Are We Interested In Making ESP Function Strongly And Reliably?
A response to J.E. Kennedy
Charles T. Tart
Department of Psychology
University of California, Davis
Davis, California 95616
(1980, The Journal of the American Society for Psychical Research.)
Published in the Journal of the American Society for Psychical Research, Vol. 74, April 1980, pp. 210-222. The Contents of this document are Copyright © 1980 by the Journal of the American Society for Psychical Research
Abstract
The major problem in parapsychological research is the lack of reproducibility of strong manifestations of psi. Research on correlates of psi, when it usually manifests so weakly, is unlikely to be productive. The author's theory that provision of immediate feedback of results might allow learning of stronger and more stable psi behavior will, if true, allow a major break through in parapsychology. In the four years since the publication of data (the first Training Study, TS) supportive of the theory, no laboratory other than the author's has attempted to replicate the procedure, but a voluminous amount of largely speculative criticism of the first TS has been published. Are parapsychologists really interested in producing strong and reliable manifestation of psi?
Kennedy's paper centers on speculations that an apparently uniquely successful experimenter might have been incompetent or dishonest. No evidence really supports such speculations, nor do the data support the idea of that experimenter's uniqueness. Some perturbations in the target sequences analyzed by Kennedy are explicable as psychokinetic perturbations of the electronic random generator used, and, in any case, are of very small magnitude compared to the magnitude of psi (sometimes operating more than 10% of the time for the overall experiment, p<10-24, two- tailed) manifested in the first TS. Further experimental work will be more productive than endless speculation.
Article
In ordinary science, when a field has chronically been making little progress, news of possible breakthroughs is welcomed, and experimenters rush off to their laboratories to try the new techniques. Sometimes the apparent discoveries turn out to be artifactual, or cannot be replicated by others, but the basic attitude is to work personally with a potentially important discovery and, if the results are promising, to develop it. After several years of development of the discovery, it is usually understood more precisely and some original misinterpretations of its nature are corrected; but the important thing is that progress has been made.
I am by no means the only one who has long recognized that a (if not the) major problem in parapsychology is that psi phenomena are generally too weak and unreliable to be either demonstrated on demand or, more importantly, studied efficiently: thus one of the major problems in our field is to discover a way to make psi phenomena stronger and more reliable. I believe Kennedy and I are in full agreement on this need. My thinking some years ago (Tart, 1966) about the cause of this unreliability and weak level of manifestation led me to hypothesize that our common testing procedures were, in reality, extinction procedures. My review of the literature and my initial promising experiments led me to believe it likely that the provision of immediate feedback to preselected, talented percipients could eliminate the common decline/extinction we see and open up a possibility of learning significantly better psi performance. Judging from my experience in other branches of science, I expected that after publication of my and my colleagues initial results, plus the support from many other experiments reviewed in those publications (Tart, l975a; l976a), other parapsychologists would begin experimenting with immediate feedback training of talented percipients in their own laboratories. If my learning theory was correct there was a chance of a very high payoff from such experimentation and a breakthrough in our field; if my theory was wrong, only a little time would be wasted in a field that was not progressing anyway.
Kennedy states that my work has aroused considerable interest among Parapsychologists, but I have begun to wonder just what the interest is in. While feedback has been included as a somewhat peripheral variable in a number of studies, to date no one other than myself and my immediate colleagues has attempted to carry out an experiment that is at all a close replication of the highly successful procedures I described in 1975. Instead, the results of that first Training Study (TS) and the theory underlying it have been subjected to an enormous amount of criticism from within Parapsychology. Some of these criticisms struck me as raising valid questions, and my responses to them were useful for clarifying issues; many others have seemed invalid and trivial to me. This total lack of replication attempts, coupled with this intense criticism, is most surprising. Aren't parapsychologists interested in actually working with a technique that might promise a major breakthrough in our field? I recommend thoughtful reflection on this question to the reader, blended with a thorough reading of Eisenbud's (1979) recent provocative paper on resistance to psi by Parapsychologists. Given this context, let us now turn to Kennedy's paper.
Following an introduction in which he briefly describes comments on my application of learning theory to psi performance, Kennedy's paper has two major sections. The first section is speculation about ways in which the very high degree of apparent psi in my first TS might have been due to incompetence or deliberate dishonesty on the part of an apparently unique experimenter, Dr. Gaines Thomas. The second section is an exploration of some small departures from randomicity in target and response sequences and their possible consequences. We shall deal first with the question of Dr. Thomas' uniqueness as an experimenter and Kennedy's implications of possible incompetence or dishonesty.
