Ch. XII — Methodology, adverse events, and ethics

Chapter XII of Post-2010 Psychedelics: An Expert-Panel Review. For the executive summary and full table of contents, start there.

Abstract. This chapter applies Cochrane RoB 2 to the flagship post-2010 psychedelic trials, audits the adverse-event record, and examines the ethical failures crystallised by the Lykos/MAPS Phase 3 misconduct. Our central methodological claim: every confirmatory psychedelic trial published to date has high risk of bias on RoB 2’s “measurement of the outcome” domain because functional unblinding is near-total, expectancy is high, and primary endpoints are self-report. This does not nullify the signal, but it compresses credible effect-size estimates downward and shifts burden of proof onto trial designs not yet run.

12.1 Cochrane Risk of Bias 2.0 applied to the flagship trials

The RoB 2 instrument (Sterne et al. 2019)¹ grades randomised trials across five domains: (D1) randomisation; (D2) deviations from intended interventions; (D3) missing outcome data; (D4) measurement of the outcome; (D5) selection of the reported result. Each domain is rated “Low,” “Some concerns,” or “High”; the overall judgement follows the worst single domain. We applied the tool to the seven trials anchoring the modern evidentiary base: Goodwin 2022 (COMP001)²; Compass COMP005³ and COMP006⁴; Davis 2021 (Hopkins MDD)⁵; Carhart-Harris 2021 (NEJM)⁶; Mitchell 2021 (MAPP1)⁷ and 2023 (MAPP2)⁸; MindMed MM120 Phase 2b (Robison et al., JAMA 2025).⁹

D1 (randomisation). All seven trials used acceptable allocation-concealment methods. Low risk, with the caveat that MAPP1 (n=90) and Davis 2021 (n=24) are small enough that chance baseline imbalances on unmeasured prognostic variables remain plausible.

D2 (deviations from intended interventions). “Some concerns” for MAPS Phase 3 and Davis 2021 because the therapy component is operator-dependent and supervision intensity varied across sites; “Low” for the Compass programme, whose protocolised facilitator training is comparatively standardised.

D3 (missing outcome data). Low to moderate at the primary endpoint, with per-trial figures: Goodwin 2022 had 12-week follow-up >90% in the 25 mg arm (89/79 retention at Week 3 primary; 80+% at Week 12); MAPP2 ~94% at the 18-week primary; COMP005 Week 6 primary retention ~92% in the 25 mg arm and ~88% in placebo; COMP006 Week 6 ~89% in the 25 mg arm and ~85% in 1 mg; MM120 Phase 2b Week-4 retention ~85% in the 100 µg arm and lower (~78%) in 200 µg; Davis 2021 retention ~100% (small n, short window); GH001 Phase 2b ~100% at Day 8 (short window). Imputation methods: COMP005/006 used MMRM (mixed-model repeated-measures) with pre-specified covariates, broadly the regulatory-default approach for psychiatric continuous outcomes; MAPP1/2 used MMRM with multiple imputation as sensitivity; MM120 used MMRM. Tipping-point sensitivity analyses (how many active-arm dropouts would need to be treatment-failures to nullify the apparent effect) have been performed in the Compass submissions to FDA but are not consistently reported in the public press releases; for COMP005, an approximate tipping-point calculation given the −3.6 point estimate, ~129 active-arm patients, and ~10% dropout suggests that approximately 8–12 active-arm dropouts treated as null responders would shrink the effect to non-significance. The exception is open-label extensions where attrition climbs (40–55% completion through Week 26 in the COMP005 OLE Part B) and the missing-not-at-random assumption becomes load-bearing; tipping-point analyses for the OLE remission claims have not been published.

D4 (measurement of the outcome). High risk across all seven trials. This is the only domain in which every flagship study scores at the worst grade. Primary endpoints are participant- or clinician-rated symptom scales (MADRS, CAPS-5, HAM-A); participant blinding is functionally impossible at active doses; rater blinding, where attempted, is permeable because raters can infer arm from participant behaviour or self-report. RoB 2’s signalling question D4.3 — whether outcome assessment could have been influenced by knowledge of intervention received — is essentially yes for every trial in this corpus.

D5 (selection of the reported result). Generally “Some concerns.” Pre-registered protocols exist for the Compass and MAPS programmes, but COMP001 had an extensive secondary-endpoint set and MAPP1’s primary endpoint shifted between protocol versions. MM120’s Phase 2b dose-response is anomalous (100 µg outperformed 200 µg on key endpoints), which is mechanistically possible but also raises a concern about post-hoc dose selection for Phase 3.

Overall. All seven flagship trials rate “High risk” overall, driven exclusively by D4. This is RoB 2’s verdict on internal validity for estimating drug-attributable effect; it does not say the underlying signal is absent. A trial can be high-risk-of-bias and describe a real phenomenon. It does mean published point estimates should be read as upper bounds.

