Published on 16 September 2026
Psilocybin trials for depression: control groups improve less. What should we conclude?
In brief
This meta-analysis looks first at what happens to the patients who receive the comparator. Across 17 double-blind randomised trials in adults, improvement in the control arms on the Montgomery-Åsberg Depression Rating Scale is 0.50 as a standardised mean change for psilocybin (4 trials, 373 participants), against 1.00 for selective serotonin reuptake inhibitors (11 trials, 4014 participants) and 1.12 for esketamine (2 trials, 573 participants). The authors report no pairwise comparison between classes. They report an omnibus test of moderation by trial class: significant for the control arms (QM 10.4; 2 degrees of freedom; p = 0.005) and for the between-arm effect sizes (QM 10.7; p = 0.005), not significant for the active arms (QM 1.21; p = 0.55). Yet the effect size of a trial is calculated as a difference from its control arm: if that arm improves half as much, the displayed gap widens without the drug having anything to do with it, and the between-arm gap does indeed reach 0.70 for psilocybin against 0.27 for SSRIs and 0.30 for esketamine. The authors put forward loss of blinding as one possible explanation among others, not as an established one. The limitations lie in the indirect nature of the comparison, the very small number of psilocybin and esketamine trials, and the fact that the three classes were not studied in the same populations.
The context
The question reaches the consulting room through the popular press, rarely through the literature. A patient reads that a substance achieves in one session what their antidepressant has not delivered in six months, and comes to ask why it is not being offered to them. The usual answer is regulatory. In France, for example, it is accurate: psilocybin is not an authorised treatment there. But that answer is insufficient: it leaves intact the idea that the product works better, and that all that is missing is an administrative signature.
The work presented here shifts the question. It does not set out to establish whether psilocybin works, but whether the magnitude attributed to it is measured under the same conditions as that of other treatments. This is a question of method, and it applies to any drug whose subjective effects are marked enough for the patient to guess their group.
The mechanism
Why a control arm that improves less inflates the treatment effect
Blinding is not an administrative ritual, it is what makes the comparator interpretable. In a conventional trial, the patient on placebo believes it possible that they received the treatment, and that belief contributes to their improvement. In a psychedelic trial, the subjective experience can be distinctive enough for that belief not to hold: the patient who perceives no alteration may conclude that they are in the control group, and their expectation collapses. Improvement in the control arm falls, and the difference between the two arms mechanically increases.
What the work measures is the improvement in the control arms, and that measurement is direct. What it does not measure is the mechanism itself. The authors state explicitly that rates of unblinding were not assessed in the included psilocybin and esketamine trials, and probably not in any of the included SSRI trials. They also point out that the comparison is indirect and can therefore offer little guidance on why the three trial populations differ: funding, publication year, number of study sites, inclusion criteria or concomitant treatments are cited as possible systematic differences. Loss of blinding is the most economical explanation for the observed result. It remains a hypothesis, not a demonstration.