Dr. Thomas' Uniqueness as an Experimenter?
In his opening abstract, Kennedy states that "highly significant results were obtained by only one experimenter" although he later qualifies this in the text to indicate he is only dealing with half of the first TS, the ten-choice trainer (TCT) results, and not the four-choice Aquarius results. Later he states that "no one in the final stage of either of Tart's two experiments has obtained convincing evidence for non-chance results with one of the ten-choice machines." I find it puzzling that Kennedy goes to such lengths to create an inaccurate picture. The first TS as a whole provided evidence for psi functioning and supported the learning theory application: since Kennedy purportedly addresses this whole issue, he cannot legitimately out half the data with no reason. Further, the publications Kennedy himself references contain data obviously contradicting his assertion that no one has obtained convincing evidence for non-chance results with one of the ten-choice trainers other than Dr. Thomas' percipients. Let us look at this in detail.
In the first TS, 10 percipients completed the final training phase on the TCT and 15 on the Aquarius trainer. Five percipients, run by four different experimenters other than Dr. Thomas, showed psi-hitting on the Aquarius at the p < .02, two- tailed level or better, one of these at the 10-4 level. Additionally, two percipients showed significant psi-missing (p < .05, two- tailed) on the Aquarius, with two more experimenters other than Dr. Thomas. Thus an accurate overall assessment of the first TS is that seven of the nine experimenters (including Dr. Thomas) had at least one percipient who showed statistically significant signs of psi on one or the other feedback training machine. These data are obvious from Tables 6 and 8 in the references Kennedy cites (Tart, l975a, 1976a).
Kennedy seems to have been misled by the very high significance levels of Dr. Thomas' significant percipients, which ranged from two-tailed ps of 4 x 10-5 to 4 x l0-28. As I pointed out several years ago (Tart, 1977c, cited by Kennedy), the same frequency of psi functioning on a ten machine will yield much higher significance levels than on a four-choice machine. When the psi coefficients (Timm, 1973) of all significant percipients are examined, Dr. Thomas' percipients' distribution (.16, .12, .07, .07, and .06) shows considerable overlap with those of the other experimenters' psi-hitting percipients (.10, .08, .08, .07, and .06). Other examples of overlap were presented in the original publications (Tart, l975a, p. 79; l976a, p. 82). Moreover, the significant negative correlation between real-time hitting and + 1 future hitting found for the TCT percipients in the first TS (depending heavily on the results of Dr. Thomas' percipients) was independently replicated with different experimenters and percipients in the second TS (Tart, l977a, 1978b; Tart, Puthoff, and Targ, 1979). Thus, while Dr. Thomas was quantitatively more successful than many other successful experimenters in the first TS, the data fall short of supporting Kennedy's characterization of him as unique.
As to Kennedy's statement that no percipient other than those of Dr. Thomas has ever shown convincing evidence" for non- chance results with one of the ten-choice machines, I can only wonder what Kennedy's personal criterion of "convincing" is. The usual scientific criterion is hitting or missing at the .05 level or better of significance under controlled conditions. Chapter 3 of the report on he first TS (Tart, 1975a, l976a) describes a pilot study on the TCT in which one percipient, run by a graduate student, showed a much higher psi coefficient than any of Dr. Thomas' percipients did, as well as one percipient showing significant (p<.01, two-tailed) psi missing. Kennedy cites the report on the results of the second TS (Tart, Palmer, and Redington, l979a), with a more automated version of the TCT, ADEPT, that eliminated most of the problems Kennedy worries about, but he seems to forget that two of the ten percipients in that study showed statistical significance, one for psi-hitting, one for psi-missing. Kennedy also cites other references (Tart, l977a, 1978b) in which I report a study with Ingo Swann on ADEPT, where psi-hitting was significant. Thus four other experimenters have obtained significant results on ten-choice liners, contrary to Kennedy's assertions. To put this in appropriate sampling perspective, in the published data cited by Kennedy, percipients other than those in the first TS were tested on ten-choice devices, and the exact binomial probability of five or more hitting at the .05 level or less is .002, two-tailed. This denial of published data represents highly selective perception.
