ESP & Parapsychology curriculum

Researchers in the field call such information "nonlocal": it would not normally be available through any channel currently known. Psi is a label for a claimed effect, not an explanation of one. When you meet the word, read it as "the result the researchers say they cannot account for in ordinary terms," then ask what ordinary account was ruled out.

The defining feature is a second mind as the source. That is why telepathy experiments put a "sender" in a separate room and why a protocol with no sender cannot, by its design, distinguish telepathy from other psi claims. When a study calls a result telepathic, check that the design actually had someone thinking about the target.

Here no other mind is involved: the target itself is the claimed source. Remote viewing, describing a distant place, is treated in the field as a variant of clairvoyance. Because a target sealed in an envelope is still a physical object, the practical question in any clairvoyance test is how well the target was kept away from every ordinary sense.

In a laboratory, "future" usually means seconds: a computer picks the target only after the participant responds. That design closes the door on someone seeing the target early, which is its appeal. It also means the randomizer becomes the critical part, since a predictable random sequence could be anticipated by ordinary learning.

Early precognition tests used card symbols, colored lamps, dice faces or computer displays, scoring each correct guess as a hit. With four options, chance is 25 percent; with two, 50 percent. Before you judge any reported hit rate, work out the chance rate from the number of options, because a "high" score means nothing until you know what guessing alone would produce.

The analysis covered 62 investigators and more than 50,000 participants. Its effect size, about 0.02 per trial, means the hit rate sat barely above chance, yet the combined result was highly significant because the trial count was enormous. Keep the two numbers apart: significance tells you an effect is unlikely to be zero, while effect size tells you how big it is.

Instead of asking people to guess, newer designs measured reaction times, preferences or arousal, the way cognitive psychology studies processes outside awareness. The change made tasks less tedious and harder to fake, but it also added measurement choices, such as which physiological index to analyze, each of which is a place where flexibility can enter.

Proponents themselves note that psi has no explanatory theory compatible with current physical and biological principles, which is why critics demand unusually strong evidence. An anomaly can later turn out to be an artifact, a statistical quirk or something new. Treat "anomalous" as an open question, never as a finding about minds.

An American society with the same name followed two years later in Boston. The founders wanted to bring careful method to a subject long left to séance rooms and popular belief. Their writers openly admitted the subject's unsavory record and argued that investigators needed extra caution precisely because the material touched people's deepest hopes.

Frank Podmore's 1894 survey states the thesis plainly: communication between minds is possible other than through the known channels of sense. The word "provisional" matters. It named the claim to be tested, and the same survey spends its opening chapter on the ordinary ways the claim could be mistaken before presenting any evidence for it.

These were the leaks of their day, named before the data were weighed. Fraud covers signaling codes between partners. Each of the others is a sensory or statistical channel that can produce hits with no deception at all. A modern protocol is, in large part, this same list turned into rules about rooms, materials and analysis.

One reported subject learned to recognize particular playing cards face down by touch after a long series of trials, and a gambler was said to have trained the same skill. Podmore judged that some such subjects were not deceiving anyone and were unaware of their own method. Sincerity, in other words, does not close a sensory channel.

An astronomer at Harvard found that two star surveyors matched each other's magnitude estimates far more often than expected. It looked like thought-transference until analysis showed both favored the same round values. The rule carries over to any guessing test: if targets are not randomized, shared preferences alone can inflate the hit rate.

When an agent holds a percipient's hand or stands close behind, slight involuntary movements can steer a guess. Podmore's survey lists contact as a reason to discount some early trials and gives more weight to series where the two were kept apart. For any demonstration, check whether the two participants had a way to touch, see or hear one another.

Run under Henry Sidgwick from 1889, it counted about 32 well-attested cases of a recognized apparition within twelve hours of that person's death, out of an estimated 1,300 such apparitions. Chance predicted roughly 1 in 19,000, the survey found about 1 in 40, and the authors concluded chance could not explain it. Every input to that ratio was a judgment about testimony.

Apparitions from the past year were reported about three times as often as those from nine or ten years earlier. Correcting for that is reasonable, but the size of the multiplier was an estimate, and it feeds straight into the final chance comparison. When a calculation of odds depends on an adjustment, ask how sensitive the conclusion is to that adjustment.

He named the problem directly: memory is untrustworthy, imagination works on emotional events, and narrators err in many ways. His remedy was the experiment, where conditions are set in advance. That reasoning is why the field moved from collecting stories to running trials, and it is still the right first question about any striking anecdote.

