Conceptual analysis of mechanisms and methods in psychedelic clinical trial design: a narrative review

Abstract

Clinical trials with psychedelics face several challenges that are not present to such a degree with other pharmacotherapeutics. Psychedelic therapies often include a significant therapeutic container, including preparatory and integrative psychotherapy, along with supportive intervention during dosing sessions. All these are likely to have an effect on the outcomes. Additionally, the influence of the therapeutic relationship between study subjects and study therapists is often more pronounced and more impactful on the outcomes as it is in pharmacotherapies that do not require psychotherapy. Perhaps the most important challenge with psychedelic-assisted therapy trials is the inability to effectively conceal the assignment in placebo-controlled settings. Many different approaches have been tried, however, all have suffered from a complete or significant functional unblinding making it difficult to discern the true therapeutic effect of the psychedelic in conjunction with the psychotherapeutic modalities which accompany it from a positive expectancy effect (often in the subjects receiving active intervention), which is further compounded by an additional negative expectancy effect (often in the subjects receiving placebo). This can be particularly problematic if functional unblinding is not just a nuisance variable but is deeply connected with the mechanism of therapeutic action itself. In this manuscript, we discuss various advantages and disadvantages of currently available approaches utilized in psychedelic trials and propose conceptual and methodological perspectives on approaching these problems.

Plain language summary

Conceptual analysis of mechanisms and methods in psychedelic clinical trial design

1. Psychedelic clinical trials face challenges with acceptance and interpretability.

2. A complex therapeutic container fragments the attribution of effect.

3. Functional unblinding challenges the standard of double-blinding.

4. Sequential trial designs addressing expectancy are confounded by carryover.

5. Statistical adjustments must deal with a unique overlap between bias and true effect.

Introduction

Functional unblinding and expectancy in psychedelic research

Recent clinical research on psychedelic-assisted therapies has produced a striking and increasingly consistent finding: brief, time-limited interventions involving compounds such as psilocybin, 3,4-methylenedioxymethamphetamine (MDMA), and ketamine can yield therapeutic effects that persist for months following one or a small number of administrations.^1,2 These outcomes challenge core assumptions of modern psychopharmacology, in which durable benefit is typically attributed to sustained receptor-level modulation and ongoing drug exposure. In psychedelic interventions, by contrast, therapeutic change appears to unfold through psychological and meaning-making processes that continue well beyond the acute drug clearance. However, currently accepted methods evaluating efficacy are met with unique challenges, chief among them the systemic difficulty in the maintenance of blinding. ³

This pattern has generated growing methodological unease. Standard double-blind randomized controlled trial (RCT) designs rely on assumptions of stable baselines, effective blinding, and the separability of pharmacologic action from subjective experience. Psychedelic-assisted therapies routinely violate these assumptions: functional unblinding is common; expectancy effects may be positive in active intervention group and negative in the placebo group.^4,5

Importantly, these challenges do not primarily reflect poor trial execution. Rather, they suggest a deeper mismatch between classical trial logic and interventions whose mechanisms appear to be experiential, belief-mediated, and at least partially irreversible. ⁶ RCTs are predicated on the assumptions of separating pharmacologic action from subjective experience, and that neither the participants nor the investigators are aware of the treatment allocation (double-blinding). These assumptions are frequently violated when highly salient psychoactive agents are employed. Even crossover designs, which may provide some balance for the expectancy by the promise that all participants shall receive all interventions, are nonetheless challenged by prolonged or incomplete washout periods that result in carryover.^7,8

Furthermore, if the psychological effect of a psychedelic is partly or entirely responsible for the therapeutic effect (or is just an inseparable correlate of such effect), then recreating the same effect using an active placebo would violate the definition of a placebo and consequently invalidate the comparison. ⁹

In their article, Yaden and Griffiths discuss the evidence for the subjective effects of psychedelics as significantly correlated with therapeutic outcomes. ⁹ In this work, they propose that the only definitive evidence to the contrary would be if the same magnitude and durability of therapeutic effects were observed in a study masking the experience with anesthesia.

While such trial has not been done with classic psychedelics, an RCT reported by Lii et al. showed that another compound, ketamine, shown to produce similar subjective experiences as psychedelics and known to be effective for depression, could not be distinguished from placebo in a trial studying the effects on depression under surgical anesthesia masking. ¹⁰ Currently, only intranasal esketamine is Food and Drug Administration (FDA) approved for this indication (i.e., treatment-resistant depression).^11,12

Both groups in the study by Lii et al. experienced a significant decrease in their respective depression scales, though they did not diverge, and the effect was lower compared to unmasked ketamine trials. The authors present a robust discussion on potential causes of their observations, including interference from anesthetics among other things. They bring up the likelihood of a successfully aborted expectancy effect as the explanation in several spots, though the missing subjective experience with or without an appropriate therapeutic integration may be more likely to account for such difference (the authors briefly consider this possibility in the discussion). ¹⁰

How can we approach this topic?

