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Originally published
in the Journal
of Parapsychology,
Vol. 56, No. 2,
June 1992, pp. 97-113.
CRITIQUE OF THE PEAR
REMOTE-VIEWING EXPERIMENTS
By George P. Hansen, Jessica Utts, Betty Markwick
_____________________________________________________
ABSTRACT: The Princeton Engineering Anomalies Research (PEAR)
program has produced a number of experimental reports discussing remote-viewing
results and analyses. This work is reviewed with attention to methodological
and statistical issues. The research departs from criteria usually
expected in formal scientific experimentation. Problems with regard
to randomization, statistical baselines, application of statistical models,
agent coding of descriptor lists, feedback to percipients, sensory cues,
and precautions against cheating. Many of the issues of remote-viewing
methodology were identified by Stokes and Kennedy over 10 years ago.
It is concluded that the quoted significance values are meaningless because
of defects in the experimental and statistical procedures.
__________________________________________________
In the last 10 years, the Princeton Engineering Anomalies
Research (PEAR) laboratory has conducted extensive research on remote viewing.
This work has been reported in a number of publications, including Dunne,
Jahn, and Nelson (1983), Jahn and Dunne (1987), Jahn, Dunne, and Nelson
(1987), Nelson, Jahn, and Dunne (1986). Briefer accounts can be found
in Jahn (1982), Jahn and Dunne (1986), and R. G. Jahn, Dunne, and E. G.
Jahn (1980, 1981), Jahn, et al. (1983), Nelson and Dunne (1987).
The most recent report (Dunne, Dobyns, & Intner, 1989) includes results
of 336 formal trials and constitutes the single largest data base of remote
viewing that has been reported in some detail.
Surprisingly, this research received little attention
in five large critical works on parapsychology (Alcock, 1990; Druckman
& Swets, 1988; Hansel, 1989; Hyman, 1989; and Palmer, 1985).
It is also noteworthy that the work has been given virtually no coverage
in two parapsychology textbooks (Edge, Morris, Rush, & Palmer, 1986;
Nash 1986). Palmer (1985, p. 57) defended his omission saying “As
procedural details of the subsequent trials are not included in the report,
a methodological critique cannot be undertaken.” Although the report
(Dunne, et al., 1983) contained 178 pages, some might consider Palmer’s
statement to be reasonable. Only pages 3 - 7 (dou-
____________
An earlier version of this paper was presented at the
34th annual conference of the Parapsychological Association in Heidelberg,
Germany, in August 1991.
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ble-spaced) are devoted to procedure; most of the report consists of
tables and graphs.
Since the release of Palmer’s report, the PEAR remote
viewing-experiments have been presented in three refereed journal articles
(Jahn & Dunne, 1986; Jahn, Dunne, & Nelson, 1987; Nelson, Jahn,
& Dunne, 1986). This research is becoming frequently cited; for
instance, Braude (1987) described it as “careful work” (p. 573).
McConnell (1987, p. 204-205) approvingly quoted the results. T. Rockwell
and W. T. Rockwell (1988) said: “They have avoided questions of sensory
leakage in remote perception” (p. 361), “and they have carried the statistical
analysis rigorously to the ends of any possible argument we can envision”
(p. 362). They made similar statements in a popular magazine (T.
Rockwell & W. T. Rockwell, 1989). Nelson and Radin (1987) specifically
touted the work as meeting Alcock’s (completely erroneous) statistical
objections. Beloff (1989, p. 365) declared their statistical procedure
to be “a valid method of assessment.” Popular authors Alexander,
Groller, and Morris (1990) and Ellison (1988) have also promoted the research.
Scott (1988) briefly critiqued the work, and a more detailed comment on
the methodology, statistics, and reporting now seems appropriate.
A Brief Overview of the PEAR Remote-Viewing Trials
An up-to-date summary of the PEAR remote-viewing work is
given by Dunne, Dobyns, and Intner (1989). They report results for
a total of 411 trials, of which 336 are designated as formal.
