equals the
P-value, allowing us to avoid complications arising
from differences between Bayesian and classical
answers.
After observing zl = 2.46, the posterior distribu-
tion of 0 is
7r(0 I z1) = N(0 12.46, 1).
Question 1 then has the answer (using predictive
Bayesian reasoning)
P(rejecting at level a I z1)
f00 1 e /22-0)27r(OI 7_) dO dz
1W ~/_27r
ca - 2.46
where CF is the standard normal cdf and ca is the
(one-sided) critical value corresponding to the level,
M. J. Bayarri is Titular Professor, Department of a, of the test. For instance, if a = 0.05, then this
Statistics and Operations Research, University of probability equals 0.7178, demonstrating that there
Valencia, Avenida Dr. Moliner 50, 46100 Burjassot, is a quite substantial probability that the second
Valencia, Spain. James Berger is the Richard M. experiment will fail to reject. If a is chosen to be
Brumfield Distinguished Professor of Statistics, the observed significance level from the first exper-
.*Iea9&,ZG0Qi1O8 : CIAeR0P9&00789ROO 1tG001( 0dk6 that the
Purdue uApj3 WQ EaCzR
 Approved For Release 2000/08/08 : CIA-RDP96-00789R003100010001-6
second experiment will reject is just 1/2. This is
nothing but a statement of the well-known martin-
gale property of Bayesianism, that what you "ex-
pect" to see in the future is just what you know
today. In a sense, therefore, question 1 is exposed
as being uninteresting.
Question 2 more properly focuses on the fact that
the stated goal of replication here is simply to
reduce uncertainty in stated conclusions. The an-
swer to the question follows immediately from not-
ing that the posterior from the combined data
(z1, z2) is
r(0 I z1, z2) = N(O I (zl + z2)/2, 1//),
P(Ho Idata) = (D (-(z1 + z2)/v"2-)?
Setting this equal to P(Ho I z1) and solving for z2
yields z2 = (v - 1)z1 = 1.02. Any value of z2
greater than this will increase the total evidence
against H0, while any value smaller than 1.02 will
decrease the evidence.
Replication to Detect Bias
The aspirin example dramatically raises the is-
sue of bias detection as a motive for replication.
Professor Utts observes that replication 1 gives
results that are fully compatible with those of the
original study, which could be interpreted as sug-
gesting that there is no bias in the original study,
while replication 2 would raise serious concerns of
bias. We became very interested in the implicit
suggestion that replication 2 would thus lead to
less overall evidence against the null hypothesis
than would replication 1, even though in isolation
replication 2 was much more "significant" than
was replication 1. In attempting to see if this is so,
we considered the Bayesian approach to study of
bias within the framework of the aspirin example.
EXAMPLE 2. For simplicity in the aspiring exam-
ple, we reduce consideration to
0 = true difference in heart attack rates between
Xi =
aspirin and placebo populations multiplied by
1000;
difference in observed heart attack rates be-
tween aspirin and placebo groups in original
study multiplied by 1000;
difference in observed heart attack rates be-
tween aspirin and placebo groups in Replica-
tion i multiplied by 1000.
one is very confident that the Xi have mean 0.
Using normal approximations for convenience, the
data can be summarized as
Xr - N(x110, 4.82), X2 - N(x2 10, 3.63)
with actual observations x1 = 7.704 and x2 =
13.07.
Consider now the bias issue. We assume that the
original experiment is, somewhat suspect in this
regard, and we will model bias by defining the
mean of Y to be
'1 0 + /3,
where 0 is the unknown bias. Then the data in the
original experiment can be summarized by
Y--N(y171,1.54),
with the actual observation being y = 7.707.
Bayesian analysis requires specification of a prior
distribution, r((3), for the suspected amount of bias.
Of particular interest then are the posterior distri-
bution of 0, assuming replication i has been
performed, given by
ir(i31 y, xi)
(( 1
a7r(1)exp1-2(1. 42+v2) ~a-(y-xi)]2
where vie is the variance (4.82 or 3.63) from repli-
cation i; and the posterior probability of H0, given
by
P(Ho I y, xi)
an ai
(b (Y
1.54 ci2 + 1.542
1.(i4
Xi 7r (a 1 y, xi) 0.
Qi v2 - 1.542
Recall that our goal here was to see if Bayesian
analysis can reproduce the intuition that the origi-
nal experiment could be trusted if replication 1 had
been done, while it could not be trusted (in spite of
its much larger sample !size) had replication 2 been
performed. Establishing this requires finding a
prior distribution r(f3) for which 7r(1 I y, x1) has
little effect on P(Ho I y x1), but Tr(/3I y, x2) has a
large effect on P(Ho I y, x2). To achieve the first
objective, 7r(1) must be tightly concentrated near
zero. To achieve the second, zr(/3) must be such that
large I y - x2 11 which suggests presence of a large
We assume that the replication studies are ex- bias, can result in a st bstantial shift of posterior
tremely well designed and implemented, so that mass for 0 away from zero.
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A sensible candidate for the prior density 7r(13)
is the Cauchy (0, V) density
TV[1 + (0/ V)2] .
1.54/100)). The effect of this is to essentially ignore
the original experiment in overall assessments of
evidence. For instance, P(H0 I y, x3) = 3.81 x
10-11, which is very close to P(H0 I x3) = 3.29 x
10-11. Note that, if 0 were set equal to zero, the
overall posterior probability of Ho (and P-value)
would be 2.62 x 10-13.
Thus Bayesian reasoning can reproduce the intu-
ition that replication which indicates bias can cast
considerable doubt on the original experiment,
while replication which provides no evidence of
bias leaves evidence from the original experiment
intact. Such behavior seems only obtainable, how-
ever, with flat-tailed priors for bias (such as the
Cauchy) that are very concentrated (in comparison
with the experimental standard deviation) near
zero.
Flat-tailed densities, such as this, are well known
to have the property that when discordant data is
observed (e.g., when (I y - x2 1 is large), substan-
tial mass shifts away from the prior center towards
the likelihood center. It is easy to see that a normal
prior for 0 can not have the desired behavior.
Our first surprise in consideration of these priors
was how small V needed to be chosen in order for
P(Ho I y, x1) to be unaffected by the bias. For
instance, even with V = 1.54/100 (recall that 1.54
was the standard deviation of Y from the original
experiment), computation yields P(H0I y, x1) =
4.3 x 10-5, compared with the P-value (and poste-
rior probability from the original experiment as-
suming no bias) of 2.8 x 10'. There is a clear
lesson here; even very small suspicions of bias can
drastically alter a small P-value. Note that replica-
tion 1 is very consistent with the presence of no
bias, and so the posterior distribution for the bias
remains tightly concentrated near zero; for in-
stance, the mean of the posterior for 0 is then
7.2 x 10-6 , and the standard deviation is 0.25.
When we turned attention to replication 2, we
found that it did not seriously change the prior
perceptions of bias. Examination quickly revealed
the reason; even the maximum likelihood estimate
of the bias is no more than 1.4 standard deviations
from zero, which is not enough to change strong
prior beliefs. We, therefore, considered a third
experiment, defined in Table 1. Transforming to
approximate normality, as before, yields
X3 --- N(x3 1 0 , 3.48),
with x3 = 22.72 being the actual observation. The
maximum likelihood estimate of bias is now 3.95
standard deviations from zero, so there is potential
for a substantial change in opinion about the bias.
Sure enough, computation when V = 1.54/100
yields that E[l31 y, x3] = -4.9 with (posterior)
standard deviation equal to 6.62, which is a dra-
matic shift from prior opinion (that 0 is Cauchy (0,
TABLE 1
Frequency of heart attacks in replication 3
Aspirin
Placebo
Parapsychology experiments usually consider
testing of Ho: No parapsychological effect exists.
Such null hypotheses are often realistically repre-
sented as point nulls (see Berger and Delampady,
1987, for the reason that care must be taken in
such representation), in which case it is known that
there is a large difference between P-values and
posterior probabilities (see Berger and Delampady,
1987, for review). The article by Jefferys (1990)
dramatically illustrates this, showing that a very
small P-value can actually correspond to evidence
for Ho when considered from a Bayesian perspec-
tive. (This is very related to the famous "Jeffreys"
paradox.) The argument in favor of the Bayesian
approach here is very strong, since it can be shown
that the conflict holds for virtually any sensible
prior distribution; a Bayesian answer can be wrong
if the prior information turns out to be inaccurate,
but a Bayesian answer that holds for all sensible
priors is unassailable.
Since P-values simply cannot be viewed as mean-
ingful in these situations, we found it of interest to
reconsider the example in Section 5 from a Bayes
factor perspective. We considered only analysis of
the overall totals, that is, x = 122 successes out of
n = 355 trials. Assuming a simple Bernoulli trial
model with success probability 0, the goal is to test
Ho:O = 1 /4 versus H1:0 # 1/4.
To determine the Bayes factor here, one must
specify g(0), the conditional prior density on H1.
Consider choosing g to be uniform and symmetric,
that is,
Yes No 1 1 1
G,(0) = 2r' for 4 - rs0 s 4 +r,
5 2309
54 2116 to, otherwise.
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Crudely, r could be considered to be the maximum
change in success probability that one would expect
given that ESP exists. Also, these distributions are
the "extreme points" over the class of symmetric
unimodal conditional densities, so answers that hold
over this class are also representative of answers
over a much larger class. Note that here r s 0.25
(because 0 0.5
are essentially irrelevant, but if it were deemed
important to take them into account one could use
the more sophisticated binomial analysis in Berger
and Delampady (1987).
For g, the Bayes factor of H1 to H0, which is to
be interpreted as the relative odds for the hypothe-
ses provided by the data, is given by
(1/(2r))1..25+re122(1 - 0) 355-122 dO
25-r
(1/4)122(1 - 1/4) 355-122
(63.13)
11
[t r - .0937 (r + .0937)
( .0252 , + ( .0252
This is graphed in Figure 1.
The P-value for this problem was 0.00005, indi-
cating overwhelming evidence against H. from a
classical perspective. In contrast to the situation
studied by Jefferys (1990), the Bayes factor here
does not completely reverse the conclusion, show-
ing that there are very reasonable values of r for
which the evidence against Ho is moderately
strong, for example 100/1 or 200/1. Of course, this
evidence is probably not of sufficient strength to
overcome strong prior opinions against H. (one
Comment
I
0.05 0.1 0.15 0.2 0.25
FIG. 1. The Bayes factor of H1 to Ho as a function of r, the
maximum change in success probability that is expected given
that ESP exists, for the ganzfeld experiment.
obtains final posterior odds by multiplying prior
odds by the Bayes factor). To properly assess
strength of evidence, we feel that such Bayes factor
computations should become standard in parapsy-
chology.
As mentioned by Professor Utts, Bayesian meth-
ods have additional potential in situations such as
this, by allowing unrealistic models of iid trials to
be replaced by hierarchical models reflecting differ-
ing abilities among subjects.
ACKNOWLEDGMENTS
M. J. Bayarri's research was supported in part
by the Spanish Ministry of Education and Science
under DGICYT Grant BE91-038, while visiting
Purdue University. James Berger's research was
supported by NSF Grant DMS-89-23071.
