Do we need a new psychical research ?

by Susan Blackmore

Published in the Journal of the Society for Psychical Research, 55, 49-59

Text of a lecture delivered to the Society on 12 March 1987.


Psychical research has failed to establish itself as a respected area of scientific inquiry, to resolve its many controversies or to contribute to our understanding of human nature. The progress of psychical research is reviewed with particular reference to the six topics of the original research committees of the SPR. Some of these topics were dropped while others went on to form the basis of modern psychical research and parapsychology. But although research techniques have greatly improved, the same questions are still being asked after one hundred years.

The concept of psi, with its negative definition, is to blame. The nature of the phenomena, such as apparitions, altered states, OBEs, NDEs and lucid dreams is destroyed in an exclusive search for psi. The founders of psychical research were concerned about the nature of human experience and suffering, and the place of man in the cosmos but they failed to establish a science which would deal adequately with these questions. We might still do so. We need the courage and aspirations of our founders, but we need to learn from their mistakes and begin again in a psychical research without psi.

Psychical research has failed. It has failed not only to fulfil the hopes of its founders of one hundred years ago, but it has failed to establish itself as a respected area of scientific enquiry and, more generally, to contribute substantially to our understanding of human nature.

I would like here to do three things. First I shall defend my view that psychical research has failed. Next I shall ask, if it is such a failure, should we abandon it? or do we need a new psychical research? Finally (and as you might guess I shall not argue for abandoning our subject) I shall ask just what kind of new psychical research there could be.

So first, has our subject really failed so dismally? A dispassionate look at our Society’s activities suggests that it has not lived up to its early ambitions. We do not hold’crowded lectures in our own well appointed lecture theatre, nor are we established in a University department. Also there are not many of us. This year, in 1987, the SPR has 830 members; not an enormous increase over the 700 or so who were members in 1887. Size, you may protest, is not everything. No indeed it is not, but what else could we boast? As a Society we are not very well known and are still considered as a fringe group, accorded rather little respect or academic standing. And as for research—most of us do not do very much and there is pitifully little money with which to encourage more.

Compare this state of affairs with that of one hundred years ago. In 1887 SPR Council Members and Honorary Members included a past and a future Prime Minister; eight Fellows of the Royal Society, two bishops and some outstanding literary figures of the day (Gauld 1968). These people had chosen to align themselves with what they saw as an unpopular, but important, subject. Indeed Gladstone once declared it ‘The most important work, which is being done in the world. By far the most important.’ (Gauld 1968, p. 140). Would anyone say that of Psychical Research today?

Frederick Myers, one of the greatest contributors to early Psychical Research, described ‘The consciousness that the hour at last had come; that the world-old secret was opening out to mortal view; that the first carrier pigeon had swooped into this fastness of beleaguered men’ (Gauld 1968, p. 149).

But what became of that first carrier pigeon? Is it still flying around here waiting to impart its message? Did anyone listen to what it had to say?

Certainly the poor pigeon failed to found a great psychical research. So how and why has Psychical Research failed to live up to those high hopes?

To say that it has failed implies that we have some idea of what success might have been. So let us imagine we are living one hundred years ago. How might wehave expected our subject to progress?

I suppose we might imagine something like this:—It would begin by defining its subject area; it would check on the supposed phenomena to see which were valid and which not; and then proceed to develop experimental methods for exploring their characteristics and concomitants, then theories to account for the phenomena and finally techniques for a relevant technology.

Judged against such an ambitious programme psychical research has not done too well. It could even be argued that the subject never got off the ground in the first two objectives—defining its subject area and confirming the existence of the phenomena.

This was, I suggest, not for want of trying. At the meeting in 1882 at which the SPR was formally constituted, its stated aim was ‘to investigate that large body of debatable phenomena designated by such terms as mesmeric, psychical and spiritualistic’.’ Now these are somewhat vaguely conceived topics but we should not perhaps be unrealistic. After all physics did not begin with a clearly defined area of study, nor did chemistry or biology. Indeed, if biology is defined as the study of living things, the problem of distinguishing the living from the non-living makes it clear that definitions are rather hard. However, Psychical Research very soon struck a problem peculiar to itself; and one which is still with it today.