Trustworthiness
Kennedy is legitimately concerned with the trustworthi ness of the various people involved in psi studies. To deal with this, he sets up a hierarchy of trustworthiness. At the bottom of his hierarchy, the experimental percipients are not to be trusted at all, and experiments should be designed so they cannot cheat even if they try. Next up in the hierarchy are undergraduate students and "hired-hand experimenters," neither of whom are considered very trustworthy. Professionals are third up in his hierarchy, and Kennedy apparently feels we must trust them sometimes for lack of any choice, but they certainly can be incompetent or cheat, so the fourth level is two-experimenter designs where one experimenter can watch the other. Implicitly, there is a fifth level of multiple experimenters watching one another, even though Kennedy feels that there is no absolutely fraud-proof experiment.
Since Gaines Thomas was a college senior at the time he served as an experimenter, he is quite low on Kennedy's trustworthiness hierarchy, and so Kennedy speculates about a variety of methods whereby Thomas, either through incompetence in following instructions or deliberate violation of instructions, could have produced high hit scores without any ESP being involved. These methods include selecting targets he thought a percipient would be likely to choose instead of following the instructions of the random number generator, or changing a target in mid-trial to fit in with the momentary response bias of a percipient.
Since his work as an experimenter in my first TS, Gaines Thomas went on to get his Ph.D. in clinical psychology, and is currently employed in that profession. In terms of Kennedy's own status hierarchy, Dr. Thomas' professional position and possession of a Ph.D. now give Thomas equal or higher status in the trustworthiness hierarchy than that of Kennedy. Thus Dr. Thomas comments on Kennedy's speculations, in terms of Kennedy's own hierarchy, should be given as high or higher weight as Kennedy's speculations. Dr. Thomas reviewed an earlier draft of Kennedy's paper, and dismissed Kennedy's speculations as groundless and insulting. The relevant parts of Dr. Thomas' letter to me are a follows:
"As to my practice of setting all of the switches except for the correct one and the accurate recording of hits, on the last trial each run I set all of the switches except the correct one in order to signal the subject that the run was completed and that he/she could relax. I was well aware that the hit counter would indicate one more hit than was correct in the event that the subject had made an error in his last trial, or, in the case of the subject making a hit on [his] last trial, that the hit counter would indicate one less than the actual number of hits. I was quite careful about making the correct recording of hits, given my way of ending each run.
In [regard] to the question as to whether an inexperienced experimenter could have rejected the first outcome of the RNG thinking that any target generated by the RNG must be random, I was well aware that the randomicity would be [affected] by one not accepting each target that was generated by the RNG, and I accepted, as a matter of standard procedure, each target as it was presented by the RNG. I made no attempt to arbitrarily select targets based on the subjects' response habits.
As far as whether or not I manipulated the targets in order to increase the number of the subjects' hits, I can only say that I made no such attempt and I am angered at what appeared to be his insinuation that I was dishonest or inept in my conducting the experiment and recording the results" (Thomas, personal communication, May 20, 1979).
I made Dr. Thomas' letter available to Kennedy before his final preparation of his manuscript. In spite of the fact that Dr. Thomas indicated that Kennedy's speculations have no foundation, Kennedy has chosen to present them anyway. I believe that Kennedy feels the small variations from pure randomicity in the experimental data lend some sort of support to his speculations, but, as I have argued in several other places (Tart, l977c, l978c, 1979a, l979b), these variations in randomicity are trivial compared to the magnitude of psi seen in the experiment; they may represent PK variations, and the trans-temporal inhibition effect is incompatible with an experimenter incompetence or fraud hy pothesis.
Let me now deal in some detail with Kennedy's analyses of my data.
PK Action on thre Random Generator
As I have suggested elsewhere (Tart, 1978b, l978c, l979a; Tart, Puthoff, and Targ, 1979), I suspect that the high-level results of the first TS were due to a combination of both ESP and PK. The percipients' task was to score high, and the experimenter also wished the percipient to score high. Scoring high could be done by a) percipients using clairvoyance, or telepathy to read the experimenter's mind and so push the right button; or (b) percipients using PK to influence the random number generator (RNG) to change to their desired (consciously or unconsciously) target on particular trials; or (c) the experimenter using PK to influence the RNG to come up with targets that are either likely ones for the percipients, given the experimenter's estimate of their biases, or specific responses precognized the experimenter. I have thought about this possible mixture of ESP and PK for several years in an attempt to try to see how to analyze the separate components, but without success. Kennedy proposes that "the PK hypothesis would be supported by verifying that there are non-random patterns in the target data and that the patterns interact with the subject's response habits in ways that produce hits." While I agree with this in principle, in practice we have no independent measure of all of the percipients' response habits, only a measure taken when they were actually responding to targets. Thus the "response habits" we single out from the data could simply be an ESP following of momentary variations in the RNG pattern rather than generalized response habits of the percipients. Therefore it is not clear to me how the PK factor can be quantitatively assessed. It is also well to bear in mind that the size of the various non-random effects in the RNG are quite small compared with the percipients' hit rate.