His aim was to separate the subject from its origins in séances. His first major publication impressed many readers with a large database gathered under controlled conditions. Even the field's sharpest critics credit the ambition: Rhine introduced the laboratory guessing test, which made psi claims countable and therefore testable.

Critics then turned to the methods, where, in one later reviewer's account, they had more success. The episode is worth remembering because it separates two questions. Correct arithmetic on the data says chance alone is unlikely; it says nothing about whether the cards could be seen, the records were accurate or the sequence was truly random.

According to the 1995 government-commissioned review, the failure of several scientists to replicate the results mattered more than any single methodological complaint, and the problem has followed the field ever since. A result that appears only in one laboratory may reflect that laboratory's conditions, so independent replication is the test that matters most.

High early hits and low later hits can average out to chance, so the pattern let null results be read as hidden evidence. The critic Ray Hyman pointed out that declines were claimed across score sheets, halves and whole experiments, and that some workers even reported inclines. A sign that shows up in nearly any form cannot serve as a prediction.

After S. G. Soal failed to replicate Rhine, he reanalyzed his data this way and found two subjects whose guesses matched the next or the previous card. Each new alignment is one more test, so some will look significant by chance. A pattern found by searching counts as evidence only if a fresh study predicts it beforehand and then finds it again.

Hyman listed negative hitting and increased variability among the signs offered when the ordinary test failed. If above-chance scores, below-chance scores and declining scores all count, the hypothesis no longer forbids any result. Settle in writing, ahead of the experiment, which result would count against the claim, and then stick to that.

At SRI, a 1988 review of its own work found free-response trials, where a person describes a target, far more successful than forced-choice ones. Hyman read the turnover differently: each generation's best evidence was later dropped as flawed. Both readings agree on the fact that Rhine-era card data are no longer offered as the strongest case.

A small p-value makes chance an unlikely explanation, and 0.05 is the usual threshold for calling a result significant. It does not give the probability that psi is real, and it does not weigh any other ordinary explanation. Read "p = 0.002" as "rare under pure chance," then ask what else besides chance could produce it.

This is why a single positive study proves little, and why reviewers on both sides of the psi debate asked for replication before accepting non-chance results. Run twenty independent tests of a nonexistent effect and you expect one success. When a laboratory has run many tests, tally the tests first and the hits second.

Statistician Jessica Utts used a birth-ratio example: 70 boys in 100 births, against 51 percent expected, gives p = 0.0001, while 7 in 10 gives p = 0.19. Both are 70 percent. Calling the small study a failed replication would be wrong. A replication succeeds when its effect falls within the expected range of the original, not when its p-value repeats.

A medium effect is meant to be visible to a careful observer and a large one to anyone. Most psi effects reported in the remote-viewing and ganzfeld literature sit near or below the small benchmark. That is why they need hundreds of trials to detect, and why a single dramatic demonstration does not resemble what the laboratories actually report.

Utts made this point explicitly: nothing about a viewer's words can be modeled as random, so the random step must be the target draw, with every candidate equally likely. A protocol that lets someone pick a "suitable" target, or that uses an untested randomizer, has no valid chance baseline at all, however careful the rest of it looks.

Hyman argued that real distributions only approximate the textbook ones, which rarely matters in ordinary work. With enormous trial counts, though, a slight flaw in the assumed chance rate, such as a randomizer that is not quite uniform, can be detected as "significant." More power is not always more truth; it can also mean more sensitivity to an imperfect baseline.

Hyman contrasted this with magnetism or forgetting, whose existence nobody needed a significance test to confirm; research there studies how they vary. When an effect exists only as a statistical departure, every assumption behind the baseline becomes part of the claim. Proponents reply that many real effects in medicine and psychology are also small and statistical.

In the original ganzfeld database one experimenter supplied nearly half the trials, and another's effects were all negative. Pooling by trials gives one average; weighting experimenters equally gives another. When a "consistent" average is cited across programs, ask whose data dominate it and whether the parts agree.

This was the first item on a checklist Utts gave for a well-designed remote-viewing experiment. Contact includes conversation, a glance, a tone of voice or a hint about how a session is going. The rule is strict because a cue does not need to be deliberate to work, and the person giving it may not realize it happened.

In a free-response study the judge decides which candidate best matches a description, so the judge's knowledge is part of the measurement. A judge who has heard that today's session "felt strong" may read the transcript differently. Keep the judge as ignorant as the participant until the ranking is recorded.

Every chance calculation assumes this equality. If a person picks the target, their tastes can line up with a viewer's tastes; if a randomizer has a bias, a viewer can learn it. Check that the randomizing method was named, tested and applied the same way on every trial.