This paper offers readers interested in statistical account of how both design and inferential aspects
science multiple views of the controversial history of statistics have been pivotal issues in evaluating
of parapsychology and how statistics has con- the outcomes of experiments that study psi abili-
tributed to its development. It first provides an ties. It then emphasizes how the idea of science as
replication has been key in this field in which
results have not been; conclusive or consistent and
thus meta-analysis has been at the heart of the
Ree Dawson is Senior Statistician, New England literature in parapsychology. The author not only
Biomedical Research Foundation, and Statistical reviews past debate on how to interpret repeated
Consultant, RFE/RL Research Institute. Her mail- psi studies, but also provides very detailed informa-
ing address is 177 Morrison Avenue, Somerville, tion on the Honorton-Hyman argument, a nice
Massachusetts 02144. illustration of the challenges of resolving such de-
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REPLICATION IN PARAPSYCHOLOGY
bate., This debate is also a good example of how
statistical criticism can be part of the scientific
process and lead to better experiments and, in gen-
eral, better science.
The remainder of the paper addresses technical
issues of meta-analysis, drawing upon recent re-
search in parapsychology for an in-depth applica-
tion. Through a series of examples, the author
presents a convincing argument that power issues
cannot be overlooked in successive replications and
that comparison of effect sizes provides a richer
alternative to the dichotomous measure inherent in
the use of p-values. This is particularly relevant
when the potential effect size is small and re-
sources are limited, as seems to be the case for psi
studies.
The concluding section briefly mentions Bayesian
techniques. As noted by the author, Bayes (or em-
pirical Bayes) methodology seems to make sense for
research in parapsychology. This discussion exam-
ines possible Bayesian approaches to meta-analysis
in this field.
BAYES MODELS FOR PARAPSYCHOLOGY
The notion of repeatability maps well into the
Bayesian set-up in which experiments, viewed as a
random sample from some superpopulation of ex-
periments, are assumed to be exchangeable. When
subjects can also be viewed as an approximately
random sample from some population, it is appro-
priate to pool them across experiments. Otherwise,
analyses that partially pool information according
to experimental heterogeneity need to be consid-
ered.. Empirical and hierarchical Bayes methods
offer a flexible modeling framework for such analy-
ses, relying on empirical or subjective sources to
determine the degree of pooling. These richer meth-
ods can be particularly useful to meta-analysis of
experiments in parapsychology conducted under
potentially diverse conditions.
For the recent ganzfeld series, assuming them
to be independent binomially distributed as dis-
cussed in Section 5, the data can be summed
(pooled) across series to estimate a common hit
rate. Honorton et al. (1990) assessed the homogene-
ity of effects across the 11 series using a chi-square
test that compares individual effect sizes to
the weighted mean effect. The chi-square statistic
Xio -= 16.25, not statistically significant (p =
0.093), largely reflects the contribution of the last
"special" series (contributes 9.2 units to the Xio
value), and to a lesser extent the novice series with
a negative effect (contributes 2.5 units). The outlier
series can be dropped from the analysis to provide a
more conservative estimate of the presence of psi
effects for this data (this result is reported in Sec-
tion 5). For the remaining 10 series, the chi-square
value x' 9 7.01 strongly favors homogeneity, al-
though more than one-third of its value is due to
the novice series (number 4 in Table 1). This pat-
tern points to the potential usefulness of a richer
model to accommodate series that may be distinct
from the others. For the earlier ganzfeld data ana-
lyzed by Honorton (1985b), the appeal of a Bayes or
other model that recognizes the heterogeneity
across studies is clear cut: Xzs = 56.6, p = 0.0001,
where only those studies with common chance hit
rate have been included (see Table 2).
Historic reliance on voting-count approaches to
determine the presence of psi effects makes it natu-
ral to consider Bayes models that focus on the
ensemble of experimental effects from parapsycho-
logical studies, rather than individual estimates.
Recent work in parapsychology that compares ef-
fect sizes across studies, rather than estimating
separate study effects, reinforces the need to exam-
ine this type of model. Louis (1984) develops Bayes
and empirical Bayes methods for problems that
consider the ensemble of parameter values to be
the primary goal, for example, multiple compar-
isons. For the simple compound normal model,
Yt - N(01, 1), 0i - N(?, r2), the standard Bayes
estimates (posterior means)
2
0*=?+D(Y1- t) and D= 1+T2
where the 0i represent experimental effects of in-
terest, are modified approximately to
01 =?+ /D(Y,-?)
when an ensemble loss function is assumed. The
new estimates adjust the shrinkage factor D so
that their sample mean and variance match the
posterior expectation and variance of the 0's. Simi-
lar results are obtained when the model is gener-
TABLE 1
Recent ganzfeld series
Pilot
22
0.36
-0.58
0.44
Pilot
9
0.33
-0.71
0.71
Pilot
36
0.28
-0.94
0.37
Novice
50
0.24
-1.15
0.33
Novice
50
0.36
-0.58
0.30
Novice
50
0.30
-0.85
0.31
Novice
50
0.36
-0.58
0.30
Novice
6
0.67
0.71
0.87
Experienced
7
0.43
-0.28
0.76
Experienced
50
0.30
-0.85
0.31
Experienced
25
0.64
0.58
0.42
Overall
355
0.34
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384 J. UTTS
TABLE 2
Earlier ganzfeld studies
vides more convincing Oupport that all 0i > --1.10,
although posterior estimates of uncertainty are
needed to fully calibitate this. For the earlier
ganzfeld data in Table 2, ensemble loss can simi-
larly be used to determine the number of studies
with Oi < -1.10 and specifically whether the nega-
tive effects of studies 4 and 24 (Y4 = -1.21
and Y24 = -1.33) occujrred as a result of chance
fluctuation.
Features of the ganzfeld data in Section 5, such
as the outlier series, suggest that further elabora-
tion of the basic Bayesian set-up may be necessary
for some meta-analyses' in parapsychology. Hierar-
chical models provide a natural framework to spec-
ify these elaborations' and explore how results
change with the prior specification. This type of
sensitivity analysis can expose whether conclusions
are closely tied to prior beliefs, as observed by
Jeffreys for RNG data (see Section 7). Quantifying
the influence of model components deemed to be
more subjective or less certain is important to broad
acceptance of results as evidence of psi performance
(or lack thereof).
Consider the initial model commonly used for
Bayesian analysis of discrete data:
Yi I pi, ni - B(pi, ni),
Bi - N(?, T2)', Oi = logit(pi),
with noninformative priors assumed for ? and r2
(e.g., log r locally uniform). The distinctiveness of
the last "special" serie and, in general, the differ-
ent types of series (pilot versus formal, novice ver-
sus experienced) raises he question of whether the
experimental effects follow a normal distribution.
Weighted normal plots (Ryan and Dempster, 1984)
can be used to graphically diagnose the adequacy of
second-stage normality (see Dempster, Selwyn and
Weeks, 1983, for examples with binary response
and normal superpopulation).
Alternatively, if noniliormality is suspected, the
model can be revised to include some sort of heavy-
tailed prior to accommodate possibly outlying se-
ries or studies. West (1985) incorporates additional
scale parameters, one for each component of the
model (experiment), that flexibly adapt to a typi-
cal Oi and discount their influence on posterior
estimates, thus avoiding under- or over-shrinkage
due to such Oi. For example, the second stage
can specify the prior as 4 scale mixture of normals:
32 0.44 -0.24 0.36
7 0.86 1.82 1.09
30 0.43 -0.28 0.37
30 0.23 -1.21 0.43
20 0.10 -2.20 0.75
10 0.90 2.20 1.05
10 0.40 -0.41 0.65
28 0.29 -0.90 0.42
10 0.40 -0.41 0.65
20 0.35 -0.62 0.47
26 0.31 -0.80 0.42
20 0.45 -0.20 0.45
20 0.45 -0.20 0.45
30 0.53 0.12 0.37
36 0.33 -0.71 0.35
32 0.28 -0.94 0.39
40 0.28 -0.94 0.35
26 0.46 -0.16 0.39
20 0.60 0.41 0.46
100 0.41 -0.36 0.20
40 0,33 -0.71 0.34
27 0.41 -0.36 0.39
60 0.45 -0.20 0.26
48 0.21 -1.33 0.35
722 .38
alized to
N(0i, oi2).
unequal variances, Yi --
For the above model, the fraction of of above (or
below) a cut point C is a consistent estimate of the
fraction of 0i > C (or Oi < C). Thus; the use of
ensemble, rather than component-wise, loss can
help detect when individual effects are above
a specified threshold by chance. For the meta-
analysis of ganzfeld experiments, the observed bi-
nomial proportions transformed on the logit (or
aresin,/) scale can be modeled in this framework.
Letting di and mi denote the number of direct hits
and misses respectively for the ith experiment, and
pi as the corresponding population proportion of
direct hits, the Yi are the observed logits
Yi = log(di/mi)
and oil, estimated by maximum likelihood as
1/d i + 1/mi, is the variance of Yi conditional on
Oi = logit(pi). The threshold logit (0.25) = 1.10 can
be used to identify the number of experiments for
which the proportion of direct hits exceeds that
expected by chance.
Table 1 shows Yi and of for the 11 ganzfeld
series. All but one of the series are well above the
threshold; Y4 marginally falls below -1.10. Any
shrinkage toward a common hit rate will lead to an
estimate, 04* or 04, above the threshold. The use of
ensemble loss (with its consistency property) pro-
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REPLICATION IN PARAPSYCHOLOGY 385
maximum likelihood estimation that modify the
sampling error distribution to yield estimates that
are "robust" against outlying observations.
Like its maximum likelihood counterparts, in ad-
dition to the robust effect estimates 0,*, the Bayes
model provides (posterior) scale estimates -y7. These
can be interpreted as the weight given to the data
for each 0i in the analysis and are useful to diag-
nosing which model components (series or studies)
are unusual and how they influence the shrinkage.
When more complex groupings among the 0, are
suspected, for example, bimodal distribution of
studies from different sites or experimenters, other
mixture specifications can be used to further relax
the shrinkage toward a common value.
For the 11 ganzfeld series, the last "outlier"
series;, quite distinct from the others (hit rate =
0.64), is moderately precise (N = 25). Omitting it
from the analysis causes the overall hit rate to drop
from 0.344 to 0.321. The scale mixture model is a
compromise between these two values (on the logit
scale), discounting the influence of series 11 on the
estimated posterior common hit rate used for
shrinkage. The scale factor y*i, an indication of
how separate 01, is from the other parameters, also
causes 011 to be shrunk less toward the common hit
rate than other, more homogeneous Oi, giving more
weight to individual information for that series (see
West, 1985). The heterogeneity of the earlier
ganzfeld data is more pronounced, and studies are
taken from a variety of sources over time. For these
data, the ry,* can be used to explore atypical studies
(e.g., study 6, with hit rate = 0.90, contributes more
than 25% to the X23 value for homogeneity) and
groupings among effects, as well as protect the
analysis from misspecification of second-stage
normality.
Variation among ganzfeld series or studies and
the degree to which pooling or shrinking is appro-
priate can be investigated further by considering a
range of priors for r2. If the marginal likelihood of
T2 dominates the prior specification, then results
should not vary as the prior for T2 is varied. Other-
wise, it is important to identify the degree to which
subjective information about interexperimental
variability influences the conclusions. This sen-
sitivity analysis is a Bayesian enrichment of
the simpler test of homogeneity directed toward
determining whether or not complete pooling is
appropriate.
To assess how well heterogeneity among his-
torical control groups is determined by the data.
