Every psychedelic Phase 3 readout arrives with a topline number and a press release built around it. The number is usually real. Whether it means what the press release implies depends on five things that rarely make the headline: whether the blind held, whether expectancy was controlled by design, whether a dose-response relationship corroborates the effect, how missing data were handled, and whether the durability claim describes the intervention or an ongoing protocol that includes retreatment. This is a working reference for reading past the topline. It will be updated as trial designs evolve.
The blinding question, briefly
Psychedelics produce an unmistakable subjective experience. In a two-arm trial against inert placebo, most participants and many raters can tell within the first hour which arm they are in, and that knowledge can inflate a self-reported outcome on its own, independent of any drug effect. This is functional unblinding, and this desk has covered its mechanics in depth elsewhere. The short version for reading a readout: a failed blind is expected, not disqualifying, and the question is never whether it held. It is what the sponsor’s design did to measure the failure or route around it, an active low-dose comparator, a biomarker that does not depend on self-report, or a formal unblinding assessment reported alongside the primary result. If none of those appear, treat the effect size as an upper bound, not a settled number.
Expectancy, and how serious designs handle it
Expectancy is the broader version of the blinding problem. Enrollment itself selects for people who believe psychedelics will help them, often after reading about the trial specifically because of that belief, and the elaborate preparation sessions that precede dosing in most protocols build expectation further before a single dose is given. A trial that reports a large effect without addressing this is reporting the belief and the drug effect bundled together. The stronger designs use an active comparator dosed high enough to produce its own noticeable effects, so that both arms have something to attribute their expectations to, or they build in a dose-response arm specifically to separate pharmacology from anticipation. The comparator dose matters: a low-dose active comparator strong enough to blur the distinction, without being clinically active itself, is a much harder bar than a comparator so faint every participant can identify it as the low arm.
Dose-response as an unblinding workaround
A well-built dose-response design, comparing a full dose, a partial dose, and sometimes a further reduced dose, does two things at once. It generates a pharmacological signal, since a genuine drug effect should scale with dose in a way pure expectancy generally does not. And it provides a partial blind, since a lower but still-active dose makes it harder for participants to sort themselves cleanly into “got the real thing” and “got nothing.” COMP006, Compass Pathways’ second pivotal trial in treatment-resistant depression, used exactly this structure, 25 mg against 10 mg against a 1 mg control, and its separation between the 25 mg and 1 mg arms held through a blinded period out to 26 weeks, a real methodological point in its favor. Definium’s lysergide program takes the logic further with a 2:1:2 randomization built around a 50-microgram arm specifically intended to sit close enough to the active dose that patients cannot reliably self-sort. Neither design eliminates the blinding problem. Both are direct, serious attempts to manage it rather than ignore it, and that distinction is worth checking for in any new trial.
What an active comparator gives up, and what it preserves
No comparator is free. Niacin, used as a physiologically active but non-psychedelic placebo in some psilocybin trials, produces a noticeable flush that gives participants something to attribute a sensation to, but it does nothing to address the deeper expectancy problem tied to preparation and belief. A low-dose active comparator, by contrast, directly attacks the sorting problem but introduces a new one, since the comparator itself may carry a small effect that narrows the measured difference versus the full dose, understating rather than overstating benefit. Reading a trial well means checking not just whether a comparator was used, but which specific problem it was built to solve, and what it necessarily left unaddressed.
Biomarkers as corroboration, not proof
A subjective self-report scale is easiest to inflate through expectancy. A trial that pairs its primary endpoint with an independent, objective measure, direct receptor-occupancy imaging, a connectivity or neuroplasticity marker, a physiological correlate, gives the reader something expectancy cannot easily move. This desk has covered exactly this kind of work in the Copenhagen program directly measuring LSD’s occupancy of the serotonin 2A receptor at a range of doses, pharmacodynamic ground truth that clinical dosing decisions have mostly had to assume rather than see. A biomarker that moves in the same direction as the subjective result is corroboration. It is worth remembering that corroboration is still not proof the subjective result is unbiased, and the current state of psychedelic biomarker research is early enough that absence of a biomarker should not by itself be read as a red flag; most trials still do not include one.
Attrition and the difference between intention-to-treat and completers
How a trial handles participants who leave before the final assessment can move a reported result substantially, and it is one of the easiest things to miss on a fast read. An intention-to-treat analysis counts every randomized participant, typically treating missing data conservatively, while a completers-only or observed-data analysis reports only on those who stayed, which tends to look better precisely because people who are doing poorly are more likely to drop out. Compass’s COMP006 26-week data is a clean, recent example of why this distinction matters in practice. The company’s own slides label the Week 26 durability analysis as post hoc and explicitly state that results from Week 9 onward are based on observed data only, no imputation for participants who left. Reading the responder math against the trial’s own defined denominators showed the headline 39 percent figure was actually the more conservative of two possible readings, using the full randomized arm rather than only the smaller evaluable-at-Week-6 population as its base. That is the outcome you want to see: a sponsor’s chosen convention turning out to be the stricter one. It is not guaranteed, and checking the denominator is the only way to know which way a given trial cut it.
Retreatment, and what “durable” is actually describing
A related question sits underneath any six-month or twelve-month durability claim: how many participants received an additional intervention along the way. In COMP006, 58 percent of the 25 mg arm received retreatment after Week 9, either another dose or a protocol-permitted antidepressant. That does not invalidate the durability finding. It does mean the population whose response was “maintained” is not, for most participants, a population that received one or two doses and was simply observed. It is a population managed under an ongoing treatment protocol that allowed supplemental dosing. The honest framing distinguishes single-intervention durability from durability-under-an-ongoing-protocol, and sponsor language does not always make the distinction obvious. Checking the retreatment rate, and what retreatment was allowed to consist of, is a five-minute check that changes what a headline durability number can actually support.
Secondary endpoints: statistical versus clinical meaning
A trial can hit its primary endpoint by a statistically significant margin that is clinically underwhelming, or clear a smaller but more clinically meaningful bar on a secondary measure. Remission rates, functional outcome scales, and durability curves are usually secondary endpoints, not statistically powered the way the primary is, which is exactly why post hoc secondary analyses need the same denominator scrutiny described above. A secondary endpoint that moves in the right direction is supportive. It is not, on its own, a second confirmed finding with the same evidentiary weight as the primary result.
The checklist
Before treating a psychedelic trial’s headline as settled, five questions are worth running through. Was unblinding measured or addressed by design, and if so, how. Was expectancy controlled for, through an active comparator, a dose-response arm, or some other structural choice, rather than left unaddressed. Is there a dose-response relationship or a biomarker that corroborates the subjective result. How was attrition handled, intention-to-treat or observed-data-only, and does the denominator in the headline number match the denominator in the fine print. And do the secondary endpoints, durability curves, and retreatment rates support the primary claim once read at the same level of scrutiny as the primary itself.
None of these questions are grounds to dismiss a positive result. Every major psychedelic trial this desk has covered, Compass’s COMP005 and COMP006, Definium’s lysergide program, Cybin’s CYB003, the MDMA-assisted therapy trials that ultimately did not clear the FDA, has real signal in it somewhere. The five questions are the difference between reading that signal accurately and reading the press release. A sponsor who has clearly built their trial to survive this checklist, an active comparator chosen for the right reason, a biomarker included even though it is not required, a durability analysis that discloses its own denominator, deserves more confidence than one who has not. That distinction, more than any single topline number, is what separates a result likely to hold up from one that will look smaller the next time someone checks.