This article originally appeared in The Skeptic, Volume 22, Issue 2, from 2012.

I would like to respond to many of the issues raised by Wiseman, Watt, and Roe. Unfortunately, space limitations allow me to focus on one or two. So I will confine my reply to just a couple that seem most central to my essay.

I was puzzled by Chris Roe’s statement, “Hyman makes a number of vague allusions to a lack of quality in parapsychological research…” I was unaware that I had made such allusions, vague or otherwise. I assume that Roe has been misled by a possible ambiguity when I wrote:

“These neoparapsychologists… acknowledge that the evidence for psi is inconsistent, elusive, and fails to meet accepted scientific standards.”

In this context, both the neoparapsychologists and I are not addressing the issue of whether the quality of individual experiments meets “accepted scientific standards” such as appropriate controls for possible confounds and proper application of statistical analyses. Rather, we are focusing on the consistency of outcomes across a series of experiments.

The problem at issue is not whether the individual experiments employ adequate methodology, but rather do the outcomes from separate experiments show consistent, lawful and reproducible patterns. The neoparapsychologists agree with me that they do not. The “accepted scientific standards” are those that require that a finding has to be independently reproducible before it can be accepted as a legitimate subject for scientific scrutiny.

Neoparapsychologists do find some consistent tendencies in the results of psi experiments such as experimenter effects, decline effects, reversal of effects and the like. But even these tendencies are far from predictable; along with other inconsistencies in the outcomes, they are what put the findings outside the scope of orthodox science.

Since the time of Galileo, Kepler, Harvey, and Newton, modern science has flourished just because it focused only on phenomena that were available for public scrutiny, were lawful, and could be independently replicated. Claims that challenged existing theories were taken seriously when they were supported by evidence that met these criteria of consistency. Claims such as N-rays, Martian Canals, polywater, mitogenetic radiation, and cold fusion which were based on evidence that could not be reliably replicated were rejected. It is worth noting that the proponents of these rejected claims also attributed the inability to consistently replicate to experimenter effects, reversal effects, decline effects and the sort of inconsistencies that plague psi research. As I pointed out in my essay, science can only succeed when it studies phenomena that are lawful and reliably reproducible.

Roe makes another point to which I think I should respond. He wrote:

“Hyman bemoans parapsychology’s poor replication record and… rather selectively uses one study by Broughton and Alexander (1977) to illustrate his point…”

He is correct that I deliberately selected this study to make my point. I could have just as well have chosen some other studies such as the failure to replicate the PEAR experiments (Jahn et al., 2000). Like the attempted replication of the PEAR experiments, the Broughton and Alexander experiment met all the criteria of a replication attempt that should have succeeded if, indeed, there had been a real effect. The experiment was prospective in that it was designed to test a prediction that the results of the autoganzfeld experiments were real and replicable. The design and procedures were deliberately made to be as similar as possible to original experiments. Even some of the very same equipment was used. The authors made sure to include a sufficient number of subjects and trials so that lack of power would not be a factor. They not only tested for the entire primary, but also the secondary effects that were part of the original findings. In addition, the experimenters were experienced parapsychologists.

The failure of this direct replication cannot be easily dismissed as due to low power, experimenter effect, non-standardness of design, or any of the other excuses that often are used to explain away negative findings.

Roe apparently believes that the results of psi research, while indeed showing some inconsistencies, are basically replicable. To me, the most sobering consideration for a parapsychologist in regards to replicability is that, unlike every other area of inquiry that claims to be a science, parapsychology is the only one that lacks a ‘paradigm’ experiment. As Kuhn (1977) acknowledges, his original conception of paradigms referred to standard experiments that science textbooks provide students. Each area of science has its own set of standard experiments that serve as exemplars of the field. A standard experiment could be given as a laboratory assignment with the expectation that the students could replicate the original results.

Psychology, for example, has hundreds, even thousands, of such standard experiments. Every introductory psychology lab can assign the students paradigms in sensation, perception, memory, problem solving and other areas with the confidence that the students will replicate the original results. As just one illustration, consider Ebbinghaus’s classic experiment on the laws of forgetting. The student can conduct the experiment on herself or on another person and will obtain essentially the same lawful curve that Ebbinghaus reported in 1885.

As I pointed out, parapsychology does not have even one paradigm experiment. The problem is deeper than just the inability to consistently get significant departures from chance. The loose connection between theory and experimental results in parapsychology means that the constraints on how psi should manifest itself in the data are weak. Ultimately, the decision to claim that psi is present relies on a significant departure from chance. Parapsychologists have no disciplined way to decide when psi is present and when it is not; nor do they have any principled way to decide whether an effect in experiment A is due to the same cause as the same sized effect in experiment B. This is equivalent to declaring that any outcome showing a drop in the proportion of recalled syllables over time is a successful replication of Ebbinghaus’s original experiment even if the resulting function clearly differs from the original curve.

Yet, parapsychologists often seem willing to claim a successful replication in cases where only a departure from chance occurs in the new experiment. (See the example I described wherein parapsychologists claimed that the autoganzfeld experiments successful replicated the original ganzfeld experiments.) Replication, in orthodox science, refers to reproducing a pattern of results not just an abstract ‘effect.’ Even given the loose concept of replication that parapsychologists often use, their results clearly do not replicate.