Dempster, Selwyn and Weeks (1983) propose three
priors for r2 in the logistic-normal model. The prior
distributions range from strongly favoring individ-
ual estimates, p(T2)dr oc r-1, to the uniform refer-
ence prior p(T2)dT < r-2, flat on the log r scale, to
strongly favoring complete pooling, p(T2)dr a T_3
(the latter forcing complete pooling for the com-
pound normal model; see Morris, 1983). For their
two examples, the results (estimates of linear treat-
ment effects) are largely insensitive to variation in
the prior distribution, but the number of studies in
each example was large (70 and 19 studies avail-
able for pooling). For the 11 ganzfeld series, r2 may
be less well determined by the data. The posterior
estimate of r2 and its sensitivity to p(T2)dr will
also depend on whether individual scale parame-
ters are incorporated into the model. Discounting
the influence of the last series will both shift the
marginal likelihood toward smaller values of r2
and concentrate it more in that region.
The issue of objective assessment of experiment
results is one that extends well beyond the field of
parapsychology, and this paper provides insight into
issues surrounding the analysis and interpretation
of small effects from related studies. Bayes meth-
ods can contribute to such meta-analyses in two
ways. They permit experimental and subjective evi-
dence to be formally combined to determine the
presence or absence of effects that are not clear cut
or. controversial (e.g., psi abilities). They can also
help uncover sources and degree of uncertainty in
the scientific conclusions.
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Comment
In my experience, parapsychologists use statis-
tics extremely carefully. The plethora of widely
significant p-values in the many thousands of pub-
lished parapsychological studies must give us pause
for thought. Either something spooky is going on,
or it is possible for a field to exist on error and
artifact for over 100 years. The present paper offers
a useful review by an expert and a glimpse at some
tantalizing new studies.
My reaction is that the studies are crucially
flawed. Since my reasons are somewhat unusual, I
will try to spell them out.
I have found it impossible to usefully judge what
actually went on in a parapsychology trial from
their published record. Time after time, skeptics
have gone to watch trials and found subtle and
not-so-subtle errors. Since the field has so far failed
to produce a replicable phenomena, it seems to
me that any trial that asks us to take its find-
ings seriously should include full participation by
qualified skeptics. Without a magician and/or
knowledgeable psychologist skilled at running ex-
periments with human subjects, I don't think a
serious effort is being made.
I recognize that this is an unorthodox set of
requirements. In fact, one cannot judge what
"really goes on" in studies in most areas, and it is
Persi Diaconis is Professor of Mathematics at Har-
vard University, Science Center, 1 Oxford Street,
Cambridge, Massachusetts 02138.
impossible to demand wide replicability in others.
Finally, defining "qualified skeptic" is difficult. In
defense, most areas have many easily replicable
experiments and many have their findings ex-
plained and connected by unifying theories. It sim-
ply seems clear that wien making claims at such
extraordinary variance' with our daily experience,
claims that have been made and washed away so
often in the past, such extraordinary measures are
mandatory before one has the right to ask outsiders
to spend their time in review. The papers cited in
Section 5 do not actively involve qualified skeptics,
and I do not feel they have earned the right to our
serious attention.
The points I have made above are not new. Many
appear in the present article. This does not dimin-
ish their utility nor applicability to the most recent
studies.
Parapsychology is worth serious study. First,
there may be something there, and I marvel at the
patience and drive of people like Jessica Utts and
Ray Hyman. Second, if it is wrong, it offers a truly
alarming massive case study of how statistics can
mislead and be misused. Third, it offers marvelous
combinatorial and inferential problems. Chung,
Diaconis, Graham and. Mallows (1981), Diaconis
and Graham (1981) and Samaniego and Utts
(1983) offer examples not cited in the text. Finally,
our budding statistics students are fascinated by its
claims; the present paper gives a responsible
overview providing background for a spectacular
classroom presentation.
Comment: Parapsychology -On the Margins
of Science?
Professor Utts reviews and synthesizes a large lish the existence of paranormal phenomena. The
body of experimental literature as well as the scien- organization and clarity of her presentation are
tific controversy involved in the attempt to estab- noteworthy. Although ][ do not believe that this
paper will necessarily Change anyone's views re-
garding the existence ofparanormal phenomena, it
does raise very interestitig questions about the pro-
Joel B. Greenhouse is Associate Professor of Statis- cess by which new ideas are either accepted or
tics, Carnegie Mellon University, Pittsburgh, Penn- rejected by the scientific community. As students of
sylvania 1 521 3-3890. science, we believe that scientific discovery
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advances methodically and objectively through the
accumulation of knowledge (or the rejection of false
knowledge) derived from the implementation of the
scientific method. But, as we will see, there is more
to the acceptance of new scientific discoveries than
the systematic accumulation and evaluation of
facts. The recognition that there is a social process
involved with the acceptance or rejection of scien-
tific knowledge has been the subject of study of
sociologists for some time. The scientific commu-
nity's rejection of the existence of paranormal phe-
nomena is an excellent case study of this process
(Allison, 1979; Collins and Pinch, 1979).
Implicit in Professor Utts' presentation and
paramount to the acceptance of parapsychology as
a legitimate science are the description and docu-
mentation of the professionalization of the field of
parapsychology. It is true that many researchers in
the field have university appointments; there are
organized professional societies for the advance-
ment of parapsychology; there are journals with
rigorous standards for published research; the field
has received funding from federal agencies; and
parapsychology has received recognition from other
professional societies, such as the IMS and the
American Association for the Advancement of Sci-
ence (Collins and Pinch, 1979). Nevertheless, most
readers of Statistical Science would agree that
parapsychology is not accepted as part of orthodox
science and is considered by most of the scientific
community to be on the margins of science, at best
(Allison, 1979; Collins and Pinch, 1979). Why is
this the case? Professor Utts believes that it is
because people have not examined the data. She
states that "Strong beliefs tend to be resistant to
change even in the face of data, and many people,
scientists included, seem to have made up their
minds on the question without examining any em-
pirical data at all."
The history of science is replete with examples of
resistance by the established scientific community
to new discoveries. A challenging problem for sci-
ence is to understand the process by which a new
theory or discovery becomes accepted by the com-
munity of scientists and, likewise, to characterize
the nature of the resistance to new ideas. Barber
(1961) suggests that there are many different
sources of resistance to scientific discovery. In 1900,
for example, Karl Pearson met resistance to his use
of statistics in applications to biological problems,
illustrating a source of resistance due to the use of
a particular methodology. The Royal Society in-
formed Pearson that future papers submitted to the
Society for publication must keep the mathematics
separate from the biological applications.
entific ideas, and the one referred to by Professor
Utts above, is the prevailing substantive beliefs
and theories held by scientists at any given time.
Barber offers the opposition to Copernicus and his
heliocentric theory and to Mendel's theory of ge-
netic inheritance as examples of how, because of
preconceived ideas, theories and values, scientists
are not as open-minded to new advances as one
might think they should be. It was R. A. Fisher
who said that each generation seems to have found
in Mendel's paper only what it expected to find and
ignored what did not conform to its own expecta-
tions (Fisher, 1936).
Pearson's response to the antimathematical prej-
udice expressed by the Royal Society was to estab-
lish with Galton's support a new journal,
Biometrika, to encourage the use of mathematics in
biology. Galton (1901) wrote an article for the first
issue of the journal, explaining the need for this
new voice of "mutual encouragement and support"
for mathematics in biology and saying that "a new
science cannot depend on a welcome from the fol-
lowers of the older ones, and [therefore] ... it is
advisable to establish a special Journal for Biome-
try." Lavoisier understood the role of preconceived
beliefs as a source of resistance when he wrote in
1785,
I do not expect my ideas to be adopted all at
once. The human mind gets creased into a way
of seeing things. Those who have envisaged
nature according to a certain point of view
during much of their career, rise only with
difficulty to new ideas. (Barber, 1961.)
I suspect that this paper by Professor Utts syn-
thesizing the accumulation of research results sup-
porting the existence of paranormal phenomena
will continue to be received with skepticism by the
orthodox scientific community "even after examin-
ing the data." In part, this resistance is due to the
popular perception of the association between para-
psychology and the occult (Allison, 1979) and due
to the continued suspicion and documentation of
fraud in parapsychology (Diaconis, 1978). An addi-
tional and important source of resistance to the
evidence presented by Professor Utts, however, is
the lack of a model to explain the phenomena.
Psychic phenomena are unexplainable by any cur-
rent scientific theory and, furthermore, directly
contradict the laws of physics. Acceptance of psi
implies the rejection of a large body of accumulated
evidence explaining the physical and biological
world as we know it. Thus, even though the effect
size for a relationship between aspirin and the
prevention of heart attacks is three times smaller
A:noth r obvious source f esistan to new sci- than the effect size observed in the anzfeld data
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388 J. UTTS
base, it is the existence of a biological mechanism tions about the role of publication bias. Publication
to explain the effectiveness of aspirin that ac- bias or "the file-drawer problem" arises when only
counts, in part, for acceptance of this relationship. statistically significant findings get published,
In evaluating the evidence in favor of the exis- while statistically nonsignificant studies sit unre-
tence of paranormal phenomena, it is necessary to ported in investigators' file drawers. Typically,
consider alternative explanations or hypotheses for Rosenthal's method (1079) is used tQ calculate the
the results and, as noted by Cornfield (1959), "If "fail-safe N," that is,l the number of unreported
important alternative hypotheses are compatible studies that would have to be sitting in file-drawers
with available evidence, then the question is unset- in order to negate the significant effect. Iyengar
tled, even if the evidence is experimental" (see and Greenhouse (1988) describe a modification of
also Platt, 1964). Many of the experimental results Rosenthal's method, however, that gives a fail-safe
reported by Professor Utts need to be considered in N that is often an order .of magnitude smaller than
the context of explanations other than the exist- Rosenthal's method, suggesting that the sensitivity
ence of paranormal phenomena. Consider the of the results of meta-analyses of psi experiments to
following examples: unpublished negative studies is greater than is
(1) In the various psi experiments that Professor
Utts discusses, the null hypothesis is a simple
chance model. However, as noted by Diaconis (1978)
in a critique of parapsychological research, "In
complex, badly controlled experiments simple
chance models cannot be seriously considered as
tenable explanations: hence, rejection of such mod-
els is not of particular interest." Diaconis shows
that the underlying probabilistic model in many of
these experiments (even those that are well con-
trolled) is much more complicated than chance.
(2) The role that experimenter expectancy plays
in the reporting and interpreting of results cannot
be underestimated. Rosenthal (1966), based on a
currently believed.
Even if parapsychology is thought to be on the
margins of science by the scientific community,
parapsychologists should not be held to a different
standard of evidence to support their findings than
orthodox scientists, but like other scientists they
must be concerned with spurious effects and the
effects of extraneous variables. The experimental
results summarized by !Professor Utts appear to be
sensitive to the effect of alternative hypotheses like
the ones described above. Sensitivity analyses,
which question, for example, how large of an effect
due to experimenter expectancy theme would have
to be to account for the effect sizes being reported
meta-analysis of the effects of experimenters' ex- in the psi experiments, are not a dressed here.
pectancies on the results of their research, found Again, the ability to account for an eliminate the
that experimenters tended to get the results they role of alternative hypotheses in xplaining the
expected to get. Clearly this is an important po- observed relationship between aspiri and the pre-
tential confounder in parapsychological research. vention of heart attacks is another reason for the
Professor Utts comments on a debate between acceptance of these results.