If the same photograph a sender held is shown to the judge, creases, fingerprints or wear can distinguish it from decoys that nobody touched. Using duplicate sets, one for the trial and one for judging, closes this channel. The fix is cheap, which is why its absence in an older study is a serious mark against it.

If a study can be halted whenever results happen to look good, random swings upward get captured and swings downward get ignored. Some statistical methods allow other stopping rules, but each must be unambiguous and declared beforehand. When you read a study, look for where the trial count was decided.

Dropping a session because the participant felt ill is legitimate only if the decision is made while the target is still unknown. Otherwise, misses can be explained away and hits kept. The same logic applies to choosing an analysis after seeing the data, which the same checklist also ruled out.

In early SRI work, natural sites were used once each and transcripts sometimes mentioned an earlier session's target. Knowing which sites were already used narrowed the field for the judge with no psi needed. In any series, check whether one trial's information could leak into scoring another.

The 1995 review describes this as one statistical flaw of early remote-viewing studies. Chance scoring assumes each target could receive each rank with equal probability. A judge's reasonable instinct, "I already used that one," violates the assumption and can inflate scores. Each session should be judged as if it were the only one.

When an experimenter drives to a location, the length of the trip or details that later reach the viewer can narrow the possibilities. Later designs replaced travel with randomly chosen photographs under double-blind conditions. Whenever a target is a real place, ask what the timing and logistics of reaching it could reveal.

Translucent half spheres, often split ping-pong balls, sit over the eyes, and white or pink noise plays through headphones for 15 to 30 minutes after a relaxation phase. Honorton, Braud and Parker pioneered it in 1974 and 1975 on the idea that a uniform sensory field favors inner impressions about a hidden target. The setting is a hypothesis about conditions, not evidence by itself.

The participant may judge for themselves, or the recording may go to an outside judge who rates each candidate. Whoever judges, the description is open-ended, so matching it to a picture is a judgment. That is why the person who interacts with the participant must stay blind to the target until the rating is finished.

Each session gives one hit or miss, and results are reported as the proportion of hits. A hit rate of 32 percent therefore means about 7 more hits per 100 sessions than chance predicts. Given any ganzfeld figure, subtract the 25 percent chance rate first; the whole claim sits in what remains.

If the target is chosen after judging, the task is precognition; chosen before with no sender, clairvoyance; chosen before and shown to a partner in a distant room, telepathy, the classic version. The participant's experience is identical in all three. A difference between them therefore has to be found in the data, not assumed from the label.

Ray Hyman criticized the database's flaws, and the two then wrote a joint communiqué agreeing that the overall effect could not reasonably be explained by selective reporting or multiple analysis, while setting stricter guidelines for future work. The exchange is a model of productive disagreement: the critic and the proponent agreed on what a better experiment would need.

Milton and Wiseman reported an effect size of about 0.013 for 1987 to 1997. Utts, counting raw trials with an exact binomial test, found 327 hits in 1,198 sessions, about 27 percent, p = 0.036. Same studies, different unit of analysis, opposite verdicts. When two analyses disagree, find the choice that separates them.

Its authors report that frequentist and Bayesian models agreed, that the result passed four publication-bias tests, and that selected participants showed about three times the effect of unselected ones. It was preregistered as a registered report, which limits flexible choices. As with any meta-analysis, the next question is whether independent teams reach the same figure.

Its results, published by Bem and Honorton in 1994, showed 106 hits in 329 sessions, 32.2 percent against 25 percent. Hyman acknowledged that the design removed all but one of the flaws he had listed. Three later laboratories, in Amsterdam, Edinburgh and North Carolina, reported hit rates of 33 to 37 percent.

He looked for this deliberately, as a check on randomization, and found it in every breakdown he tried. Proponents read it as another feature of psi. A pattern like this does not prove an artifact, but it is exactly what a flaw in target selection or presentation would produce, so it points to where the next design should tighten.

Most targets in the original ganzfeld database were still pictures, so the closest like-for-like comparison showed no effect. Hyman asked whether the right summary was the combined average or the dynamic clips alone. Whenever a result is carried by one subgroup, ask whether that subgroup was predicted in advance or found afterward.

Its authors removed six outliers, three high and three low, to make the set homogeneous, and combined 24 pre-1985 studies with 78 from 1985 to 2010. Hyman objected that the older studies had obvious flaws and should not be merged with newer ones. Every pooled figure rests on inclusion choices like these.

The ganzfeld meta-analysis calculated that about 2,414 hidden studies would be needed. Scargle pointed out that the decision not to publish is not neutral: the studies left unpublished are likely the weaker ones, so assuming they average exactly zero is unsafe. Treat a large fail-safe number as a weak reassurance.