This article originally appeared in The Skeptic, Volume 22, Issue 2, from 2012.

Ray Hyman would have us believe that “parapsychology is dead”. In this response I shall consider the reasons he provides for this claim and show – to paraphrase Mark Twain, an early member of the Society for Psychical Research and author of articles on ‘mental telegraphy’ (Bratcher, 2008) – that the report of parapsychology’s death is an exaggeration.

Hyman claims that the goal of parapsychology is (and implicitly always has been) to gain the recognition of the scientific community and to meet the most exacting of scientific standards of evidence, and in this respect parapsychology has been unsuccessful. I am happy to concede that this may have been one of a number of motivations behind the approach adopted by J.B. and Louisa Rhine in founding and developing their laboratory at Duke University from the 1930s to the 1960s (a period that Beloff, 1993, refers to as the “Rhine Revolution”), but of course it is far removed from the primary aim of parapsychology. The founders of the SPR did not set out on a public relations exercise but rather were committed to extend the reach of the scientific method to include more contentious claims, 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 recognized hypothesis”.

Contemporary definitions of the discipline similarly emphasize the application of available methodological and conceptual tools to make best sense of an array of phenomena that superficially seem difficult to accommodate in our current worldview, so that parapsychology is the “study of experiences which, if they are as they seem to be, are in principle outside the realm of human capabilities as presently conceived by conventional scientists” (Irwin & Watt, 2007, p. 1, emphasis added). As Caroline Watt has described in this exchange, this means that parapsychologists are increasingly interested in “what seems psychic but isn’t” (Morris, 1986) in their efforts to understand phenomena rather than seeking support for some prior esoteric worldview (which at times they are unfairly caricatured as doing). However, parapsychologists recognise that this work towards conventional explanations must be complemented with more direct tests of the putative phenomena under controlled conditions if we are to do justice to the experiences that people report, particularly given that the results of such experiments are claimed to provide evidence for anomalies in information exchange that might require revisions in elements of our worldview (but see Dobyns, in press).

In the next section I shall briefly consider whether parapsychologists have grounds to claim persuasive evidence for the occurrence of effects under conditions that preclude normal explanations, but first would like to respond to Hyman’s claim that parapsychology’s attempts at scientific respectability are “unrealistic and unachievable”. Of course, acceptance is a matter of degree and much work remains to be done, but there has been some positive movement in the normalisation of academic parapsychology in recent years, in the UK at least. Delanoy (in press) has noted that at least 16 UK universities have fulltime academic staff whose doctoral training was solely or primarily in parapsychology, and a similar number are currently engaged in graduate training that is accredited by these institutions.

Parapsychology has featured regularly at conferences organised by the British Psychological Society (I personally have had papers accepted for the BPS’s annual conference as well as those organised by the sections concerned with Social Psychology, Transpersonal Psychology and Consciousness and Experiential Psychology), which tends to argue against an institutional antipathy. ‘Anomalistic psychology’ has been included in the specification for A2 Psychology (the standard pre-university qualification) by the Assessment and Qualifications Alliance (AQA), the assessment body that has much the largest market share of the 50,000 students who take Psychology each year. This specification includes elements on experimental testing of ESP and PK, so that future undergraduates will come to university with a grounding in parapsychology and an expectation that the subject will be represented on any comprehensive undergraduate syllabus. This is not really the profile of a subject that is “consigned to the fringes of academia”, as Richard Wiseman claims in his contribution here.

Hyman makes a number of rather vague allusions to a lack of quality in parapsychological research, which undermines any claim to have demonstrated the occurrence of an anomalous effect. He asserts, for example, that the evidence “fails to meet established scientific criteria”, but apart from some general concerns about the limitations of meta-analysis (which are clearly not specific to parapsychology) it is not clear in what way(s) parapsychological research is deficient; without specifying what “established criteria” are required for a study to qualify as of high quality this claim remains insubstantial and unfalsifiable – it is not a scientific claim.

So what might those criteria include? Watt and Nagtegaal (2004) have described the use of double-blind methods – in which the experimenter and others who may have some involvement in the data generation and recording phases are at that time unaware of the nature of the target and so cannot  unwittingly cue the participant – as a possible indicator of study quality (while acknowledging that otherwise poor-quality designs could still include blinds). It is well established that the outcome of a study can be affected by the experimenter’s prior knowledge and expectations, leading to artifacts if this is not adequately addressed (Rosenthal, 1976). But when Sheldrake (1999) surveyed various journal publications he found that the use of double-blinds was very rare in the physical and biological sciences (0% and 0.8% respectively), somewhat more common in medical sciences (24.2%) but most common in parapsychology (85.2%); surprisingly, other research in psychology and animal behaviour used blinded methods even less than in medicine (4.9%), despite the emphasis on the problems of demand characteristics in social science methods training. Watt and Nagtegaal (2004) conducted a second survey to see if Sheldrake’s findings could be replicated and found a similar profile (parapsychology: 79.1%, Psychology: 14.5%). By this criterion, then, it is difficult to justify the general claim that parapsychological research is methodologically poor in comparison with other social science research.

