Multi-Arm Multi-Stage (MAMS) vs. Response-Adaptive Randomisation (RAR): A Practical Guide for Medical Device Clinical Investigations

Medical device clinical investigations, as formally regulated under FDA Investigational Device Exemption (IDE) rules or EU MDR/ISO 14155 guidelines, increasingly incorporate adaptive methodologies to improve efficiency and patient outcomes. Two primary approaches have emerged: Multi-Arm Multi-Stage (MAMS) designs, which evaluate arms at predefined milestones to drop inferior treatments or stop early for efficacy, typically maintaining a fixed allocation ratio among remaining arms; and Response-Adaptive Randomisation (RAR), which continuously shifts the randomisation probabilities of future patients toward better-performing treatments throughout the investigation.

The choice between these methods depends on investigation characteristics including endpoint timing, data infrastructure, regulatory requirements, and scientific objectives. This guide examines the mathematical foundations and operational considerations for each approach to help biostatisticians and sponsors select the most appropriate method.

Fundamental Differences Between MAMS and RAR

The core distinction lies in the mechanism of adaptation. MAMS designs adapt by eliminating underperforming arms or stopping the investigation entirely at discrete interim analyses. Between these analyses, randomisation remains fixed (e.g., 1:1 among active arms).

Conversely, RAR designs adapt the allocation ratio itself. Rather than dropping arms, RAR continuously updates the probability of assignment, skewing enrolment toward the treatment arms demonstrating the best outcomes. This fundamental difference has profound implications for statistical methodology, operational complexity, and regulatory considerations.

Feature	MAMS	RAR
Adaptation mechanism	Drops arms at discrete interim analyses	Continuously shifts allocation ratios
Randomisation ratio	Fixed between interim analyses	Continuously updated
Endpoint timing	Tolerant of delayed endpoints	Requires rapid endpoint assessment
Type I error control	\alpha-spending plus multi-arm adjustment	Usually simulation-based calibration
Data infrastructure	Periodic clean data cuts sufficient	Real-time data systems required
Temporal drift vulnerability	Moderate	High
Power at fixed sample size	Stable across scenarios, but still requires simulation to characterise	Variable; may gain or lose depending on target allocation
Estimation after adaptation	Biased; established correction methods	Biased; correction methods less standardised
Regulatory familiarity	High (group sequential framework)	Moderate, with specific reservations

Multi-Arm Multi-Stage (MAMS): Mathematical Framework and Implementation

MAMS designs adapt through formal interim analyses. The mathematics centres on group sequential testing, where investigators evaluate treatment effects and apply pre-specified stopping rules for efficacy or futility.

Let H_{0,i} denote the null hypothesis for treatment i against control. This hypothesis is tested at each of the interim analysis stages k = 1, 2, \ldots, K using test statistics Z_{i,k}, which are compared against predefined boundaries:

• If Z_{i,k} \geq U_k, stop for efficacy and reject H_{0,i}
• If Z_{i,k} \leq L_k, drop treatment i for futility
• If L_k < Z_{i,k} < U_k, continue enrolling 1:1 in remaining arms

The Lan-DeMets approach allocates Type I error across K analyses using \alpha(t_k) = f(t_k), where t_k = I_k / I_{\max} is the information fraction and f(t) is the spending function. For the O’Brien-Fleming boundary:

f(t) = 2 - 2\Phi!\left(\frac{z_{1-\alpha/2}}{\sqrt{t}}\right)

This function applies stringent boundaries early in the investigation when data are sparse, reaching \alpha at t = 1. Note that f(t) returns the cumulative error spent by information fraction t; the increment available at stage k is f(t_k) - f(t_{k-1}).

Multiple comparisons present a dual challenge. Lan-DeMets \alpha-spending controls the Type I error rate across repeated interim looks, but a separate adjustment is needed for the multiplicity of K experimental arms. Because the test statistics are correlated through the shared control arm, a Bonferroni correction is unnecessarily conservative. The standard approach for MAMS designs is the generalised Dunnett test (Magirr, Jaki & Whitehead, 2012), which accounts for both the number of arms and the number of stages. It is worth noting that whether family-wise error rate control is even required in multi-arm investigations remains genuinely contested; regulators have varying expectations depending on the confirmatory or exploratory nature of the investigation.

Worked Example: Cardiac Stent Investigation

Consider a cardiac stent investigation testing three new drug-eluting stents (A, B, C) against standard care (D). After enrolling 200 patients (1:1:1:1 fixed allocation), the first interim analysis is conducted. Stent A shows a 15% reduction in target vessel revascularisation, while Stents B and C perform similarly to the control.

Using an O’Brien-Fleming spending function with a Dunnett-based multi-arm adjustment, each stent is compared against standard care against an efficacy boundary U_1 and a futility boundary L_1. These are derived at the design stage from the number of arms, the number of planned analyses, and the information fraction at each.