Methodologically, we chose to follow the scale for the assessment of narrative review articles (SANRA). ¹³

We formulated three basic questions to explore (sections “Is functional unblinding necessarily detrimental?” “What are the barriers in aligning psychedelic research with currently accepted methods?” and What opportunities exist, and what can be modified to align psychedelic research with currently accepted methods?): (1) “Is functional unblinding necessarily detrimental?”—by choosing this as the opening question, we aimed to qualitatively assess the problem of functional unblinding as potentially the biggest methodological problem facing psychedelic research; (2) “What are the barriers in aligning psychedelic research with currently accepted methods?”—in this follow up question, we aimed to explore various methodological aspects contributing to the difficulty of aligning psychedelic research with the rest of the traditional psychopharmacology research; (3) “What opportunities exist, and what can be modified to align psychedelic research with currently accepted methods?”—by posing this question, we aimed to address the issues identified in the previous question. From September 2025 through January 2026, we performed a search using PubMed database without time restrictions and with combinations of terms, including: [psychedelics] AND/OR [ketamine] AND/OR [psychedelic-assisted psychotherapy] AND/OR [psychedelic-assisted therapy] AND/OR [ketamine-assisted psychotherapy] AND/OR ketamine-assisted therapy] AND/OR [randomized controlled trials] AND/OR [RCT] AND/OR [unblinding] AND/OR [functional unblinding] AND/OR [carryover] AND/OR [carryover effect], along with additional methodological search terms related to specific methodologies we deemed more closely aligned with psychedelic research. These additional search terms were derived from the initial search using the terms specified above and served to compare previously tried methodology with other instruments that could lend themselves to psychedelic research.

Is functional unblinding necessarily detrimental?

Szigeti et al. recently suggested a correction for the expectancy bias via Correct Guess Rate Curve, which provides statistical adjustment based on the proportion of correct subject assignment guesses. ¹⁴ In a discussion on unblinding in a different manuscript, Szigeti et al. also introduce an important concept of “malicious” vs “benign” unblinding, with the malicious unblinding representing the recognition of the agent’s non-therapeutic effects while in the latter benign unblinding simply recognizes the positive therapeutic effect itself and thus cannot retroactively affect its development. ¹⁴ This question is mainly reviewed in section “Psychedelic therapy as a new therapeutic paradigm” below.

What are the barriers in aligning psychedelic research with currently accepted methods?

Nayak and Zahid, in their 2025 paper on blinding in psychedelic trials describe the reasons for the 2024 failure to convince the US FDA of MDMA’s efficacy for post-traumatic stress disorder (PTSD). The Psychopharmacologic Drugs Advisory Committee members reportedly cited concerns over functional unblinding as the reason for uncertainty around the study results, which met the pre-defined endpoints. ³ We explore this question in sections “Limitations of conventional and alternative trial designs and controls” and “Implications of reduced psychotherapeutic containers for commercialization and trial design.”

What opportunities exist and what can be modified to align psychedelic research with currently accepted methods?

We review a selection of designs with advantageous characteristics aligned with psychedelic research in section “Limitations of conventional and alternative trial designs and controls.” In section “Implications of reduced psychotherapeutic containers for commercialization and trial design,” we try to balance challenges with opportunities, and we propose methods for statistical handling of carryover and unblinding in sections “Statistical management of the carryover effect in crossover RCTs and SMART designs” and “Where do we go from here? Methodological realignment addressing expectancy.”

Psychedelic therapy as a new therapeutic paradigm

Neurobiological changes observed during the psychedelic state—such as transient increases in neural flexibility—normalize within days or weeks, whereas clinical gains often persist for months. ⁶ This temporal dissociation points toward downstream psychological processes as the primary mediators of durability.

A coherent account of these effects is that psychedelic therapy operates through belief-system and learning reorganization. Beliefs about the self, relationships, threat, and meaning organize perception, emotion, and behavior across psychiatric conditions. Conventional psychotherapies such as cognitive-behavioral therapy, acceptance and commitment therapy, and exposure-based treatments explicitly target these belief structures through experiential learning, with durable change understood as stabilized belief revision rather than transient symptom relief.^{15 –17}

During the acute state, emotionally salient and often autobiographically meaningful experiences can destabilize rigid belief hierarchies, allowing alternative interpretations to be experienced rather than merely evaluated. When these experiences are integrated, revised beliefs may exert persistent causal influence on emotional regulation and behavior. Consistent with this view, qualitative features of the psychedelic experience—such as emotional breakthrough, insight, and connectedness—predict long-term outcomes more strongly than dose or baseline symptom severity.^{18 –20}

This framework reframes expectancy effects. In classical trial logic, expectancy is treated as a short-lived bias to be minimized through blinding or statistical correction. In psychedelic therapy, expectancy-related processes may represent early phases of belief updating rather than extraneous distortion. Anticipatory openness and meaning attribution shape experiential engagement and consolidation, blurring the boundary between expectancy and mechanism. ⁹

In that sense, adjusting for the recognition of the psychedelic effects may incorrectly, yet significantly, adjust away part or all of the therapeutic effect itself. This would be particularly prominent with macrodoses of psychedelics where the recognition is often >94%. ¹⁴

Limitations of conventional and alternative trial designs and controls

In response to the difficulty of blinding high-dose psychedelics with inert placebos, researchers have employed diverse mitigation strategies, notably including the use of active comparators and low doses of psychedelics presumed to be psychologically inert. Active placebos are intended to reduce the risk of unblinding by mimicking the non-therapeutic side effects of the experimental treatment, minimizing the differences between treatment and control conditions.