Hyman bemoans parapsychology’s poor replication record and, taking the Ganzfeld method as his example case, rather selectively uses one study by Broughton and Alexander (1997) to illustrate his point – one could just as easily have chosen Parker’s (2000) automated Ganzfeld database, consisting of 150 trials that gave a hit rate of 36% (z = 3.02), or Dalton’s (1997) series of 128 trials that gave a hit rate of 47% (h = .46). Which of these should we prefer? None. While it is tempting to focus on the outcomes of individual studies, particularly when so few people are professionally engaged in parapsychological research and it takes so long to build up anything like a reasonable database, we must accept that individual studies are susceptible to giving outcomes that reflect sampling error and also are affected by idiosyncratic features of the experimental environment – not obscure or mystical features, but ordinary factors such as experimenter-participant rapport or differences in recruitment strategy. For this reason we should prefer summary reviews (while remaining cognizant of their shortcomings) when making judgments about the robustness of effects. That is not to suggest that the outcomes from ganzfeld studies are robust and heterogeneous (they are not), but a good case can be made to argue that at least some of this variation is due to different researchers posing different research questions as they move from simply demonstrating a phenomenon to characterising and explaining it. This typically leads to variations in the procedure followed so that more or less conducive conditions can be compared or more radical departures from established procedure can be tested, with the expectation that not all variations are likely to be psi-conducive. In this context simply combining outcomes across studies to give a bottom-line effect size would be rather naïve (see Roe, in press a, for a fuller consideration of this point). Where ganzfeld studies have been coded according to the degree to which they adhere to Honorton’s ‘standard’ protocol (Bem, Palmer & Broughton, 2001), there is a very strong correlation between ‘standardness’ and effect size, with the subset of studies that closely replicate Honorton’s approach giving a hit rate of 31.2% that is highly significant and falls comfortably within Bem and Honorton’s 95% confidence interval for their autoganzfeld effect size estimate. That looks rather like replication to me.

A number of other strands of research in parapsychology offer some promise of also reliably capturing (admittedly small) effects, including work that takes more direct physiological measures (e.g., Radin, 2004) and studies that look for incidental psi effects in overtly cognitive tasks (e.g., Bem, 2008; Luke, Roe & Davison, 2008). Space does not permit me to consider these in any detail, but work to date suggests that these effects are reasonably replicable – certainly in comparison to the rather weak and inconsistent effects that are regarded as support for the more sceptical claim that paranormal beliefs are associated with cognitive deficits or social marginality (see Roe, in press b). I would be interested to know what levels of replication would be regarded as appropriate or reasonable for parapsychological work with human participants.

Finally, I should like to respond to the tendency of sceptical commentators to refer to the achievements of parapsychology in relation to the time since it became recognisable as a separate discipline. In this exchange, for example, Wiseman complains that “after over a century of work mainstream science remains sceptical of psi” and Hyman begins by noting that parapsychology has lasted “approximately 160 years”. This rhetorical device encourages the reader to assume that extension over time also translates into extensive and intensive activity, so raising their expectations about the degree of progress that might be reasonable. Against this, any actual progress pales, and the reader is moved to conclude that the phenomena are non-existent rather than elusive. But Caroline Watt has already drawn attention to the fact that very few persons are professionally involved in parapsychology, and even these typically have to combine their research activity with other academic duties. This situation is not new: Thouless (1953, p. 23) warned that “experimental workers in our subject are so few that we cannot afford wasted effort”, and Schouten (1993) calculated that the person-hours invested across the lifetime of parapsychology from its beginnings with the establishment of the Society for Psychical Research in 1882 equates to only two months’ of research in conventional psychology in the United States. In that context the body of evidence may seem more impressive.

But limitations in human resources and in funding affect more than gross productivity; they also shape the character of the research that is carried out. Elsewhere (Roe, in press c) I have described parapsychology as a “butterfly science” in which key researchers seem to shift from one protocol to another as they fall in and out of fashion much as a butterfly flits from flower to flower. Sceptical commentators have tended to regard this as suspect, much as Wiseman does in his commentary here. However, in my view this pattern occurs because the small number of researchers in parapsychology includes a disproportionately large number of innovators and early adopters and too few technicians. Innovators thrive on developing new protocols or adapting methods from other areas and in demonstrating ‘proof of principle’ by reporting significant psi effects using such methods; ‘early adopters’ are quick to seize on these new approaches and technologies and are responsible for the first wave of independent replications. However, relatively quickly the innovators lose interest in simple confirmations and move on to develop yet more methods and approaches, with the early adopters soon following suit. I am sure that this pattern also occurs in other disciplines, but with their greater numbers they also include many able technicians who are willing to conduct the kinds of modest replication extensions that Kuhn would have called ‘normal science’. (We have fewer technicians, but they do exist; for example, I found that there had been ten further ganzfeld studies conducted after the last meta-analytic reviews, and this database was independently significant – see Roe, in press a). The pattern is exacerbated by the intense competition for funding, which encourages novelty and innovation and which requires that results are forthcoming in the short to medium term; both of these select against the systematic and methodical programmes of the would-be technician that could provide the empirical foundation that sceptics are looking for.