In the very first issue of the Proceedings the objects of the Society are laid out. This document mentions the ‘remarkable phenomena, which are prima facie inexplicable on any generally recognised hypothesis, and which, if incontestably established, would be of the highest possible value’.’ This was obviously the precursor of our more familiar aims and objectives printed in every issue of our Journal today; ‘to examine without prejudice or prepossession and in a scientific spirit those faculties of man, real or supposed, which appear to be inexplicable on any generally recognised hypothesis’.

The problem is, as has so often been pointed out, the negative definition. To qualify as subjects for psychical research, phenomena must be inexplicable. This problem was never resolved over the years. The negative was never converted into a positive. In the 1930s the new parapsychology was launched by the Rhines, in Durham, North Carolina. They hoped to have a more scientific approach and made many advances in operationalising their terms and developing new experimental methods. However parapsychology is defined as ‘The branch of science that deals with psi communication, i.e., behavioural or personal exchanges with the environment which are extrasensorimotor – not dependent on the senses and muscles’ (Journal of Parapsychology)—another negative definition.

You may wonder whether this is really such a serious problem but I think it is. At the level of individual research it means that the motivation of the psychical researcher who hopes to find psi, has to be oriented not towards positive study of the phenomena, but at least in part to looking for (and eliminating) alternatives. The better the research rules out these alternatives the more convincing it will be to sceptics, but the less likely it is to demonstrate the ‘inexplicable’. At the institutional level it means that the subject is ever shrinking. Edwin Boring most cogently described it when he said ‘That failure is success in psychic research is a consequence of the fact that ESP is negatively defined’ (Boring 1966, p. xiv).

When any phenomenon is successfully accounted for it ceases to fall within the negative definition. So every scientific success is a loss to psychical research. And what would normally be considered failure—that is failing to find any explanation—keeps phenomena within the field and so is success, of a kind, for psychical research. We are thus committed to an ever-shrinking subject area. So far that shrinkage has not stopped and we have to ask whether it will stop before there is nothing left.

But surely, we might protest, definitions are not so important. We know what we mean by psychic phenomena, even if we can’t define them. So let’s get on to the second stage and investigate them.

I think this is what our founders tried to do. They accepted the many problems and set about making a list of the phenomena they wanted to tackle.

In 1882, in that same statement of objectives, the first Council listed six committees which it had appointed to begin research. They soon became known as the committees on thought-reading, mesmerism, Reichenbach, apparitions and haunted houses, physical phenomena and lastly the literary committee. Let us briefly consider what happened to these six topics.

The first committee, on thought transference, is in many ways the most relevant to today’s problems. Its work began well. Barrett, Gurney and Myers explained the dangers which faced them in investigating the phenomena.

‘Wild hypotheses as to how they happen are confronted with equally wild assertions that they cannot happen at all’ (Barrett el al. 1882). Of the two, they concluded, the assumption of a priori impossibility was the most to be deprecated. And so they set about examining the fact of transmission before worrying about the medium.

They published their first report in the first issue of the new Proceedings, describing several ‘experiments’ including those in which the subjects were the five daughters of a clergyman called Mr. Creery. Typically someone thought of a name, or a playing card, or a familiar household object, and the girls could apparently guess, almost always correctly, what had been chosen. The authors discussed muscle reading and involuntary guidance and concluded that these could not be responsible for the impressive results. It is interesting that right at the start they point out that the word ‘thought-reading’ was used only as a ‘popular and provisional description, and is in no way intended to exclude an explanation resting on a physical basis’ (Barrett el al. 1882, p. 33).

So the enterprise began well, with a determination to rule out obvious errors, an open-minded attempt to test whether the phenomena really did exist and an eye to possible theories for the future. But I should add (and I shall return to this later) that it was fed by a hope that the phenomena would prove to be real and would, in their words, ‘necessitate a modification of that general view of the relation of mind to matter to which modern science has long been gravitating’ (Barrett et al. 1882, p. 34).

All did not continue so smoothly, however. The powers of the Creery sisters began to wane and very soon they were caught using a simple code. The members of the committee argued about whether such impressive results could have been obtained and whether the results would have gradually declined in the way they did had such a primitive code been used, and what weight should now be apportioned to the earlier results.

It is a familiar argument. In the succeeding hundred years we have met it again and again, in different forms. If we take a quick flight through those hundred years we can see in almost every decade a new method or experiment which was, for a longer or shorter period, the latest hope for incontestable evidence for thought transference or telepathy.