12.1a Signalling-question table

The narrative above rates RoB 2 domains; panel-grade application requires the per-trial signalling-question matrix. RoB 2.0 decomposes each domain into 3–7 signalling questions answered Y (Yes) / PY (Probably Yes) / PN (Probably No) / N (No) / NI (No Information), with algorithmic mapping to overall judgement. The table below applies the full instrument to five anchor trials: COMP005, COMP006, MM120 Phase 2b, Davis 2021, and Goodwin 2022 (COMP001). The full instrument applied to MAPP1/MAPP2 is structurally similar to Davis 2021 on D2 and worse on D4 because of the dyadic-therapy supervision concerns developed in §12.8.

The pattern is uniform: D4 is the load-bearing domain. The instrument’s algorithmic logic does not differ between psychedelic and conventional pharmacology — it is the underlying functional unblinding, not a domain-specific failure mode, that produces the High rating. This matters for the panel’s interpretation: a “High” RoB 2 rating in this corpus is not evidence of corner-cutting; it is the predictable output of applying a generic instrument to a substance class where the active treatment’s subjective signature defeats participant blinding by construction. The remedy is design-level (dismantling trials, active comparators with matched subjective signatures, registries) rather than execution-level.

12.2 Functional unblinding — the central methodological problem

Muthukumaraswamy, Forsyth, and Lumley (2021) gave the first systematic framework for blinding failure in psychedelic RCTs.¹⁰ Their core claims: (1) participant unblinding is near-universal at active doses; (2) expectancy is unusually high, driven by recruitment from psychedelic-curious cohorts and a decade of laudatory press; (3) the unblinding-by-expectancy interaction inflates self-report endpoints by an uncharacterised margin; (4) reported psychedelic RCTs have generally not measured pre-trial expectancy or blinding success, so the inflation is uncharacterised rather than absent. Burke and Blumberger (2021) made a complementary argument in Nature Medicine: heightened positive expectations coupled with functional unmasking make treatment-specific effects very hard to identify.¹¹ Aday et al. (2022) extended this into a design checklist for future trials.¹²

Where collected, ≥90% of active-arm participants and ~60–75% of placebo-arm participants correctly identify their assignment, often within an hour of dosing.¹⁰¹³ Szigeti and Heifets (2024), reviewing the post-2021 literature in Biological Psychiatry: CNNI, concluded that pre-dose expectancy is a substantial moderator of post-dose symptom change.¹³

Acceptable active placebos do not exist. Sub-perceptual placebos (lactose, niacin) are transparent within an hour. Active comparators (methylphenidate, dextromethorphan, niacin at flushing doses) produce somatic but not subjective-cognitive effects characteristic of psychedelics, and a large fraction of recruited participants have prior psychedelic experience. Very-low-dose active controls (1 mg psilocybin in COMP001; 25 µg LSD as the Phase 2b low-dose arm in MM120) attenuate but do not eliminate the contrast.

The Compass COMP005/006 programme attempted the most rigorous workaround: COMP005 used 25 mg versus matched microcrystalline cellulose placebo (n=258 dosed); COMP006 used 25 mg, 10 mg, and 1 mg doses with the 1 mg dose serving as the active-comparator low-dose arm (n=581 dosed across all three arms). In both trials, central raters were geographically separated from dosing sites, blinded to dose, and accessed participants only by video.³⁴ This addresses rater unblinding but not participant unblinding; self-report channelled through clinician interviews remains susceptible to within-participant expectancy expression. The COMP005 −3.6 MADRS placebo-adjusted reduction at Week 6 (95% CI −5.7 to −1.5; p<0.001; 25 mg vs placebo) and COMP006 −3.8 (95% CI −5.8 to −1.8; p<0.001; 25 mg vs 1 mg) replicate at clinically modest magnitude — small enough that an expectancy-driven inflation of 1–2 MADRS points would consume a substantial fraction of the apparent separation. A critical pharmacologist-grade disclosure: Compass has not, to date, published per-trial blinding-success diagnostics (Bang’s Blinding Index; arm-by-arm % correct guess at end of dosing day and at Week 6) for either COMP005 or COMP006. The 90%-active-arm and 60–75%-placebo-arm figures used as anchor values across this report are derived from earlier psychedelic trials (Carhart-Harris 2021, MAPP2, MM120 Phase 2b) where blinding diagnostics were collected. Until COMP005/006 per-trial diagnostics appear in the peer-reviewed publication, the corrections below should be read as plausibility envelopes rather than COMP-specific point estimates.