We will summarize the protocol for the 336 formal trials as presented in
their report.
A percipient (receiver) attempts to describe an unknown
geographical location where an agent (sender) is, has been, or will be
situated at a specified time.1 In each case the agent
and the percipient were known to each other. The date and time of
the geographical target site visitation were specified in advance.
In the “volitional” mode (211 trials) the agent was free to choose the
target, whereas in the “instructed” mode (125 trials) the target site was
randomly selected without replacement from a pool of potential targets.
Different series generally used different target pools. During a
trial,
__________
1 PEAR titles their procedure “precognitive
remote perception” (emphasis added); however, a substantial number of trials
involved retrocognitive or real-time remote viewing.
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the agent spent about 15 minutes immersed in the scene, consciously
aware of the intent of the experiment. The percipient usually selected
a convenient time, sometimes several days before or after the specified
target visitation, and unmonitored, recorded perceptions by writing, drawing,
or occasionally, by tape-recording them.
For most of the trials (the 277 ab initio trials) the
first step of the analysis was to have the agent and the percipient each
give yes/no responses to a “descriptor” list of 30 questions. The
responses to these questions describe the target location. The original
59 formal trials were conducted before the list had been developed and
thus were coded by independent judges (ex post facto).
In order to assess the quality of a match between a target
and a response, in this procedure a score is calculated for each trial.
PEAR developed 5 different scoring procedures. Most recently they
have focused on their Method B, which we discuss here. For the computation,
weighting factors (alphas) were used, where each alpha was the proportion
of target sites for which the descriptor question was answered affirmatively.
The numerator of the score was created by adding 1/alpha(i) if question
i was answered correctly as “yes” by the percipient, and 1/(1-alpha(i))
if question i was answered correctly as “no” by the percipient. The
denominator was calculated by adding these terms as if all 30 questions
had been answered correctly (highest possible score).
The next step in the analysis was to create an array of
“mismatch” scores by matching descriptor lists for targets and responses
from different trials. There were 327 unique targets in all of the
series. The 106,602 scores for the “universal empirical chance distribution”
were derived by matching each of those targets with the first response
generated for each of the other 326 targets (327 x 326 = 106,602).
The mean and standard deviation of this “universal empirical
chance distribution” were .5025 and .1216, respectively. The shape
of the empirical distribution approximated the normal curve. Therefore,
z scores for each correctly matched target-response pair were derived
by computing the score for the match and then standardizing it by subtracting
.5025 and dividing the result by .1216. These calculations were repeated
for several subsets of trials in order to do comparisons (e.g. instructed
vs. volitional target selection). For such comparisons, the score
for a trial was computed using the alphas derived from the subset in which
the trial occurred.
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The Journal of Parapsychology
The overall results for the formal trials gave a composite z of
6.355, with a corresponding p value of 1.04 x
10-10.
Methodological Problems
Randomization
Randomness is the foundation upon which all statistical
inference is built. Without any source of randomness, it is impossible
to assign probabilities to events. In ESP experiments, subjects’
responses cannot be considered random in any sense, and it has therefore
long been recognized that targets must be randomly selected. In fact,
telepathy research was one of the very first areas in any science to adopt
formal randomization (Hacking, 1988). Stanford reports that random
selection is “regarded as a sine qua non of adequate ESP-test methodology”
(Dr. Stanford replies..., 1986, p. 14). Morris (1978, p. 51) states
“Targets must be selected randomly, rather than by any human decision or
fixed set of rules, because such rules and decisions are inevitably patterned
or biased and thus are either potentially inferrable by the subject or
else may inadvertently match a similar pattern or bias in the subject’s
responses.” This is not merely a hypothetical issue. One of
us (Hansen) has observed a number of ganzfeld sessions with naive subjects
who did not understand that targets were randomly selected.2
During the judging phase, several subjects specifically commented that
they were considering picking the judging pool item that would most appeal
to the sender (believing the sender had been the one to select the target).