A survey of all finished studies at the Koestler Parapsychology Unit in Edinburgh produced those figures. A comparable mainstream set, the TESS social-science studies, published 20 percent of null results against 60 percent of strong ones. The authors concluded that both fields showed a strong bias toward publishing positive work, a fact that any pooled estimate has to absorb.

The authors named this practice and noted that researchers rarely count it as unpublished data, since the study was never finished. The discarded sessions are still real results. When a report mentions protocol adjustments early in a study, ask what happened to the data collected before them.

Most laboratories run pilot sessions to learn the equipment. If the pilot looks good it can be counted as part of the real study, and if not, it is set aside. The choice depends on the outcome, so it biases the total. The cleanest remedy is to declare in advance that pilot data never count.

In the survey of psychologists the authors drew on, more than half were estimated to have collected more data than planned. About 45 percent of ganzfeld sample sizes looked fixed in advance, such as 10, 20 or 30, while the rest were irregular. A round, declared sample size is a small but real sign of discipline.

The authors called this outcome somewhat surprising, since students are taught that optional stopping inflates scores. A practice can distort the p-value more than the average hit rate, and its effect depends on the design. The lesson is to measure a practice's impact in the case at hand rather than assume it.

With no anomaly at all, the simulation fit the real data only with unrealistic settings. With a 27 percent hit rate built in, the fit was good, and the corrected result remained significant at p = 0.003. The authors concluded the published figure was likely inflated, while the remaining excess could be an unidentified practice or a genuine effect.

At that effect size, a study needs roughly 700 people for an 80 percent chance of reaching p < 0.05. Small studies cannot reliably find such an effect, so a literature of small studies will show a jumble of hits and misses. The authors suggested coordinated large studies, which is the direction later replication projects took.

Uncorrected effect sizes were about 0.50 for artistic samples against 0.14 for unselected ones. Proponents read this as evidence that ability varies; it also means fewer studies, a smaller base, and more room for chance. A moderator found across many analyses becomes persuasive only when it is predicted and confirmed in new, preregistered work.

Kenneth Kress, a CIA physicist who managed early contracts, described it as akin to clairvoyance and set it beside psychokinesis, the claimed influence of a person on a machine or object. His 1977 internal review covered only those two claims, because those were the ones the agency had paid to test.

Kress noted that in 1952 the Department of Defense heard a lecture on possible uses of extrasensory perception in psychological warfare. Later, under a project called ULTRA, the CIA commissioned a review from the director of an Oxford parapsychology laboratory, who concluded that ESP was demonstrated but neither understood nor controllable. Nothing followed for about a decade.

An early demonstration involved a subject said to disturb a shielded magnetometer at Stanford. A few days of tests in August 1972 cost $874, and the CIA observers found the subject's descriptions of hidden objects accurate enough to fund more work. Small, informal demonstrations launched a program that ran for more than two decades.

One subject seemed to raise a thermistor's temperature but the other could not; the second reproduced sealed drawings while the first produced nothing; repeating an experiment with the same person did not give consistent results. Kress later wrote that he began to doubt his own objectivity. Inconsistency like this is the pattern that later reviewers placed at the center of the case.

That is about 100 hits above the 625 expected. Agency reviewers suspected the machine was not random and that the subject had learned its patterns. Kress had the recorded machine states reanalyzed, which found no nonrandomness, and a retest gave 28 percent. The case shows the right move: compare performance with the machine's actual behavior, not its assumed behavior.

Given only coordinates and a map, Price drew a gantry crane that two analysts judged accurate; one wrote that he either saw it remotely or was told what to draw by someone who knew. Asked why he had missed four derricks, Price said they were gone; reconnaissance showed them still standing. Because good and bad details came mixed, the overall result was not judged useful.

Kress's agency reviewers made this point about Price's data, and the 1995 evaluation later made it about the whole operational program. An evaluator who already knows the site can pick out the hits afterward. An analyst who needs the information cannot, and that is the only situation in which intelligence has value.

He described skeptics who would not believe the material even if it were true, and believers who took one unexplained success as proof after a personal conversion experience. Both, he argued, made careful evaluation harder. The fair stance is to state what evidence would move you, in either direction, before looking at it.

He reported that tantalizing but incomplete data had come out of agency-funded work, and that funding faded amid institutional caution, including what he called the "Proxmire Effect," fear of public ridicule over unusual contracts. His paper is a participant's account, written from inside the program, so read it as testimony about the work as well as about the results.