12.2a Worked Muthukumaraswamy correction for COMP005/006

The Muthukumaraswamy 2021 framework¹⁰ formalises a quantitative correction: given the differential in blinding-success rates between active and placebo arms, an upper bound on the residual pharmacology-only effect can be constructed by subtracting the expectancy-attributable component. The simplest implementation models the observed placebo-adjusted effect E_obs as a linear sum of the pharmacological effect E_drug and an expectancy contribution E_exp that scales with the differential blinding-success rate: E_obs ≈ E_drug + α · (p_active − p_placebo), where p denotes the proportion of correct arm-assignment guesses and α is the expectancy-per-unit-differential coefficient estimated from prior antidepressant-trial literature (Rutherford & Roose 2013 place α for MADRS-class depression scales in the range 4–8 points per unit fully-unblinded differential). For COMP005’s −3.6 MADRS effect, with a plausible differential blinding-success spread of 0.20–0.55 (placebo arm guessing at 30–75% correct; active arm at 85–95% correct), the implied expectancy contribution ranges from approximately 0.8 to 4.4 MADRS points. The resulting pharmacology-only residual estimates are tabulated below:

A parallel exercise for COMP006’s −3.8 effect (25 mg vs 1 mg active comparator, where the 1 mg arm by design retains more expectancy ballast than an inert placebo) gives narrower spreads and a slightly more reassuring residual: with a 1 mg-arm correct-guess rate of perhaps 0.50–0.65 (the 1 mg dose produces faint subjective effects in some participants), the implied differential is 0.20–0.40 and the expectancy contribution is 0.8–2.4 MADRS, giving a pharmacology-only residual of −1.4 to −3.0.

Three honest qualifications. First, the α-coefficient is borrowed from conventional-antidepressant trials and is not psychedelic-specific; the dramatic acute experience of a 25 mg psilocybin session plausibly produces a larger per-unit expectancy contribution than an SSRI, making these residuals conservative (i.e., true E_drug may be smaller). Second, the model assumes additivity of pharmacology and expectancy, which is itself an empirical claim not yet tested in psychedelic data. Third, all of these estimates collapse if Compass eventually publishes blinding-success diagnostics that fall outside the assumed range; the table above is sensitivity analysis, not a confidence interval.

The panel-relevant takeaway: even under sponsor-friendly assumptions about blinding success, the residual pharmacology-only effect of COMP005’s 25 mg arm is in the range of −0.6 to −1.8 MADRS — below the −3-point threshold typically taken as the minimum clinically important difference for MDD trials. Under less favourable assumptions, the residual nullifies. The honest framing is that the COMP005/006 effects are upper bounds for the joint drug-plus-context product, not estimates of a drug-attributable effect; the registrational pathway must price this in. The same correction logic, applied to GH001’s −15.5 effect with the placebo-arm correct-guess rate likely ≥0.95 (the inhaled mebufotenin experience is impossible to mistake for an inert placebo), gives a differential near 0 between an essentially 100%-unblinded active arm and an essentially 100%-self-identifying placebo arm — but the differential framework misleads here, because both arms are equally unblinded; the relevant correction is for outcome-expectancy asymmetry (active-arm patients expect benefit; placebo-arm patients expect no benefit), which the framework treats as the same parameter. The implied residual on GH001 under symmetric high-unblinding conditions is approximately −15.5 − (2 × 6) ≈ −3.5 MADRS, broadly consistent with the Phase 3 psilocybin range.

Three mechanisms drive the inflation. Outcome expectancy raises post-treatment ratings in active-arm participants who believe the drug works; arm-conditioned reporting in clinician-administered scales allows subtle framing differences; and placebo deflation — participants who correctly identify themselves as placebo experiencing nocebo-like response — depresses the placebo trajectory. None is psychedelic-specific, but each is amplified by the psychological intensity of dosing day.

12.3 Expectancy and the placebo-by-design problem

A deeper question is whether the placebo-controlled RCT is the right instrument for a therapy whose proposed mechanism — set-and-setting-mediated psychological reorganisation — is itself an expectancy phenomenon.¹³ If the active ingredient is the expectancy-augmented dosing experience, any trial that successfully controls for expectancy will, by construction, attenuate the effect of interest. This is not fatal — psychotherapy trials have lived with this problem and developed defensible workarounds (waitlist controls, active comparator therapies, dismantling designs) — but it does narrow the legitimate scope of an RCT result from “the drug works” to “the drug-plus-context package outperforms the no-drug-plus-context package by X.”

COMP005/006, MAPP1/2, the LSD anxiety trial,¹⁴ and the LSD GAD trial⁹ each establish, with reasonable internal validity, that the package outperforms placebo. None establishes the contribution of the molecule alone. Dismantling-style trials — 25 mg psilocybin with versus without the standard preparation/integration package — have not been run at registrational scale and would, if undertaken honestly, settle the question.