At best this research cycle is frustrating in diverting resources away from a potentially fruitful avenue of research; at worst it looks suspicious to the outsider, who expects to see continuing and systematic work using a particular method for so long as it is productive, particularly where great claims were initially made for it – why are there so few micro-PK studies? So few ganzfeld studies? I agree with Wiseman and Watt that collectively parapsychologists need to address this issue by collaborating on a more systematic programme of research, one that goes beyond proof of principle and first wave independent replications. I believe that parapsychologists would be resolved to commit to such a programme, but in practice it would require a radical overhaul of the few funding mechanisms that are available to parapsychology for it to succeed; without a commitment of significant resources over the longer term it is difficult to see how parapsychologists could commit to Wiseman’s three basic rules.

References

• Beloff, J. (1993). Parapsychology: A concise history. London: Athlone Press.
• Bem, D.J. (2008). Feeling the future III: Additional experimental evidence for apparent retroactive influences on cognition and affect.International Conference of the Society for Psychical Research held Jointly with the Parapsychological Association, University of Winchester, UK, 13th to 17th August, 2008.
• Bratcher, C. (2008). Mark Twain and ‘mental telegraphy’. International Conference of the Society for Psychical Research held Jointly with the Parapsychological Association, University of Winchester, UK, 13th to 17th August, 2008.
• Dalton, K. (1997). Exploring the links: Creativity and psi in the ganzfeld. Proceedings of Presented Papers: The Parapsychological Association 40^thAnnual Convention in Conjunction with the Society for Psychical Research, 119-134.
• Delanoy, D. (in press). Parapsychology in a university setting. In C.A Roe, L. Coly & W. Kramer (Eds.) Utrecht II: Charting the future of parapsychology. NY: Parapsychology Foundation, Inc.
• Dobyns, Y. (in press). Physics with an open mind. In C.A Roe, L. Coly & W. Kramer (Eds.) Utrecht II: Charting the future of parapsychology. NY: Parapsychology Foundation, Inc.
• Luke, D.P., Roe, C.A., & Davison, J. (2008). Testing for forced-choice precognition using a hidden task: Two replications. Journal of Parapsychology, 72, 133-154.
• Morris, R.L. (1986). What psi is not: The necessity for experiments. In H.L. Edge, R.L. Morris, J. Palmer, & J.H. Rush, Foundations of parapsychology: Exploring the boundaries of human capability (pp. 70-110). London: Routledge & Kegan Paul.
• Radin, D.I. (2004). Electrodermal presentiments of future emotions. Journal of Scientific Exploration, 18, 253-273.
• Roe, C.A. (in press a). The role of altered states of consciousness in extrasensory experiences. In M. Smith (Ed.), Developing perspectives on anomalous experience. Jefferson, NC: McFarland & Co.
• Roe, C.A. (in press b). Anomalistic psychology. In N. Holt & R. Lewis (Eds) A2 Psychology 2009 AQA A Specification: The Student’s Textbook. London: Crown House Publishing.
• Roe, C. A. (in press c). Personal reflections on Utrech II. In C.A. Roe, L. Coly, & W. Kramer (Eds) Utrecht II: Charting the future of Parapsychology. NY: Parapsychology Foundation, Inc.
• Schouten, S. (1993). Are we making progress? In L. Coly & J. McMahon (Eds.) Psi research methodology: A re-examination. (pp. 295-322). NY: Parapsychology Foundation, Inc.
• Thouless, R.H. (1953). Experimental design in parapsychology. Proceedings of the first international conference of parapsychological studies (pp. 21-23). New York, NY: Parapsychology Foundation, Inc.
• Watt, C., & Nagtegaal, M. (2004). Reporting of blind methods: An interdisciplinary survey. Journal of the Society for Psychical Research, 68, 105-114.

This article originally appeared in The Skeptic, Volume 22, Issue 2, from 2012.

I agree with much of what Ray Hyman has to say about the demise of parapsychology. When the field was founded around the turn of the last century it was over-brimming with optimism, with proponents of the paranormal hoping that science would rapidly yield overwhelming evidence to support the existence of psychic ability and survival of bodily death, and the world would quickly embrace a more spiritually-oriented conception of mankind. History has proved them wrong. After over a century of work, mainstream science remains sceptical of psi and parapsychology has been consigned to the fringes of academia.

Of course, this is not to suggest that many parapsychologists themselves have come to disbelieve in psychic powers. In fact, many argue that the evidence for psychic abilities is either convincing, or at least strong enough to justify further work. The main problem is that the databases they draw upon are constructed retrospectively, and the alleged affects have a curious habit of not replicating in prospective studies.

Faced with a lack of replicability, parapsychologists often turn to another alleged psi-conducive procedure, again piece together evidence to support this technique, and again find that it fails to produce replicable effects. This is not a recent phenomenon, with commentators remarking on this pattern throughout the history of the field. For example, writing over thirty years ago, parapsychologist Joseph Gaither Pratt (1978) noted:

One could almost pick a date at random since 1882 and find in the literature that someone somewhere had recently obtained results described in terms implying that others should be able to confirm the findings…One after another, however, the specific ways of working used in these initially successful psi projects have fallen out of favor and faded from the research scene – except for the latest investigations which, one may reasonably suppose, have not yet had enough time to falter and fade away as others before them have done.