However, selecting an adequate active placebo is exceptionally challenging. An ideal agent must induce the physical or subtle perceptual changes associated with the onset of the active drug without triggering the full therapeutic psychoactive state. This pursuit introduces a core philosophical paradox: If the drug’s therapeutic effect is primarily mediated by the intense psychological state (altered consciousness, a powerful experience, suggestibility), then a “perfect” active placebo designed to reliably mimic this state without the drug component may itself constitute an equally effective, non-psychedelic therapy, thereby undermining the control condition. In such a scenario, the comparison is not between an active drug and a control, but between two different agents that activate the same therapeutic psychological effect, potentially yielding a non-significant result that obscures the utility of the approach.

This extreme difficulty in validating a truly inert, yet experientially compelling, active placebo argues against the feasibility of relying on traditional placebo-controlled RCTs as the sole gold standard.

There are attempts to create non-psychedelic analogs of various psychedelics, whose stimulating effect on neuroplasticity and some therapeutic effects may be preserved, and for those, the conventional design may be more successful in future clinical trials. Hereafter, we will discuss the limitations of additional trial designs that have been proposed or tested in the field of psychedelic therapy (see summary Table 1).

Table 1.

Comparative analysis of trial designs.

Design	Psychedelic trial applicability	Key methodological constraint	Bias addressed
Conventional placebo-controlled double-blind parallel-group RCT	Limited (with high doses)	Reliance on an effective active placebo blinding	Generalizability (via randomization)
Conventional multi-arm parallel-group RCT	More suitable than simple placebo-controlled double blind RCT	Persistent, though lower, potential for unblinding	Generalizability (via randomization)
Zelen trial	More suitable than simple placebo-controlled double blind RCT	Ethical complexity (partial non-disclosure); increased sample size; randomization failure	Disappointment (via non-disclosure)
Sequential, multiple-assignment, randomized trial	More suitable than multi-arm RCT and Zelen trial	Typically requires complex weighted GEE analysis; higher implementation complexity	Within-subject variability (via adaptive re-randomization); potential to address carryover bias in traditional parallel designs by explicitly estimating carryover effect a
Crossover RCT	Better for temporary effects	Therapeutic carryover effects (addressed via statistical adjustment) a	Within-subject variability (via crossover treatment); potential to address carryover bias; expectancy and disappointment (via assured receipt of all tested treatment modalities)

^aCarryover effect is the net carryover of each active treatment compared with the carryover of the placebo.

GEE, generalized estimating equations; RCT, randomized controlled trial.

Zelen trial designs

In 1979, Marvin Zelen suggested that the randomization takes place before the consent. The aim was to retain the advantage of a single randomization process as applied to the same pool of candidates for enrollment into a conventional double-blind placebo-controlled trial. To offset the expectancy/disappointment as well as other issues, Zelen suggested that the candidates then be consented only to the procedures assigned to their arm, leaving out the procedures not offered to them completely. In essence, subjects treated with psychotherapy alone could not be disappointed for not receiving psychedelics since they do not know about such intervention in another arm of the trial. ²¹

Among the drawbacks of this design falls the preserved expectancy effect on the subjects consented to receive psychedelics, however. Another issue is that individual subjects are effectively consented for different trials despite unified randomization. This is by virtue of having a different study description in their respective consent forms, which may in turn cause non-random attrition of subjects choosing not to consent to the study. In smaller or otherwise tight-knit communities, the existence of a parallel arm receiving a different treatment may become known, which could theoretically contribute to some erosion of trust between the subjects and investigators. For these reasons, investigators may encounter problems receiving approvals from institutional review boards (IRBs) and ethical committees on the grounds of ethical uncertainty regarding partial non-disclosures.

Multi-arm conventional RCT evaluating varying dose–response

Proving a dose-dependent magnitude of response would seem to lend credence to the veracity of psychedelics’ effects in trials using this method to offset the stark difference between the effects of a psychedelic versus placebo. ²⁰ This is especially true when there is a significant overlap in the psychedelic experiences, mitigating the unblinding problem among various doses.

The main weakness of evaluating multiple groups of subjects is the reduced number of subjects per group compared to a two-armed RCT design. This proportional reduction in the number of subjects per group reduces the statistical efficiency, and the preparation of multiple assignments will likely add some logistical complexity as well. Another challenge lies in the correct selection of the doses to study, especially with respect to their overlap in psychedelic effects aiming to lower the rate of complete functional unblinding for the purpose of more reliable between-dose comparisons.