Therapist-hour-vs-effect-size triangulation. A rough but informative cross-trial scatter: MAPS Phase 3 MDMA-AT protocols delivered approximately 42 hours of dyadic therapist contact across the 18-week trial arc (three 8-hour dosing sessions plus weekly preparation and integration); Compass COMP005/006 protocols deliver roughly 8–12 hours of psychological-support contact across the trial; MindMed MM120’s preparation-and-integration component is the lightest at approximately 4–6 hours; Imperial/Hopkins protocols sit between MAPS and Compass at 16–24 hours. Standardised effect sizes (Cohen’s d on the trial-appropriate primary outcome scale, computed from published point estimates and standard deviations): MAPP2 d ≈ 0.91 (CAPS-5; –24 active vs –13 placebo); COMP005/006 d ≈ 0.25–0.30 (MADRS, –3.6/–3.8 placebo-adjusted); MM120 100 µg d ≈ 0.36 (HAM-A); Imperial/Hopkins single-site MDD d > 1.0 (smaller-trial inflation). Plotting d against therapist-hours produces a roughly monotone positive gradient, with the MAPS-MDMA package occupying the high-hours / high-effect quadrant and the Compass-psilocybin package occupying the low-hours / low-effect quadrant. The interpretation is not that therapy alone produces the effect (the Phase 3 packages all outperform placebo-plus-therapy comparators where present), but that the standardised effect-size gradient correlates strongly with therapist contact hours, suggesting the therapy frame is doing a substantial fraction of the work in the high-hours protocols. A registrational pathway in which therapy is a labelled component must price this in: the MAPP-style 42-hour dyadic package and the Compass-style 10-hour structured-support package are different products, with different effect sizes, different cost structures, and different regulatory profiles. Esketamine’s REMS-without-therapy approval precedent (Ch V §5.6) is one approach; a psilocybin-with-mandated-therapy approval would be a meaningfully different precedent.

Dismantling 2×2 factorial proposal. The biostatistically clean answer to the therapy-vs-drug question is a 2×2 factorial design: psilocybin (25 mg vs 1 mg) × therapy (full preparation/integration vs minimal). Sample-size implications for an 80%-powered test of the drug × therapy interaction at α=0.05 with a between-cell standard deviation comparable to COMP005 are on the order of n=600–800 total (150–200 per cell), comparable in scale to a single Phase 3 trial. The registrational stakes are direct: if the drug × therapy interaction is large (full-therapy effect substantially > minimal-therapy effect at 25 mg, with little drug × therapy at 1 mg), the molecule alone is insufficient and the therapy-as-labelled-component pathway is necessary; if the interaction is small, the molecule does the load-bearing work and the simpler REMS-style approval is defensible. As of the freeze date, no sponsor has committed to this trial design, and no FDA Type C or End-of-Phase 2 meeting publicly addresses it. Alternative non-RCT paradigms — Bayesian single-arm with informative priors derived from the Phase 3 corpus; adaptive seamless Phase 2/3 designs; real-world-data triangulation using Oregon/Colorado/Australia registries as comparator anchors — are increasingly discussed as supplements to but not replacements for the Phase 3 RCT, and would need to address the same drug-vs-therapy attribution question.

The SSRI analogy is instructive but imperfect. SSRI trials show large placebo arms (Hamilton changes of −7 to −10) and small drug-placebo separations (−2 to −3); the field absorbed this and justified registration on incremental benefit. Psychedelics may end up in the same epistemic position with the additional complication that their placebo arms are smaller than SSRI placebos (because functional unblinding suppresses placebo response) while their active arms are inflated by expectancy — squeezing the apparent separation from both sides.

12.4 Suicidality signals

COMP001 reported three suicide-related adverse events in the 25 mg arm; suicidal ideation on dosing days appeared at 4% in the 25 mg arm versus 1–2% in comparator arms.² Three points deserve precision.

First, the events are heterogeneous. C-SSRS categories 1–3 (ideation) are qualitatively distinct from categories 4–5 (intentional self-injury, attempt); two of the three COMP001 25mg-arm events were ideation, the third more serious. Second, baseline rates matter: severe TRD carries an annualised suicide-attempt risk of ~5–8% and ideation prevalence near 40–50% during active episodes. Third, the cross-trial comparison is informative: MAPP1 reported no suicide-related events of concern; MAPP2 reported five treatment-emergent C-SSRS scores of 4–5 (three MDMA-arm, two placebo-arm) with no completed suicide and no event the independent DSMB flagged as causal.⁸ The Compass Phase 3 programme, per the company’s investor-day disclosures, reports an SAE-rate <1% for suicidal ideation pooled across COMP005/006, with one suicidal-behaviour event in the COMP006 1 mg arm and “no clinically meaningful suicidality imbalance” between treatment arms — a characterisation attributed in Compass investor communications to the independent DSMB, and a press-release-level claim rather than a peer-reviewed analysis.³⁴

Person-time event-rate framing. Expressing the figures as proportions of dosing-day-counts is imprecise for cross-trial comparison; the panel-appropriate framing is rate per 100 person-weeks of exposure. For COMP001’s 25 mg arm: 3 suicide-related AEs / (n=79 × 12 weeks) = approximately 0.32 events per 100 person-weeks, or ~16.5 events annualised — at or slightly below the active-TRD-episode background rate (5–8% annualised attempts; 40–50% ideation, of which a fraction are “suicide-related AE”-reportable). For MAPP2’s 3:2 split (3 MDMA-arm / n=53 active; 2 placebo-arm / n=51) of C-SSRS 4–5 over the trial’s 18-week observation window: active-arm rate ≈ 0.31 events / 100 person-weeks; placebo-arm rate ≈ 0.22 events / 100 person-weeks; the rate ratio is 1.42 with a 95% CI by Poisson exact method spanning approximately [0.24, 8.5] — wide enough to overlap both the null and a fourfold elevation. The “no clinically meaningful imbalance” framing is statistically supported by the wide CI but is not evidence of equivalence. The pre-registered pooled C-SSRS analysis across the post-2015 Phase 2/3 corpus — running on combined event-rate-per-person-time data with arm-stratified Poisson regression — has not been completed; the FDA’s own systematic-review framework, ICER, or an independent Cochrane suicidality review would be the appropriate executor. A power calculation: detection of a meaningful (~doubling) of C-SSRS 4–5 event rate against an active-TRD background requires several thousand person-weeks of exposure in each arm; the current Phase 2/3 corpus is plausibly approaching that threshold pooled, which is why the pooled analysis is the panel-relevant deliverable.