This constant ‘ship jumping’ is one of the defining features of psi research, with new paradigms emerging every decade or so. Take, for example, the different trends in ESP research that have emerged over the years.

Initial work, conducted between the early 1930s and late 1950s primarily involved card guessing experiments, in which people were asked to guess the identity of specially printed playing cards carrying one of five simple symbols. By the mid-1960s parapsychologists had realised that such studies were problematic to replicate and so turned their attention to the possibility of participants predicting the outcome of targets selected by machines, and dream telepathy.

In the mid-1970s and early 1980s the ganzfeld experiments and remote viewing took over as dominant paradigms. In 1987, a major review of the area by parapsychologists K. Ramakrishna Rao and John Palmer argued that two sets of ESP studies provided the best evidence for the replicability of psi: the ganzfeld experiments and the differential ESP effect (wherein participants apparently score above chance in one condition of an experiment and below chance in another).

More recently parapsychologists have shifted their attention to alleged presentiment effects, wherein participants appear to be responding to stimuli before they are presented. Finally, there are now signs that the next new procedure is likely to adopt a neuropsychological perspective, focusing on EEG measurements or functional MRI scans as people complete psi tasks.

As Ray Hyman notes, this pattern of false dawns has driven some researchers to argue that psi is inherently impossible to replicate, essentially marking the end of the field as a scientific endeavour. But before researchers rush through the exit door, I think it is worth giving psi one last chance by staging one final attempt to create a database that provides the best-shot of deciding the existence of psi.

To achieve this, I believe that the researchers involved need to learn from the mistakes of the past and stick to three basic rules: First, they should stop trying lots of new procedures and instead identify one or two that have already yielded the most promising results. Second, they should arrange for several labs to carry out strict replications that are both methodologically sound and incorporate the most psi-conducive conditions possible. Third, the problems associated with retrospective meta-analysis should be avoided by pre-registering the key details involved in each of the studies. 

If this approach yields a significant and replicable effect then the scientific mainstream would be forced to take the topic seriously and allow parapsychology in from the cold. If it fails the field needs to have the courage to accept the null hypothesis. In short, the time has come to put up or shut up.

References

• Pratt, J.G. (1978). Prologue to a debate: Some assumptions relevant to research in parapsychology. The Journal of the American Society for Psychical Research, 72, 127-139.
• Article by Caroline Watt: “Putting things in perspective“.
• Hyman, R., & Honorton, C. (1986). A joint communiqué: The psi ganzfeld controversy. Journal of Parapsychology, 50, 351-364.
• Lucadou, W. von, Römer, H., & Walach, H. (2007). Synchronistic phenomena as entanglement correlations in Generalized Quantum Theory. Journal of Consciousness Studies, 14, 50-74.
• Lucadou, W. von & Zahradnik, F. (2004). Predictions of the Model of Pragmatic Information about RSPK. Proceedings of the 47th Annual Convention of the Parapsychological Association, pp. 99-112. Vienna, August 5-8.
• Schlitz, M., Wiseman, R., Watt, C., & Radin, D. (2006). Of two minds: Skeptic-proponent collaboration within parapsychology. British Journal of Psychology, 97, 313-322.
• Watt, C. (2005). Presidential Address: Parapsychology’s contribution to psychology: A view from the front line. Journal of Parapsychology, 69, 215-232.
• Watt, C., Watson, S., & Wilson, L. (2007). Cognitive and psychological mediators of anxiety: Evidence from a study of paranormal belief and perceived childhood control. Personality and Individual Differences, 42, 335-343.

This article originally appeared in The Skeptic, Volume 22, Issue 2, from 2012.

Parapsychology has long had its critics. Indeed, in my presidential address to the Parapsychological Association I argued that critics (whether situated within or outside the discipline) play a vital role for the field in helping to tighten up methodology (Watt, 2005). I deliberately avoid the term ‘sceptic’ since that simply refers to taking a questioning stance, which we should all be routinely doing as scientists. James Alcock’s (2003) critique, though itself containing some overly sweeping statements, nevertheless makes some quite devastating points and is essential reading for students of parapsychology. Other well-informed critics, such as our two preceding authors, deserve praise for making strenuous efforts to engage deeply with the field’s published literature and its researchers (Hyman & Honorton, 1986), and for rolling up their sleeves and actually collecting data in collaboration with parapsychologists, for example to explore topics such as the effects of the experimenter’s psi belief on study outcome (Schlitz, Wiseman, Watt & Radin, 2006).