Honorton and Hyman, parapsychologist and critic, A major new technology discussed by Professor
respectively, regarding evidence for psi abili- Utts in synthesizing the experimental parapsychol-
ties, and, although not necessarily a result of ex- ogy literature is meta-analysis. Until recently, the
perimenter expectancy, describes how "... each quantitative review and synthesis of a research
analyzed the results of all known psi ganzfeld literature, that is, meta-analysis, was considered by
experiments to date, and reached strikingly differ- many to be a questionable research (tool (Wachter,
ent conclusions." 1988). Resistance by statisticians to; meta-analysis
(3) What is an acceptable response in these ex- is interesting because,, historically,', many promi-
periments? What constitutes a direct hit? What if nent statisticians found the combining of informa-
the response is close, who decides whether or not tion from independent studies to be an important
that constitutes a hit (see (2) above)? In an example and useful methodology (see, e.g., Fisher, 1932;
of a response of a Receiver in an automated ganzfeld Cochran, 1954; Mosteller and Bush, 1954; Mantel
procedure, Professor Utts describes the "dream-like and Haenszel, 1959). Perhaps the more recent skep-
quality of the mentation." Someone must evaluate ticism about meta-analysis is because' of its use as a
these stream-of-consciousness responses to deter- tool to advance discoveries that th mselves were
mine what is a hit. An important methodological the objects of resistance, such as the efficacy of
question is: How sensitive are the results to differ- psychotherapy (Smith and Glass, 1977) and now
ent definitions of a hit? the existence of paranormal phenomena. It is an
(4) In describing the results of different meta- interesting problem for the history of science to
analyses, Professor Utts is careful to raise ues- explore why and when in the dev to ment of a
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of a discipline it turns to meta-analysis to answer
research questions or to resolve controversy (e.g.,
Greenhouse et al., 1990).
One argument for combining information from
different studies is that a more powerful result can
be obtained than from a single study. This objective
is implicit in the use of meta-analysis in parapsy-
chology and is the force behind Professor Utts'
paper. The issue is that by combining many small
studies consisting of small effects there is a gain in
power to find an overall statistically significant
effect. It is true that the meta-analyses reported by
Professor Utts find extremely small p-values, but
the estimate of the overall effect size is still small.
As noted earlier, because of the small magnitude of
the overall effect size, the possibility that other
extraneous variables might account for the rela-
tionship remains.
Professor Utts, however, also illustrates the use
of meta-analysis to investigate how studies differ
and to characterize the influence of difficult covari-
ates or moderating variables on the combined esti-
mate of effect size. For example, she compares the
mean effect size of studies where subjects were
selected on the basis of good past performance to
studies where the subjects were unselected, and she
compares the mean effect size of studies with feed-
back to studies without feedback. To me, this latter
use of meta-analysis highlights the more valuable
and important contribution of the methodology.
Specifically, the value of quantitative methods for
Comment
Ray Hyman
Utts concludes that "there is an anomaly that
needs explanation." She bases this conclusion on
the ganzfeld experiments and four meta-analyses of
parapsychological studies. She argues that both
Honorton and Rosenthal have successfully refuted
my critique of the ganzfeld experiments. The meta-
analyses apparently show effects that cannot be
explained away by unreported experiments nor
over-analysis of the data. Furthermore, effect size
does not correlate with the rated quality of the
experiment.
research synthesis is in assessing the potential ef-
fects of study characteristics and to quantify the
sources of heterogeneity in a research domain, that
is, to study systematically the effects of extraneous
variables. Tom Chalmers and his group at Harvard
have used meta-analysis in just this way not only
to advance the understanding of the effectiveness of
medical therapies but also to study the characteris-
tics of good research in medicine, in particular, the
randomized controlled clinical trial. (See Mosteller
and Chalmers, 1991, for a review of this work.)
Professor Utts should be congratulated for her
courage in contributing her time and statistical
expertise to a field struggling on the margins of
science, and for her skill in synthesizing a large
body of experimental literature. I have found her
paper to be quite stimulating, raising many inter-
esting issues about how science progresses or does
not progress.
This work was supported in part by MHCRC
grant MH30915 and MH15758 from the National
Institute of Mental Health, and CA54852 from the
National Cancer Institute. I would like to acknowl-
edge stimulating discussions with Professors Larry
Hedges, Michael Meyer, Ingram Olkin, Teddy
Seidenfeld and Larry Wasserman, and thank them
for their patience and encouragement while prepar-
ing this discussion.
Neither time nor space is available to respond in
detail to her argument. Instead, I will point to
some of my concerns. I will do so by focusing on
those parts of Utts' discussion that involve me.
Understandably, I disagree with her assertions that
both Honorton and Rosenthal successfully refuted
my criticisms of the ganzfeld experiments.
Her treatment of both the ganzfeld debate and
the National Research Council's report suggests
that Utts has relied on second-hand reports of the
data. Some of her statements are simply inaccu-
rate. Others suggest that she has not carefully read
what my critics and I have written. This remote-
ness from the actual experiments and details of the
Ray Hyman is Professor of Psychology, University of arguments may partially account for her optimistic
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the reported data at face value and focuses on
the statistical interpretation of these data.
Both the statistical interpretation of the results
of an individual experiment and of the results of a
meta-analysis are based on a model of an ideal
world. In this ideal world, effect sizes have a
tractable and known distribution and the points in
the sample space are independent samples from a
coherent population. The appropriateness of any
statistical application in a given context is an em-
pirical matter. That is why such issues as the
adequacy of randomization, the non-independence
of experiments in a meta-analysis and the over-
analysis of data are central to the debate. The
optimistic conclusions from the meta-analyses as-
sume that the effect sizes are unbiased estimates
from independent experiments and have nicely
behaved distributional properties.
Before my detailed assessment of all the avail-
able ganzfeld experiments through 1981, I accepted
the assertions by parapsychologists that their
experiments were of high quality in terms of stat-
istical and experimental methodology. I was sur-
prised to find that the ganzfeld experiments,
widely heralded as the best exemplar of a suc-
cessful research program in parapsychology, were
characterized by obvious possibilities for sensory
leakage, inadequate randomization, over-analysis
and other departures from parapsychology's own
professed standards. One response was to argue
that I had exaggerated the number of flaws. But
even internal critics agreed that the rate of defects
in the ganzfeld data base was too high.
The other response, implicit in Utts' discussion of
the ganzfeld experiments and the meta-analyses,
was to admit the existence of the flaws but to deny
their importance. The parapsychologists doing the
meta-analysis would rate each experiment for qual-
ity on one or more attributes. Then, if the null
hypothesis of no correlation between effect size and
quality were upheld, the investigators concluded
that the results could not be attributed to defects in
methodology.
This retrospective sanctification using statistical
controls to compensate for inadequate experimental
controls has many problems. The quality ratings
are not blind. As the differences between myself
and Honorton reveal, such ratings are highly sub-
jective. Although I tried my best to restrict my
ratings to what I thought were objective and ea-
sily codeable indicators, my quality ratings pro-
vide a different picture than do those of Honorton.
Honorton, I am sure, believes he was just as
objective in assigning his ratings as I believe I was.
Another problem is the number of different prop-
ity omitted many attributes that I included in
my ratings. Even in those cases where we used
the same indicators to ! make our assessments, we
differed because of ou; scaling. For example, on
adequacy of randomization I used a simple dicho-
tomy. Either the experimenter clearly indicated
using an appropriate randomization procedure or
he did not. Honorton converted this to a trichoto-
mous scale. He distinguished between a clearly
inadequate procedure such as hand-shuffling and
failure to report how the randomization was done.
He then assigned the lowest rating to failure to
describe the randomization. In his scheme, clearly
inadequate randomization was of higher quality
than failure to describe the procedure. Although we
agreed on which experiments had adequate ran-
domization, inadequate randomization or inade-
quate documentation, the different ways these were
ordered produced important differences between us
in how randomization related to effect size. These
are just some of the reasons why the finding of no
correlation between effect size and rated quality
does not justify concluding that the observed flaws
had no effect.
I will now consider some of Utts' assertions and
hope that I can go into more detail in anoth-
er forum. Utts discusses the conclusions of the
National Research Council's Committee on
Techniques for the Enhancement of Human Per-
formance. I was chairperson of that committee's
subcommittee on paranormal phenomena. She
wrongly states that we restricted our evaluation
only to significant studies. I do not know how she
got such an impression since we based our analysis
on meta-analyses whenever these were available.
The two major inputs for the committee's evalua-
tion were a lengthy evaluation of contemporary
parapsychology experiments by John Palmer and
an independent assessment of these experiments by
James Alcock. Our sponsors, the Army Research
Institute had commissioned the report from the
parapsychologist John Palmer. They specifically
asked our committee to provide a second opinion
from a non-parapsychological perspective. They
were most interested inthe experiments on remote
viewing and random number generators. We de-
cided to add the ganzfeld experiments. Alcock was
instructed, in making his evaluation, to restrict
himself to the same experiments in these categories
that Palmer had chosen. In this way, the experi-
ments we evaluated, which included both signifi-
cant and nonsignificant ones, were, in effect,
selected for us by a prominent parapsychologist.
Utts mistakenly asserts that my subcommittee
on parapsychology commissioned Harris and Rosen-
erties that are rated. Honorton's ratings of ual- thal to evaluate ara s cholo ex eriments for
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REPLICATION OF PARAPSYCHOLOGY
us. Harris and Rosenthal were commissioned by
our evaluation subcommittee to write a paper on
evaluation issues, especially those related to exper-
imenter effects. On their own initiative, Harris and
Rosenthal surveyed a number of data bases to illus-
trate the application of methodological procedures
such as meta-analysis. As one illustration, they
included a meta-analysis of the subsample of
g:trzfeld experiments used by Honorton in his
rebuttal to my critique.
Because Harris and Rosenthal did not them-
selves do a first-hand evaluation of the ganzfeld
experiments, and because they used Honorton's rat-
ings for their illustration, I did not refer to their
analysis when I wrote my draft for the chapter on
the paranormal. Rosenthal told me, in a letter, that
he had arbitrarily used Honorton's ratings rather
than mine because they were the most recent avail-
able. I assumed that Harris and Rosenthal were
using Honorton's sample and ratings to illustrate
meta-analytic procedures. I did not believe they
were making a substantive contribution to the
debate.
Only after the committee's complete report was
in the hands of the editors did someone become
concerned that Harris and Rosenthal had come to a
conclusion on the ganzfeld experiments different
from the committee. Apparently one or more com-
mittee members contacted Rosenthal and asked him
to explain why he and Harris were dissenting.
Because some committee members believed that
we should deal with this apparent discrepancy, I
contacted Rosenthal and pointed out if he had used
my ratings with the very same analysis he had
applied to Honorton's ratings, he would have
reached a conclusion opposite to what Harris and
he had asserted. I did this, not to suggest my
ratings were necessarily more trustworthy than
Honorton's, but to point out how fragile any conclu-
sions were based on this small and limited sample.
Indeed, the data were so lacking in robustness that
the difference between my rating and Honorton's
rating of one investigator (Sargent) on one at-
tribute (randomization) sufficed to reverse the con-
clusions Harris and Rosenthal made about the
correlation between quality and effect size.
Harris and Rosenthal responded by adding a foot-
note to their paper. In this footnote, they repor-
ted an analysis using my ratings rather than
Honorton's. This analysis, they concluded, still sup-
ported the null hypothesis of no correlation be-
tween quality and effect size. They used 6 of my 12
dichotomous ratings of flaws as predictors and the z
score and effect size as criterion variables in both
multiple regression and canonical correlation anal-
lation between criterion variables and flaws of
"only" 0.46. A true correlation of this magnitude
would be impressive given the nature and split of
the dichotomous variables. But, because it was not
statistically significant, Harris and Rosenthal con-
cluded that there was no relationship between
quality and effect size. A canonical correlation on
this sample of 28 nonindependent cases, of course,
has virtually no chance of being significant, even if
it were of much greater magnitude.