The interim decision applies a separate rule to each arm, so more than one of the following can occur at the same analysis:

• If Stent A crosses U_1, the investigation stops early for overwhelming efficacy.
• If Stents B and C fall below L_1, they are dropped, and the investigation continues with fixed 1:1 allocation between Stent A and Standard Care.
• If neither boundary is crossed, the investigation continues with 1:1 allocation among all remaining arms.

Note that with a 12-month target vessel revascularisation endpoint, the number of patients with mature outcomes at the point 200 are enrolled may be considerably smaller than 200. The information fraction, not the enrolment fraction, drives the boundary calculation.

This approach requires sophisticated upfront planning. Sponsors must specify exactly when interim analyses occur, the exact boundaries for dropping arms, and how Type I error is controlled. Regulatory agencies appreciate this level of pre-specification because it ensures investigation integrity and prevents ad-hoc decision-making.

Response-Adaptive Randomisation (RAR): Bayesian and Frequentist Approaches

Response-adaptive randomisation operates at a much more granular level, updating beliefs about treatment effectiveness as patient outcomes accrue. Rather than dropping arms, RAR shifts allocation probabilities. The mathematical foundation typically involves Bayesian updating, where the investigation maintains probability distributions representing current beliefs about each treatment’s efficacy.

Thompson sampling maintains posterior distributions for each treatment’s efficacy parameter. For binary outcomes, if treatment i has observed s_i successes in n_i trials, the posterior under a \mathrm{Beta}(\alpha, \beta) prior becomes:

\theta_i \mid \text{data} \sim \mathrm{Beta}!\left(\alpha + s_i,; \beta + n_i - s_i\right)

At each allocation, a value \tilde{\theta}_i is sampled from each posterior, and the next patient is assigned to the treatment with the highest sampled value. The allocation probability for treatment i is therefore:

\pi_i = P!\left(\theta_i = \max_j \theta_j ;\middle|; \text{data}\right)

This is the posterior probability that treatment i is the best among the available options, and it holds exactly by construction rather than as a limiting result.

In practice, raw Thompson sampling is rarely used unmodified in confirmatory settings. Tempering the allocation probabilities, raising them to a power c \in (0,1) and renormalising, moderates the skew and improves power. Protecting the control allocation at a fixed proportion is also common, and is often what makes RAR viable in a multi-arm investigation at all.

Allocation probabilities can alternatively be driven by posterior means. Because posterior means do not sum to one across arms, they must be normalised:

\mu_i = \frac{\alpha_i + s_i}{\alpha_i + \beta_i + n_i}, \qquad \pi_i = \frac{\mu_i}{\sum_{j=1}^{K} \mu_j}

A frequentist alternative is the Randomised Play-the-Winner (RPW) rule of Wei and Durham (1978), which uses an urn model rather than a direct probability calculation. The urn begins with u balls of each treatment type. A ball is drawn and the corresponding treatment assigned; a success on treatment A adds w balls of type A, while a failure on treatment A adds w balls of type B. The per-patient assignment probability is governed by the current urn composition, which converges to a limit determined by the failure rates q_i = 1 - p_i:

\lim_{n \to \infty} \frac{n_A}{n} = \frac{q_B}{q_A + q_B}

This allocates more patients to the treatment with the lower failure rate. For example, if the true failure rates are q_A = 0.2 and q_B = 0.4, the limiting allocation to treatment A is 0.4 / 0.6 \approx 67%. This differs from the simpler success-proportion heuristic p_A / (p_A + p_B) \approx 57%, which is sometimes described as RPW but is a different rule with different asymptotic behaviour.

Additional RAR rules include Covariate-Adjusted Response-Adaptive (CARA) randomisation, which models success probability as:

\operatorname{logit}!\big(P(Y = 1 \mid X, Z)\big) = X^{\mathsf{T}}\beta + Z^{\mathsf{T}}\gamma + (X \otimes Z)^{\mathsf{T}}\delta

where X are baseline covariates and Z indicates treatment assignment. The interaction term \delta is what makes this a CARA model rather than a covariate-adjusted analysis: without it the treatment effect is common to all patients and there is nothing for allocation to condition on.

For continuous outcomes following N(\mu_i, \sigma^2), assuming known variance and a flat prior, Thompson sampling updates:

\mu_i \mid \text{data} \sim N!\left(\hat{\mu}_i,; \frac{\sigma^2}{n_i}\right)

where \hat{\mu}_i is the sample mean for treatment i. If \sigma^2 is unknown, the marginal posterior follows a t-distribution and a prior on \sigma^2 must be specified; the normal form above is then an approximation that is poor at small n_i.

Worked Example: AI Diagnostic System Investigation

Consider a clinical investigation testing three approaches for detecting diabetic retinopathy: AI-only, traditional ophthalmologist review, and combined AI plus ophthalmologist verification, with concordance against an adjudicated reference standard as the endpoint.