A subject’s preferences and biases are likely to shift
over time and may vary with factors like moods. For instance, someone
who is depressed might be less likely to notice bright colors and activity.
Since the agent is completely free to choose the target in the volitional
mode, the percipient might be able to infer characteristics of the selected
target from knowledge of the agent’s mood. Because the targets are
geographical locations, other factors might be inferred by the percipient.
For example, if the weather was cold or rainy, the agent might choose an
indoor location in order to remain comfortable. Similarly, an agent
who was aware of the likes and dislikes of the percipient could choose
a target to maximize the chances of a match.
__________
2 The subjects were indeed earlier
told that the target was randomly selected, but there is a great amount
of information for new subjects to absorb. They usually don’t understand
all aspects of the procedure the first time they take part.
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Dunne et al. (1989) report that 211 of 336 formal trials
(63%) were in the “volitional” mode. For these, there was no random
selection of the target whatsoever. This is virtually unique in modern
parapsychology. For the remaining 125 trials, only in the most recent
report is there any information as to how the random selection was made.
The information provided is very limited and does not meet the reporting
guidelines recommended by Hyman and Honorton (1986).
Agent Coding of the Descriptor Lists
As explained above, PEAR uses a descriptor checklist of
30 items to define a geographical site for statistical evaluation.
Nelson et al. (1986) report that “encoding of the target is normally performed
by the agent at the time of visitation” (p. 279). This coding is
a subjective procedure and can introduce artifacts even though the target
site is randomly selected. For instance, Descriptor 6 reads:
“Is any significant part of the scene hectic, chaotic, congested, or cluttered?”
This is vague and open to interpretation. Houck (1986, p. 36), using
a similar descriptor list, noted: “People simply do not answer the questions
about the same scene in the same way.” An agent sensitive to a percipient’s
predispositions or current mood might very well code vague descriptors
to be consistent with the coding anticipated to be done by the percipient
on the given day.
This issue can be conceptualized as a problem of nonrandom
target selection. For purposes of statistical evaluation, the actual
target is the encoded descriptor list. The encoding of the
list is done by the agent, who consciously selects descriptors (even though
the target site may have been randomly determined). This flaw
has long been understood, and there are several variants of it. Materials
produced by the agent at the time of the trial (or later) should not be
used in the judging process. Stokes (1978a, 1978b) noted that if
photographs of the target site were taken at the time of sending, it would
be inappropriate to use them in the judging procedure. Photographs
could reveal which aspects of the site the agent found most interesting.
Kennedy (1979a) also raised the issue. Both commentators made the
point directly in regard to Dunne’s early remote-viewing work, which is
now included in the PEAR data base (in the “ex post facto” category).
Schlitz and Gruber (1981) published a rejudging and reanalysis of one of
their own experiments because information from the agent was provided to
the original judges; the recomputed p value was less extreme than
the first result (by a factor
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of about 300). Humphrey, May, and Utts (1988, p. 382) noted that
“in an actual experimental series, it is critical that the target fuzzy
sets be defined before the series begins. Because of the potential
of information leakage due to bias on the part of the analyst, it is an
obvious mistake to attempt to define the target fuzzy set on a target-by-target
basis in real time.” Their footnote added: “This is actually a quite
general comment that applies to any descriptor list technology”
(emphasis in the original). Problems of this sort are very easily
avoided. The simple, straightforward remedy, as noted by Humphrey,
et al., is to encode all potential target sites before the experiment begins.
