The difference between ‘placebo group’ and ‘placebo control’: a case study in psychedelic microdosing

The study re-analyses data from a previously conducted "self-blinding" citizen science microdose trial using simulation and statistical methods designed to assess the impact of imperfect blinding. In the self-blinding trial participants packaged their own microdoses and placebo capsules (non-transparent gel capsules and empty capsules, respectively), labelled them with QR codes so investigators could log ingestion without informing participants, and followed a 4-week schedule taking two microdoses per week in the active condition. For the present analysis the investigators used only data from the first week to make datapoints independent; this yielded n = 233 datapoints. The trial enrolled people who planned to microdose of their own accord; no clinical supervision or financial compensation was provided. Ethical approval and informed consent were obtained as reported. Outcome measures were split into acute and post-acute assessments. Acute outcomes (assessed 2–6 hours after ingestion) included the Positive and Negative Affect Schedule (PANAS), a cognitive performance score (CPS) aggregated from six computerized tasks, and visual analogue scales (VAS) for mood, energy, creativity, focus and temper. Post-acute outcomes (assessed the day after ingestion) comprised the Warwick–Edinburgh Mental Wellbeing Scale (WEMWBS), the Quick Inventory of Depressive Symptomatology (QIDS), the State–Trait Anxiety Inventory (STAI‑T) and the Social Connectedness Scale (SCS). For each capsule taken participants also made a binary guess whether it was placebo or microdose; this correct-guess data underpins later analyses. Methodologically the paper used two complementary approaches. First, a computational "activated expectancy bias" (AEB) model was simulated; this model has three binary nodes representing treatment (TRT), perceived treatment (PT) and treatment expectancy (TE), plus a continuous outcome node. The simulations explored four configurations in which the direct treatment effect (DTE) and AEB pathways were present or absent. Treatment effects in both simulated and empirical data were estimated with an outcome ~ treatment linear model implemented via the lme package in R. Second, the authors developed the Correct Guess Rate Curve (CGRC) adjustment, a novel resampling technique intended to estimate what trial results would look like under perfect blinding, using data from an imperfectly blinded trial. Empirical scores were stratified into the four treatment/guess combinations (PL/PL, AC/PL, PL/AC, AC/AC); kernel density estimation (KDE, implemented with scikit‑learn in Python) modelled each stratum and random samples were drawn to construct pseudo-datasets with a target correct-guess rate (for example CGR = 0.5 to mimic perfect blinding). The resampling was repeated 100 times and the mean treatment estimate and p-value across resamples reported as the CGR-adjusted result. The authors note that their CGR method produces pseudo-experimental, not truly randomised, data and discuss potential dependence and duplication issues arising from resampling.