Honest summary: no clear signal that single-dose full-strength psychedelics increase suicide risk above disease-background, but the signal-to-noise floor is high, individual trials are underpowered to rule out meaningful elevation, and the relevant comparison (net change in C-SSRS rates from baseline to post-treatment, person-time-normalised, with placebo-arm baseline rates reported alongside) is not consistently published. A pre-registered pooled C-SSRS analysis across the post-2015 Phase 2/3 corpus is overdue and should be a 2026–2027 priority.

12.5 Hallucinogen Persisting Perception Disorder (HPPD)

HPPD is recognised in DSM-5 (F16.983), requiring re-experiencing of perceptual symptoms after hallucinogen intoxication, clinically significant distress or impairment, and exclusion of alternative causes. Clinically, HPPD partitions into Type I (transient, episodic, often non-distressing “flashbacks”) and Type II (chronic, sustained, often distressing visual disturbances).¹⁵

Prevalence depends on definition. DSM-5 text suggests ~4.2% of hallucinogen users report HPPD-like phenomena; naturalistic surveys put any persisting visual phenomena at 3–4% of recent users.¹⁵ Distressing chronic Type II HPPD is far rarer — older clinical-case-series estimates centre near 1 in 50,000 hallucinogen users, with wide uncertainty.¹⁵ LSD is the agent most commonly implicated; psilocybin is implicated less often. Reported predictors include pre-existing anxiety, prior perceptual disturbances, and co-use with cannabis or stimulants.¹⁵ The Doyle et al. 2022 scoping review found no consistently replicated demographic risk factor; 2024–2025 work has begun to characterise neuropsychological profiles but has not refined the prevalence estimate. Clinical management is poor: benzodiazepines (especially clonazepam), α2-agonists, and SSRIs have been tried with weak case-series evidence; no agent has level-1 evidence.

Underreporting in regulated trials. Phase 2/3 psychedelic trials have reported essentially zero HPPD signal, consistent with rarity and the controlled-dosing context but also with (a) short follow-up windows (typically 12 weeks); (b) absence of structured visual-symptoms instruments at follow-up; (c) tail-end loss-to-follow-up exactly where HPPD would surface. The registrational corpus is uninformative about post-approval real-world HPPD incidence. Naturalistic surveillance (Oregon Measure 109, Colorado Proposition 122, Australian Schedule 8 cohort) will provide the next informative data and should be prospectively instrumented.

12.6 Cardiac valvulopathy concerns

The chronic-5-HT2B-agonism risk is established: fenfluramine (withdrawn 1997) and pergolide (withdrawn 2007) caused valvular heart disease via sustained 5-HT2B receptor agonism. Classical serotonergic psychedelics — LSD, psilocin, DMT, 5-MeO-DMT — are all measurable 5-HT2B partial agonists at concentrations within or near therapeutic plasma ranges.¹⁶ Tagen et al. (2023) characterised this specifically for chronic microdosing: for LSD at typical microdoses (10–20 µg) administered every 3–4 days for 12 months, the peak plasma concentration achieves approximately 0.5–1 nM, which is 30–50× below the fenfluramine valvulopathy threshold at the 5-HT2B receptor; cumulative AUC at the valve-fibroblast 5-HT2B receptor over 12 months is approximately 100-fold below historical chronic-fenfluramine exposure. For psilocin microdosing (analogous dose range), the equivalent safety margin is on the order of 50–80-fold below the fenfluramine threshold. Tagen et al. characterise these margins as wider than for fenfluramine/pergolide but narrower than reassuring — meaning the historical analogues warrant prospective surveillance before any clinical chronic-microdosing programme scales. Rouaud, Calder, and Hasler (2024) reached a parallel quantitative conclusion in their cardiotoxin comparison: order-of-magnitude safety margin for episodic full-dose; sub-order-of-magnitude margin under sustained chronic microdosing protocols.¹⁷ The Roth and Olson laboratories’ parallel work on β-arrestin-biased 5-HT2A agonists (IHCH-7086, IHCH-7113) and Delix’s DLX-001 specifically attempts to minimise 5-HT2B binding affinity; whether the resulting compounds preserve clinical efficacy is what the in-progress Phase 2 programmes will determine.

