Why psychedelic science keeps asking whether the trip matters, and why its methods cannot answer

There is a finding that psychedelic science has repeated for fifteen years, and it is the closest thing the field has to a mechanism.

The finding is this: people who have more intense mystical experiences during a psychedelic session get better outcomes afterwards. Roland Griffiths reported it in cancer patients. Leor Roseman reported it in treatment-resistant depression. Albert Garcia-Romeu reported it in smokers trying to quit. Michael Bogenschutz reported it in alcohol use disorder. A 2022 systematic review found that ten of twelve studies examining the relationship established a significant association of correlation, mediation, or prediction. When David Yaden and Roland Griffiths wrote, in 2021, that "the subjective effects of psychedelics are necessary for their enduring therapeutic effects," this body of correlations was the evidence they had in hand.

It is a genuinely important claim. If the experience is the mechanism, psychedelic therapy needs therapists, preparation, integration, eight-hour sessions, and everything that makes it expensive and hard to scale. If the experience is not the mechanism — if it is what David Olson has called an epiphenomenon riding on top of the neuroplasticity that does the real work — then the future is a pill you take on a Tuesday and go back to work.

The entire architecture of the field's next decade rests on which of those is true.

This essay is about a narrow and unglamorous claim: that the field's standard method for answering the question cannot answer it. Not that the answer is one thing or the other. That the instrument, as currently deployed, is incapable of returning a trustworthy signal in either direction. Two failures compound. The first is a power problem, which is fixable with money. The second is a measurement problem, which is not.

I. What a null looks like when it arrives

Start with a recent, ordinary example — not because it is important, but because it is typical.

In June 2026, Raynara Bolcont and colleagues at the Federal University of Rio Grande do Norte published a secondary analysis in the Journal of Psychopharmacology, pooling wellbeing outcomes from two of their inhaled-DMT trials: a phase I dose-escalation study in healthy volunteers and a phase IIa open-label trial in treatment-resistant depression. Twenty-five healthy participants in the analysed sample. Fourteen patients. Anxiety, life satisfaction, and quality of life tracked out to twelve months in the patient group.

Buried in the results, after the headline findings, is a subsection on correlations. The team had administered the full battery of psychedelic experience measures: the Mystical Experience Questionnaire, the Five Dimensions of Altered States of Consciousness scale, the Hallucinogen Rating Scale, visual analogue scales for intensity and valence. They correlated these against every wellbeing outcome.

Nothing survived correction for multiple comparisons. Not in the healthy volunteers. Not in the patients.

The paper reports this plainly, in two sentences, and moves on. The discussion continues to lean on "the importance of subjective meaning-making and integration processes." The null is noted and then, functionally, ignored.

Now: what should a reader take from that?

The tempting reading — and I have seen versions of it circulating already — is that the trip didn't matter here. The mystical experience scores predicted nothing, so the mystical experience did nothing. That reading is wrong, and it is worth being precise about why it is wrong, because the precision is where the argument lives.

II. The power problem: what n=14 can see

Statistical power is the probability that a study will detect an effect that is genuinely there. It is determined by the size of the effect, the size of the sample, and the significance threshold. The convention, since Cohen, is that 80% power is adequate — you want at least a four-in-five chance of finding what you are looking for.

Here is how much sample you need to detect a correlation at 80% power, two-sided, uncorrected:

True correlationParticipants needed
r = 0.1 (small)783
r = 0.2194
r = 0.3 (medium)85
r = 0.447
r = 0.5 (large)29
r = 0.620

Bolcont had 25 and 14.

But the more useful way to present this — and the way I wish more papers would — is to invert it. Rather than asking "what was the power to detect a medium effect," ask: what is the smallest correlation this study could reliably have found? This is the minimum detectable correlation, and it is a property of the design, not of any assumption about the truth.

For these two samples, computed exactly:

UncorrectedBonferroni ÷6Bonferroni ÷20
Healthy (n=25)r = 0.54r = 0.63r = 0.68
Patients (n=14)r = 0.69r = 0.78r = 0.82

Read that table slowly.

Uncorrected, the patient cohort could only reliably detect a correlation of 0.69 or larger. Bolcont ran the correction across substantially more than six comparisons — the exact count is not fully specified in the paper, which is itself a reporting failure worth noting — but at any plausible number, the patient sample was capable of detecting only correlations of roughly 0.8 and above. A correlation of 0.8 between a questionnaire administered on the day and a quality-of-life score twelve months later would be one of the strongest findings in the history of clinical psychology. It would be extraordinary. Nothing in this literature is that large. The largest reported MEQ–outcome correlations sit around 0.5 to 0.6, and most are well below.