I am already on record as agreeing with some of the critical points reiterated by Ray Hyman and Richard Wiseman, particularly about the need to focus on the most promising paradigms, and to conduct prospective meta-analyses (Watt, 2005). However, without making too many excuses, I think we need to remind ourselves of a few features of parapsychology as a field of enquiry that make it difficult to reach closure on the psi question. There are probably fewer than 100 researchers world-wide who are actively engaged in psi research. Of these, many – like me – will spend a proportion of their limited resources on the psi question, but will also be engaged in broader research into paranormal experiences and beliefs (e.g., Watt, Watson & Wilson, 2007). They feel the broader research is important because of the wide public prevalence of these experiences and beliefs, and they feel that the psi hypothesis is not the sole interesting question to be asked (though it may be the most revolutionary one from a theoretical point of view). For example, in 2008 at the main gathering for research-active parapsychologists, the Annual International Convention of the Parapsychological Association, only 10 out of 22 full papers (i.e., 45%) presented new data testing the psi hypothesis. If we look at it purely as a numbers game, it would be surprising if much could be learned about the possible existence and nature of psi under these circumstances. Since it’s unlikely that the field will attract more resources without persuasive evidence for psi, we find ourselves in a Catch-22 situation. I think the only way out is for the field to be more systematic and organized in how it tests the psi hypothesis. However, this would require individuals to give up pet theories and cherished paradigms, and sociological rather than scientific factors might hinder this kind of organized effort.

Particularly in the UK and Continental Europe, ‘doing parapsychology’ is increasingly becoming integrated with mainstream academia rather than being an activity that is pursued at independent (and often isolated) private research institutions. While in many ways parapsychologists are satisfied in achieving their goal of integration, it comes at a cost because these researchers are also coping with the heavy teaching and administrative loads that are part and parcel of modern academic life. Like their academic colleagues, unless they can bring in funding to buy themselves out of these duties, they struggle to find the time to conduct research. Catch-22 again! So, while critics may bemoan parapsychology’s lack of productivity regarding the psi question, we should remember that this may in part be due to hindrances to activity on this question.

Ray Hyman introduces us to ‘neoparapsychologists’, and although I recognize the gist of their ideas in his portrayal, I disagree that all proponents of this view of psi are stating that the nature of psi is such that it cannot be tested in a scientific manner. I am not an expert on their claims but my understanding is that there are different shades to the neoparapsychologists’ argument. Some theoretical standpoints hold that in controlled laboratory testing psi cannot be observed in the usual manner, such as repeatedly looking for a main predicted effect, but that testable predictions can be made. Because this is a relatively recent development, neoparapsychologists are currently developing answers to the question of how to apply this model of psi to data gathered in the laboratory. For example, rather than look for a main psi effect, one suggestion is to design the experiment to include a number of psychological and physical variables so that a correlation matrix can be produced. The psi effect is expected to manifest in the number and strength of correlations between these variables, while the null hypothesis is represented by the number of significant correlations expected by chance. The exact pattern of extra-chance correlations is not expected to replicate in subsequent experiments, but their number and strength is expected to replicate if the experimental conditions are the same (Lucadou, Römer & Walach, 2007). Outside the lab, testable predictions have also been made concerning how reports of spontaneous ostensibly paranormal phenomena would be affected by various manipulations under the neoparapsychological model of psi (Lucadou & Zahradnik, 2004). So, while it’s not easy being in parapsychology, I wouldn’t call for the undertakers just yet.

This article originally appeared in The Skeptic, Volume 22, Issue 2, from 2012.

The discipline of parapsychology, which was earlier known as psychical research, lasted approximately 160 years. It no longer exists. This claim will likely surprise those who call themselves “parapsychologists” as well as those readers who know that annual meetings still occur and parapsychology journals are still published. So the title of this article needs an explanation.

Parapsychology was a discipline that openly claimed to be a science and actively sought evidence for psi that would meet strict scientific criteria. Henry Sidgwick (1882), in his Presidential Address to the first meeting of the Society for Psychical Research (SPR), declared that the evidence that had been collected during the preceding 30 years demonstrated scientifically the reality of supernatural phenomena. The problem was that the majority of the scientific community did not agree. The SPR’s objective was to collect even more of the same kind of evidence until the scientific community accepted it.

The goals of parapsychology as a discipline were clear: Parapsychology wanted to gain the recognition of the scientific community as a legitimate field of science. In addition, parapsychology’s mission was to collect evidence for the existence of psi that would meet the strictest scientific criteria. These goals remained central to parapsychology’s aims until fairly recently.

During the past decade, a growing number of parapsychologists have acknowledged that these goals are unrealistic and, indeed, unachievable (Bierman, 2001; Jahn & Dunne, 2008; Kennedy, 2001, 2003; Ludacou, 2001). These neoparapsychologists, as I shall call them, acknowledge that the evidence for psi is inconsistent, elusive, and fails to meet accepted scientific criteria. Such misgivings had been expressed by many earlier parapsychologists. What make the current admissions different is that the neoparapsychologists claim that the evidence for psi in principle cannot meet scientific standards. Indeed, they argue that the inability to be captured by scientific methodology is an intrinsic property of psi.

Bierman, Jahn, Kennedy, Ludacou and those parapsychologists who both agree and disagree with them will continue to do research and write about parapsychology. But a discipline that relies on evidence that cannot meet scientific standards is no longer the parapsychology that the founders had hoped to create. It is in this sense that parapsychology, as it was conceived by its founders and promoted by its practitioners, has ceased to exist.

What About Contemporary Claims That Psi has been Proven?