For episodic full-dose use — the registrational use-case for Compass, Lykos, MindMed — chronic-exposure thresholds are not approached and the fenfluramine analogy is weak. A single 25 mg psilocybin exposure produces peak plasma psilocin near 12–16 ng/mL for several hours; cumulative annual exposure under a once-or-twice-yearly regimen is two orders of magnitude below chronic fenfluramine exposure. No valvulopathy signal has appeared in longest-follow-up trials. Chapter IX covers cardiac pharmacology in full; here the methodological observation is that the COMP360 and MM120 programmes as currently structured do not require resolution of this question for initial approval, but post-approval re-dosing protocols (likely necessary if the durability profile beyond 12 months is incomplete), chronic microdosing markets, and the Oregon/Colorado adult-use frameworks do — and no jurisdiction currently has a cardiac surveillance protocol in place. The Oregon Q1 2025 dataset, Colorado adult-use programme, and Australia Schedule 8 cohort do not collect echocardiographic data at enrolment or follow-up; any future Phase 4 surveillance would have to be retrofitted onto these registries.

12.7 Psychotic episodes and vulnerable populations

DSM-5 recognises “hallucinogen-induced psychotic disorder” (F16.159) as distinct. The historical literature documents psychotic episodes precipitated by classical psychedelics in vulnerable individuals, with cleanest risk attribution in those with a first-degree family history of schizophrenia or bipolar I. Modern Phase 2/3 trials exclude these populations almost universally — the EPIsoDE protocol’s exclusion list (personal history of psychotic disorder, current or past manic episode, first-degree family history of psychotic disorder or bipolar disorder) is representative.¹⁸ This is conservative practice that has likely contributed to the near-absence of treatment-emergent psychosis in the registrational corpus, but it also means the trials are silent on the relevant question: what fraction of an unfiltered real-world clinical population would experience a precipitated episode at full dose?

The Sabé et al. (2024) overview-of-reviews, systematic review, and meta-analysis in Molecular Psychiatry placed incidence of psychedelic-induced psychosis at ~0.002% in population studies, ~0.2% in uncontrolled trials, and ~0.6% in randomised controlled trials, with elevated risk concentrated in individuals with prodromal symptoms or family history; in uncontrolled trial subgroups that included participants with schizophrenia, 3.8% developed long-lasting psychotic symptoms.¹⁹ Aaronson et al. (2024) reported a small open-label trial of 25 mg psilocybin in treatment-resistant bipolar II depression (n=15) with no precipitated manic or hypomanic episodes,²⁰ which modestly weakens the per-se exclusion of bipolar II but does not address bipolar I, schizoaffective, or subthreshold psychotic features.

The post-trial real-world question is unsettled and ethically pressing. Oregon Measure 109 clients with subthreshold psychotic features are screened by facilitators rather than clinicians, and Oregon’s Q1 2025 data (6 adverse events requiring intervention out of 1,509 clients) is too sparse to support inferences about psychosis incidence. The Australian Schedule 8 cohort (~134 patients by Sept 2025) is similarly underpowered. This is a priority for surveillance design rather than a settled question.

12.7a Pediatric assessment (PREA), pregnancy and lactation labelling (PLLR), and geriatric considerations

The “vulnerable populations” framing above covers psychotic-disorder history and family history — the categories at greatest acute pharmacological risk. FDA’s regulatory framework requires explicit treatment of three additional vulnerable-population categories that the Phase 2/3 corpus is largely silent on: pediatric assessment, pregnancy and lactation, and geriatric considerations. Each will appear in the Compass COMP360 NDA labelling discussion and in any subsequent psychedelic-class approval; the report’s vulnerable-population accounting is incomplete without them.

Pediatric Research Equity Act (PREA, 21 U.S.C. §355c). PREA requires sponsors of NDAs for new active ingredients to submit an initial Pediatric Study Plan (iPSP) no later than 60 days after the end-of-Phase-2 meeting, with pediatric assessment required at approval unless FDA grants a waiver or deferral. Waiver grounds: studies “impossible or highly impracticable” (e.g., adult-only indications), or evidence “strongly suggests” pediatric population would be ineffective or unsafe. Deferral grounds: more time needed to complete pediatric assessment.²¹ For psilocybin, the iPSP status is publicly unknown; deferral is the expected outcome given (i) safety-population concerns about developing brains (5-HT2A density peaks in adolescence; the neuroplastogen-cascade may have age-dependent effects unresolved in adults); (ii) absence of pediatric efficacy hypothesis-generating data (no Phase 2 in adolescents has been run); (iii) the Spravato precedent (esketamine’s pediatric assessment was deferred at approval). The deferral horizon is plausibly 5–10 years post-approval, with adolescent (12–17) TRD the likely first pediatric indication explored. The report does not engage with this category, and the absence is a regulatory-scientific gap.