The defense agency's direct involvement began about 1985. The program had three parts: operations against foreign targets, laboratory research, and assessment of foreign work. When the CIA considered taking it over in 1995, it commissioned the American Institutes for Research (AIR), a nonprofit research organization, to evaluate the first two parts.

Both were described as fair and open-minded, and two AIR scientists with no background in parapsychology joined them to give a neutral methodological view. The panel read about 80 publications. Pairing opposed experts and having them reply to each other is a design worth copying whenever a contested claim needs a hearing.

A rank of one means the true target matched best. Over many trials, an average rank reliably below three is the claimed evidence. The method gives no extra credit for a near-perfect match, which makes it conservative. Its effect size is the distance of the average rank from three, divided by the square root of two.

By the convention of 0.2 as small, both are small effects, comparable to the ganzfeld replications she tabulated alongside them. She read the similarity as replication. Hyman answered that matching effect sizes across very different designs can arise for different reasons, so similar numbers are not proof of one shared cause.

The analysis also reported that six selected subjects outperformed others, that training did not reliably improve performance, and that distance and electromagnetic shielding seemed not to matter. Utts acknowledged that some early studies had methodological problems. A tiny p-value over a mixed set of studies says chance is unlikely, not which of the studies is sound.

The panel noted that the two agreed far more than they disagreed. Their main dispute was not whether the hit rate exceeded chance but why. Reading the whole program, and most psi debates, hinges on keeping two questions apart: "is there a non-chance effect?" and "what causes it?"

Hyman reported that this judge was familiar with each viewer's style and might read "bridge" as anything over water. Both reviewers saw a risk of unintended influence on the matching, called criterion contamination. The panel concluded that until independent judges agree, the source of the effect cannot be located.

The panel called this monomethod bias: a subtle influence specific to one method can repeat in every study that shares it, so consistency across such studies is weaker evidence than it looks. Hyman added that secrecy had kept outside laboratories from criticizing or repeating the work. Independent replication varies exactly the parts a single laboratory holds constant.

Users reported that reports sometimes caught broad background features but missed the concrete specifics intelligence needs; they were inconsistent, often wrong on details and needed heavy interpretation. Viewers and managers also said reports had been changed to fit known background cues. The panel recommended ending operational support.

Utts made this point about early SRI cases, adding that one cannot be certain a viewer never spoke with someone who knew the site. She compared it to dreams of plane crashes: some dreamers will dream one before a real crash. Anecdotes persuade; only controlled designs measure.

The Army Research Institute asked for that review of performance-enhancement techniques. Since then, the 1995 report noted, perhaps 50 to 100 more studies had been run, some designed to answer the council's methodological complaints. The 1995 evaluation therefore asked whether the newer work changed the verdict, and concluded it did not justify continuing the program.

The hypothesis in each case was that the reversed version would show the same result as the normal one. Because the causal event comes after the response, sensory leakage of the target is impossible by design. What remains open is everything else: randomization, analysis choices, and how many versions were run.

Chance is 50 percent, so the claimed effect is a small lean above that. The choice is recorded before the computer selects the target, which is what makes it a precognition test. This exact task later became the subject of a large multi-laboratory replication.

In ordinary priming, a word like "beautiful" shown just before a pleasant photo speeds the judgment that the photo is pleasant. Bem's version showed the word afterward. If timing could reverse causation, reaction times would still differ. Such tasks use many trials per person, so the analysis choices, such as outlier handling, carry real weight.

A 2012 meta-analysis of 26 reports from 1978 to 2010 gave an average effect size of 0.21. Measures included skin conductance, heart rate and pupil size, which also means several measures that could be analyzed. The analysis drew a published critique and a reply, so it remains a disputed result rather than a settled one.

Its combined z was 6.40. Excluding Bem's own experiments, independent replications gave 0.06. An effect of 0.09 is under a tenth of a standard deviation, far below the conventional "small" benchmark of 0.2. The paper was written by proponents, Bem among them, which makes the independent subset the figure to watch.

Fast-thinking protocols averaged 0.11 and slow-thinking ones 0.03, which was not significant. The authors note the split was made after the fact. A subgroup division chosen after seeing the data can always find a stronger part, so treat it as a hypothesis for the next study rather than a result.

Judd and colleagues showed that ignoring variation among pictures or words inflates false positives well above the nominal 5 percent in many psychology designs. A result can rest on the specific stimuli used rather than on people in general. Ask whether a study's conclusions would survive a fresh set of stimuli.

If each study has a modest chance of significance, a long unbroken run of successes is itself improbable. Two analysts, Francis and Schimmack, made this argument; the meta-analysis authors report that most of their bias tests found little sign of selective reporting. Learn the test: a record with too few failures is evidence about the record.