The only genuine response habit that is widespread among percipients that I feel can be assessed relatively independently of the particular results is their tendency not to respond with the same number as the previous target was; i.e., to produce very large, negative - 1 temporal deviations. I have found it to be an almost universal phenomenon over several times as many percipients as participated in the first TS, including many percipients not showing any significant hitting scores (so that their response patterns were presumably not influenced by ESP). We shall return to this response pattern below.
Temporal Displacement Patterns
Kennedy's discussion of the + 1 future displacement effect found in my data, and attributed by me to transtemporal inhibition (Tart, 1977a, l978b; Tart, Puthoff, and Targ, 1979), is marred by his incorrect understanding of the theory of trans-temporal inhibition. For example, Kennedy states the rationale for the trans-temporal inhibition hypothesis seems questionable "since, if the targets are independent, any information (be it positive or negative about past or future targets) would be of no value in discerning the current target. In fact, it would seem that responding to other targets could only interfere with ESP performance." The rational for trans-temporal inhibition is not that percipients desire to respond to future and past targets while they are also trying respond to a present-time target, but that this kind of responding an inherent feature of the lower spatial and temporal localization of the psi process per se. It does indeed interfere with responding to the present time target, and that is the whole point of the theory. Readers interested in the theory should refer back to my original publications for clarification.
Kennedy speculates that the + 1 future displacement missing could indicate that the targets were influenced to avoid the previous calls, this being coupled with percipients' known avoidance of calling doubles to a significant extent. Reconcludes that this type of effect would increase the likelihood of getting direct hits: elsewhere, in material cited by Kennedy (Tart, 1978b, e.g.), I have already analyzed this possibility for the even worse case of no XX doublets and shown that a corrected analysis of direct-hitting results is still enormously significant (p< 10-13, two-tailed). A psychokinetic effect to make the next target not correspond to the present-time call would indeed produce +1 future missing (but not real-time hitting), but why either experimenters or percipients would unconsciously undertake this activity to a large extent in two separate experiments, plus other unpublished data I have collected, is not clear.
Effects of Lack of Target Doublets
Kennedy and others have made much of the lack of XX target doublets for all of the first TS experimenters, and the slightly greater lack for Dr. Thomas. Kennedy reports my hypothesis (Tart, 1978b; Tart, Puthoff, and Targ, 1979) that this resulted from faulty experimenter operation of the RNG push button; although he states that while this speculation sounds quite plausible, it apparently has not been verified by asking the experimenters about it. If Kennedy would read the source he quotes (Tart, 1978b, p. 220) more carefully he would see that the hypothesis was developed from "questioning one of the experimenters...." Several other experimenters have since confirmed it.
In terms of the effects of this lack of XX doublets, I have previously presented an extreme-case analysis where there would be no XX doublets at all, and the probability of a hit would be about one-ninth instead of one-tenth. Re-evaluating the results of the experiment with this new probability makes only trivial changes in the level of results (Tart, 1978b; Tart, Puthoff, and Targ, 1979).
Kennedy further speculates that this lack of XX doublets interacting with the response biases of the percipients would produce higher levels of hits and the displacement effects which I have interpreted as trans-temporal inhibition. I find Kennedy's mathematical arguments somewhat difficult to follow at times and of questionable validity. Rather than engage in extended mathematical speculations with little supporting data, I have empirically evaluated the effect.