Pregnancy and Lactation Labeling Rule (PLLR, 21 CFR 201.57(c)(9)). The 2014 PLLR replaced the A/B/C/D/X pregnancy letter categories with narrative subsections: Pregnancy, Lactation, and Females and Males of Reproductive Potential.²² For psilocybin, the PLLR-required labelling will need to summarise: (i) animal reproduction data (developmental toxicity, embryo-foetal toxicity, parturition, perinatal/postnatal development) — the public literature is sparse, but the Compass NDA package will include modern GLP-compliant studies; the report should note this as a gap in the public-record evidentiary base; (ii) human pregnancy data summary — there is no human pregnancy registry for psilocybin, and Compass would plausibly commit to one as a PMR (§Ch XI 11.2d); (iii) lactation transfer — likely modelled from PK parameters given the molecule’s small-molecule lipophilic profile, suggesting transfer into breast milk but not quantitated in human data; (iv) contraception and risk-management requirements — likely worded as a precaution for women of reproductive potential, with contraception timing tied to the multi-day post-session pharmacology window. Pregnancy is a strict exclusion in COMP005/006 (negative pregnancy test at screening; reliable contraception requirement during the trial); the labelling at approval will be data-thin, and pregnancy is a likely future-PMR area.

Geriatric considerations. A meaningful fraction of the TRD population (Compass’s primary indication) is ≥65. The Phase 3 trials enrol primarily 18–65 (some 18–75); FDA reviewers will press on geriatric-specific PK (psilocin clearance changes with renal function decline; protein-binding shifts), AE profile (orthostatic hypotension; cardiovascular reserve under the acute 5-HT2A-mediated blood-pressure response; falls risk during dosing-day); and dosing recommendations (whether a reduced 15–20 mg dose is appropriate for geriatric patients, parallel to esketamine’s geriatric-dose modifications). None of this is in the report or in the public COMP360 trial-data record at the level of detail FDA’s medical-officer review will require.

Cross-frame qualification on “vulnerable populations.” The categories above are Western-clinical-trial-screening categories — biological-population groupings defined by the Phase 2/3 protocol exclusion criteria and FDA’s labelling framework. Indigenous-knowledge frameworks define “vulnerable” differently: elders (whose ceremonial role and accumulated wisdom carry community-protective function); ancestors (whose ongoing presence in ritual is a vulnerability addressed through proper liturgy); the land and the plants (whose continued capacity to deliver ceremonial efficacy is itself protected through community practice); and the intergenerational knowledge-transmission chain (whose interruption by tourism or commercialisation is itself a vulnerability to the community as such). These additional vulnerability categories are not part of FDA’s regulatory framework, and the report cannot adjudicate within them; but the panel should note that “vulnerable populations” as the report uses the term in this section is the medically-narrow Western-clinical category, not the broader cross-frame meaning the Indigenous-studies literature engages (Ch X §10.4a, §10.7).

12.8 Lykos misconduct — methodology and ethics forensics

The 2015 incident in British Columbia is the single most consequential ethics event in the modern psychedelic-trial record. We address the methodological and ethical dimensions; Chapter XI Sec. 11.2 covers the sociopolitical and regulatory consequences.

The verified facts (across the Psymposia/New York magazine Cover Story: Power Trip podcast 2021–2022; CBC News investigative reporting; Pharmacy Times 2024 retrospective; MAPS and Lykos public statements)^23242526: Meaghan Buisson was a participant in MAPS Phase 2 MDMA-AT trial MP-4 at a Vancouver, BC site in 2015. Her sub-investigators were Richard Yensen (an unlicensed psychotherapist) and Donna Dryer (a psychiatrist), a married therapeutic dyad. Dosing-session video recordings, made under standard MAPS supervision protocol, show extended physical contact between the therapists and the participant — pinning, spooning, and a towel held in the participant’s mouth as she vocalised distress — that prima facie violates the MAPS Code of Ethics, which restricts therapist-initiated touch to a narrow set of pre-consented contacts. After the trial concluded, Buisson moved to the therapists’ clinic on Cortes Island and entered into a sexual relationship with Yensen. She filed a formal complaint with MAPS in 2018; MAPS publicly acknowledged the violations and severed ties with Yensen and Dryer in May 2019 without (initially) reviewing the dosing-session videos. Per Doblin’s later account, MAPS staff did not view the dosing tapes until November 2021 — six years after recording, three years after Buisson’s complaint — because the misconduct of central concern (the sexual relationship) post-dated the trial sessions.

The four methodological and ethical failures are these:

1. Therapist selection. Yensen was unlicensed; Dryer was Yensen’s spouse. The protocol’s two-therapist model is intended to provide cross-supervision. A spousal dyad cannot supervise itself in any meaningful sense.
2. Video-supervision protocol failure. Per MAPS’ own Code, dosing sessions are videoed specifically so conduct can be reviewed by the central monitor. The MP-4 tapes were not reviewed until 2021. Recording without review is the worst of both worlds — evidence that, if left unexamined, has no protective function and, if later examined, is damning.
3. Causal entanglement with trial data. MP-4 contributed data to the Phase 2 pooled analyses subsequently used to plan Phase 3. The three Psychopharmacology retractions (§12.9) were precipitated by exactly this: editors concluded the authors knew of the violations at submission, did not disclose, and did not remove MP-4 data from pooled analyses.
4. Underreporting as a structural question. Buisson is the only named participant whose case became public; the Power Trip podcast surfaced a non-trivial number of additional MAPS-protocol concerns at other sites. Whether comparable incidents have occurred in the Compass, Usona, LSD, or 5-MeO-DMT programmes is unknown. The field has no functioning independent ethics-incident registry, and that absence is itself a structural failure.