Wagenmakers and colleagues used one default Bayesian test; Bem and colleagues argued for another, and Rouder and Morey criticized both. The dispute shows that a Bayesian answer depends on the alternative hypothesis it is given. Read any Bayes factor together with the effect sizes its alternative allowed.

The combined p-value was 0.83, one-tailed. Experimenters left the room and a computer ran the task, following Bem's own advice for limiting experimenter effects. Preregistration fixed the analysis before data came in, so this result cannot be dismissed as a fishing expedition, though a sample of 150 is too small to rule out a very tiny effect.

Correcting "ctt" to "cat" is a judgment call, and making it while knowing the word's condition opens a path for unconscious bias. Bem acknowledged the issue but argued the scores barely changed. The replications had two raters blind to condition code every unrecognized word. Any manual correction should be made blind to the hypothesis.

A one-tailed test counts only results in the predicted direction, halving the p-value for a given effect. It is defensible when the direction is truly fixed in advance, as Bem's team argued for replications. It becomes a problem when used on a first, exploratory test. Check which tail was planned, and when.

After two review rounds, the panel agreed the protocol was methodologically sound and secure against questionable research practices. Getting both sides to approve a design before data exist removes the most common reply to a null result, "the study was done wrong," and the most common reply to a positive one.

Ten laboratories in nine countries took part, with the protocol preregistered and every participant run on the same software. Choosing one well-defined task, rather than a family of variants, means a single clear answer. It also means the result speaks to that task, not to every claim of precognition.

That is slightly below the 50 percent chance rate and well below Bem's 53.07. At this size, a real effect like Bem's would have shown up clearly. The project also reported that the probability of a true hit rate above 50.6 percent was under 1 percent. A large, preregistered null speaks more strongly than any number of small ones.

A non-significant result alone cannot show absence; it may only show too little data. An equivalence test fixes a cutoff below which an effect is too small to matter, here 51 percent, then asks whether the data exclude anything bigger. They did. When you want to claim "no effect," look for this kind of test.

Sequential designs let a study end early when evidence is decisive, which saves effort, but only because the checkpoints and the rules were set in advance. That is the opposite of optional stopping. The difference is not whether you look at the data early; it is whether looking can change what you decide.

The project called this direct data deposition with born-open data, plus automatic real-time reports. Nobody could quietly drop sessions or edit records, because the public copy existed from the first trial. Transparency during collection, not only after it, closes the gap where errors, bias or fraud could otherwise hide.

Even a preregistered study can drift: an experimenter phrases instructions differently or handles an unexpected event in an improvised way. The project treated proving fidelity as part of the method. Ask of any striking result how anyone outside the room could confirm the procedure was followed.

Every participant, at every site, used the same program through a web browser. That removes a whole class of explanations, from accidental version differences to deliberate manipulation, without accusing anyone. Good controls protect honest researchers as much as they guard against dishonest ones.

The "sheep-goat" idea holds that believers score above chance and skeptics below. The project tested for consistent individuals by correlating each person's odd and even trials and found no such pattern. A claimed individual difference should show up as consistency within the same person, which is a test you can run on any data set.

A participant tries to push a generator's output in a chosen direction, and the result is compared with the generator's expected behavior. Because any single deviation is tiny, the claim is always statistical, and it depends on knowing exactly how the generator behaves when nobody is trying.

A true random number generator relies on a quantum process, which makes each output unpredictable from the ones before, unlike software that computes a pseudo-random sequence. That rules out learning the sequence. It does not rule out drift or bias in the hardware, which still has to be checked against long control runs.

Heterogeneous means the studies disagreed with one another more than chance variation allows. A tiny average built from inconsistent studies can reflect a few unusual results rather than one steady effect. The authors of a later test listed both points, along with failed replications, as the reasons the scientific community remained doubtful.

The original study had 97 participants and about 2.5 million trials. The 2000 replication, run jointly with laboratories in Freiburg and Giessen, had 227 participants and more than 2 million trials. The original laboratory took part and reported the null, which is the system working as intended.

The Bayes factor was about 10 in favor of the null hypothesis. The study was intended as a decisive test and stopped by a rule fixed in advance. Its authors, whose own earlier study had reported positive evidence, stated plainly that micro-PK did not appear in the data, which is the kind of reporting that makes a field credible.

Unlike repeated significance testing, this method was designed for continuous monitoring, provided the target strength is fixed beforehand. It can also end in strong support for the null, which a classic significance test cannot give. The weakness to check is the prior on effect size, which shapes how fast evidence accumulates.