The study at a glance
| Question, population, outcome measure | |
|---|---|
| Population | |
| Adults enrolled in double-blind randomised trials for a major depressive episode or treatment-resistant depression. Trials conducted exclusively in people younger than 18 or older than 65 years, crossover designs and trials lasting less than two weeks were excluded. | |
| Focus of the analysis | |
| The control arms first and foremost. The active arms and the between-arm differences were also analysed, which allows the two to be compared. | |
| Comparison | |
| Three classes set side by side: psilocybin (4 trials, 373 participants), SSRIs (11 trials, 4014 participants), esketamine (2 trials, 573 participants). | |
| Outcome | |
| Standardised mean change in MADRS score, from baseline to at most six weeks after randomisation, within each arm. Standardised mean difference for the between-arm gaps. | |
| Comparators | |
| Inert placebo, low-dose psilocybin or niacin. One of the four psilocybin trials used escitalopram combined with 1 mg of psilocybin as its comparator, that is, an active antidepressant. | |
| Design | |
| Meta-analysis of 17 randomised trials, indirect comparison, random-effects models and meta-regression on trial population. The trials were not identified by a database search but taken from three earlier reviews published between March 2019 and December 2024: a meta-analysis for psilocybin, a US Food and Drug Administration review for esketamine, and an individual participant data meta-analysis for SSRIs. |
Quality control
| Item checked | Judgement |
|---|---|
| Protocol registration before analysis | Not found |
| FindingThe version consulted states that the PRISMA reporting guideline was followed, but mentions no protocol registration, on PROSPERO or elsewhere. | |
| Selection of trials | Not original |
| FindingNo literature search of its own. The 17 trials retained come from 26 trials identified in three earlier reviews, 9 having been excluded. The corpus therefore inherits the selection criteria of those three sources. | |
| Independence from the psychedelic field | Could not be checked |
| FindingNeither the funding statement nor the conflict of interest disclosures appear in the version consulted. A correction concerning the conflict of interest disclosures was published by the journal on 11 September 2025. No conclusion about the presence or absence of conflicts can be drawn here. | |
| Homogeneity of the psilocybin trials | Not quantified |
| FindingNo I² or other heterogeneity statistic is reported in the version consulted. The authors themselves describe the available psilocybin literature as “small and heterogenous”, without quantifying it. | |
| Comparability of the three classes | Indirect |
| FindingThe esketamine trials concern treatment-resistant depression, the SSRI trials major depressive episodes, the psilocybin trials both. The comparison between classes is not randomised. The authors stress that most SSRI trials date from the 1980s and 1990s whereas all psilocybin trials were published after 2020, which makes the effect of the era inseparable from that of the class. | |
| Number of trials per class | Two to eleven |
| FindingTwo trials for esketamine, four for psilocybin, eleven for SSRIs. So few trials for two of the three classes limits the precision of each pooled estimate. | |
The findings
| Outcome | Result |
|---|---|
| Control arms, psilocybin | 0.50 (standard error 0.15) |
| ReadingThe lowest value of the three, and also one of the least precise. The authors report no 95% confidence intervals for these pooled estimates, only standard errors. | |
| Control arms, SSRIs | 1.00 (standard error 0.08) |
| ReadingA large and precise improvement on the comparator, in line with what the antidepressant literature has long documented. | |
| Control arms, esketamine | 1.12 (standard error 0.17) |
| ReadingThe highest value of the three, even though these trials recruit treatment-resistant patients, in whom one would expect the opposite. It is also the least precise estimate, resting on only two trials. | |
| Omnibus test of moderators, control arms | QM 10.4; 2 degrees of freedom; p = 0.005 |
| ReadingTrial class significantly moderates improvement on the comparator. This is an omnibus test across the three classes, not a series of pairwise comparisons: the authors report no pairwise p value between classes. | |
| Omnibus test of moderators, active arms | QM 1.21; 2 degrees of freedom; p = 0.55 |
| ReadingThis analysis was indeed carried out, and it detects no difference between classes. Improvement in the active arms is of the same order for all three drugs, 1.21 for psilocybin, 1.28 for SSRIs, 1.43 for esketamine. This is the most instructive result of the work: what sets psilocybin apart plays out on the comparator side, not on the treatment side. | |
| Gap between active and control arms | 0.70 psilocybin; 0.27 SSRIs; 0.30 esketamine |
| ReadingStandardised mean differences, with standard errors of 0.12, 0.05 and 0.12 respectively. The omnibus test of moderators on these gaps is significant (QM 10.7; 2 degrees of freedom; p = 0.005). Trial class explains 40.9% of the variance in comparator outcomes, 34.8% of the variance in between-arm gaps, and 0% of the variance in active arm outcomes. | |