Sequential, multiple-assignment, randomized trial designs

Another design involving multiple parallel groups with differing doses or interventions would be the sequential, multiple-assignment, randomized trial (SMART).^22,23 These designs start with a conventional randomization process into parallel groups (see Figure 1 for an example of the SMART design). Treatment assignments may include a placebo or an alternative active agent. At the end of the first period, effects (+, −) are assessed. For example, if a subject was originally randomized to psychedelic and had a positive effect to that treatment, they would continue with that treatment in the second period. Conversely, if the subject had a negative response to the psychedelic, they could either crossover to ketamine, or they could be assigned in the second period to a different active treatment (e.g., selective srotonin-reuptake inhibitors (SSRI)). A similar approach would be used if the original randomized treatment was either placebo or ketamine. This improves statistical efficiency by adding a within-subject comparison to a between-group comparison.

Figure 1.

Sequential, multiple-assignment, randomized trial.

SMART designs, however, add significant complexity to the trial logistics, and any potential improvements in statistical efficiency will be diminished once the assignment tree branching expands. However, it remains an issue whether we can obtain unbiased estimates of treatment effect and improved statistical efficiency by having lower variance estimates from a SMART design compared with a strictly parallel design, and detailed simulation studies need to be performed in order to quantitatively explore both issues.

Variations on crossover RCT design

A crossover RCT can theoretically address both expectancy and disappointment, by assuring all participants that they will receive the active intervention. ⁷ While this structure does not solve the problem of functional unblinding during the active and control sessions, the effect of unblinding may not be as durable given the sense of fairness in all participants receiving all planned interventions. The methodological suitability of the crossover RCT, and its simple two-arm version in particular, for macrodose psychedelic therapy is unclear.

Specifically, there is hesitation regarding any additional benefits from the increased statistical power of within-subject comparisons over a conventional placebo-controlled double-blind RCT’s parallel-group comparison since the inherent vulnerabilities to expectancy/disappointment bias of the conventional RCT remain to a certain degree, and in addition—the carryover effect from treatment period to placebo/alternative period (or vice versa) can further bias the comparison.

A complete washout may be hard to achieve since many of the effects of a single/short-term therapy have been reported to last up to 6 or even 12 months, and if so—it would significantly prolong the duration (and possibly the logistical complexity) of the trial. ²⁴

Nevertheless, hereafter, we attempt a few compelling arguments why crossover RCTs may still be useful in psychedelic-assisted therapy trials:

Statistical adjustment for the carryover effect

Sparrow et al. outlined a solution for an adjustment of the carryover effect in cases of incomplete washout which, similar to psychedelics, is an issue in Parkinson’s disease trials. ⁸ In short, they described a mixed model regression method equating the expected value of the outcome (dependent) variable with a term composed of four (or more) independent effects that are estimated by a combination of the following regression coefficients β₁ for baseline (pretrial) effect, β₂ for a treatment effect, β₃ for a period effect and β₄ for a carryover effect (additional β _s can be added based on the number of consecutive periods with differing treatment assignments in the trial). Similar statistical modeling can draw data for simulations from suitable prior studies with psychedelics as well (see sections “Statistical management of the carryover effect in crossover RCTs and SMART designs” and “Where do we go from here? Methodological realignment addressing expectancy” on statistical management of carryover and expectancy, respectively, below for more detail on this).^25,26

In comparison to Zelen trial designs

Crossover RCTs mitigate the expectancy/disappointment bias by assuring everyone of receiving all treatment modalities proposed within the trial, though whether the magnitude of disappointment mitigation during the control period would be equivalent to the Zelen-proposed uninformed (control) cohorts is debatable. The expectancy of effect within the Zelen-proposed informed (treatment) cohorts should be the same as in the treatment period of a crossover RCT.

Additionally, all patients in crossover RCTs consent to the same trial description of the trial avoiding some of the ethical and failed randomization risks discussed previously for Zelen trial designs.

In comparison to multi-arm conventional RCTs evaluating dose–response

The multi-arm design can be used in crossover RCTs and can thus increase the expectancy blurring of the level of expectancy between various doses and compound the bias mitigation achieved by the assurance of the same treatment exposure (in a different order) for everyone.

Crossover RCTs would also increase the statistical power stemming from within-subject comparison potentially decreasing the total number of subjects needed. However, it would add complexity by adding one additional treatment period in a two-arm and two more treatment periods in a three-arm study.

In comparison to SMART designs

The SMART designs are in many ways very similar to more complex crossover RCTs with some important differences. Their typical continuation of the positive responders with their first-assignment treatment, which gives them the structure of a parallel-group design, does not allow the inclusion of those subsets of patients in the efficient within-subject comparisons; there is a relatively high logistical complexity of the trial. SMART designs may offer additional flexibility in reassigning the non-responders to a different treatment modality at various times. However, this may complicate statistical comparisons in which the duration of exposure can be reasonably assumed to be associated with the outcome.

Pragmatic, real-world longitudinal trials

Crossover RCTs would also be relatively easy to set up in pragmatic trials following clinical interventions over extended periods of time. Such designs may be less affected by carryover than rapid-sequence trials, while preserving within-subject comparisons for statistical efficiency and matching power.

Additionally, pragmatic longitudinal trials in real-world settings would offer the benefit of separating the long-term treatment effectiveness from efficacy under strict per protocol rules, and even from the effectiveness assessed by intention-to-treat analyses within the constraints of shorter clinical trials. Intensive shorter trial participants are often subject to the influence of being closely monitored (i.e., “Hawthorne effect”) and also vulnerable to a greater influence of the expectancy bias by way of limited follow-up duration, which may miss the distinction between a short-term expectancy-related improvement and a more durable treatment effect (see Figure 2 as an example of crossover RCT proceedings).