So the patient analysis was, in a meaningful sense, designed to detect an effect that nobody believes exists. It was not testing the hypothesis. It was going through the motions of testing the hypothesis.

The healthy sample is better but not good: it could see r = 0.54 uncorrected, and roughly 0.63 to 0.68 once corrected. Its power to detect a medium correlation of 0.3 was 30.6% uncorrected, and 11.8% under a six-test correction. Under a twenty-test correction, 5.8%. At that point the test is a coin flip weighted heavily towards "no."

Here is the part that matters for how you read the paper. A null from a design like this is not evidence that the effect is absent. But it is also not evidence that the effect is present and was missed. It is compatible with a true correlation of zero, and equally compatible with a true correlation of 0.4. The study cannot distinguish between those worlds. It never could have.

This is the symmetry that gets lost. It is tempting, having correctly demolished the "no correlation, therefore no mechanism" reading, to swing to "no correlation, therefore the effect was probably there and they missed it." That is the same error wearing a different hat. Low power does not make the null hypothesis false. It makes the study silent. The honest summary of Bolcont's correlation subsection is: this analysis rules out a very large association and nothing else.

There are tools for saying this properly. Equivalence testing — Daniel Lakens' work is the standard reference — asks not "is the effect zero" but "can we reject effects at least as large as X?" Bayes factors quantify how much the data favour the null over a specified alternative. Neither is exotic. Neither appears in this paper, or, as far as I can find, in any psychedelic trial's treatment of an experience–outcome null. The field reports nulls as though non-significance were a finding, and then either ignores them or overreads them, depending on which way the author's sympathies run.

III. The mediation problem: an order of magnitude worse

The correlation is the easy version. What the field actually claims is mediation — not that experience and outcome travel together, but that the drug works through the experience. That is a stronger claim, and it needs much more data.

Three propositions get run together in this debate, and they are not the same:

  1. Acute experience correlates with later improvement.
  2. Acute experience statistically mediates the treatment effect.
  3. Acute experience is causally necessary for the treatment effect.

A correlation can exist without mediation. Mediation can be estimated without being causally identified. A mediator can contribute substantially without being necessary. These are four different questions and the literature routinely uses evidence for the first as though it settled the third.

The sample sizes diverge sharply. Fritz and MacKinnon's 2007 paper in Psychological Science remains the canonical reference: 100,000 simulations per cell, tabulating the n required for 80% power across six mediation tests and every combination of path strengths. Using their coding (small = 0.14, medium = 0.39, large = 0.59), the requirements for the joint significance test — one of the more powerful, and among their recommended methods:

The bias-corrected bootstrap, consistently the most powerful test they examined, needs 462 for the small-small case and 148 for medium-medium.

You may have seen the number 20,886 quoted in discussions of mediation power, including in an earlier draft of my own thinking on this. It is real — it is Fritz and MacKinnon's headline figure — but it deserves care. It belongs specifically to Baron and Kenny's causal-steps test in the small-small-zero condition, which is to say: the least efficient common method, under complete mediation, with two small paths. It is a demonstration of how catastrophically bad the old approach can be in the worst case, not a general benchmark for what testing mediation costs. Quoting it as though it were the price of admission is rhetorical inflation, and it invites the obvious rebuttal. The useful numbers are the ones above: dozens to several hundred, depending on path strengths and method.

Even so, the gap is the point. A two-arm trial detecting a large drug-versus-placebo difference needs roughly 26 per arm. Establishing what mediates that difference needs, at plausible path strengths, somewhere between 74 and 530. Every psychedelic trial in this literature sits in the gap between those two numbers.

Fritz and MacKinnon's own literature survey found the median mediation study used 187 participants, with an upper quartile of 352 — and concluded that 75% of published mediation studies had less than 80% power to find a mediated effect involving a small path. Psychedelic trials are not at 187. Roseman's landmark analysis had 20. Griffiths' cancer trial had around 50. Falchi-Carvalho's DMT phase IIa had 14.