| Response under the control condition | 19% psilocybin; 33% SSRIs; 42% esketamine |
| ReadingResponse defined as a reduction of at least 50% in MADRS score. That is 14 percentage points lower for psilocybin than for SSRIs, and 23 points lower than for esketamine. The authors present these rates descriptively, without a statistical test. | |
Critical appraisal
| Domain | Judgement |
|---|---|
| Relevance of the question | High |
| FindingThe work examines a bias that affects an entire field, not a single drug. The approach can be carried over to any intervention with marked subjective effects. | |
| Internal validity | Moderate |
| FindingThe comparisons between classes rest on unmatched trials, with different populations, eras, durations and comparators. The authors rule out differential dropout specifically as an explanation, but acknowledge that the other confounders cannot be disentangled. | |
| Statistical precision | Uneven |
| FindingThe estimate is narrow for SSRIs, supported by eleven trials and 4014 participants. It is markedly less precise for psilocybin and esketamine, whose standard errors are twice as large. The gap between classes therefore rests on the two least well estimated arms. | |
| Fit between claim and evidence | Sound |
| FindingThe authors conclude, in conditional terms, that this result “might indicate that psilocybin’s antidepressant efficacy is overestimated compared with that of SSRIs and esketamine”, and put forward loss of blinding as one hypothesis among others. That caution must be preserved whenever the result is reported. | |
| What the study does not say | Worth remembering |
| FindingIt does not establish the cause of the observed gap, measures no rate of unblinding, and provides no correction factor applicable to the published effect sizes of psilocybin. | |
Level of evidence
A meta-analysis of randomised trials, but an indirect comparison between three unmatched bodies of trials, which lowers confidence below that of a meta-analysis of direct randomised comparisons. Confidence is high in the observed fact: the control arms of psilocybin trials improve less than those of SSRI and esketamine trials, and trial class significantly moderates this result. It is moderate in the proposed explanation, loss of blinding, which is coherent but not tested here, and which the authors present as one hypothesis among several. It is low for any quantitative extrapolation, of the kind that would claim psilocybin’s effect to be overestimated by a given amount: the work does not allow the correction to be quantified. The distinction runs as follows: the descriptive result is demonstrated, the blinding explanation is suggested, and the size of the correction is, for now, a matter of opinion.
The colleague test
What an experienced colleague would say if you put this study to them in two minutes, between two consultations.
“So we are not saying that psilocybin does not work. We are saying that the way we measure what it does flatters it, because the patient in the control group often guesses they received nothing. Overestimated, not ineffective. That is not the same sentence.”
What this means in practice: faced with a patient who has read that a psychedelic outperforms antidepressants, the answer is not to dispute the result but to explain how it is produced. That explanation is one patients can hear, and it avoids a stance of refusal.
What you can do with this
- Faced with a request for psilocybin, separate three things: whether it can be obtained at all outside research where you practise (in France, for example, it is not available outside a research protocol), the existence of an efficacy signal in the active arms, and the uncertainty about the true size of the gap with the comparator.
- Do not answer that a psychedelic trial is of poor quality. Answer that its comparator is hard to keep blind, which is a constraint of the product and not a failing of the investigators.
- Remember that improvement in the active arms is of the same order for all three classes. It is the comparator that differs, not the treatment, and that is what should temper the reading of published effect sizes.
- Apply the same vigilance to esketamine trials, where blinding is also fragile, and where improvement in the control arm is, in this analysis, the highest of the three.
- In teaching, this work is a ready-made resource for explaining what a comparator is, and why an effect size never exists independently of its control arm.
- The course of action is set out in the NICE decision tree for depression in adults.
Frequently asked questions
Does this meta-analysis show that psilocybin is ineffective for depression?
No. It shows that the gap between active and control arms is larger in psilocybin trials, and that this gap stems from the behaviour of the control arm rather than that of the active arm, since improvement on active treatment is of the same order in all three classes. The authors infer from this, in conditional terms, that its efficacy might be overestimated compared with that of SSRIs and esketamine.
By how much might the effect of psilocybin be overestimated?