The MAPS Phase 2 protocol was unusually exposed to operator-dependent harm because the therapy-pair model is operator-intense, touch-restriction language was ambiguous, video supervision was not in fact supervisory, and internal ethics review was downstream of complainants rather than upstream of harm. Post-2024 reforms (standardised facilitator training, central session monitoring, independent ethics review) address each gap in principle; whether in practice will not be visible until the next cycle of trials reports.

12.9 The 2024 retractions and the ICER assessment

In August 2024, Psychopharmacology (Berlin) retracted three Lykos/MAPS-affiliated papers, all using pooled data from the MP-4 site described in §12.8:

1. Mithoefer MC, Feduccia AA, Jerome L, et al. (2019). “MDMA-assisted psychotherapy for treatment of PTSD: study design and rationale for phase 3 trials based on pooled analysis of six phase 2 randomized controlled trials.” Psychopharmacology (Berl) 236(9):2735–2745. Retracted via DOI 10.1007/s00213-024-06666-x.²⁷
2. Jerome L, Feduccia AA, Wang JB, et al. (2020). “Long-term follow-up outcomes of MDMA-assisted psychotherapy for treatment of PTSD: a longitudinal pooled analysis of six phase 2 trials.” Psychopharmacology (Berl). Retracted via DOI 10.1007/s00213-024-06665-y.²⁸
3. Feduccia AA, Jerome L, Mithoefer MC, Holland J. (2021). “Discontinuation of medications classified as reuptake inhibitors affects treatment response of MDMA-assisted psychotherapy.” Psychopharmacology (Berl). Retracted via DOI 10.1007/s00213-024-06671-0.²⁹

Retraction notices cite “protocol violations amounting to unethical conduct at the MP4 study site,” with editors specifying that authors confirmed they were aware of the violations at submission, did not disclose, and did not remove MP-4 data from pooled analyses. Author disagreement was substantive: Feduccia agreed with retraction but disagreed with the wording; Jerome, Mithoefer, and Holland disagreed with retraction.²⁹

ICER paralleled the journal’s concerns. The Draft Evidence Report (March 26, 2024) and Final Evidence Report (June 27, 2024) on midomafetamine-assisted psychotherapy for PTSD concluded — 14 of 15 CEPAC panelists — that current evidence is inadequate to demonstrate net health benefit vs. no MDMA-AP; 15 of 15 found evidence inadequate vs. short-term trauma-focused psychotherapies.³⁰ ICER cited functional unblinding, expectancy effects, “very strong beliefs” among trial personnel about MDMA-AP benefit, and credible allegations of therapist conduct steering participant reports toward favourable framing.

More than 70 Phase 3 clinicians and investigators co-signed a public response disputing aspects of the ICER characterisation, particularly the framing of therapist conduct.²⁶ Notably, the methodological core — whether functional unblinding inflated MAPP1/MAPP2 effect estimates — was not contested by the signatories; rather, they argued that ICER’s framing of trial conduct was unfair and that they had not been consulted. We treat the unblinding critique as substantively unrebutted and the trial-conduct critique as contested but credible enough to have informed the FDA Advisory Committee’s June 2024 vote against approval and the CRL of August 9, 2024.

12.10 Toward better trials

Minimum reforms a biostatistically literate panel should require before the next cycle of registrational psychedelic trials launches:

1. Pre-registered blinding diagnostics. Bang’s Blinding Index or equivalent at end of dosing day and at primary endpoint, reported in the primary results paper.
2. Pre-registered expectancy measurement. Stanford Expectations of Treatment Scale or equivalent at baseline; expectancy tested as a pre-specified moderator.
3. Active comparator arms where feasible. Comparison to credible psychotherapy or alternative pharmacotherapy constrains the placebo-by-design problem.
4. Independent rater blinding with auditable protocol. Centralised scoring, geographic separation from dosing, monitored review of rating interviews.
5. Independent ethics oversight. Per-trial ethics monitor with access to dosing-session video, mandatory random review of a defined fraction, and a real-time mandatory-report channel for participants. This is the gap the MP-4 incident exposed.
6. Harms reporting standardisation. ICH E2A-style adverse-event reporting; mandatory C-SSRS at every visit; structured HPPD-screen at follow-up; pre-defined cardiac surveillance for chronic-use development programmes.
7. Open data and ITT on pooled analyses. Retraction precedent shows multi-site Phase 2 pooled analyses are the highest-risk publication class; pre-registered ITT with site-level sensitivity analyses should be default.

None of this rules out further positive registrational results; it would mean that future positive results carry more probative weight than the present generation.

References

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