I want to state the scope of this claim carefully, because the absolute version is not defensible. I cannot prove that no psychedelic trial has ever been powered for mediation; proving a universal negative requires a comprehensive search and trial-by-trial power calculations, and pooled or industry datasets might complicate it. What I can say is this: I could not identify a single individual psychedelic treatment trial that was prospectively powered to test the mediation pathway it went on to report. The trials commonly cited on both sides of this debate — the ones that constitute the evidence base for the field's central mechanistic claim — are, without exception I could find, far too small for the analysis they perform.

That applies symmetrically. Roseman's n=20 finding that OBN predicts outcome is subject to the same constraint as Bolcont's n=14 finding that it doesn't. A significant result from an underpowered design is not reassuring; it is, if anything, a warning, because the only effects such a design can detect are implausibly large ones, and the published estimate is therefore almost certainly inflated. The positive literature and the negative literature are made of the same unreliable material. This is not a case where one side has the data.

IV. The fork: dose is upstream of everything

Suppose you solved the money problem. Suppose someone funds a 600-person psilocybin trial with a pre-registered mediation model. Would that settle it?

No. And this is where the argument stops being about resources.

The problem is that dose causes the mystical experience and dose causes the outcome. Higher doses produce higher MEQ scores — this is well established, and confirmed in post-hoc analyses across the literature. Higher doses produce better clinical outcomes. So a raw correlation between MEQ and outcome is exactly what you would observe in a world where the MEQ→outcome path is precisely zero and dose is doing all the work through some entirely non-experiential route. The correlation is a fork, not a chain.

The field knows this. Yaden and Griffiths' claim rests explicitly on the studies where "the participant-rated intensity of the overall drug effects are statistically controlled for" — Griffiths' 2016 cancer trial used partial correlation controlling for intensity, and reported that 18 of 20 self-rated outcomes still correlated with MEQ30. That is a serious response and it should be credited.

But it is not sufficient, for a reason worth being precise about. Controlling for a single self-rated "intensity" scalar does not deconfound dose. Dose has many downstream consequences — pharmacological, physiological, contextual, and the sheer fact of a longer and more eventful day — and "how intense was it, 0 to 10" captures one thin projection of them. Adjusting for that projection leaves the rest of the fork intact.

The more careful framing: randomising dose does not randomise the experience. Randomisation buys you an unconfounded estimate of the treatment effect. It buys you nothing for the mediator, because participants are not randomly assigned to their mystical experiences — they arrive at them through a process shaped by dose, expectancy, trait absorption, prior experience, and the room. Causal mediation analysis can proceed under explicit assumptions about mediator–outcome confounding, with sensitivity analysis to probe how badly violations would hurt. That is legitimate methodology and I do not want to overstate this: mediation is not unidentifiable in principle. But the required assumptions are strong, largely untestable in this setting, and — crucially — larger samples do not repair them. You can buy your way out of the power problem. You cannot buy your way out of the identification problem.

This is why the experimental dissociation attempts matter so much more than another correlational analysis, however large.

The most direct is Lii and colleagues' 2023 trial at Stanford, published in Nature Mental Health: 40 adults with depression received intravenous ketamine or saline while under general anaesthesia for unrelated surgery, removing the conscious experience entirely. Ketamine did not beat placebo (MADRS difference −5.82, 95% CI −13.3 to 1.64, p = 0.13), and the masking held — post-hoc guessing was at chance.

It is the most informative experiment in this area and it should be read with restraint. It is a dissociation attempt, not a clean subtraction of experience. General anaesthesia changes physiology, inflammation, concomitant medication, perioperative context, and the patient's entire frame around the event. You cannot cleanly read it as "experience removed, drug stopped working." It is also ketamine, not a classic psychedelic, and the design does not transfer easily — the surgeries averaged over four hours, which accommodates ketamine and not psilocybin.

The psychoplastogen programme approaches from the other side: tabernanthalog, Cameron and Olson's non-hallucinogenic ibogaine analogue, produces antidepressant-like effects in rodents without the head-twitch response. Aarrestad et al. confirmed in 2025 that it works through 5-HT2A and that its spinogenesis is required for the sustained effect. It is real science and it is preclinical. As of mid-2026 the human efficacy data remain thin. The dissociation argument rests, for now, on animals.

Both programmes are trying to do the same thing: break the fork experimentally, because it cannot be broken statistically. That is the correct instinct, and it is where the field's methodological energy should be going.