What this amounts to is that the alleged contra-
dictory conclusions of Harris and Rosenthal are
based on a meta-analysis that supports Honorton's
position when Honorton's ratings are used and
supports my position when my ratings are used.
Nothing substantive comes from this, and it is
redundant with what Honorton and I have already
published. Harris and Rosenthal's footnote adds
nothing because it supports the null hypothesis
with a statistical test that has no power against a
reasonably sized alternative. It is ironic that Utts,
after emphasizing the importance of considering
statistical power, places so much reliance on the
outcome of a powerless test.
(I should add that the recurrent charge that the
NRC committee completely ignored Harris and
Rosenthal's conclusions is not strictly correct. I
wrote a response to the Harris and Rosenthal paper
that was included in the same supplementary
volume that contains their commissioned paper.)
Utts' discussion of the ganzfeld debate, as I have
indicated, also shows unfamiliarity with details.
She cites my factor analysis and Saunders' critique
as if these somehow jeopardized the conclusions I
drew. Again, the matter is too complex to discuss
adequately in this forum. The "factor analysis" she
is talking about is discussed in a few pages of my
critique. I introduced it as a convenient way to
summarize my conclusions, none of which depended
on this analysis. I agree with what Saunders has to
say about the limitations of factor analysis in this
context. Unfortunately, Saunders bases his criti-
cism on wrong assumptions about what I did and
why I did it. His dismissal of the results as
"meaningless" is based on mistaken algebra. I in-
cluded as dummy variables five experimenters in
the factor analysis. Because an experimenter can
only appear on one variable, this necessarily forces
the average intercorrelation among the experi-
menter variables to be negative. Saunders falsely
asserts that this negative correlation must be -1.
If he were correct, this would make the results
meaningless. But he could be correct only if there
were just two investigators and that each one ac-
counted for 50% of the experiments. In my case, as
yses. The reported an "ad'usted" canonical corre- I made sure to check ahead of time, the use of five
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experimenters, each of whom contributed only a
few studies to the data base, produced a mildly
:negative intercorrelation of -0.147. To make sure
even that small correlation did not distort the re-
sults, I did the factor analysis with and without the
dummy variables. The same factors were obtained
in both cases.
However, I do not wish to defend this factor
analysis. None of my conclusions depend on it. I
would agree with any editor who insisted that I
omit it from the paper on the grounds of redun-
dancy. I am discussing it here as another example
that suggests that Utts is not familiar with some
relevant details in literature she discusses.
Utts may be correct. There may indeed be an
anomaly in the parapsychological findings. Anoma-
lies may also exist in non-parapsychological do-
mains. The question is when is an anomaly worth
taking seriously. The anomaly that Utts has in
mind, if it exists, can be described only as a depar-
ture from a generalized statistical model. From the
evidence she presents, we might conclude that we
are dealing with a variety of different anomalies
instead of one coherent phenomenon. Clearly, the
reported effect sizes for the experiments with ran-
dom number generators are orders of magnitude
lower than those for the ganzfeld experiments. Even
within the same experimental domain, the effect
sizes do not come from the same population. The
effects sizes obtained by Jahn are much smaller
than those obtained by Schmidt with similar ex-
periments on random number generators. In
the ganzfeld experiments, experimenters differ
significantly in the effect sizes each obtains.
This problem of what effect sizes are and what
they are measuring points to a problem for para-
psychologists. In other fields of science such as
astronomy, an "anomaly" is a very precisely speci-
fied departure from a well-established substantive
theory. When Leverrier discovered Neptune by
studying the perturbations in the orbit of Uranus,
he was able to characterize the anomaly as a very
precise departure of a specific kind from the orbit
expected on the basis of Newtonian mechanics. He
knew exactly what he had to account for.
The "anomaly" or "anomalies" that Utts talks
about are different. We do not know what it is that
we are asked to account for other than something
that sometimes produces nonchance departures
from a statistical model, whose appropriateness is
itself open to question.
The case rests on a handful of meta-analyses that
suggest effect sizes different from zero and uncorre-
lated with some non-blindly determined indices of
quality. For a variety pf reasons, these retrospec-
tive attempts to find evidence for paranormal phe-
nomena are problematical. At best, they should
provide the basis for pparapsychologists designing
prospective studies in which they can specify, in
advance, the complete sample space and the critical
region. When they get to the point where they can
specify this along with, some boundary conditions
and make some reasonable predictions, then. they
will have demonstrated something worthy of our
attention.
In this context, I agree with Utts that Honorton's
recent report of his automated ganzfeld experi-
ments is a step in the right direction. He used the
ganzfeld meta-analyses.
and the criticisms of the
existing data base to design better experiments and
make some predictions. Although he and Utts be-
lieve that the findings of meaningful effect sizes in
the dynamic targets and a lack of a nonzero effect
size in the static targets are somehow consistent
with previous ganzfeld results, I disagree. I believe
the static targets are closer in spirit to the original
data base. But this is a minor criticism.
Honorton's experiments have produced intrigu-
ing results. If, as Utts suggests, independent labo-
ratories can produce similar results with the same
relationships and with the same attention to rigor-
ous methodology, then parapsychology may indeed
have finally captured its elusive quarry. Of course,
on several previous occasions in its century-plus
history, parapsychology has felt it was on the
threshold of a breakthrough. The breakthrough
never materialized. We will have to patiently wait
to see if the current situation is any different.
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REPLICATION OF PARAPSYCHOLOGY 393
Comment
Robert L. Morris
Experimental sciences by their nature have found
it relatively easy to deal with simple closed sys-
tems. When they come to study more complex, open
systems, however, they have more difficulty in gen-
erating testable models, must rely more on multi-
variate approaches, have more diversity from
experiment to experiment (and thus more difficulty
in constructing replication attempts), have more
noise in the data, and more difficulty in construct-
ing a linkage between concept and measurement.
Data gatherers and other researchers are more
likely to be part of the system themselves. Exam-
ples include ecology, economics, social psychology
and parapsychology. Parapsychology can be re-
garded as the study of apparent new means of
communication, or transfer of influence, between
organism and environment. Any observer attempt-
ing to decide whether or not such psychic communi-
cation has taken place is one of several elements in
a complex open system composed of an indefinite
number of interactive features. The system can be
modeled, as has been done elsewhere (e.g., Morris,
1986) such as to organise our understanding of how
observers can be misled by themselves, or by delib-
erate frauds. Parapsychologists designing experi-
mental studies must take extreme care to ensure
that the elements in the experimental system do
not interact in unanticipated ways to produce arti-
fact or encourage fraudulent procedures. When re-
searchers follow up the findings of others, they
must ensure that the new experimental system
sufficiently resembles the earlier one, regarding its
important components and their potential interac-
tions. Specifying sufficient resemblance is more dif-
ficult in complex and open systems, and in areas of
research using novel methodologies.
As a result, parapsychology and other such areas
may well profit from the application of modern
meta-analysis, and meta-analytic methods may in
turn profit from being given a good stiff workout by
controversial data bases, as suggested by Jessica
Utts in her article. Parapsychology would appear to
gain from meta-analytic techniques, in at least
three important areas.
First, in assessing the question of replication
rate, the new focus on effect size and confidence
intervals rather than arbitrarily chosen signifi-
cance levels seems to indicate much greater consis-
tency in the findings than has previously been
claimed.
Second, when one codes the individual studies for
flaws and relates flaw abundance with effect size,
there appears to be little correlation for all but one
data base. This contradicts the frequent assertion
that parapsychological results disappear when
methodology is tightened. Additional evidence on
this point is the series of studies by Honorton and
associates using an automated ganzfeld procedure,
apparently better conducted than any of the previ-
ous research, which nevertheless obtained an effect
size very similar to that of the earlier more diverse
data base.
Third, meta-analysis allows researchers to look
at moderator variables, to build a clearer picture of
the conditions that appear to produce the strongest
effects. Research in any real scientific discipline
must be cumulative, with later researchers build-
ing on the work of those who preceded them. If our
earlier successes and failures have meaning, they
should help us obtain increasingly consistent,
clearer results. If psychic ability exists and is suffi-
ciently stable that it can be manifest in controlled
experimental studies, then moderator variables
should be present in groups of studies that would
indicate conditions most favourable and least
favourable to the production of large effect sizes.
From the analyses presented by Utts, for instance,
it seems evident that group studies tend to produce
poor results and, however convenient it may be to
conduct them, future researchers should apparently
focus much more on individual testing. When doing
ganzfeld studies, it appears best to work with dy-
namic rather than static target material and with
experienced participants rather than novices. If
such results are valid, then future researchers who
wish to get strong results now have a better idea of
what procedures to select to increase the likelihood
of so doing, what elements in the experimental
system seem most relevant. The proportion of stud-
ies obtaining positive results should therefore
increase.
However, the situation may be more complex
than the somewhat ideal version painted above. As
noted earlier, meta-analysis may learn from para-
psychology as well as vice versa. Parapsychological
Robert L. Morris occupies the Koestler Chair of data may well give meta-analytic techniques a good
Parapsychology in the Department of Psychology at workout and will certainly pose some challenges.
the UniAVf0-V'jiF ' Iie 4: CIS ~ 16 e6~ cr~ibed above,
m. apparent y einploy~ e o e judge or
inburgh 8 9JZ, United King Ptrq0bV(
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evaluator. Certainly none of them cited any corre-
lation values between evaluators, and the correla-
tions between judges of research quality in other
social sciences tend to be "at best around .50,"
according to Hunter and Schmidt (1990, page 497).
Although Honorton and Hyman reported a rela-
tively high correlation of 0.77 between themselves,
they were each doing their own study and their
flaw analyses did reach somewhat different conclu-
sions, as noted by Utts. Other than Hyman, the
evaluators cited by Utts tend to be positively ori-
ented toward parapsychology; roughly speaking, all
evaluators doing flaw analyses found what they
might hope to find, with the exception of the PK
dice data base. Were evaluators blind as to study
outcome when coding flaws? No comment is made
on this aspect. The above studies need to be repli-
cated, with multiple (and blind) evaluators and
reported indices of evaluator agreement. Ideally,
evaluator attitude should be assessed and taken
into account as well. A study with all hostile evalu-
ators may report very high evaluator correlations,
yet be a less valid study than one that employs a
range of evaluators and reports lower correlations
among evaluators.
But what constitutes a replication of a meta-
analysis? As with experimental replications, it may
be important to distinguish between exact and con-
ceptual replications. In the former, a replicator
would attempt to match all salient features of the
initial analysis, from the selection of reports to the
coding of features to the statistical tests employed,
such as to verify that the stated original protocol
had been followed faithfully and that a simi-
lar outcome results. For conceptual replication,
replicators would take the stated outcome of the
meta-analysis and attempt their own independent
analysis, with their own initial report selection
criteria, coding criteria and strategy for statistical
testing, to see if similar conclusions resulted. Con-
ceptual replication allows more room for bias and
resultant debate when findings differ, but when
results are similar they can be assumed to have
more legitimacy. Given the strong and surpris-
ing (for many) conclusions reached in the meta-
analysis reported by Utts, it is quite likely
that others with strong views on parapsychology
will attempt to replicate, hoping for clear confirma-
tion or disconfirmation. The diversity of methods
they are likely to employ and the resultant debates
should provide a good opportunity for airing the
many conceptual problems still present in meta-
analysis. If results differ on moderator variables,
there can come to be empirical resolution of the
results unfold. Wit
h
rega
differences assfurther
d
r
Q,
t
j
to flaw attent 'ibhll such Y
cused fi %q
nE6X t cQY 4
tY~e t 0 8
dance of existing faults; and how to avoid them. If
results are as strong ' under well-controlled con-
ditions as under sloppy ones, then additional
research such as that done by Honorton and associ-
ates under tight conditions should continue to pro-
duce positive results.