Although the neoparapsychologists argue that the evidence for psi cannot be scientifically demonstrated, others, in stark contrast, insist that psi has been conclusively proven with scientifically impeccable evidence. (As far as I can tell, the advocates of these opposing claims do not acknowledge each other’s existence.) The statistician and parapsychologist, Jessica Utts (1995, p. 289), wrote that, “[u]sing the standards applied to any other area of science, it is concluded that psychic functioning has been well established.” Perhaps the most outspoken advocate of the reality of psi is Dean Radin (1997). He has maintained that “we are forced to conclude that when psi research is judged by the same standards as any other scientific discipline, then the results are as consistent as those observed in the hardest of the hard sciences!” (Radin, 1997, p. 58; italics in the original).

Despite the boldness of these assertions, their support is illusory. Both Utts and Radin rely completely on the results of meta-analyses. I conducted the first meta-analysis on parapsychological data in my critique of the ganzfeld research (Hyman, 1985). Honorton (1985) did the second meta-analysis in response to mine. The fact that we came to very different conclusions doing meta-analyses on the identical data base should alert us to the fact that meta-analyses lack statistical robustness. In spite of the fact that parapsychologists subsequently began relying on meta-analysis as the main technique to support their claims, the procedures are fraught with so many blemishes that the support they offer is vacuous.

Space limits preclude discussing all the limitations of the meta-analyses, but some of the main issues are statistical, such as the heterogeneity of effect sizes that plagues almost all of these meta-analyses. Among other things this makes the use of the Stouffer Z inappropriate and overly optimistic. It also raises questions about the meaningfulness of the combined effect size. Meta-analyses are also retrospective. Using them to argue that the evidence is replicable is misleading. Replicability means that we can use current outcomes to predict new outcomes. This is something that parapsychology has been unable to do. Rather than list several more limitations of using meta-analysis to establish that psi exists and that the supporting evidence is replicable, I will highlight just one very serious problem.

Several meta-analyses have been conducted on the ganzfeld experiments. More than 100 such experiments have been reported beginning in 1974 to the present. With one controversial exception, the various meta-analyses report combined effect sizes that are positive and significantly different from zero. An effect size is simply a difference between an actual outcome and an outcome expected by chance. This difference is “standardized” by dividing it by the standard deviation (which is a measure of the variability among the subjects in an experiment). The use of effect sizes to compare the results from different experiments makes sense if the various outcomes are conceptually coherent. Just about every meta-analysis in parapsychology violates this requirement.

Let me give an example. The autoganzfeld experiments were touted as a successful replication of the original ganzfeld experiments (Bem & Honorton, 1994). As I have previously pointed out (Hyman, 1994), the autoganzfeld experiments failed to replicate the original experiments. The original ganzfeld experiments all used static targets. The meta-analysis of these experiments yielded a highly significant combined effect size. The autoganzfeld experiments used both static and dynamic targets. The resulting effect size (combining both types of targets) was approximately the same size as that for the original ganzfeld experiments as well as statistically significant. This is the basis for declaring a successful replication. The static targets, however, when considered separately, had an effect size

consistent with zero. In addition, the outcome for these static targets, which are the most relevant to the original experiments, was significantly different from the outcome for the original experiments. In other words, the autoganzfeld failed to replicate the original experiments. Bem and other parapsychologists simply ignored my argument and continued to claim that the autoganzfeld experiments were a successful replication. The neoparapsychologists agree with my position on this issue.

Broughton and Alexander (1997) attempted a direct replication of the autoganzfeld experiments. They even used some of the same equipment that Honorton and his colleagues had employed in their experiments. The result was a failure to replicate not only the overall results of the first autoganzfeld experiments, but also all of the secondary effects that were originally reported. The Broughton and Alexander experiment failed to replicate both the autoganzfeld experiments as well as the original ganzfeld experiments. Despite this, all of the major meta-analyses of the ganzfeld experiments include the original ganzfeld experiments, the autoganzfeld experiments and the Broughton and Alexander experiments. When you include the effect sizes from these three data bases, the combined effect size is both positive and “significant”. This is interpreted by Radin, Utts and others as proof that psi exists and that the supporting evidence is replicable.

An unfortunate consequence of relying upon meta-analyses to support claims of psi is that experiments that blatantly fail to replicate one another can be combined in a way that seems to say otherwise. Ironically, the very same meta-analyses that are used by some parapsychologists to boldly proclaim that the evidence for psi is replicable have been used as one of the major supports for just the opposite conclusion (Bierman, 2001). Bierman considered many of the major meta-analyses that have been done in parapsychology. For each meta-analysis he fitted regression lines to the effect sizes plotted against the year they were obtained. In all cases the slopes of the regression lines were negative. In other words, they all demonstrated a decline effect. At the beginning of each programme of parapsychological research, the effect sizes tended to be positive and significant, but as the years progressed, the effect sizes in each research programme tended to become zero. This “erosion of evidence” as some parapsychologists call it, was also noticed by many parapsychologists before its confirmation by the meta-analyses.

Some of the neoparapsychologists realize that if psi were a real effect, at least in the sense understood by orthodox science, that instead of a decline, effect sizes should show an incline over time.

Is the Elusive Nature of the Evidence an Inherent Property of Psi?