The smokers were expected to influence how often cigarette-related pictures appeared. No such pattern appeared for non-smokers or in a simulation with no observers. An effect that grows and then vanishes on replication is what chance swings in a sequential test can look like, and also what proponents call a decline effect.

One such model, built on the idea of "pragmatic information," holds that the more novel an effect, the less likely its successful replication. Whatever its merits, a theory that predicts non-replication is very hard to test. Ask of any such model what observation it forbids; if none, it cannot be tested.

They presented it as an exploratory observation, not as evidence for micro-PK. That is the correct handling: a pattern spotted after the main test fails is a new hypothesis to test in new data, never a rescue of the original claim. Watch for writers who quietly turn this kind of observation into a finding.

He later explained in detail how he and his partner had fooled the investigators. Hyman retold the story to make a general point: being unable to imagine a method is not evidence that none exists. A protocol must hold up against deception that the designers have not thought of.

Those trials, and the Smith-Blackburn series after them, were later set aside as defective. Hyman used the sequence to argue that each generation's best evidence for psi has been discarded by the next. Proponents answer that methods improved each time. Both views agree that early confidence was misplaced.

Critics grew suspicious because the results were too good and because Soal lost the original records under suspicious circumstances. For years their proposed explanations required elaborate collusion among several respected people. The case is a warning that a too-perfect record deserves more scrutiny, not less.

It needed only one person and a simple, clever trick that nobody had anticipated, and its discovery came partly by fortunate accident. That a researcher within the field exposed it is part of the record, and it shows self-correction can come from inside. Fraud gets caught by examining the raw data, not by arguing over whether something sounds plausible.

He compared new experimental designs to new computer programs that need debugging, and noted that removing obvious flaws can leave more subtle ones. The first years of results from a fresh design therefore carry less weight than results from a design that many critics have attacked and others have reused.

The authors set this rate after noting that a survey-based estimate of about 4 percent for psychologists converged with what had been detected in experimental parapsychology. A small fraud rate can still matter when the effect being studied is tiny, because a few fabricated studies can supply much of the excess.

On one side, heavy scrutiny and journals that publish null results reduce the pressure; on the other, some researchers may be defending a worldview. Unable to settle it, they assumed the same rates as experimental psychology. When you lack data on a group, a neutral assumption stated openly is fairer than a guess in either direction.

Unlike a p-value, it compares two specific hypotheses, such as "there is an effect of this rough size" against "there is none." It can favor either. The meta-analysis authors gave Jeffreys' labels: 1 to 3 barely worth mentioning, 3 to 10 substantial, 10 to 30 strong, and above 100 decisive.

In the authors' example, someone who gives psi 20 percent, prior odds of 0.25, and sees a Bayes factor of 3 ends at odds of 0.75, still leaning against it. Above a factor of 4 they would lean toward it. Someone starting at one in a million would need a factor of millions. Prior odds are where the "extraordinary claims" principle lives.

Huge samples can yield enormous Bayes factors for tiny effects, in the same way they yield tiny p-values. Either number only says that, under the model used, the pooled data depart from pure chance; neither says why. Questionable practices, publication bias or a flaw shared across studies are also ways of not being pure chance.

Proponents accept that this justifies a higher bar. They argue it does not justify rejecting evidence before examining it, pointing to aspirin, whose effect was used long before it was explained. Both points can be held at once: a missing mechanism raises the prior bar, and evidence that clears it still counts.

The meta-analysis authors note that psychologists, aware of past claims that failed to survive replication, are among the most skeptical academics about psi. That skepticism is a choice about which error costs more. Being explicit about it lets two readers agree on the data while disagreeing about the decision.

Ioannidis called that probability the positive predictive value. With low prior odds, even well-run studies yield many false positives among their significant results. For psi, where prior odds are disputed, this is the honest center of the disagreement: the same significant result means different things under different priors.

Both points lower power, and low power means a larger share of significant results are flukes. Psi effects are small, and many psi studies have been small. Weight one large, well-run study above many small ones that each just reach significance.

Ioannidis noted that prejudice need not be financial; commitment to a theory or one's own past findings is enough. That applies to proponents defending psi and to critics invested in its absence. Standard, preregistered analyses reduce flexibility for everyone.

Ioannidis called this rapid alternation of extreme claims and opposite rebuttals the Proteus phenomenon. A celebrated result followed by a wave of failed replications has this shape. Expect the first results in an exciting area to be the most extreme and the later, larger ones to be smaller.

The research on paranormal belief studies these errors as ordinary features of human thinking, present in everyone to varying degrees. Studying them is not a way of calling believers irrational. It is a way of explaining why a striking experience can feel like evidence even when chance is enough to produce it.