In addition to the replication issue, there are
some other problems that need to be addressed. So
far, the assessment of moderator variables has been
univariate, whereas a multivariate approach would
seem more likely to produce a clearer picture. Mod-
erator variables may eovary, with each other or
with flaws. For instance, in the dice data higher
effect sizes were found for flawed studies and for
studies with selected subjects. Did studies using
special subjects use weaker procedures?
Given the importance attached to effect size and
incorporating estimates: of effect size in designing
studies for power, we must be careful not to assume
that effect size is independent of number of trials or
subjects unless we have empirical reason to do so.
Effect size may decrease with larger N if experi-
menters are stressed or bored towards the end of a
long study or if there pare too many trials to be
conducted within a short period of time and sub-
jects are given less time to absorb their instructions
or to complete their tasks. On one occasion there is
presentation of an estimated "true average effect
size," (0.18 rather than ;0.28) without also present-
ing an estimate of effect size dispersal. Future
investigators should have some sense of how the
likelihood that they will obtain a hit rate of 1 /3
(where 1 /4 is expected) will vary in accordance
with conditions.
There are a few additional quibbles with particu-
lar points. In Utts' example experiment with Pro-
fessor A versus Professor B, sex of professor is a
possible confounding variable. When Honorton
omitted studies that did; not report direct hits as a
measure, he may havel biased his sample. Were
there studies omitted that could have reported di-
rect hits but declined todo so, conceivably because
they looked at that measure, saw no results and
dropped it? This objection is only with regard to the
initial meta-analysis and is not relevant for the
later series of studies which all used direct hits. In
Honorton's meta-analysis of forced-choice precogni-
tion experiments, the comparison variables of feed-
back delay and time interval to target selection
appear to be confounded. Studies delaying target
selection cannot provide trial by trial feedback, for
instance. Also, I am unsure about using an approxi-
mation to Cohen's h for assessing the effect size for
the aspirin study. There would appear to be a very
striking effect, with the aspirin condition heart
tion. #
con i 0 wAft'deMpbecNel por ione of
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REPLICATION OF PARAPSYCHOLOGY
misses estimated; perhaps Cohen's h greatly un-
derestimates effect size when very low probability
events (less than 1 in 50 for heart attack in the
placebo condition and less than 1 in a 100 for
aspirin) are involved. I'm not a statistician and
thus don't know if there is a relevant literature on
this point.
Comment
Dr. Utts's discussion stimulates me to offer some
comments that bear on her topic but do not, in the
main, fall into an agree-disagree mode. My refer-
ences refer to her bibliography.
Let me recommend J. Edgar Coover's work to
statisticians who would like to read about a pretty
sequence of experiments developed and executed
well before Fisher's book on experimental design
appeared. Most of the standard kinds of ESP exper-
iments (though not the ganzfeld) are carried out
and reported in this 1917 book. Coover even began
looking into the amount of information contained
in cues such as whispers. He also worked at expos-
ing mediums. I found the book most impressive. As
Utts says in her article, the question of significance
level was a puzzling one, and one we still cannot
solve even though some fields seem to have stan-
dardized on 0.05.
When Feller's comments on Stuart and Green-
wood's sampling experiments came out in the first
edition of his book, I was surprised. Feller devotes
a problem to the results of generating 25 symbols
from the set a, b, c, d and e (page 45, first edition)
using random numbers with 0 and 1 corresponding
to a, 2 and 3 to b, etc. He asks the student to find
out how often the 25 produce 5 of each symbol. He
asks the student to check the results using random
number tables. The answer seems to be about 1
chance in 500. In a footnote Feller then says "They
[random numbers] are occasionally extraordinarily
obliging: c.f. J. A. Greenwood and E. E. Stuart,
Review of Dr. Feller's Critique, Journal of Para-
Frederick Mosteller is Roger I. Lee Professor of
Mathematical Statistics, Emeritus, at Harvard Uni-
versity and Director of the Technology Assessment
Group in the Harvard School of Public Health. His
mailing address is Department of Statistics, Har-
vard University, Science Center, I Oxford Street,
The above objections should not detract from the
overall value of the Utts survey. The findings she
reports will need to be replicated; but even as is,
they provide a challenge to some of the cherished
arguments of counteradvocates, yet also challenge
serious researchers to use these findings effectively
as guidelines for future studies.
psychology, vol. 4 (1940), pp. 298-319, in particular
p. 306." The 25 symbols of 5 kinds, 5 of each,
correspond to the cards in a parapsychology deck.
The point of page 306 is that Greenwood and
Stuart on that page claim to have generated two
random orders of such a deck using Tippett's table
of random numbers. Apparently Feller thought that
it would have taken them a long time to do it. If
one assumes that Feller's way of generating a ran-
dom shuffle is required, then it would indeed be
unreasonable to suppose that the experiments could
be carried out quickly. I wondered then whether
Feller thought this was the only way to produce a
random order to such a deck of cards. If you happen
to know how to shuffle a deck efficiently using
random numbers, it is hard to believe that others
do not know. I decided to test it out and so I
proposed to a class of 90 people in mathematical
statistics that we find a way of using random num-
bers to shuffle a deck of cards. Although they were
familiar with random numbers, they could not come
up with a way of doing it, nor did anyone after class
come in with a workable idea though several stu-
dents made proposals. I concluded that inventing
such a shuffling technique was a hard problem and
that maybe Feller just did not know how at the
time of writing the footnote. My face-to-face at-
tempts to verify this failed because his response
was evasive. I also recall Feller speaking at a
scientific meeting where someone had complained
about mistakes in published papers. He said essen-
tially that we won't have any literature if mistakes
are disallowed and further claimed that he always
had mistakes in his own papers, hard as he tried to
avoid them. It was fun to hear him speak.
Although I find Utts's discussion of replication
engaging as a problem in human perception, I do
always feel that people should not be expected to
carry out difficult mathematical exercises in their
head, off the cuff, without computers, textbooks or
advisors. The kind of problem treated requires
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after a careful analysis is completed, there can be
vigorous reasonable arguments about the appropri-
ateness of the formulation and its analysis. These
investigations leave me reinforced with the belief
that people cannot do hard mathematical problems
in their heads, rather than with an attitude toward
or against ESP investigations.
When I first became aware of the work of Rhine
and others, the concept seemed to me to be very
important and I asked a psychologist friend why
more psychologists didn't study this field. He re-
sponded that there were too many ways to do these
experiments in a poorly controlled manner. At the
time, I had just discovered that when viewed with
light coming from a certain angle, I could read the
Rejoinder
I would like to thank this distinguished group of
discussants for their thought-provoking contribu-
tions. They have raised many interesting and di-
verse issues. Certain points, such as Professor
Mosteller's enlightening account of Feller's posi-
tion, require no further comment. Other points in-
dicate the need for clarification and elaboration of
my original material. Issues raised by Professors
Diaconis and Hyman and subsequent conversations
with Robert Rosenthal and Charles Honorton have
led me to consider the topic of "Satisfying the
Skeptics." Since the conclusion in my paper was
not that psychic phenomena have been proved, but
rather that there is an anomalous effect that needs
to be explained, comments by several of the discus-
sants led me to address the question "Should Psi
Research be Ignored by the Scientific Community?"
Finally, each of the discussants addressed repli-
cation and modeling issues. The last part of my
rejoinder comments on some of these ideas and
discusses them in the context of parapsychology.
CLARIFICATION AND ELABORATION
Since my paper was a survey of hundreds of
experiments and many published reports, I could
obviously not provide all of the details to accom-
pany this overview. However, there were details
lacking in my paper that have led to legitimate
questions and misunderstandings from several of
the discussants. In this section, I address specific
points raised by Professors Diaconis, Greenhouse,
backs of the cards of rry parapsychology deck as
clearly as the faces. While preparing these remarks
in 1991, Ifound a note on page 305 of volume 1 of
The Journal of Parapsychology (1937) indicating
that imperfections in the cards precluded their use
in unscreened situations, but that improvements
were on the way. Thus I sympathize with Utts's
conclusion that much is to be gained by studying
how to carry out such work well. If there is no ESP,
then we want to be able to carry out null experi-
ments and get no effect, otherwise we cannot put
much belief in work on small effects in non-ESP
situations. If there is ESP, that is exciting. How-
ever, thus far it does not look as if it will replace
the telephone.
Hyman and Morris, by either clarifying my origi-
nal statements or by adding more information from
the original reports.
Points Raised by Diatoms
Diaconis raised the point that qualified skeptics
and magicians should be active participants in
parapsychology experiments. I will discuss this
general concept in the next section, but elaborate
here on the steps that were taken in this regard for
the autoganzfeld experir rents described in Section
5 of my paper. As reported by Honorton et al.
(1990):
Two experts on the simulation of psi ability
have examined the autoganzfeld system and
protocol. Ford Kross has been a professional
mentalist [a magician who simulates psychic
abilities] for over 20 years ... Mr. Kross has
provided us with the following statement: "In
my professional capacity as a mentalist, I have
reviewed Psychophysical Research Laborato-
ries' automated ganzfeid system and found it to
provide excellent security against deception by
subjects." We have received similar comments
from Daryl Bem, Professor of Psychology at
Cornell University. Professor Bem is well
known for his research in social and personal-
ity psychology. He is also a member of the
Psychic Entertainers Association and has per-
formed for many years: as a mentalist. He vis-
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ited PRL for several days and was a subject in
Series 101" [pages 134-1351.
Honorton has also informed me (personal communi-
cation, July 25, 1991) that several self-proclaimed
skeptics have visited his laboratory and received
demonstrations of the autoganzfeld procedure and
that no one expressed any concern with the secu-
rity arrangements.
This may not completely satisfy Professor Diaco-
nis' objections, but it does indicate a serious effort
on the part of the researchers to involve such peo-
ple. Further, the original publication of the re-
search in Section 5 followed the reporting criteria
established by Hyman and Honorton (1986), thus
providing much more detail for the reader than the
earlier published records to which Professor
Diaconis alludes.
Points Raised by Greenhouse
Greenhouse enumerated four items that offer al-
ternative explanations for the observed anomalous
effects. Three of these (items 2-4) will be addressed
in this section by elaborating on the details pro-
vided in my paper. His item 1 will be addressed in
a later section.
Item 2 on his list questioned the role of experi-
menter expectancy effects as a potential confounder
in parapsychological research. While the expecta-
tions of the experimenter may influence the report-
ing of results, the ganzfeld experiments (as well as
other psi experiments) are conducted in such a way
that experimenter expectancy cannot account for
the results themselves. Rosenthal, who Greenhouse
cites as the expert in this area, addressed this in
his background paper for the National Research
Council (Harris and Rosenthal, 1988a) and con-
cluded that the ganzfeld studies were adequately
controlled in this regard. He also visited the auto-
ganzfeld laboratory and was given a demonstration
of that procedure.
Greenhouse's item 3, the question of what consti-
tutes a direct hit, was addressed in my paper but
perhaps needs elaboration. Although free-response
experiments do generate substantial amounts of
subjective data, the statistical analysis requires
that the results for each trial be condensed into a
single measure of whether or not a direct hit was
achieved. This is done by presenting four choices to
a judge (who of course does not know the correct
answer) and asking the judge to decide which of the
four best matches the subject's response. If the
judge picks the target, a direct hit has occurred.