V. The threshold: what no sample size can fix

Now the part that I think is genuinely underappreciated, and which makes the whole correlational enterprise look shakier than either camp admits.

Even a perfectly estimated correlation of exactly zero, from a sample of ten thousand, would not show that the experience is unnecessary.

Consider a mechanism with a threshold. Suppose what matters therapeutically is having a sufficiently profound experience — crossing some line — and that once you are over the line, further intensity adds nothing. A step function, not a slope.

Now run a trial at a therapeutic dose. Nearly everyone crosses the line. Your MEQ scores cluster in the upper range, and the variance you are correlating against outcome is variance among people who all had the experience. In that world, the correlation between MEQ score and outcome is approximately zero — and the experience is causally necessary for every single person's improvement.

This is not a hypothetical contrivance. The field already behaves as though it believes in thresholds. Roseman's analysis defines "complete" oceanic boundlessness by a cutoff of OBN > 0.6 and analyses above and below it. The MEQ literature has, since Griffiths' earliest work, used the notion of a "complete mystical experience" — a categorical designation requiring 60% of the maximum on each of four dimensions. The field's own constructs are thresholded. Its statistics are linear. Nobody seems to find this odd.

Restriction of range compounds it, and can be quantified. Under standard range-restriction correction, if the true correlation across the full possible range of experience is 0.5, but your trial only samples the upper portion — say your observed standard deviation is 60% of what it would be across the full range — the correlation you observe drops to 0.33. At 40% of the full SD, it drops to 0.23. At 30%, 0.17. A real, substantial relationship shrinks towards invisibility purely because you sampled the wrong part of the curve. And this happens before the power problem gets to it. In a sample of 14, an attenuated correlation of 0.17 is not merely non-significant; it is unmeasurable.

Then add measurement. The MEQ-30 is a retrospective self-report, administered after the session, asking people to rate ineffability on a Likert scale. If clinical improvement colours how meaningful the experience seems in recall — and it would be strange if it didn't — then part of the correlation runs backwards, outcome to experience. More sample does not fix reverse causation. And if the therapeutic ingredient is something the MEQ doesn't index — emotional breakthrough, psychological flexibility, a specific autobiographical insight, the quality of the relationship in the room — then you are correlating the wrong variable, precisely measured, with great statistical rigour, forever.

Put these together and the shape of the problem changes. The field has standardised on an instrument (retrospective mystical-experience self-report), a functional form (linear correlation), and a sampling regime (everyone at a therapeutic dose, in the upper range of the instrument) that between them may be incapable of detecting the mechanism they are meant to test — in either direction. A positive result is confounded by dose. A null result is consistent with a threshold mechanism working perfectly. And both are usually computed on samples too small to distinguish 0.0 from 0.4.

That is not a gap in the evidence. That is a research programme measuring the wrong quantity with the wrong model at the wrong sample size, and then arguing about the results.

VI. What the regulator noticed

It is worth saying that this is not a fringe complaint, and the pressure is now coming from outside the field as well as inside it.

When the FDA's advisory committee met on Lykos' MDMA-assisted therapy in June 2024, it voted 9–2 that the data did not establish efficacy and 10–1 that benefits did not outweigh risks. Among the central concerns: functional unblinding. Roughly 90% of participants in the MDMA arm correctly guessed their assignment. A Complete Response Letter followed.

The final FDA guidance, Psychedelic Drugs: Considerations for Clinical Investigations, was published in July 2026 and speaks directly to the identification problem. It notes that functional unblinding can produce expectation bias in participants who experience perceptual disturbances and in those who observe them, and it recommends blinding questionnaires for subjects and raters alike, plus expectancy evaluation both pre-randomisation and at end of treatment.

The relevance here is specific: expectancy inflates the mystical-experience rating and the self-reported outcome. Shared method variance can manufacture the correlation from nothing. Muthukumaraswamy, Forsyth and Lumley made this argument in 2021 and noted that many trials never measured or reported expectancy at all. Szigeti's self-blinding microdose study — 191 participants — showed how completely a self-reported wellbeing effect can evaporate once expectancy is controlled.

An ACTTION systematic review of 86 psychedelic studies found that 94% were nominally blinded, but only 17% included blind assessment, and of those, only eight checked whether participants' blinding had held. When a regulator and a systematic review independently arrive at the same diagnosis as the statistics, the diagnosis is probably right.