The work does not allow this to be quantified. It establishes a gap between outcomes on the comparator, not a correction factor applicable to published effect sizes.
Were the differences between psilocybin, SSRIs and esketamine tested pairwise?
No. The authors report an omnibus test of moderation by trial class, significant for the control arms and for the between-arm gaps, not significant for the active arms. No pairwise p value between two classes is given.
Why do control arms in esketamine trials improve so much when the patients are treatment-resistant?
This is an observation the study reports without settling it. The authors note that esketamine, like psilocybin, is administered on site and in the presence of health care professionals, and that it produces immediate adverse effects liable to break the blind. This hypothesis is not tested.
Can psilocybin be offered to a patient with depression outside a clinical trial?
In France, no: outside a research protocol, it cannot be offered. Elsewhere, the answer depends on the rules in force where you practise, a question this meta-analysis does not address. In every case, the regulatory status should be checked on the date of the consultation.
Is the unblinding problem specific to psychedelics?
Nothing in this work allows that to be claimed, since only three classes were compared. The question arises for any intervention whose felt effects may allow the patient to identify their group, which includes other psychotropic drugs and some stimulation devices. This extension is an inference, not a result.
Annotated bibliography
Source study. Hieronymus F, López E, Werin Sjögren H, Lundberg J. Control Group Outcomes in Trials of Psilocybin, SSRIs, or Esketamine for Depression: A Meta-Analysis. JAMA Network Open, 2025, volume 8, issue 7, article e2524119. DOI 10.1001/jamanetworkopen.2025.24119. PMID 40736734. A correction concerning the conflict of interest disclosures was published by the journal, JAMA Network Open, 2025, volume 8, issue 9, article e2536707, titled “Error in Conflict of Interest Disclosures” (PMID 40932724).
Funding. No funding statement appears in the version consulted. It is therefore not possible to state that this work was funded, or that it was not.
Competing interests. No conflict of interest disclosure appears in the version consulted. The correction published by the journal concerns this point, as its title on the PubMed record shows, but its text was not consulted. No claim that there are no conflicts can therefore be made here.
Protocol registration. The version consulted states that the PRISMA reporting guideline was followed. No protocol registration number, PROSPERO or other, appears in it.
Sources of the included trials. The 17 trials come from three earlier works: Freitas RR et al., Australian and New Zealand Journal of Psychiatry, 2025, volume 59, issue 2, pages 128 to 151, for psilocybin; the US Food and Drug Administration clinical review of esketamine, application number 211243Orig1s000, March 2019; Hieronymus F et al., World Psychiatry, 2022, volume 21, issue 3, pages 472 and 473, for SSRIs.
Benchmarks cited by the authors. Jones BDM et al., JAMA Network Open, 2021, volume 4, issue 9, article e2125531, mean effect size of 1.05 on the comparator in treatment-resistant depression. Cuijpers P et al., Epidemiology and Psychiatric Sciences, 2024, volume 33, article e56, effect sizes of 0.64 for care as usual and 0.37 for waiting list in psychotherapy trials. The value of 0.50 observed here for the control arms of psilocybin trials therefore sits on the side of the least active control conditions.
What was consulted. Verification carried out on the full text of the publication, 30 pages, including the structured abstract, the methods, the results, Table 1 of MADRS scores at baseline and at evaluation, Table 2 of response and study withdrawal rates, Figures 1 and 2, the discussion, the limitations and the 36 references. The supplementary material, announced by the publication in the form of a data sharing statement, was not supplied and was therefore not consulted. The funding and conflict of interest statements do not appear in the version consulted. The correction published by the journal on 11 September 2025 is flagged on the version consulted; its title, “Error in Conflict of Interest Disclosures”, was checked against its PubMed record (PMID 40932724) on 16 September 2026, but its text was not consulted. The DOI and PMID were checked against the bibliographic record. This analysis underwent an independent double reading.