For many years the experiments with Smith and Blackburn were taken as watertight evidence for thought transference, until in 1911 Blackburn ‘confessed’ that they had cheated (Blackburn 1985). When Smith denied this some people chose to believe him. Then there were Coover’s (1917) apparently unsuccessful experiments, which were later reinterpreted as having been successful. Soon came the Rhines’ pioneering experiments of the 1930s and 1940s (Rhine 1934). The initial value of these was later challenged (e.g. Hansel 1966) but in the 1950s the research of Soal with his star subject, Basil Shackleton, became prominent (Soal and Bateman 1954). Although there were many who doubted their validity, these results were widely accepted as evidence for telepathy for thirty years. That is until the investigations of Markwick in 1978 (see also Markwick 1985). The 1960s saw the rise of dream telepathy research in which it seemed that the elusive phenomena might more easily be captured during altered states (Ullman, Krippner and Vaughn  1973) but this too proved ultimately unreplicable and was abandoned. Then came Geller and we were back to the old argument about ‘once a cheat always a cheat?’.

Finally in the 1970s the ganzfeld was hailed as the latest in a long line of ‘repeatable’ experiments. Then during the past few years Ray Hyman (1985) and Charles Honorton (1985) initiated the ‘Ganzfeld Debate’ and with others are still arguing out all the issues. While many are still convinced by the overall evidence from the ganzfeld, numerous experimental flaws have been pointed out.

Moreover most of the evidence is provided by just two researchers, Honorton and Sargent and Sargent’s work has recently been called into question (Blackmore 1987). Undoubtedly there will be further research paradigms to replace this one but if history repeats itself they will only have ten or fifteen years in which they appear convincing.

All of this research can be seen as starting from the work on thought transference, but what do we make of the evidence now? Did the Creery sisters always cheat or only sometimes? And what of Soal, or Geller? We can see that right from the start psychical research fell into this problem. It was always having to judge evidence retrospectively—to decide whether something was or was not the inexplicable phenomenon they were after. And at any time thereafter newer and better explanations might be offered.

Fundamentally this is yet again a problem of negative definitions. For if one could positively demonstrate the operation of thought transference, by some tell-tale sign, or characteristic, then we could see whether it occurred on any particular occasion and so end the argument and the negative definition.

This approach was tried much later in the search for ‘the fingerprints of psi’. These might include such pointers as the decline effect, differential effects or expectation effects. From these, Rhine argued, one could deduce that psi was at work, even though the overall results might not be very strong, or even significant. This move might have led to real progress—if it had genuinely provided a way of recognizing the action of psi. However, like so many other well-intentioned approaches in this subject, it ultimately failed. Positional effects were hard to find, and even harder to distinguish from chance fluctuations. Also such effects can easily come about in alternative ways. For example the sheep/goat effect may be expected to appear in badly controlled experiments because believers in psi would have more motivation to use any available cues than non-believers. Non-believers might even be motivated to depress their scores artifactually. It seems that psi, if it exists, has no easily measurable fingers.We cannot tell exactly when it is operating and are therefore led, time and again, into the same old arguments.

Of course other things have changed. In a sense the early psychical researchers did not want to find evidence for thought-reading. They were much more interested in finding evidence for survival after death and the possibility of thought-reading made much of the evidence for survival potentially only evidence for communication between the living.

Later on Rhine took a further step in arguing that telepathy, as it had quickly come to be known, was actually an untestable hypothesis. The Rhines used the term extrasensory perception—not so different from the Committee’s own term ‘supersensuous perception’. And they distinguished telepathy, clairvoyance and precognition. However, once they had argued for the existence of clairvoyance it was a small step to arguing that all cases of telepathy could actually be clairvoyance in disguise. And so Rhine stopped talking about telepathy and referred to G.E.S.P. for conditions which would allow either. This was despite the fact that then, as now, telepathy seems the most plausible form of ESP and is the most widely believed in.

The development of these terms appeared constructive, but I would argue that it only made the basic problems worse. Evidence for survival is impossible to find if you  can always  put  it  down  to  GESP.  Testing  alternative  theories  of out-of-body experiences, near-death experiences, or apparitions or hauntings is impossible if every bit of evidence might be interpreted as clairvoyance. The super-ESP hypothesis is a direct consequence of negatively defined, untestable concepts and leads only to the dead-end in which we find ourselves.