It is true that different judges may differ on their
cal question is the same. Under the null hypothe-
sis, since the target is randomly selected from the
four possibilities presented, the probability of a
direct hit is 0.25 regardless of who does the judg-
ing. Thus, the observed anomalous effects cannot
be explained by assuming there was an over-
optimistic judge.
If Professor Greenhouse is suggesting that the
source of judging may be a moderating variable
that determines the magnitude of the demonstrated
anomalous effect, I agree. The parapsychologists
have considered this issue in the context of whether
or not subjects should serve as judges for their own
sessions, with differing opinions in different labora-
tories. This is an example of an area that has been
suggested for further research.
Finally, Greenhouse raised the question of the
accuracy of the file-drawer estimates used in the
reported meta-analyses. I agree that it is instruc-
tive to examine the file-drawer estimate using more
than one model. As an example, consider the 39
studies from the direct hit and autoganzfeld data
bases. Rosenthal's fail-safe N estimates that there
would have to be 371 studies in the file-drawer to
account for the results. In contrast, the method
proposed by Iyengar and Greenhouse gives a file-
drawer estimate of 258 studies. Even this estimate
is unrealistically large for a discipline with as few
researchers as parapsychology. Given that the av-
erage number of trials per experiment is 30, this
would represent almost 8000 unreported trials, and
at least that many hours of work.
There are pros and cons to any method of esti-
mating the number of unreported studies, and the
actual practices of the discipline in question should
be taken into account. Recognizing publication bias
as an issue, the Parapsychological Association has
had an official policy since 1975 against the selec-
tive reporting of positive results. Of the original
ganzfeld studies reported in Section 4 of my paper,
less than half were significant, and it is a matter of
record that there are many nonsignificant studies
and "failed replications" published in all areas of
psi research. Further, the autoganzfeld database
reported in Section 5 has no file-drawer. Given the
publication practices and the size of the field, the
proposed file-drawer cannot account for the ob-
served effects.
Points Raised by Hyman
One of my goals in writing this paper was to
present a fair account of recent work and debate in
parapsychology. Thus, I was disturbed that Hy-
man, who has devoted much of his career to the
opinions of whether or not there has been a direct study of parapsychology, and who had first-hand
hit on a ~t eu 1xv ]~ se UuM tug CI P` -8b 9 O r3108010001 6ports, be-
Ftlap
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J. Urrs
lieved that some of my statements were inaccurate
and indicated that I had not carefully read the
reports. I will address some of his specific objec-
tions and show that, except where noted, the accu-
racy of my original statements can be verified by
further elaboration and clarification, with due apol-
ogy for whatever necessary details were lacking in
my original report.
Most of our points of disagreement concern
the National Academy of Sciences (National Re-
search Council) report Enhancing Human Per-
formance (Druckman and Swets, 1988). This
report evaluated several controversial areas, in-
cluding parapsychology. Professor Hyman chaired
the Parapsychology Subcommittee. Several back-
ground papers were commissioned to accompany
this report, available from the "Publication on
Demand Program" of the National Academy
Press. One of the papers was written by Harris and
Rosenthal, and entitled "Human Performance
Research: An Overview."
Professor Hyman alleged that "Utts mistakenly
asserts that my subcommittee on parapsychology
commissioned Harris and Rosenthal to evaluate
parapsychology experiments for us ...." I cannot
find a statement in my paper that asserts that
Harris and Rosenthal were commissioned by the
subcommittee, nor can I find a statement that
asserts that they were asked to evaluate parapsy-
chology experiments. Nonetheless, I believe our
substantive disagreement results from the fact
that the work by Harris and Rosenthal was writ-
ten in two parts, both of which I referenced in
my paper. They were written several months
apart, but published together, and each had
its own history.
The first part (Harris and Rosenthal, 1988a) is
the one to which I referred with the words
"Rosenthal was commissioned by the National
Academy of Sciences to prepare a background
paper to accompany its 1988 report on parapsychol-
ogy" (p. 372). According.; to Rosenthal (personal
communication, July 23, 1991) he was asked to pre-
pare a background paper to address evaluation
issues and experimenter effects to accompany the
report in five specific areas of research, including
parapsychology.
The second part was a "Postscript" to the com-
missioned paper (Harris and Rosenthal, 1988b), and
this is the one to which I referred on page 371 as
"requested by Hyman in his capacity as Chair of
the National Academy of Sciences' Subcommittee
on Parapsychology." (It is probably this wording
that led Professor Hyman to his erroneous allega-
tion.) The postscript began with the words "We
have
Hyman, chair of the subcommittee on parapsychol-
ogy, in which he raises questions about the pres-
ence and consequence of methodological flaws in
the ganzfeld studies. . .
In reference to this postscript, I stand corrected
on a technical point, because Hyman himself did
not request the responso to his own letter. As noted
by Palmer, Honorton anjd Utts (1989), the postscript
was added because:
At one stage of the process, John Swets, Chair
of the Committee, actually phoned Rosenthal
and asked him to withdraw the parapsychology
section of his [commissioned] paper. When
Rosenthal declined, Swets and Druckman then
requested that Rosenthal respond to criticisms
that Hyman had included in a July 30, 1987
letter to Rosenthal [page 381.
A related issue on which I would like to elaborate
concerns the correlation between flaws and success
in the original ganzfeld data base. Hyman has
misunderstood both my position and that of Harris
and Rosenthal. He believes that I implicitly denied
the importance of the ;flaws, so I will make my
position explicit. I do not think there is any evi-
dence that the experimental results were due to the
identified flaws. The flaw analysis was clearly use-
ful for delineating acceptable criteria for future
experiments. Several experiments were conducted
using those criteria. The results were similar to the
original experiments. I believe that this indicates
an anomaly in need of iin explanation.
In discussing the paper and postscript by Harris
and Rosenthal, Hyman stated that "The alleged
contradictory conclusions [to the National Research
Council report] of Harris and Rosenthal are based
on a meta-analysis that supports Honorton's posi-
tion when Honorton's (flaw] ratings are used and
supports my position when my ratings are used."
He believes that Harris and Rosenthal (and I) failed
to see this point because the low power of the test
associated with their analysis was not taken into
account.
The analysis in question was based on a canoni-
cal correlation between ':flaw ratings and measures
of successful outcome far the ganzfeld studies. The
canonical correlation was 0.46, a value Hyman finds
to be impressive. What] he has failed to take into
account however, is that a canonical correlation
gives only the magnitude of the relationship, and
not the direction. A careful reading of Harris and
Rosenthal (1988b) reveals that their analysis actu-
ally contradicted the idea that the flaws could
account for the successful ganzfeld results, since
"Interestingly, three of the six flaw variables corre-
been asked to r and o a lette e elm t t Sl w an nic l variable
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and with the outcome canonical variable but three Paranormal (CSICOP) was established in 1976 by
correlated negatively" (page 2, italics added). philosopher Paul Kurtz and sociologist Marcello
Rosenthal (personal communication, July 23, 1991) Truzzi when "Kurtz became convinced that the
verified that this was indeed the point he was time was ripe for a more active crusade against
trying to make. Readers who are interested in parapsychology and other pseudo-scientists" (Pinch
drawing their own conclusions from first-hand and Collins, 1984, page 527). Truzzi resigned from
analyses can find Hyman's original flaw codings in the organization the next year (as did Professor
an Appendix to his paper (Hyman, 1985, pages Diaconis) "because of what he saw as the growing
44--49). danger of the committee's excessive negative zeal
Finally, in my paper, I stated that the parapsy- at the expense of responsible scholarship" (Collins
chology chapter of the National Research Council and Pinch, 1982, page 84). In an advertising
report critically evaluated statistically significant brochure for their publication The Skeptical In-
experiments, but not those that were nonsignifi- quirer, CSICOP made clear its belief that paranor-
cant. Professor Hyman "does not know how [I] got mal phenomena are worthy of scientific attention
such an impression," so I will clarify by outlining only to the extent that scientists can fight the
some of the material reviewed in that report. There growing interest in them. Part of the text of the
were surveys of three major areas of psi research: brochure read: "Why the sudden explosion of inter-
remote viewing (a particular type of free-response est, even among some otherwise sensible people, in
experiment), experiments with random number all sorts of paranormal `happenings'? ... Ten years
generators, and the ganzfeld experiments. As an ago, scientists started to fight back. They set up an
example of where I got the impression that they organization-The Committee for the Scientific In-
evaluated only significant studies, consider the sec- vestigation of Claims of the Paranormal."
tion on remote viewing. It began by referencing a During the six years that I have been working
published list of 28 studies. Fifteen of these were with parapsychologists, they have repeatedly ex-
immediately discounted, since "only 13 ... were pressed their frustration with the unwillingness of
published under refereed auspices" (Druckman and the skeptics to specify what would constitute ac-
Swets, 1988, page 179). Four more were then dis- ceptable evidence, or even to delineate criteria for
missed, since "Of the 13 scientifically reported an acceptable experiment. The Hyman and Honor-
experiments, 9 are classified as successful" (page ton Joint Communique was seen as the first major
179). The report continued by discussing these nine step in that direction, especially since Hyman was
experiments, never again mentioning any of the the Chair of the Parapsychology Subcommittee of
remaining 19 studies. The other sections of the CSICOP.
report placed similar emphasis on significant stud- Hyman and Honorton (1986) devoted eight pages
ies. I did not think this was a valid statistical to "Recommendations for Future Psi Experiments,"
method for surveying a large body of research. carefully outlining details for how the experiments
should be conducted and reported. Honorton and
Minor Point Raised by Morris his colleagues then conducted several hundred
The final clarification I would like to offer con- trials using these specific criteria and found essen-
cerns the minor point raised by Professor Morris, tially the same effect sizes as in earlier work for
that "When Honorton omitted studies that did not both the overall effect and effects with moderator
report direct hits as a measure, he may have biased variables taken into account. I would expect Profes-
his sample." This possibility was explicitly ad- sor Hyman to be very interested in the results of
dressed by Honorton (1985, page 59). He examined these experiments he helped to create. While he did
what would happen if z-scores of zero were inserted acknowledge that they "have produced intriguing
for the 10 studies for which the number of direct results," it is both surprising and disappointing
hits was not measured, but could have been. He that he spent only a scant two paragraphs at the
found that even with this conservative scenario, end of his discussion on these results.
the combined z-score only dropped from 6.60 to Instead, Hyman seems to be proposing yet an-
5.67. other set of requirements to be satisfied before
parapsychology should be taken seriously. It is dif-
SATISFYING THE SKEPTICS ficult to sort out what those requirements should be
from his account: "[They should] specify, in ad-
Parapsychology is probably the only scientific vance, the complete sample space and the critical
discipline for which there is an organization of region. When they get to the point where they can
skeptics trying to discredit its work. The Commit- specify this along with some boundary conditions
tee for the Scientific Investigation of Claims of the and make some reasonable predictions then they
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will have demonstrated something worthy of our
attention."
Diaconis believes that psi experiments do not
deserve serious attention unless they actively in-
volve skeptics. Presumably, he is concerned with
subject or experimenter fraud, or with improperly
controlled experiments. There are numerous docu-
mented cases of fraud and trickery in purported
psychic phenomena. Some of these were observed
by Diaconis and reported in his article in Science.
Such cases have mainly been revealed when inves-
tigators attempted to verify the claims of individ-
ual psychic practitioners in quasi-experimental or
uncontrolled conditions. These instances have re-
ceived considerable attention, probably because the
claims are so sensational, the fraud is so easy to
detect by a skilled observer and they are an easy
target for skeptics looking for a way to discredit
psychic phenomena. As noted by Hansen (1990),
"Parapsychology has long been tainted by the
fraudulent behavior of a few of those claiming psy-
chic abilities" (page 25).