Shielding of Agent from Percipient
Although Dunne et al. (1989, pp. 4-5) state that “precautions
are taken to ensure that perceptions are recorded and filed before percipients
have any sensory access to target information,” the report contains no
details as to how the agent and percipient were kept apart (to convincingly
exclude sensory leakage between the two). This is of concern because
it is reported that “percipients usually select the time and place most
convenient for them to generate their descriptions, and no experimenters
or monitors are present during the perception period” (Dunne, et al., 1989,
p. 4). Virtually no precautions are described that would preclude
the agent’s and percipient’s coming in contact, or a third party coming
into contact with each of them, and innocently conveying information about
the target. Needless to say, this is not usual procedure in parapsychology.
Potential Cheating by Subjects
Deception by subjects has long been a problem in psi research
(Hansen, 1990), and experimenters have an obligation to guard against trickery.
Because of the lack of methodological controls described above, there is
a potential for cheating. When the target is selected by the agent,
there may be collusion between the agent and percipient. Further,
the protocol allows cheating by one partner acting alone. One may
try to consciously match the response biases of the other. Morris
(1982) specifically addressed the consequence of nonrandom target selection
in relation to cheating. He wrote: “Unless selected randomly from
an equally attractive target pool, targets are likely to have certain sensible,
preferable characteristics that
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would allow a psychic familiar with whomever chose the target to infer
rationally the nature of the target” (p. 21). PEAR’s methods made
it easy to cheat. Without the use of randomly selected targets and
adequate shielding of the agent from the percipient, it is virtually impossible
to detect even simple trickery. Parapsychologists have long been
aware of such problems and have issued strong warnings. Rhine and
Pratt (1957/1962) wrote: “With GESP and pure telepathy, precautions have
to be elaborate and have to be adapted to the special needs of the experimental
situation. This methodological problem is often taken too lightly;
as we have said, GESP is the hardest psi-test procedure to control adequately
against error, especially error due to deception.” (p. 37).
We should point out that we have no reason to think cheating actually took
place in the PEAR research. Dunne et al. (1989) noted that positive
effects come from a large portion of the subjects. However, according
to their Tables E and F, Subject 10 contributed 77 trials as percipient
and 167 as agent, for a total of 244 trials (i.e., over 70% of the formal
trials). Because the procedures allow deception by either percipient
or agent acting alone, the contribution of that subject should be considered.
If we remove Subject 10’s trials from the set, the z score drops
from 6.355 ( p = 1.04 x
10-10
) to 2.17 ( p = .015, one-tailed).3
Statistical Issues
Free-response ESP statistical issues are quite complex
and involve many subtleties. The reader unfamiliar with the topic
may wish to consult Utts (in press) for an overview as well as the other
references we cite. In this section we will give rather brief descriptions
of the problems as they relate to the PEAR analyses. Here we restrict
our discussion to use of PEAR’s preferred Method B for calculation of scores.
In the Appendix we describe an optimal-guessing strategy that could artifactually
inflate scoring for Method A. As we demonstrate, the potential inflation
is severe.
Stacking
The database contains instances of stacking, that is, a
single target with multiple responses (see Thouless and Brier, 1970, for
a dis-
__________
3 For purposes of the computation
we assumed, as did PEAR, that the trials were independent. We recognize
this to be an invalid assumption.
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cussion). Such responses cannot be considered statistically independent.
This problem has been recognized from the early card-guessing experiments
(e.g., Goodfellow, 1938), and Child (1978) has given a good illustration
of how it can affect a free-response situation. Random selection
of targets is necessary (but not sufficient) for statistical
independence. Dunne et al. (1989) report that 120 of the 336 formal
trials involved multiple percipients. They do give a breakdown of
results for trials with single and multiple percipients. However,
for the overall result, the 120 trials are considered to be individual
and independent; there appears to be no correction included for the nonindependence.
Dependence Due to Target Selection Method
For the “Instructed” trials, in which the target site is
randomly selected, it is stated that “the target is determined by random
selection, without replacement, from a pool of potential targets
prepared in advance” (emphasis added) (Dunne et al., 1989, p. 13).