So where did the research on thought transference ultimately lead? There is no doubt at all that the experimental techniques and use of statistics have greatly progressed. But the basic problems have not gone away. However, much more telling, I believe, is to look at the fundamental research questions which were being asked. We can quickly see that they have not changed at all. From the Creery’s to the ganzfeld the essential question is the same—Can information be transmitted from one person to another without the use of the recognized senses? That question has neither been answered, nor has it changed in one hundred years of research. In Lakatos’ (1978) terms there has been no progressive problemshift at all. And the fate of unprogressive research programmes is ultimately to be abandoned.

So the hopes of Barrett, Gurney and Myers have not been fulfilled. In one hundred years, research has never overcome the problems of definition nor progressed from, in their terms, ‘inquiring into the fact of transit’ to determining the medium. We are still utterly ignorant of what, if anything, we have to explain.

The second committee was that on mesmerism. In their first report, published in 1883, the committee state ‘the main cause of the increasing incredulity and contempt shewn towards mesmerism, as such, has been, not an error, but a truth, or at least a partial truth,—the discovery, namely, of a real means of explaining many of the facts, without resorting to any “mesmeric” hypothesis’ (Barrett et al. 1883, p. 218). Those which could be explained were labelled hypnotic and the more far-fetched mesmeric. The Committee were at that time open-minded as to whether they would find any truly ‘mesmeric’ effects, but as time progressed it became more and more evident that they would not. The study of hypnosis continued within psychical research as a method of eliciting psychical effects. For example mediums were hypnotized and asked to project themselves to a distant room, or to smell substances at a distance, or feel pin pricks made in the air some feet away from their bodies (e.g. Blackmore 1982). More recently have been experiments using hypnosis to elicit psi. Indeed Honorton has argued that overall the evidence suggests that hypnotized subjects perform better at ESP tasks than non-hypnotised ones. However, research into hypnosis itself has been carried out by psychologists, psychiatrists, and medical researchers, not by psychical researchers. And of mesmerism nothing has been heard for a long time.

The third committee was to investigate the experiments of Baron Reichenbach, who claimed to have demonstrated the existence of a ‘magnetic light’ visible around magnets and the human body and suggested an ‘odic force’ to account for it. The committee began with careful experiments and corresponded with physicists who suggested alternative explanations for the lights seen (Barrett et al. 1883). The Odic force was relatively short lived, and although similar ideas appeared in later studies, for example of the aura, this whole area was more or less dropped from psychical research.

The fourth committee considered apparitions and haunted houses, topics which were to remain a part of psychical research to the present. However, I can discern no great progress here cither. There has certainly been development in the methods used. We have distinguished the poltergeist from the ghost and developed techniques for studying both, but two things have not happened. First we have not convinced science at large that there are such things at all. And second we do not have, in spite of many brave attempts, any viable theory of hauntings, ghosts or poltergeists.

The Physical Phenomena Committee studied spiritualism. Did that succeed in its objectives? From one point of view I  could argue that it did.  Numerous fraudulent mediums were detected by the committee and others in the SPR—which is success of a sort. Now, one hundred years later the phenomena of most interest have ceased almost entirely and many would argue that this is precisely because the investigation was effective and the SPR should be congratulated. Others would argue that the phenomena were genuine or at least some of them were. If you take this point of view then the research has to be seen as a failure, because we have learned next to nothing about how the physical phenomena of spiritualism operate. Once again it seems to be a case of success is failure in psychical research.

Finally, there was the literary committee, which. produced a prodigious amount of work, culminating in the publication of ‘Phantasms of the Living’ by Gurney, Myers and Podmore (1886); a collection of hundreds of cases which stand today as an invaluable source of people’s reported experiences. Many of the cases were apparitions seen at or about the moment of death and three hypotheses were put forward to account for them. One was a collection of normal explanations, such as chance, poor memory and so on. The second was telepathy by the living and the third communication from the dead. Today we have progressed little further beyond the position reached within a few years of the founding of the SPR. We may have more sophisticated theories about the forms of psi, but essentially the argument is still between those three hypotheses and I don t think anyone would argue that we have convincing evidence for any.