Earlier work comparing several reasoning tasks found that perception of randomness predicted belief level better than base-rate or expected-value problems did. One interpretation is a tendency to see random coincidences as meaningfully connected, so chance events read as signals.

The probability of A and B together can never be larger than the probability of A alone. In studies, paranormal believers made more conjunction errors than non-believers. A vivid story that links details, such as a dream that matched a phone call, can feel more probable precisely because it is more detailed, which is the reverse of the arithmetic.

The scale used separates traditional beliefs, which include religious beliefs, witchcraft and precognition, from New Age beliefs such as psi, spiritualism and astrology. The two seem to serve different functions, one social and cultural, one personal. "Paranormal belief" is not a single trait, so a finding about one type may not hold for another.

The trait measured, called Unusual Experience, belongs to schizotypy, a set of personality traits present across the general population; it is not a diagnosis. Belief appeared to offer a framework for interpreting such experiences. Taking the experiences seriously while testing the explanation offered for them is the fair approach.

Context changes how people reason, so a skill measured with neutral puzzles may not show up when the topic is emotionally loaded. The practical rule is to restate a striking coincidence in neutral terms, such as "one of many daily events matched one of many thoughts," before judging how unlikely it was.

The authors stated this limitation themselves and called for longitudinal research. Biased thinking might feed belief, belief might shape reasoning, or some third factor might produce both. Apply the same caution you apply to psi claims: a correlation in one sample does not establish a direction of cause.

His list ran from the Creery sisters and Smith-Blackburn, through Rhine's cards and Soal's experiments, to the ganzfeld, random generators and remote viewing. He contrasted Newton's prism experiment and Ebbinghaus's forgetting curve, which still replicate. A strong result in a mature science stays strong; that is the standard he applied.

She reasoned that different experiments would need different hidden flaws that happened to produce similar effects, and that fraud would require many cooperating people. Her conclusion was that existence was established and research should turn to how it works. This is the strongest proponent case, and it should be learned in that form.

Many different factors can push results away from a chance model by similar small amounts. He also noted that averages depend on how studies are weighted. The exchange teaches a general rule: matching numbers point to a common cause only after the other possible causes have been excluded.

A statistical anomaly is defined negatively, as something not yet explained. Without a theory that sets boundary conditions, no result can count against the claim and none can confirm a specific mechanism. Asking "what would this theory forbid?" is the cleanest single test of any explanation.

The 1995 panel agreed that how often an effect appears should not decide whether it is worth pursuing. It also accepted Hyman's practical point: weak, erratic effects cannot guide action. Holding both is fair: an anomaly can merit research while still being useless for application.

That wording is the careful summary of decades of research. It grants the numbers, refuses the inference, and leaves open that adequate evidence could someday be provided. Summarize any contested finding in the same three parts: the measurement, the inference it does not support, and the evidence that would change the verdict.

Even then, he said, the result would establish an anomaly, not yet psi. Specifying the standard in advance is fair to proponents, because it tells them what to do, and it binds the critic, because meeting it should change his view. Write down the evidence that would change your mind before you look.

Preregistration does not make a result true, but it removes the most common ways a false one is produced: choosing analyses after seeing data, stopping when convenient and reporting only the successful variant. A result without it is best read as exploratory, however striking.

The Transparent Psi Project showed this is possible on a contested topic. If a new study was designed only by people who expected one outcome, ask whether the other side would have accepted its protocol. If not, its result will settle little, whichever way it comes out.

Direct deposition to an independent repository, with real-time reports, makes the record public from the first trial. Data released only at the end can be complete and honest, but readers must take more on trust. The more extraordinary the claim, the less trust it should require.

A lean of one percentage point above a 50 percent chance rate looks nothing like the dramatic success that anecdotes suggest. Small effects need large samples and are easily mimicked by small biases. Knowing the size tells you what kind of evidence and what sample size it would take to confirm.

The curtain task's 53.07 percent came from a single program of studies; the replication's 49.89 percent came from more than 37,000 trials under joint supervision. Small studies are noisy and pass through a publication filter, whereas a large planned study has neither problem. Judge evidence by quality and sample size rather than by tallying papers.

Logs, recordings, central software and outside auditors let others confirm what happened in each session. Without them, readers rely on the authors' description alone. When a report gives little detail about how sessions were actually run, treat that missing detail as missing evidence.

The consensus panel fixed in advance what each possible outcome would mean, so nobody could reinterpret the result afterward. You can apply the same discipline to your own judgment. It protects against believing too easily and against dismissing too easily, which are the two errors this subject invites.