The “without replacement” procedure determines that the trials are not
statistically independent, and this must be accounted for in the statistical
method. The PEAR analysis failed to take it into consideration.
In the Appendix we show that this and related flaws can result in a p
value incorrect by several orders of magnitude.
A further problem develops if the percipient is given
trial-by-trial feedback in a “without replacement” sampling regime (Stokes,
1981). As Kennedy (1979b) pointed out, the percipient might systematically
avoid describing features of previous targets. This can introduce
a severe artifact (for a discussion see Hyman, 1977, 1988). This
is a serious problem in the PEAR analysis because the mismatch distribution
is used to assess the significance of the correct matches. If a percipient
avoids descriptors in one trial based on feedback from previous trials,
then the mismatch scores could be artifactually deflated.
Target Pool Definition
Target pools with varying characteristics were used in
different series. In the case of a randomly selected target from
a prespecified pool, the subjects should not be able to infer the identity
of the target, but might have some idea about the range of targets in that
particular pool. For instance, they might know that the target possibilities
lie in the Princeton area and not, say, on the plains of
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North Dakota. Responses to the pools in the two areas may
be quite different and may reflect the available information. The
analyses conducted by PEAR often lump targets from a variety of pools together
for computing mismatches. Thus, in the analyses, responses are compared
with some targets that were not available for actual random selection for
that trial. This can introduce an artifact in the baseline.
PEAR’s Position
In the summer of 1988, the PEAR group was given a manuscript
written by Hansen which raised many of the points discussed in this paper.
Perhaps the Dunne et al. (1989) technical report was an attempt to address
those points as well as criticisms raised by Scott (1988). A primary
strategy of PEAR’s report was to compare subgroups. Sometimes this
was done against the global baseline distribution, and sometimes new baseline
distributions were created by mismatching target and response pairs within
the subgroups. For instance, they did evaluate the results of separate
agent-percipient pairs. However, such comparisons do not answer the
numerous problems outlined above. The difficulties are inherent in
the methodologies and statistical models they used.
The Dunne et al. (1989) technical report also contains
a number of invalid statistical arguments. For example, their Figure
1 and the accompanying discussion are designed to show that, if matched
scores are compared to local mismatch distributions, then encoding biases
cannot artifactually inflate the z scores. However, the whole
argument hinges on the assumption that biases are uniform within
a subset. This assumption was also invoked for use with a pseudo-data
simulation in an effort to justify the scoring procedure. Unless
a subset consists of a single trial there is no way to justify this assumption.
For instance, an agent-percipient pair might have some summer trials and
some winter trials, with different biases. May et al. (1990, p. 202)
also provide an illustration how biases can vary.
Discussion
The problems enumerated above are severe. For a number
of reasons it is most surprising that the research departs from usually
expected criteria. Jahn and Dunne seem to have been aware of criticisms
of earlier work for they say:
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The Journal of Parapsychology
Irrespective of the particulars,
this type of experiment has become popular in contemporary parapsychological
research because of its relatively high yield, low cost, and evident range
of possible practical applications. It has also become a target of
much critical commentary because of its high vulnerability to sloppy protocols
and data-processing techniques. The most frequently cited criticisms
include possibilities of inadvertent or deliberate sensory cuing of either
participant, inadequately randomized target selection practices, shared
conscious or subconscious preferences of the percipient and agent, and
faulty statistical treatment. (Jahn and Dunne, 1987, p. 157)
Ironically, the above-mentioned issues have not been
adequately recognized by PEAR in regard to their own program. Remote-viewing
research has been conducted for over 15 years and is thus not a recently
developed procedure in parapsychology. In new areas of investigation
in any science, one expects some deficiencies, but one also expects a steady
improvement of methods as the studies continue. The procedures and
methodological issues of remote viewing have received considerable attention
in the literature. The difficulties are easy and inexpensive to overcome
with correct experimental design.