So having looked at the main topics of early psychical research can we assess the progress? Some topics were very quickly dropped, like Reichenbach’s claims or, a little more slowly, mesmerism. Others, like spiritualism, failed to live up to their early expectations but carried on with ever less impressive phenomena. Others, like thought transference, went on to provide the mainstay of later parapsychology, but with many persistent problems. Perhaps most damning to our subject is that topics in which progress is possible have often been abandoned to others because they did not fit into our negative definition. I am thinking here not only of hypnosis and trance states but of multiple personality mystical experiences, near-death and out-of-body experiences, and lucid dreams In all these progress is now being made, but outside of psychical research and largely ignoring it. So how does this match up against my imaginary scheme at the start? I would say—not very well.

As a field of study we have never succeeded in defining our subject, other than negatively. We have not convinced the critics that we have valid phenomena worthy of study. We have certainly developed numerous techniques and experimental methods but we have no viable theory to account for the supposed phenomena. And no technology at all, for we cannot produce or control them. Perhaps more importantly, we may best judge the success of a subject by the questions it asks and one thing is very clear from our brief perusal of psychical research—we are still asking more or less the same questions as we were one hundred years ago. And we still have no answers.

This, then, is my contention that psychical research has failed. So what now? Shouldn’t we just abandon the whole enterprise? Isn’t one hundred years of failure enough?

No. Like Sidgwick I feel that we may have been rash in commencing our enterprise but once we have undertaken the task it would show deplorable levity to abandon it (Sidgwick 1889).

Now you may argue, as Gibson once did (Gibson 1979), that I am just trying to get my fifty cents worth for all the trouble expended in a blind alley. I agree that psychical research is in a blind alley but one way out is always to retrace our steps and start again, trying not to repeat the same mistakes.

So how could we do that? What are we trying to do and what have we learned from those mistakes? What indeed was Sidgwick’s task and why did our founders begin in the first place?

Many have argued that psychical research began because of the intolerable strain which 19th century materialism put on people’s views of the world and of their place within it. The science of the time was enormously successful. Darwinism revitalized biology and provided a consistent framework for its progress for the next hundred years and more, but it relegated man to, in the words of the time, ‘a descendent of the apes’. Physics and chemistry solved numerous problems and gave rise to a vast technology as well as to the concept of a billiard ball universe in which free-will had no place. To people brought up in a Christian society with a belief in God as creator, and man as made in his likeness, this was hard to bear.

Alan Gauld, in his book on the founders of Psychical Research, argues that fundamentally they were hoping to stop the victory of materialism. And he likens Psychical Research to ‘a candle in the darkness which was beginning to loom on every side’ (Gauld 1968, p. 149).

But if materialism can be said to be ‘looming darkness’, that candle certainly dispelled little of it. Materialism, in one form or another, is here to stay. Almost all  scientists  use  materialistic  assumptions  in  their  work:  a  majority  of philosophers hold one or another version of it and psychical research has done nothing to overcome it. The mistake was perhaps ever to think that it could. Whether or not there are anomalies which will require extraordinary explanation, the notion of psi is incapable of overthrowing anything. The key to our mistake is that we have invented the empty notion of psi and expected it to explain whole realms of human experience. This it cannot do.

The phenomena are essentially accounts of people’s experiences. Even if there are psi-like anomalies, their occurrence would explain, at best, a small part of those experiences. We would still need a complete psychology of ‘psychic’ experiences. Even more so, if there are no anomalies, do we need it. Are we to leave this entirely to psychologists (who don’t seem to be much interested in such experiences) or make it part of a wider psychical research?

The same mistake is made constantly and in many guises. I was reminded of it by a recent film ‘The Golden Child’ in which a spiritually advanced young Tibetan boy is abducted from his monastery and taken to the United States. There, among other feats, he demonstrates his powers by making a Pepsi Cola can dance about outside his cage. It is as though the possession ofPK powers somehow explains a spiritual way of being but this it cannot and could never do. This is a mistake well worth avoiding.

So where do we begin? What really do we want to understand? Is it our place in the world, the nature of human life and suffering? the potential of human consciousness? Or do we just want to track down the hypothetical psi?

If it is the latter, as some parapsychologists would say, then we should carry on undaunted into what I have called the blind alley. For the elusive path out might yet be found. The discovery of a repeatable experiment may yet transform a stagnant subject. Personally I doubt it will ever be found (though one cannot ruleit out) and I would not choose this path.

Myers once said that for him the most important question was ‘Is the universe friendly?’ and he was deeply concerned with the basis of morals and the government of the universe (Gauld 1968, p. 149). And Gurney once told William James that ‘the mystery of the universe and the indefensibility of human suffering were never far from him’ (Gauld 1968 p. 156).