Figure 2.

Crossover randomized controlled trial.

Implications of reduced psychotherapeutic containers for commercialization and trial design

Current commercialization efforts in psychedelic-assisted treatment increasingly rely on a deliberately attenuated psychotherapeutic framework, often described as “psychological support” rather than psychotherapy. This model typically emphasizes basic preparation, non-directive presence during dosing, and limited post-session integration, with the stated aim of easing scalability, regulatory acceptance, and workforce implementation. While such simplification may facilitate dissemination, it also materially alters the intervention being studied and delivered. If durable therapeutic effects are mediated primarily by belief-system change and meaning-making, then reduction of the psychotherapeutic container has significant implications for both trial validity and real-world effectiveness. ²⁷

Reduced psychotherapy as an unacknowledged intervention modification

Psychedelic-assisted therapy is increasingly recognized as a complex intervention in which pharmacologic, psychological, relational, and contextual elements are inseparably intertwined. ²⁰ Consistent with the broader psychotherapy literature on common factors, elements such as therapeutic alliance, expectancy, trust, empathy, relational safety, and therapist presence may account for a substantial portion of clinical change, even when they are not described as formal psychotherapy. ²⁸ Trials demonstrating durable benefit have typically employed substantial preparatory work, extended dosing-day therapeutic engagement, and structured integration sessions, even when these elements are intentionally framed as supportive rather than interpretive. ²⁹ This does not necessarily mean that all such interventions are psychotherapy in the conventional sense. Rather, it indicates that nominally supportive elements may still contain clinically meaningful therapeutic processes, including alliance, trust, expectancy, relational safety, emotional attunement, and meaning-making. When commercialization efforts systematically reduce these components, the intervention may shift from one designed to consolidate belief revision into stable meaning frameworks toward one that relies predominantly on the acute drug-induced state and spontaneous post hoc adaptation.

From a trial-design perspective, this creates a potential efficacy–effectiveness gap, although the direction of this gap may vary. Regulatory approval may be based on outcomes observed under conditions of substantial preparation, facilitator engagement, and integration, while some post-approval delivery models may offer a materially thinner intervention that cannot reliably reproduce those outcomes. Conversely, some trials may employ relatively limited psychological support, whereas real-world clinical practice may embed psychedelic administration within ongoing psychotherapy or a more robust therapeutic relationship. In this opposite scenario, clinical effectiveness may differ from trial efficacy because the intervention delivered in practice contains more psychotherapeutic support than the intervention tested in the trial. Thus, the central methodological issue is not whether trials always include more psychotherapy than clinical practice, but whether the therapeutic container is sufficiently specified, measured, and modeled across both research and implementation settings.^{30 –32}

Consequences for mechanism: From belief revision to transient state effects

If belief-system reorganization constitutes one important mechanism of durability, then preparation and post-session support may plausibly function as phases of therapeutic learning. Preparation may establish safety, intention, expectancy, and a frame for approaching challenging or meaningful material. Integration may help translate acute experiential content into changes in self-concept, threat appraisal, relational expectations, and values-based behavior.^29,33 However, this claim should be stated cautiously. Current evidence does not yet establish that integration, considered a discrete intervention, independently enhances therapeutic outcome across psychedelic trials. Indeed, several recent trials using relatively limited integration have reported clinically meaningful outcomes, and available evidence may more strongly implicate preparation than the dose of post-session integration.^2,18,19,34 The absence of definitive evidence for integration as an independent contributor does not mean that integration is irrelevant; rather, it indicates that its role remains empirically under-specified. Future trials should therefore measure preparation, dosing-day support, integration dose, facilitator competence, and fidelity so that their separate and interactive contributions to outcome can be tested directly.

This shift risks transforming psychedelic treatment from a belief-mediated intervention into a transient state intervention characterized by short-term relief, nonspecific optimism, or temporary openness. In such cases, expectancy effects may dominate early outcomes while durability diminishes, reinforcing regulatory concerns that improvements reflect placebo-like processes rather than reproducible therapeutic mechanisms. Importantly, this does not imply that belief change is absent, but rather that it remains unstable, unexamined, or inconsistently integrated across individuals.

What is lost in meaning-making when integration is minimized

Meaning-making is not an epiphenomenon of psychedelic experience but a central process through which belief change stabilizes. When integration is minimized, several clinically relevant functions are compromised. First, narrative consolidation may be incomplete, leaving patients with intense experiential fragments that are insufficiently linked to autobiographical memory, personal history, and future-oriented self-models. Second, values clarification may fail to translate into sustained action, resulting in insight without behavioral embodiment. Third, relational embedding of new beliefs—critical for maintaining change in attachment and trauma-related conditions—may be underdeveloped in the absence of therapeutic dialogue. ¹⁶

Additionally, integration serves an essential corrective function. It is the primary context in which maladaptive interpretations, grandiosity, spiritual bypass, or rigid metaphysical conclusions can be examined and softened. Reduced integration increases the risk that such distortions become incorporated into belief systems rather than revised, potentially undermining long-term outcomes and safety. ³⁵

Implications for trial design under commercial constraints

When reduced psychotherapy is employed to ease commercialization, trial designs must explicitly account for what is being omitted. Failure to do so risks attributing diminished durability to the drug’s limitations rather than to systematic removal of an active ingredient. Several design strategies can address this problem.