Control against deception by subjects in the labo-
ratory has been discussed extensively in the para-
psychological literature (see, e.g., Morris, 1986, and
Hansen, 1990). Properly designed experiments
should preclude the possibility of such fraud.
Hyman and Honorton (1986, page 355) explicitly
discussed precautions to be taken in the ganzfeld
experiments, all of which were followed in the auto-
ganzfeld experiments. Further the controlled labo-
ratory experiments discussed in my paper usually
used a large number of subjects, a situation that
minimizes the possibility that the results were due
to fraud on the part of a few subjects. As for the
possibility of experimenter fraud, it is of course an
issue in all areas of science. There have been a few
such instances in parapsychology, but since para-
psychologists tend to be aware of this possibility,
they were generally detected and exposed by insid-
ers in the field.
It is not clear whether or not Diaconis is suggest-
ing that a magician or "qualified skeptic" needs to
be present at all times during a laboratory experi-
ment. I believe that it would be more productive for
such consultation to occur during the design phase,
and during the implementation of some pilot ses-
sions. This is essentially what was done for the
autoganzfeld experiments, in which Professor Hy-
man, a skeptic as well as an accomplished magi-
cian, participated in the specification of design
criteria, and mentalists Bem and Kross observed
experimental sessions. Bem is also a well-respected
experimental psychologist.
While I believe that the skeptics, particularly
some of the more knowledgeable members of
CSICOP, have served a useful role in helping to
improve experiments, their counter-advocacy stance
is counterproductive. If they are truly interested
in resolving the question of whether or not psi
abilities exist, I would :expect them to encourage
evaluation and experimentation by unbiased,
skilled experimenters. Instead, they seem to be
trying to discourage such interest by providing a
moving target of requirements that must be satis-
fied first.
SHOULD PSI RESEARFH BE IGNORED BY THE
SCIENTIFIC; COMMUNITY?
In the conclusion of my paper, I argued that the
scientific community should pay more attention to
the experimental results in parapsychology. I was
not suggesting that the accumulated evidence con-
stitutes proof of psi abilities, but rather that it
indicates that there is indeed an anomalous effect
that needs an explanation. Greenhouse noted that
my paper will not necessrily change anyone's view
about the existence of paranormal phenomena, an
observation with which I agree. However, I hope it
will change some views about the importance of
further investigation.
Mosteller and Diaconis both acknowledged that
there are reasons for statisticians to be interested
in studying the anomalous effects, regardless of
whether or not psi is real. As noted by Mosteller,
"If there is no ESP, thjsn we want to be able to
carry out null experiments and get no effect, other-
wise we cannot put much belief in work on small
effects in non-ESP situations." Diaconis concluded
that "Parapsychology is worthy of serious study"
partly because "If it is wrong, it offers a truly
alarming massive case study of how statistics can
mislead and be misused."
Greenhouse noted several sociological reasons for
the resistance of the scientific community to accept-
ing parapsychological phenomena. One of these is
that they directly contradict the laws of physics.
However, this assertion is not uniformly accepted
by physicists (see, e.g., ?Oteri, 1975), and some of
the leading parapsychological researchers hold
Ph.D.s in physics.
Another reason cited by Greenhouse, and sup-
ported by Hyman, is that psychic phenomena are
currently unexplainable by a unified scientific the-
ory. But that is precisely; the reason for more inten-
sive investigation. The history of science and
medicine is replete with examples where empirical
departures from expectation led to important find-
ings or theoretical models. For example, the causal
connection between cigarette smoking and lung
cancer was established only after years of statisti-
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REPLICATION IN PARAPSYCHOLOGY
cal studies, resulting from the observation by one specify what should happen if there is no such
physician that his lung cancer patients who smoked thing as ESP by using simple binomial models,
did not recover at the same rate as those who did either to find p-values or Bayes factors. As noted
not. There are many medications in common use by Mosteller, if there is no ESP, or other nonstatis-
for which there is still no medical explanation for tical explanation for an effect, we should be able to
their observed therapeutic effectiveness, but that carry out null experiments and get no effect. Other-
does not prohibit their use. wise, we should be worried about using these sim-
There are also examples where a coherent theory ple models for other applications.
of a. phenomenon was impossible because the re- Greenhouse, in his first alternative explanation
quisite background information was missing. For for the results, questioned the use of these simple
instance, the current theory of endorphins as an models, but his criticisms do not seem relevant to
explanation for the success of acupuncture would the experiments discussed in Section 5 of my paper.
have been impossible before the discovery of endor- The experiments to which he referred were either
phins in the 1970s. poorly controlled, in which case no statistical anal-
Mosteller's observation that ESP will not replace ysis could be valid, or were specifically designed to
the telephone leads to the question of whether or incorporate trial by trial feedback in such a way
not ;psi abilities are of any use even if they do exist, that the analysis needed to account for the added
since the effects are relatively small. Again, a look information. Models and analyses for such experi-
at history is instructive. For example, in 1938 For- ments can be found in the references given at the
tune Magazine reported that "At present, few sci- end of Diaconis' discussion.
entists foresee any serious or practical use for For the remainder of this discussion, I will con-
atomic energy." fine myself to models appropriate for experiments
Greenhouse implied that I think parapsychology such as the autoganzfeld described in Section 5. It
is not accepted by more of the scientific community is this scenario for which Bayarri and Berger com-
only because they have not examined the data, but puted Bayes factors, and for which Dawson dis-
this misses the main point I was trying to make. cussed possible Bayesian models.
The point is that individual scientists are willing to If ESP does exist, it is undoubtedly a gross over-
express an opinion without any reference to data. simplification to use a simple non-null binomial
The interesting sociological question is why they model for these experiments. In addition to poten-
are so resistant to examining the data. One of the tial differences in ability among subjects, there
major reasons is undoubtedly the perception identi- were also observed differences due to dynamic ver-
fied by Greenhouse that there is some connection sus static targets, whether or not the sender was a
between parapsychology and the occult, or worse, friend, and how the receiver scored on measures of
religious beliefs. Since religion is clearly not in the extraversion. All of these differences were antici-
realm of science, the very thought that parapsy- pated in advance and could be incorporated into
chology might be a science leads to what psychol- models as covariates.
ogists call "cognitive dissonance." As noted by It is nonetheless instructive to examine the Bayes
Griffin (1988), "'People feel unpleasantly aroused factor computed by Bayarri and Berger for the
when two cognitions are dissonant-when they con- simple non-null binomial model. First, the observed
tradict one another" (page 33). Griffin continued by anomalous effects would be less interesting if the
observing that there are also external reasons for Bayes factor was small for reasonable values of r,
scientists to discount the evidence, since "It is gen- as it was for the random number generator experi-
erally easier to be a skeptic in the face of novel ments analyzed by Jefferys (1990), most of which
evidence; skeptics may be overly conservative, but purported to measure psychokinesis instead of ESP.
they are rarely held up to ridicule" (page 34). Second, the Bayes factor provides a rough measure
In. summary, while it may be safer and more of the strength of the evidence against the null
consonant with their beliefs for individual scien- hypothesis and is a much more sensible summary
tists to ignore the observed anomalous effects, the than the p-value. The Bayes factors provided by
scientific community should be concerned with Bayarri and Berger are probably more conserva-
finding an explanation. The explanations proposed tive, in the sense of favoring the null hypothesis,
by Greenhouse and others are simply not tenable. than those that would result from priors elicited
from parapsychologists, but are probably reason-
REPLICATION AND MODELING able for those who know nothing about past ob-
served effects. I expect tht most parapsychologists
Parapsychology is one of the few areas where a would not opt for a prior symmetric around chance,
point null hypothesis makes some sense. We can but would still choose one with some mass below
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chance. The final reason it is instructive to exam-
ine these Bayes factors is that they provide a quan-
titative challenge to skeptics to be explicit about
their prior probabilities for the null and alternative
hypotheses.
Dawson discussed the use of more complex
Bayesian models for the analysis of the auto-
ganzfeld data. She proposed a hierarchical model
where the number of successes for each experiment
followed a binomial distribution with hit rate pi,
and logit(p1) came from a normal distribution with
noninformative priors for the mean and variance.
She then expanded this model to include heavier
tails by allowing an additional scale parameter for
each experiment. Her rationale for this expanded
model was that there were clear outlier series in
the data.
The hierarchical model proposed by Dawson is a
reasonable place to start given only that there were
several experiments trying to measure the same
effect, conducted by different investigators. In the
autoganzfeld database, the model could be ex-
panded to incorporate the additional information
available. Each experiment contained some ses-
sions with static targets and some with dynamic
targets, some sessions in which the sender and
receiver were friends and others in which they
were not and some information about the extraver-
sion score of the receiver. All of this information
could be included by defining the individual session
as the unit of analysis, and including a vector of
covariates for each session. It would then make
sense to construct a logistic regression model with
a component for each experiment, following the
model proposed by Dawson, and a term X13 to
include the covariates. A prior distribution for 0
could include information from earlier ganzfeld
studies. The advantage of using a Bayesian ap-
proach over a simple logistic regression is that
information could be continually updated. Some of
the recent work in Bayesian design could then be
incorporated so that future trials make use of the
best conditions.
Several of the discussants addressed the concept
of replication. I agree with Mosteller's implication
that it was unwise for the audience in my seminar
to respond to my replication questions so quickly,
and that was precisely my point. Most nonstatisti-
cians do not seem to understand the complexity
of the replication question. Parenthetically, when
I posed the same scenario to an audience of statis-
ticians, very few were willing to offer a quick
opinion.
Bayarri and Berger provided an insightful dis-
cussion of the purpose of replication, offering quan-
titative answers to questions that were implicit in
my discussion. Their analyses suggest some alter-
natives to power analysis that might be considered
when designing a new study to try to replicate a
questionable result.
Morris addressed the question of what con-
stitutes a replication of a meta-analysis. He
distinguished between exact and conceptual repli-
cations. Using his distinction, the autoganzfeld
meta-analysis could be viewed as a conceptual
replication of the earlier ganzfeld meta-analysis.
He noted that when such a conceptual replication
offers results similar to those of the original
meta-analysis, it lends legitimacy to the original
results, as was the case with the autoganzfeld
meta-analysis.
Greenhouse and Morris both noted the value of
meta-analysis as a method of comparing different
conditions, and I endorse that view. Conditions
found to produce different effects in one meta-
analysis could be explicitly studied in a conceptual
replication. One of thO intriguing results of the
autoganzfeld experiments was that they supported
the distinction between effect sizes for dynamic
versus static targets found in the earlier ganzfeld
work, and they supported the relationship between
ESP and extraversion found in the meta-analysis
by Honorton, Ferrari and Bem (1990).
Most modern parapsychologists, as indicated by
Morris, recognize that demonstrating the validity
of their preliminary findings will depend on identi-
fying and utilizing "moderator variables" in future
studies. The use of such; variables will require more
complicated statistical models than the simple bi-
nomial models used in the past. Further, models
are needed for combining results from several dif-
ferent experiments, thagt don't oversimplify at the
expense of lost information.
In conclusion, the anomalous effect that persists
throughout the work reviewed in my paper will be
better understood only after further experimenta-
tion that takes into acdount the complexity of the
system. More realistic, and thus more complex,
models will be needed; to analyze the results of
those experiments. This presents a challenge that I
hope will be welcomed by the statistics community.
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