If we are going to have a new psychical research we must ask ourselves just what are the questions which matter to us. I would guess that most people interested in psychical research are interested because of experiences they have had and cannot explain. These might be dramatic psychic experiences; convincing examples of telepathy or precognition; veridical astral projection or effective communication with the dead but most people’s experiences are far less veridical and much more personal than that—as a glance at any issue of our Newsletter Supplement reveals. I suspect that the crucial experiences are often things which people know in their heart are important but find it very hard to explain to anyone else. For myself, I have had out-of-body experiences and lucid dreams; experiences in which myself and the rest of the world seemed to be one; in which all change flowed in an endless now. I have learned that it is possible to see more clearly, even perhaps to ‘wake up’. These things are hard to describe; even embarrassing to speak about. But it is these experiences which brought me to psychical research.

With a few recent exceptions (e.g. Claxton 1986, Tart 1986), today’s psychology is not really interested in tackling such experiences. The sad thing about psychical research is that it is only interested in such experiences if they hold out the prospect of finding psi. If not they are rejected as ‘normal’. Even if there does appear to be psi the experiences themselves, as experiences, are often torn apart in the attempt to prise out the anomaly within. There is plenty of room for a subject which wants to tackle these experiences critically, scientifically and yet sympathetically.

I might use as an example the study of out-of-body experiences (OBEs). As travelling clairvoyance or astral projection OBEs have long been part of psychical research. Two approaches have been typical. On the one hand OBEs were taken as evidence for psi. Experiments from the 1880s to the present sought to determine whether information could be-picked up at a distance, or objects affected by the travelling ‘self’. These made little or no progress (Blackmore 1982). On the other hand the experiences have been dismissed as mere hallucinations; the products of fantasy and of little interest. Only recently has a positive approach begun to pay-off. Psychological theories like that of Irwin (1986) have produced testable predictions.

I have argued that we need to take as a starting point the fact that OBEs seem real at the time (Blackmore 1984). What seems real at any time is only a model of oneself in the world. Indeed perhaps consciousness is no more and no less than being a mental model. So to understand OBEs we need to examine how those models are constructed and how their changes produce changes in consciousness. I have applied it to changes induced during meditation and in mystical experiences (Blackmore 1986). If the conscious self is a mental model then it makes sense that there can be selfless states in which no ordinary model of self-is constructed by the system. In this way even quite strange experiences become comprehensible.  Since human information processing systems are uniquely capable of constructing complex and flexible models the potential for exploring consciousness is hardly touched upon as yet—not to mention the prospects opened by future developments in artificial intelligence.

In this and other ways we could take extraordinary experiences as our starting point. We could learn to have those experiences (surely a good basis for understanding them); even to work in altered states as Tart (1972) has suggested, to predict their occurrence, their many forms and their impact on people; in short to understand why people experience ‘other realms’ without inventing a useless notion like psi.

I believe we need to do what our founders aspired to—that is to examine the experiences without prejudice or prepossession and in a scientific spirit And we need the courage they needed. Only our courage needs to be of a different sort for we are living in different times. They needed to fight just to be allowed to study psychic phenomena while we have a Society and a PA, and journals to write up our researches for.

No, we need courage of a different sort. First we need courage to accept what one hundred years of psychical research are telling us—that we are in a blind alley and the hypothesis of psi, with its negative definition, is to blame. Next we need courage to accept what has been learned in other sciences, that probably conscious experience is totally dependent upon our brains; that we are each alone in constructed universes of our own making. If this seems like materialist darkness we must stride boldly into it. And finally we need courage to be true to our own experiences. They may be ineffable, and ever-so-difficult to describe. We may be called mystical—a much worse term of abuse than being labelled Parapsychological, but we must not let go of the nature and relevance of our own experiences.

I conclude that psychical research has failed, but we need not despair. The ‘mysteries of the universe’ which impelled our founders are still waiting to be explored. If we can avoid the pitfalls of negative definitions and the concept of one underlying process, then we can start again—to examine unexplained human experiences without prejudice or prepossession and in a scientific spirit, and so hope to build a new psychical research—one without psi.

Brain and Perception Laboratory
University of Bristol


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The document has been scanned so please let me know if you find any mistakes.