Factorial and dismantling designs can directly estimate the marginal contribution of integration by comparing full, minimal, and enhanced integration conditions while holding pharmacologic exposure constant. Adaptive designs such as SMART or longitudinal pragmatic crossover RCTs can further test integration as a targeted consolidator by escalating psychotherapeutic support when belief revision is incomplete, rather than when symptoms alone persist.^7,22 Pragmatic hybrid effectiveness–implementation trials allow evaluation of scalable delivery models while embedding fidelity measures that quantify loss of meaning-making capacity under real-world constraints.

Measuring the error of omission

The consequences of reduced preparation or integration can be operationalized as an error of omission—the absence of sufficient meaning-making inputs necessary for belief consolidation. This error can be measured empirically rather than inferred. At minimum, trials should quantify preparation and integration dose and fidelity, including number and duration of sessions, therapist competence, and adherence to integration frameworks. Process measures should assess whether belief revision occurred, using indices of psychological flexibility, maladaptive belief rigidity, self-schema change, and connectedness.^29,33,36,37

Longitudinal mediation analyses can then test whether reduced integration predicts diminished belief change and whether this, in turn, mediates loss of durability. Mixed-method approaches, incorporating brief qualitative interviews coded for narrative coherence, agency, and existential meaning, are particularly well suited to capturing meaning-making processes that elude symptom scales. By modeling integration fidelity as a mediator rather than a nuisance variable, trials can estimate the true cost of scalability-driven simplification.

Ethical and regulatory considerations

Finally, reducing integration while retaining the acute psychedelic experience raises ethical considerations. Psychedelics reliably increase emotional openness and suggestibility; diminishing post-session support shifts responsibility for meaning-making entirely onto patients during a vulnerable period. The ethical question is therefore not whether belief change occurs—it inevitably does—but whether it occurs with sufficient support to promote autonomy, coherence, and psychological safety. ³⁸ From a regulatory standpoint, transparent acknowledgment of psychotherapy’s role is preferable to implicit reliance on it while minimizing its delivery.

In sum, commercialization-driven reduction of psychotherapeutic support alters both the mechanism and reliability of psychedelic-assisted therapies. If belief-system change and meaning-making underlie durable benefit, then trial designs must either preserve sufficient integration to support this process or explicitly measure and model the consequences of its omission. Failure to do so risks underestimating efficacy, misattributing durability failures, and establishing precedents that undermine both scientific clarity and patient care.

Statistical management of the carryover effect in crossover RCTs and SMART designs

A SMART design is a hybrid design combining features of both parallel designs and crossover designs. This is because some subjects receive the same treatment in both periods while other subjects cross over to different active treatments.

It is important to make a distinction between SMART designs and the traditional crossover designs. With traditional crossover designs, all subjects receive both treatments regardless of their outcomes at the end of the first period. Thus, the treatment group comparisons are inherently all within-subject. With the SMART design, subjects who are responsive to a treatment in the first period are continued with that treatment in the second period. However, subjects who are not responsive are re-randomized to another treatment in the second period. Therefore, between-treatment group comparisons are based on a combination of between-subject comparisons and within-subject comparisons. However, we should note that the switch from a given treatment in the first period to a different treatment in the second period is conditional on the response of the subject to the treatment in the first period. This conditional crossover may bias estimates of treatment effect.

We will discuss the modeling of SMART design data with three active treatments, one of which is only introduced in the second period, one placebo treatment, and two periods (see Figure 1). We would include treatment effect with three indicator variables for treatment, one indicator variable for period, and two indicator variables for carryover of active treatment in the first period into the second period. We will use mixed model methodology with separate observations for each period for each subject. For continuous outcomes, we will use standard mixed model methodology to estimate these effects. For binary outcomes, we will use GEE with a logistic link and binomial distribution to estimate these effects. It would be of interest to perform detailed simulation studies to quantitatively assess the degree of overall bias and efficiency of the SMART design compared with a traditional crossover design.

In the context of a crossover design, we would expect that the carryover effect might be especially large in psychedelic trials due to the expectancy bias that might carry over into a second period if a psychedelic is administered in the first period.

We can model the response of a subject at a specific time (Y) (e.g., a depression scale) as a function of

1. a baseline effect (B), which is the response of the subject before the treatment in the first period is received,

2. a treatment effect (T) based on the treatment received in a specific period,

3. a period effect (P) based on the period when they receive the treatment,

4. possible carryover effect (C) of the treatment received in the previous period on the current period response.

Therefore, the model would look like

$$Y=a+B+T+P+C+e$$ (1)

where a is an intercept and e is the error from the model.