Some might argue that if one compares the “flawed” segments
with the “unflawed” and no statistically significant difference is found,
then one need not worry about the flaws. Even if such a comparison
were contemplated, it would require a valid statistical baseline.
It is not clear whether any of the trials involved adequate randomization
(details are lacking in the reports), so we are unable to make legitimate
comparisons. Even if we could make such comparisons, the lack of
a statistically significant difference would not imply that a difference
didn’t exist. It could mean that the sample sizes were too small
to provide enough power to detect a difference; the number of “unflawed”
trials is likely to be small, and maybe even zero. (For a discussion
of statistical power and sample size in parapsychology see Utts 1988).
The deficiencies provide plausible mechanisms for the
significant findings. While the actual effects of the problems we
have outlined are too complex to fully evaluate, it is instructive to see
how much of an influence would be necessary to account for the observed
results.
The mean score for the universal mismatch distribution
was .5025, and for the actual formal trials it was .5447. How many
additional descriptors would have to be answered correctly, on average,
to account for the difference of .0422? Here we will make the
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invalid assumption that the fundamental statistical procedure of
PEAR is appropriate. PEAR’s descriptor weights are unknown to us,
but can probably be realistically approximated by deriving values from
Table C-1 (Dunne et al., 1983, p. 122). It can be easily shown that
the mean value of the denominator of the score is approximately 60.
Therefore, the difference of .0422 between mismatch and match scores represents
an approximate increase of 2.532 in the numerator. The average contribution
per correctly answered question is 2.00. Therefore, slightly better
than a one question average advantage per trial, due to inflation of the
matched scores or deflation of the mismatched scores, or a combination,
would account for the difference.
Conclusions
The PEAR remote-viewing experiments depart from commonly
accepted criteria for formal research in science. In fact, they are
undoubtedly some of the poorest quality ESP experiments published in many
years. The defects provide plausible alternative explanations.
There do not appear to be any methods available for proper statistical
evaluation of these experiments because of the way in which they were conducted.
APPENDIX
Consequences of an Inappropriate Statistical Model
Dunne et al. (1989, p. 13) specifically noted that targets
were selected without replacement. This has important consequences
for statistical analysis. It has been recognized for a long time
that the analysis must consider the dependence caused by the without-replacement
condition. In fact, Puthoff, Targ, and May (1981) even published
a reanalysis of some of the early SRI remote viewing-experiments so that
this dependence was taken into account. Other examples of appropriate
analyses can be seen in Markwick (1988) and Schlitz and Gruber (1980).
An additional problem arises because in constructing their
baseline distribution, PEAR did not include the diagonal elements of the
matrix (i.e., the scores resulting from the correctly matched targets and
responses). The failure to include these elements in the baseline
distribution can artifactually enhance significance levels, as we will
show.
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Table 1
Descriptors and Probabilities
Descriptor number
|
A priori probability
|
Optimal response
|
Probability of Being Correct
|
|
|
|
|
1
|
.397
|
N
|
.603
|
2
|
.215
|
N
|
.785
|
3
|
.486
|
N
|
.514
|
4
|
.589
|
Y
|
.589
|
5
|
.154
|
N
|
.846
|
6
|
.229
|
N
|
.771
|
7
|
.537
|
Y
|
.537
|
8
|
.458
|
N
|
.542
|
9
|
.621
|
Y
|
.621
|
10
|
.715
|
Y
|
.715
|
11
|
.710
|
Y
|
.710
|
12
|
.248
|
N
|
.752
|
13
|
.439
|
N
|
.561
|
14
|
.154
|
N
|
.846
|
15
|
.360
|
N
|
.640
|
16
|
.290
|
N
|
.710
|
17
|
.743
|
Y
|
.743
|
18
|
.650
|
Y
|
.650
|
19
|
.547
|
Y
|
.547
|
20
|
.706
|
Y
|
.706
|
21
|
.495
|
N
|
.505
|
22
|
.304
|
N
|
.696
|
23
|
.621
|
Y
|
.621
|
24
|
.206
|
N
|
.794
|
25
|
.266
|
N
|
.734
|
26
|
.477
|
N
|
.523
|
27
|
.421
|
N
|
.579
|
28
|
.612
|
Y
|
.612
|
29
|
.257
|
N
|
.743
|
30
|
.645
|
Y
|
.645
|
Expected Number of Correct Bits Using the
Optimal Guessing Strategy = 19.840
Score = 19.840/30 = .6613
___________________________________________
The consequences of these two problems can be
illustrated by examining the ratings matrix of Schlitz and Gruber (1980,
p. 311). Their correctly computed probability value, by a direct
count of permutations, was 4.7x10-6.
