Text of a
lecture delivered to the Society on 12 March 1987.
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
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
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.
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
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
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
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,
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
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
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
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
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
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
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
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
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
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
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
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
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
University of Bristol
Barrett, W. F.,
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