Simulation results from the AEB model showed that CGR adjustment markedly reduces false positive findings when activated expectancy bias is present. When neither direct treatment effect nor AEB was active, both traditional (non‑CGR adjusted) and CGR‑adjusted analyses produced significant treatment p-values at approximately the nominal 0.05 rate (5%/6%). When only a direct treatment effect was present, traditional and CGR‑adjusted analyses identified a significant effect in 86% and 84% of simulations respectively (average p ≈ 0.032/0.036). When only AEB was active (no true treatment effect), the traditional analysis produced false positive treatment effects in 78% of simulations, whereas CGR adjustment produced false positives in only 3% of simulations. When both DTE and AEB were active, traditional analysis found a significant effect in 99% of trials versus 82% for CGR adjustment; moreover, traditional analysis overestimated the true effect (estimated 5.69 points vs true 3), while the CGR‑adjusted estimate was 3.04 points. Overall, CGR adjustment increased the false negative rate by ~2–4% relative to traditional analysis in scenarios with a true effect, but reduced the false positive rate by roughly 75% when AEB was present and yielded more accurate effect‑size estimates. Applying the CGR method to the empirical self‑blinding microdose data produced materially different conclusions from traditional analyses. Using standard (non‑CGR adjusted) models, statistically significant placebo–microdose differences favoured microdosing on several measures: acute PANAS (mean difference 3.2 ± 1.3; p = 0.01), energy VAS (11.5 ± 2.7; p < 0.001), mood VAS (6.4 ± 2.7; p = 0.02), creativity VAS (6.4 ± 2.5; p = 0.01), and post‑acute QIDS (−1.2 ± 0.06; p = 0.04). After CGR adjustment, none of these outcomes remained significant except the energy VAS, which retained significance at approximately p = 0.04 but with an effect size reduced by about 40% (reported Hedges' g = 0.34). Equivalence testing reported by the authors for the outcomes that lost significance (PANAS, QIDS, mood and creativity VASs), with equivalence bounds set to average within‑subject variability, indicated statistical equivalence between placebo and microdose after CGR adjustment (details and numeric thresholds provided in supplementary materials). The cognitive performance score (CPS) was largely unaffected by CGR adjustment: both p-value and effect estimate remained approximately constant, consistent with the measure being objectively assessed rather than self‑rated. Additional empirical observations relevant to blinding were reported. A brief five‑item treatment‑guess questionnaire (included in the supplement) showed that 55% of participants cited body or perceptual sensations (for example muscle tension, stomach discomfort) as the main cue for their treatment guess, whereas only 23% cited mental or psychological benefits. The authors compared the mean placebo–microdose differences on PANAS subdomains to reported day‑to‑day within‑subject variability from a no‑intervention study, and concluded that the observed mean differences were several times smaller than natural variability, arguing they would be difficult to notice and therefore suggesting perceptual side‑effects rather than perceived efficacy were the dominant source of unblinding.

The authors frame their central contribution as highlighting how imperfect blinding, coupled with a positive expectancy for the active condition, can create an "activated expectancy bias" (AEB) that inflates treatment estimates and generates false positive findings. They emphasise that a formal placebo group is not equivalent to an effectively placebo‑controlled trial: a trial may include a placebo arm but still fail to control expectancy if blinding integrity is poor. Consequently, the paper argues that claims of "placebo‑controlled" efficacy should be contingent on demonstrated empirical blinding integrity. Applied to psychedelic microdosing, the re‑analysis suggests that many small positive findings observed with traditional methods are susceptible to AEB. In the self‑blinding microdose data, the majority of prior significant outcomes lost significance after CGR adjustment, except for a small residual effect on self‑reported energy. The authors propose that microdosing behaves as an "active placebo" — it produces perceivable psychopharmacological effects that can unblind participants, but the available evidence does not yet demonstrate clear clinical benefit for mental health measures once AEB is accounted for. They acknowledge an alternative possibility: microdosing might only show efficacy at doses that necessarily produce conspicuous subjective effects, in which case placebo control may not be feasible and alternative trial designs or mechanistic evidence would be required to establish efficacy. The discussion addresses key caveats and limitations noted by the authors. CGR adjustment depends on binary treatment‑guess data, which is a crude representation of treatment belief; inclusion of guess confidence would be preferable. The method assumes that unblinding arises from perceptual cues that drive expectancy ("malicious" unblinding) rather than from genuine symptomatic improvement yielding correct guesses ("benign" unblinding). If benign unblinding predominates, CGR adjustment could introduce collider bias and produce false negatives; the authors therefore stress the need to assess the source of unblinding before applying the method. Methodological limitations of the CGR approach include resampling dependence (points may be duplicated), potential imbalance of confounders in pseudo‑datasets, and increased error rates in small samples or extreme CGRs. The authors recommend that researchers simulate performance under their own data parameters before applying CGR adjustment. Finally, the authors recommend routine assessment and reporting of blinding integrity, propose a brief five‑item treatment‑guess questionnaire (in the supplement) compatible with CGR analysis, and argue that the scientific community should treat blinding integrity as a prerequisite for judging trials as truly placebo‑controlled. They position CGR adjustment as an approximate analytical tool that can improve inference where ideal blinding is difficult to achieve, but they underscore that it does not substitute for results from genuinely blinded randomized controlled trials.