We can implement the PEAR method and form a distribution of the off-diagonal
elements. The mean of that distribution is 198.10 and the standard
deviation is 92.21. A z score can be calculated for each of
the 10 diagonal elements. The resulting composite z score
is 6.410 which corresponds to a p value of 7.28 x 10-11.
We grant that the distribution is not normal, but it can
be shown that the artifactual inflation of significance is not attributable
to non-
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normality. Fortunately we can compute an exact probability
value for a virtually equivalent statistical model (making the same false
assumption about appropriateness of the baseline distribution). The
sum of the 10 largest off-diagonal elements is less than the sum of the
diagonal elements. Conservatively, this results in a probability
of p = 80!10!/90! = 1.748 x
10-13; the corresponding normal approximation gives p
= 5.35 x 10-12.
As can be seen, in this case the PEAR method gives
a probability value incorrect by about five orders of magnitude.
The statistical method of PEAR is fundamentally flawed.
Optimal Guessing
In an article on deception, Hansen (1990, p. 52) mentioned
that an optimal-guessing strategy may allow a sophisticated form of cheating.
Even without conscious deception, some subjects might have a response pattern
which would naturally produce high scores. We will describe here
how such a strategy might be implemented. As mentioned earlier, PEAR
used five different formulas to calculate scores. We will illustrate
the optimal-guessing strategy with PEAR’s susceptible Method A. Tables
41 and 42 of Dunne et al. (1983) show that Method A tended to produce more
extreme p values than the other methods.
With Method A (Dunne et al., 1983, p. 12), a target descriptor
list is compared with that of the response, and the number of corresponding
matching bits is tallied; that is, if both lists give a positive (or negative)
response for a descriptor, the score is incremented by one; if they do
not match, the score is not increased. The resulting number is divided
by 30 (the total number of bits). Thus a score of .5 would be associated
with 15 bits that matched. Sixteen matching bits produce a score
of .533.
As described earlier, in order to establish a baseline,
Dunne et al. take targets and responses and pair all targets with mismatched
responses. For each pairing of a target and response, a score is
generated. These scores form a distribution. The mean and standard
deviation are computed. For any numeric score, a z score can
be directly calculated as previously described.
The optimal guessing strategy consists simply of saying
yes to descriptors with an a priori probability above .5 and no to descriptors
which have an a priori probability below .5. Table C-1 on page 122
of Dunne et al. (1983) gives the probability of each descriptor occurring
for a target.
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The expected score shown in Table 1 corresponds to a z
score of 1.047 as computed by the method used by Dunne et al. (1983): z
= (.6613 - .5510)/.1053 where the parameters are given on their page 92.
Using the optimal-guessing strategy, the expected
z score for one trial is 1.047. Thus, for an experiment with
100 trials, the expected z score would be 10.47. Please note
that the above analysis is an approximation that assumes independence among
items on the descriptor list.
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Princeton Arms North 1, Apt. 59
Cranbury, NJ 08512
Division of Statistics
University of California
Davis, CA 95616
5 Thorncroft
Hornchurch
Essex RM11 1EU
England
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Note: Table 1 printed in the Journal of Parapsychology was incomplete
due to error of the editors. It is correct here.
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