The model in equation (1) is based on a two-period design with three time points measured for each subject, which we will elaborate on below. It will be fit using a mixed effects regression model because the errors of the multiple time points for the same subject are not independent. To accommodate this lack of independence, we assume unstructured covariance structure, which means that the variances at each time are not the same, and the correlations between the repeated measures are also not the same.

Therefore, symbolically equation (1) can be written more formally as:

$$y_{ij}=\alpha +{\displaystyle \sum }_{k=1}^4{\beta }_k{x}_{ijk}+e_{ij},i=1,\dots ,N;j=0,1,2$$ (2)

where

$$e_i=\left(e_{i_0},e_{i_1},e_{i_2}\right)$$

$$e_i\sim N\left(0,{\Sigma }_i\right),\mathrm{where}{\Sigma }_i={\sigma }_{j_1}{\sigma }_{j_2}{\rho }_{j_1{j}_2};j_1,j_2=0,1,2$$

β₁ = BASELINE effect, β₂ = TREATMENT effect, β₃ = PERIOD2 effect, and β₄ = CARRYOVER effect, all mutually adjusted for each other.

In the above design, we note that there are three assessments, which are baseline, end of the first treatment period, and end of the second treatment period.

Also, we will use an unstructured covariance matrix. This means that the standard deviations for these three assessments are allowed to be different, and the correlation between the outcome for any two assessments is allowed to be different. It follows from the equation that we can separately estimate the effect at baseline, the effect of active treatment, the effect of period, and the effect of carryover.

This design can also be expanded to a three-period crossover design, possibly with three different treatments. In this expanded setting, instead of a single treatment effect β₂, we would have two indicators for two active treatments, for example, psychedelic or ketamine, with placebo as the reference, two indicators for period effect at the end of period 2 and period 3, respectively, and possibly two carryover effects, which would involve one-period and two-period carryover effects.

Limitations of SMART designs

One issue with the SMART design is that introducing new treatments in the second period that were not used in the first period will make it impossible to estimate the carryover effect of these new treatments because they were never introduced in the first period.

A second issue is that the switch from a given treatment in the first period to a different treatment in the second period is conditional on the response of the subject to the treatment in the first period. Therefore, this conditional crossover might bias estimates of treatment effect, period effect, or carryover effect. This would require detailed simulation studies to estimate these possible biases.

Where do we go from here? Methodological realignment addressing expectancy

Similar to the statistical management of carryover, expectancy would benefit from modeling methods that would preserve the true effect of the complete intervention (medication and psychotherapy together), while recognizing pure expectancy bias. To accomplish this, we start by considering the definition of expectancy bias-driven results and how they differ from durable treatment results.

Durability

Evaluating the decay of treatment effect over time may help distinguish study participants whose initial post-treatment evaluation reflected expectancy bias alone (positively—in those recognizing an active intervention, or negatively—placebo recipients).

Qualitative specificity clustering of multiple markers

While trials may address depressive symptoms or anxiety as the primary endpoint, there may be specific patterns of sleep or other subtle qualitative or quantitative markers (e.g., electrophysiologic markers—EEG) that may help distinguish true effect from expectancy alone.

A dose–response manipulation

The dose of medication and the “dose” of psychotherapy could be designed in various ways that would help distinguish increments of the true effect by analyzing the magnitude of response under different dosing regimens.

Broader evaluation of the totality of evidence

Before selecting the most appropriate statistical modeling adjustment method to address unblinding/expectations, the use of tools, such as Bradford Hill’s causal criteria or other causal inference estimators has helped with important advancements in medicine (e.g., Surgeon General’s reports on smoking and cancer). ³⁹ And although these are not perfect themselves, they may help move the trust in the effects of psychedelic therapy in the right direction ⁴⁰ (see Table 2 for example of Hill’s criteria applied to the evidence of psychedelic-assisted therapy in depression).

Table 2.

Example of Hill’s causal inference criteria for psychedelic-assisted therapy in depression.

Criterion	Level of evidence	Evidence summary and accurate metrics (2025/2026)	Role in offsetting unblinding
1. Strength	Very high	Pooled Hedges’ g = 0.91 (Singleton et al., 2025). 41	These effects are roughly triple those of conventional SSRIs (g ~0.3 when converted from Odds Ratios reported by Cipriani et al., 2018). 42
2. Consistency	High	Replicated in 12+ major RCTs across global sites (Johns Hopkins, Imperial, NYU, Usona, Compass).	If unblinding were the only driver, consistency would likely break down across different cultural “hype” levels and therapeutic settings.
3. Specificity	Moderate	Targets specific cognitive markers: rumination reduction, amygdala reactivity, and increased neural entropy.	Placebo effects are typically “general” (overall wellness). PAT shows specific changes in neural flexibility that correlate with symptom relief.
4. Temporality	Highest	Immediate symptom reduction seen 24 h post-dose (e.g., QIDS-SR d = 3.0 on Day 1).	Traditional antidepressants require 4–6 weeks. The immediate “strike” following the dose provides a nearly undeniable temporal link.
5. Gradient	High	Dose–response confirmed: 25 > 10 > 1 mg. 1 Outcomes also correlate with MEQ-30 (Mystical Experience) scores.9,31	If “guessing” was all that mattered, a 10 mg “trip” should theoretically produce the same outcome as 25 mg, but it doesn’t.
6. Plausibility	High	Established mechanisms: 5-HT2A agonism, BDNF-mediated synaptogenesis, and DMN disintegration.	Having a credible biological “blueprint” makes the large clinical shifts scientifically rational rather than purely psychological.
7. Coherence	High	Findings align with the biology of neuroplasticity and the psychology of emotional “breakthroughs.”	The data doesn’t conflict with known medical or biological facts; it extends the known effects of rapid-acting agents like Ketamine.
8. Experiment	Highest	Ketanserin blockade studies prove that without the specific receptor binding, the clinical effect is abolished. 43	This is the strongest evidence against pure expectancy. If it were just “belief,” the patient would still feel better even if the receptor were blocked.
9. Analogy	Moderate	Analogy to ketamine (rapid-acting) and electroconvulsive therapy (high-efficacy/low-frequency).	We already accept “non-linear” treatments in psychiatry; PAT fits the profile of established high-potency interventions.