In connection with more detailed analyses of trans-temporal inhibition effects, I have carried out a number of computer simulations to empirically evaluate the effects of various kinds of deviations from randomicity in both target and response sequences on the production of direct hits and +1 temporal displacement effects. For the cases of interest here, the target distributions were generated by shaping the output of a computer RNG program (at random intervals) so that XX target doublets occurred on the average only .035 of the time, instead of the .10 of the time we would expect the RNG had functioned perfectly. This is a good approximation of the proportion of XX target doublets that resulted from experimenter error in operation of the push button of the RNG in the fin TS. Further, response distributions were independently taken from the computer RNG, but shaped (at random intervals) to approximate the common response characteristics of almost all percipients tested to date (from the second and third TSs and various pilot studies, as well as from the first TS), namely, avoidance of calling the previous target digit quite strongly (.035 of the time instead the .10 that would be expected from a purely random source), well as avoidance of the second-to-last target digit fairly strong (.054 of the time, instead of the .10 expected from a random source). That is, I built in the common human misunderstanding that random numbers don't repeat," and it was built in to the same extent as it usually appeared in my percipients. Various levels of direct hits were then created in different runs by doctoring the response distribution at random intervals, so that, over various simulations, average hit rates of 10% (chance, no doctoring), 15%, 20%, and 25% were produced. Fifty runs of 500 trials each we simulated under these various conditions.
The results are not worth presenting in detail, as they only show that the effects are trivial in the present case. Adding these tar and response biases to otherwise random outputs did not produce any significant direct hitting (Z = .74), even with these bias cumulating their effect over 50 simulated percipients, rather than the 10 who participated in the first TS. Adding various levels simulated hits did not produce any significant correlation between direct hitting scores and + 1 temporal hitting scores, in contrast the significant negative correlations found independently in both first and second TS. Kennedy's speculations about the effects these slight deviations from randomicity in target and response sequences thus have no real empirical consequences in these data.
The Strategy Boundness Measure
Kennedy, citing Stanford (1978), dwells on the mathematical invalidity of the strategy boundness measure presented in a paper of mine (Tart, 1978b). Why both Kennedy and Stanford dwell on the invalidity of this measure at length, when I myself pointed out its invalidity in an early report, is puzzling to me. As I said at the time, the mathematical procedure lacks validity, in spite of assurance from mathematicians that it was valid, but the concept of strategy boundness is quite intriguing and should be investigated in its own right (Tart, l978b, p. 238). Various informal observations have now further strengthened my conviction that the presence of strong response habits like strategy boundness in a percipient is definitely detrimental to psi functioning.
Distribution of the Targets Relative to the Previous Target
I am quite intrigued with Kennedy's analysis showing uneven spatial displacement of targets relative to the previous target. As with other displacement effects, the effect is quite small in magnitude compared to the overall ESP results for the successful percipients. I suspect it demonstrates the PK component involved in the experiment. A percipient bias to avoid pushing a response button in the immediate vicinity of where the last target was could be taken advantage of by either the percipient or the experimenter unconsciously PKing the generator occasionally to produce a number substantially different (further away from) the previous target number. This idea is speculative, however, for the reasons discussed above about the difficulties of separating PK and ESP components in the scoring.
Mathematical Inference Strategies
Kennedy has again raised a question, originally raised by Gatlin (1979), as to whether percipients could have used some sort of mathematical inference strategy to artifactually score hits from the small departures from randomicity found in some of the first TS target sequences. This possibility has already been discussed by me at length (Tart, l978c, l979a, l979b), so I will touch only on highlights in the limited space allowed me here.
First, speculations about possible mathematical inference strategies remain just that until a strategy is specified in operational form (mathematics is highly specifiable) and empirically tested against the data. Kennedy's testing of some of his hypotheses about mathematical inference strategies is commendable, and I hope he will provide technical details on these in some future publication, as this is an interesting area in and of itself. A detailed report of results with my and Eugene Dronek's Probabilistic Predictor Program (PPP), presented at the 1979 Parapsychological Association convention, has now been submitted for publication. As Kennedy knows from a copy of this paper sent to him some time ago, the PPP, while scoring significantly above chance on a few target (and most response) sequences from the first TS, does poorly compared to the actual percipients. Judging from the brief figures Kennedy presents, the PPP is generally more powerful than his estimator program, but detailed comparisons will have to await future publications of details.