As I have indicated, several contemporary parapsychologists have marshalled impressive amounts of evidence to demonstrate that the evidence for psi is non-replicable, inconsistent, and elusive (Bierman, 2001; Jahn & Dunne, 2008; Kennedy, 2001, 2003; Ludacou, 2001). Kennedy (2003) entitled his paper, “The Capricious, Actively Evasive, Unsustainable Nature of Psi”. This title suggests the frustration that the neoparapsychologists experience. It seems as if the findings are teasing the researchers. Indeed, Kennedy’s preferred hypothesis is that some intelligent agent is somehow deliberately manipulating the evidence so that psi appears to be real but always evades being captured by the scientific method.

The neoparapsychologists discern patterns in the parapsychological data. In many cases a new line of research contains a mixture of results that include some insignificant outcomes but also many significant results. With the passing of time the significant outcomes become fewer until finally the average effect size approaches zero. Another pattern is where the results, instead of going to zero, actually change from psi-hitting to psi-missing. Of course, there is the experimenter effect: some researchers consistently get positive results (but only for a time); some consistently get negative effect sizes; and others do not get significant outcomes. The problem is that these patterns are unpredictable and cannot be captured by scientific methodology.

The neoparapsychologists do not just admit that parapsychology has failed to produce evidence that can scientifically pass scientific muster. They go further and argue that this ability to evade scientific scrutiny is an inherent and unique property of psi. Psi exists, they maintain, but it will require a new kind of science to recognize it. Jahn and Dunne (2008) call for changing the rules of science to allow psi to be accepted. This obviously begs the question that they assume psi exists. But they cannot prove it by current scientific methods. Therefore let’s change the methods to allow psi to enter the halls of science.

Because they do not doubt the existence of psi, the neoparapsychologists seek explanations for why it manifests itself in such quirky ways. Most seem to prefer analogies with the seemingly odd behaviour of quantum phenomena. Kennedy, as indicated, hypothesizes that some unknown intelligence is deliberately teasing the researchers. Such a hypothesis, which takes us back to the mischief of the ancient gods, is still another indicator of how far parapsychology is straying from the world of science.

These attempted explanations of the apparent pattern of results are little more than re-descriptions of eccentricities in the obtained results. Although the parapsychologists try to find evidence for a coherent phenomenon they label psi, they have never managed to propose a positive definition that would enable them to predict and detect the presence of psi in the data. Instead, they rely on a negative definition to detect the presence of ESP and PK. They declare psi is present whenever the outcomes vary significantly from a chance baseline and no mundane explanation is readily at hand. An example of this was discussed in my discussion of effect sizes in meta-analyses.

Alcock (2003) provides a relatively complete list of the major problems faced by parapsychology. Here, I will focus just on the lack of a positive concept and test for detecting the presence of psi. One consequence is that the parapsychologists have proposed many sufficient conditions for the presence of psi but lack any necessary conditions. For example, Rhine and other early parapsychologists made much about the discovery of the “decline effect” within parapsychological experiments. This decline effect was hailed as proof of the existence of psi, even in experiments where the overall effect size was zero. However, when the decline effect was not discovered in other experiments, this did not prevent the researchers from declaring the presence of psi if they detected some other pattern that differed from chance. This creates the unsatisfactory situation where a wide variety of patterns can be used to demonstrate the presence of psi, but there is no way to demonstrate the absence of psi. This, by itself, can contribute to a large number of spurious successes. And, of course, it makes the claims for psi unfalsifiable.

Another defect of this negative approach to the detection of psi, is that we have no disciplined way to claim that an effect size in one experiment is due to the same cause as the effect size in another experiment. I have already discussed how the neoparapsychologists create abstruse explanations to account for the peculiar patterns in the research data. These explanations assume that the various patterns all result from the bizarre and impish behaviour of a single, coherent phenomenon they call psi. But it seems much more likely that the different patterns such as the experimenter effect, the decline effect, and the reversal of effect are due to a variety of different phenomena. The lack of a positive definition and test for psi does not allow the parapsychologists to rule out this possibility.

Moreover, the claim that these evasive patterns are unique to psi research is just not true. Throughout the modern history of science, individuals have claimed to have discovered anomalies which challenged the specific scientific programme within which they were working. Some of these claims, on further investigation, turned out to be based on solid, replicable evidence. These resulted in appropriate accommodations to the relevant theory. Other such claims ultimately could not be consistently replicated and now occupy the scrap heap of science. The proponents of these discredited claims defended the failure of consistency and replicability with arguments that resemble those of contemporary parapsychologists – experimenter effects, decline effects as properties of their claimed phenomena, reversal of effects, etc.

Conclusions

If the neoparapsychologists are correct, then parapsychology, as it was envisioned during its first 160 years, is dead. To the extent that parapsychologists continue their endeavours, they will do so without a phenomenon that can be scientifically demonstrated and measured. Hopefully, the parapsychologists and the scientific community can learn important lessons from this failure. The parapsychologists attempted to be scientific by using key components of scientific methodology, but scientific methods without a lawful, systematic and replicable phenomenon cannot be science. Because it is so obvious, philosophers and other commentators on science and scientific method rarely focus on the fact that most of the day-to-day effort of scientists is devoted to making sure that their findings are trustworthy, lawful, communicable, and independently replicable. This is the necessary ingredient. Without replicable phenomena, science cannot exist.

References

• Article by Ray Hyman: “The Demise of Parapsychology, 1850-2009“.
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