BDNF, brain-derived neurotrophic factor; DMN, default mode network; PAT, Psychedlic-assisted therapy.

Measurement error correction methods

One possible approach to correcting for expectancy bias is to use measurement error methods. Specifically, you can use similar methods as have been used in nutritional epidemiology to correct for measurement error. ⁴⁴

To implement these methods, we need three prediction equations to predict

• (1) reported depression levels as a function of covariates and true depression level,

• (2) gold-standard depression level as a function of true depression level,

• (3) a biomarker of depression level as a function of true depression level and possibly other covariates.

More specifically, the first equation would express the error-prone instrument (Q) (e.g., the patient health questionnaire-9 (PHQ-9)) whose response is a function of true depression status (D) + treatment effect (T) + systematic error + random error. Thus, the total error is a combination of both systematic error due to expectancy bias and random error due to variability of both filling out the instrument and true depression status from day to day.

The second equation would consist of using intensive in-person interviews with a small number of subjects who are questioned on a daily basis for a short period of time as to their depression status (R). R is modeled as a function of true depression status (D) + systematic error + random error. The systematic error in the second equation might be associated with the systematic error in Q. An important additional assumption is that the average of many administrations of R over a long period of time will be equal to D, that is the regression coefficient will be 1, which is not the case in the first prediction equation.

The third equation would have an outcome based on a biomarker (M), which is a function of true depression status (D) + treatment modality (T) + systematic error + random error. The random error in the biomarker is independent of the error in the PHQ-9. There may also be systematic error in the biomarker where the biomarker response to true depression status may be variable from person to person. However, that systematic error is independent to the systematic error in the other two instruments (i.e., Q & R). To meet these assumptions, Gsalpha (a more precise BNDF-pathway biomarker) or a different depression scale (clinician-observed [e.g., Montgomery-Åsberg Depression Rating Scale (MADRS)], instead of subjectively reported, can be used in addition to PHQ-9 to satisfy the third equation’s requirements).^45,46

If a longitudinal design can be constructed where the difference scores in each of Q, R, and M can be obtained over the same time period, this can be used to obtain unbiased estimates of the association between the true depression status (D) and treatment (T). ⁴⁴

Limitations

Several limitations should be considered when interpreting the ideas presented in this manuscript. First, although belief-system change is proposed as a key mechanism underlying durable therapeutic effects, direct causal evidence remains limited. Associations between subjective psychedelic experience, meaning-making, and long-term improvement are well documented, but these relationships cannot fully rule out alternative explanations such as expectancy, therapeutic alliance, or other psychological and neurobiological factors.^6,9

Second, this manuscript suggests that expectancy may overlap with the therapeutic mechanism itself rather than function solely as bias. While this perspective is supported by emerging evidence, it remains difficult to test empirically. Current methods may not clearly distinguish short-term positive (and negative) expectancy effects from enduring belief change, and statistical corrections for expectancy risk removing meaningful therapeutic signal.^4,5

Third, many proposed methodological adaptations, including crossover and SMART designs, are supported primarily by conceptual reasoning and limited empirical application. These approaches may better address expectancy and carryover, but they do not eliminate core challenges such as functional unblinding, therapist effects, and relational influences. ³ Thus, they should be viewed as partial solutions rather than definitive methodological advances.

Conclusion

The methodological challenges in psychedelic research are not failures of execution or scientific rigor. They reflect a mismatch between classical pharmacologic trial design and therapies mediated by subjective experience. Psychedelic-assisted therapies disrupt fixed baselines via set and setting and resist durable blinding by blurring the boundary between pharmacologic action and psychological reorganization.

Rather than a nuisance variable, functional unblinding may in fact overlap with the therapeutic mechanism itself. Under these conditions, attempts to eliminate expectancy entirely risk removing part or all of the therapeutic signal rather than clarifying it.

Psychedelic therapy, therefore, seems to represent a new model of intervention in mental healthcare with implications for chronic conditions in physical health as well. The psychotherapeutic container, including preparation and integration, is not an optional adjunct but an active ingredient shaping both the mechanism and the outcome. Methodological progress will depend on incorporating, not eliminating, experiential factors.