Second, and quite important, there are several major effects to be accounted for in the first TS data, most notably the high direct hit rate, but also the extremely significant missing on the + 1 future target and the high and significant correlation of this missing with direct hitting, a correlation independently confirmed in the second TS. The PPP does not generate significant + 1 missing, nor this correlation. For any mathematical inference hypothesis to be strongly supported, it must not only generate high direct hit rates, comparable to those of the actual percipients; it must also generate very significant + 1 future missing which is correlated with direct hit rate. Although I have communicated this requirement to Kennedy during the preparation of his paper, he has not reported any data as to whether his inference strategies fulfill this requirement. so it is difficult to know whether to take his results very seriously
Third, Kennedy recognizes, as we discussed in correspondence, that when he predicts targets subjectively rather than using specified mathematical inference strategy, we cannot distinguish whether he is using such a rational strategy or ESP. While we prefer to believe in a mathematical interpretation, this is not a scientific interpretation until he can specify, operationalize, and empirically demonstrate the efficacy of such a strategy.
The above arguments have been presented in detail before in the cited references.
Conclusion
As I have stated in earlier responses (Tart, 1976b, l977c, 1978c) to various criticisms that have been made of the first TS, I regard the net outcome of these exchanges as further strengthening the hypothesis that an extremely significant amount of ESP was generated in the first TS, and I believe the displacement effects that I have explained under the hypothesis of trans- temporal inhibition may constitute an important insight into the mechanism whereby psi is used.
I would close by stressing that the first TS was never intended as a "fool proof" experiment showing irrefutable proof for the existence of ESP and irrefutable proof that immediate feedback inhibits decline and can lead to learning. No first experiment in any area could possibly meet such criteria and, with the use of hindsight, it is doubtful if any one experiment will ever meet such criteria. Of course there are various methodological improvements that can be made in future studies: Kennedy's suggestions repeat points I made in the original reports. The important point is that the claims for the potential efficacy of immediate feedback training might be true: if they are, exploration of immediate feedback training and mastering an understanding of relevant parameters could lead to a major break through in reliable control of psi. I suggest that colleagues who are interested in bringing psi under reliable control could better spend their time carrying out their own experiments in this area than further re-analysis, ad infinitum, of minor effects in the first TS.
Department of Psychology
University of California, Davis
Davis, California 95616
End Notes
I wish to thank Arthur Hastings, John Palmer. and Russell Targ for their helpful comments in preparing this paper.
I do not have space to comment on Kennedy's description of my theory except to note that it is not accurate in some places; the interested reader should therefore refer back to my original presentations (Tart, 1966, 197)a, 1976a, 1977b).
I am indebted to Eric Weaver, who programmed these simulations and analyses on the Prime computer at SRI International.
The largest deviation in Kennedy's Table 2 is for the -8 (counter-clockwise) position, relative to the previous target. This is a proportion of .114, instead of the .100 expected by chance. If we make the unlikely assumption that the percipients all had a guessing habit that made them tend to call eight positions counter-clockwise from the previous target, this would give them a .114 hit rate instead of the expected .100 hit rate. The least significant of Dr. Thomas' percipients, however, showed a hit rate of .156, four times as large an effect.
References
EISENBUD, J. How to make things null and void. (An essay-review of Brian Inglis' Natural and Supernatural.) Journal of Parapsy chology, 1979, 43, 140-152.
TART, C. T. Card guessing tests: Learning paradigm or extinction paradigm? Journal of the American Society for Psychical Research, 1966, 60, 46-55.
TART, C. T. Correspondence: Comments on the critical exchange between Drs. Stanford and Tart. Dr. Tart's reply to Dr. Gatlin. Journal of the American Society for Psychical Research, 1978, 72, 81-87. (c)
TART, C. T. Randomicity, predictability, and mathematical infer ence strategies in ESP feedback experiments: Discussion of Dr. Gatlin's paper. Journal of the American Society for Psychical Research, 1979, 73, 44-60. (a)
[Note 5 To save space, references already cited in the previous paper are not repeated in this list. Ed.]
TART, C. T. Could mathematical inference strategies have inflated scoring in the first feedback training study? In W. G. Roll (Ed.), Research in Parapsychology 1978. Metuchen, N. J.: Scare crow Press, 1979. Pp. 128-129. (b)
TART, C. T., AND DRONEK, E. Trying to profit from nonrandomici ty in ESP target sequences: Initial explorations with the proba bilistic predictor program. Paper presented at the Twenty-Second Annual Convention of the Parapsychological Association, Moraga, California, August, 1979.
TART, C. T., PUTHOFF, H. E., AND TARG, R. (EDS.). Mind at Large: Institute of Electrical and Electronic Engineers Symposia on Extrasensory Perception. New York: Praeger, 1979.
TlMM, U. The measurement of psi. Journal of the American Society for Psychical Research, 1973, 67, 282-294.
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