VII. What would actually settle it

I have been negative for six sections. Here is the constructive version, which is short because the remedies are not mysterious.

For readers, including readers of this publication. Treat any single-trial experience–outcome result — positive or null — as uninformative unless it comes with a minimum detectable effect. Not a power percentage against an assumed effect size; the MDC, which is a property of the design and requires no assumptions. If a paper reports a null and cannot tell you what it ruled out, it has told you nothing. If it reports a significant correlation from n=20, ask what the smallest detectable effect was, and note that the published estimate is necessarily near or above it.

For trialists. Mediation belongs at the consortium level, in the hundreds, with pre-registered paths, Monte Carlo power planning of the kind Schoemann and colleagues made freely available in 2017, and bias-corrected bootstrap or PRODCLIN indirect-effect tests. Not as a twelfth exploratory sub-analysis of a fourteen-person efficacy trial. Pre-register one primary experience→outcome path rather than running forty pairs and Bonferroni-correcting into guaranteed silence. Measure and report blinding integrity and expectancy, which the FDA now recommends anyway. And report nulls with equivalence bounds or Bayes factors, so that "we found nothing" carries information.

For the mechanistic question specifically. Test the functional form. If the field believes in thresholds enough to define "complete mystical experience" categorically, it should test threshold models against linear ones rather than assuming linearity and reporting the residue. Sample the full range of the mediator, which means dose arms low enough that some participants genuinely do not cross the line — currently avoided, because subtherapeutic arms feel like a waste of a participant. Prioritise designs that break the fork: dose-varying arms with real within-dose experience variance, anaesthesia dissociation where ethically and practically feasible, non-hallucinogenic comparators as they reach humans.

What would change my mind, in either direction. A pooled mediation analysis at n > 400, pre-registered, surviving adjustment for dose and expectancy, would be the first mediation-adequate evidence this field has produced, and a significant indirect effect there should move the prior towards "the experience matters." A replicated human trial showing full therapeutic effect with the acute experience genuinely absent — not one small ketamine study — would move it the other way. Until one of those exists, both positions are under-identified, and confident assertions in either direction are running ahead of the instruments.

VIII.

The Bolcont paper did not show that the trip is irrelevant. It also did not show that a real relationship was present and missed. Its samples could not adjudicate the question, and the paper should have said so with an equivalence bound rather than a shrug.

But Bolcont is not the problem. It is a small, honest, unremarkable instance of something structural. The field can tell you, with reasonable confidence, that outcomes improve. It cannot yet tell you why. And the gap between those two facts is not going to be closed by another correlation, however large the sample — because the sample size is only the first of the two failures, and the second one, the one about what we are measuring and what shape we expect the relationship to take, does not respond to money.

The most consequential sentence in psychedelic science right now may be one that nobody has quite written: we have standardised on an instrument that cannot detect the thing we built it to find.

That is worth more attention than another paper reporting that improvements were observed.

Sources: Bolcont et al., J Psychopharmacol 2026, DOI 10.1177/02698811261465005. Fritz & MacKinnon, Psychol Sci 2007;18(3):233–239. Yaden & Griffiths, ACS Pharmacol Transl Sci 2021;4(2):568–572. Olson, ACS Pharmacol Transl Sci 2021;4(2):563–567. Roseman, Nutt & Carhart-Harris, Front Pharmacol 2017;8:974. Griffiths et al., J Psychopharmacol 2016;30(12):1181–1197. Ko et al., Front Psychiatry 2022;13:917199. Lii et al., Nat Ment Health 2023;1(11):876–886. Cameron et al., Nature 2021;589:474–479. Muthukumaraswamy, Forsyth & Lumley, Expert Rev Clin Pharmacol 2021;14(9):1133–1152. Szigeti et al., eLife 2021;10:e62878. Strain et al., J Clin Psychiatry 2023;84(3):22r14518. Schoemann, Boulton & Short, Soc Psychol Personal Sci 2017;8(4):379–386. Lakens, Scheel & Isager, Adv Methods Pract Psychol Sci 2018;1(2):259–269. FDA, Psychedelic Drugs: Considerations for Clinical Investigations, July 2026 (Docket FDA-2023-D-1987).

Power and minimum-detectable-correlation figures computed by the author via Fisher z-transformation, two-sided, 80% power. Range-restriction attenuation via Thorndike Case II. Calculations available on request.