Starting with uninformative priors \mathrm{Beta}(1,1) for each approach, after 50 patients per arm (150 in total) the data shows: AI-only correctly diagnosed 42 cases with 8 errors; traditional review got 38 right with 12 wrong; and the combined approach achieved 47 correct with only 3 errors. The Beta distributions become \mathrm{Beta}(43, 9), \mathrm{Beta}(39, 13), and \mathrm{Beta}(48, 4) respectively.

For the next patient allocation, the system samples from each distribution many times and counts how often each approach produces the highest sample. The combined approach, with its dominant \mathrm{Beta}(48,4) distribution, wins approximately 94% of these samples, earning it an allocation probability of roughly 94% for the next patient under untempered Thompson sampling. No arm is dropped, but the AI-only and traditional review arms would receive very few future patients — which illustrates why tempering or control-arm protection is usually necessary if the investigation still needs to estimate the inferior arms with any precision.

One design caveat deserves emphasis. Where the endpoint is purely diagnostic accuracy, all three strategies can in principle be applied to the same patient. A paired multi-reader multi-case design eliminates between-patient variability entirely and is substantially more efficient than randomising patients to reading strategies. Randomised allocation, and therefore RAR, is appropriate where the diagnostic strategy determines downstream clinical management and the endpoint is a patient outcome rather than a reading-level accuracy measure.

The Delayed Response Problem

This is where RAR is most fragile. Thompson sampling does not naturally handle delayed responses; the ability to update in real time depends on immediate endpoint assessment. When diagnostic results take weeks to confirm, beliefs cannot be immediately updated for patients enrolled yesterday, and the adaptation operates on a stale and progressively less representative subset of the data.

Bai, Hu and Rosenberger (2002) addressed this theoretically, establishing the asymptotic properties of urn-based adaptive designs under delayed response. The broad finding is reassuring asymptotically: many adaptive designs retain their limiting allocation properties provided the degree of delay decays at a sufficient rate relative to sample size. This is cold comfort in a device investigation of a few hundred patients, where delay is a first-order practical problem rather than a vanishing higher-order term.

The pragmatic implementation maintains separate pending pools for each treatment, applying the adaptation rule only to data from patients whose outcomes are confirmed available by time t - d. Note that this is a change of allocation rule, not merely a change of timing: allocation is now driven by normalised posterior means rather than by Thompson sampling. The posterior mean for each arm is calculated as:

\mu_i(t) = \frac{\alpha_i + s_i(t-d)}{\alpha_i + \beta_i + n_i(t-d)}

These posterior means are then normalised to form allocation probabilities:

\pi_i(t) = \frac{\mu_i(t)}{\sum_{j=1}^{K} \mu_j(t)}

where K is the number of active treatment arms, and s_i(t-d) and n_i(t-d) represent successes and total allocations from patients whose outcomes had matured by time t-d. More recent work extends this to group-sequential updating: Zhai, Li, Zhang and Hu (2024) propose RAR procedures that update on the responses of a group of patients, either as they become available or at fixed weekly or biweekly intervals, which maps far more naturally onto the operational reality of a device investigation than per-patient updating.

Temporal Drift: A Critical RAR Caution

A central concern with response-adaptive randomisation in the literature is temporal drift. Because allocation ratios change over calendar time, any drift in patient characteristics, clinical practice, or standard of care over the course of the investigation becomes confounded with treatment assignment. A treatment that happened to be favoured during a period of easier patients accumulates an advantage that randomisation would ordinarily have removed. The effect is not subtle and does not require bad faith; it follows mechanically from the design.

This is compounded by a second problem. Early allocation decisions are made on the smallest and noisiest data, and their consequences persist. A run of good luck on one arm in the first twenty patients can skew allocation for the remainder of the investigation, and in the multi-arm case can starve the control arm precisely when it is most needed for comparison.

Proschan and Evans (2020) caution against RAR in settings where temporal drift is plausible. In device investigations, where surgical techniques, imaging technologies, patient selection criteria, and the investigational device itself may all evolve during the trial, this risk is amplified.

Mitigations exist and should be pre-specified: an initial burn-in period of equal randomisation before adaptation begins; protecting the control arm at a fixed allocation proportion; block-based rather than continuous updating; and adjusting for enrolment period in the final analysis. Saville and colleagues’ “Bayesian time machine” approach models temporal drift explicitly within the analysis rather than attempting to design around it.

Power and Allocation Variability

RAR is often presented as straightforwardly more efficient. The reality is more conditional, and the direction of the effect depends on what the allocation rule targets.

In two-arm settings, response-adaptive randomisation frequently reduces power versus fixed 1:1 randomisation at a given total sample size. Rules targeting Neyman or optimal allocation can preserve or improve power, while rules targeting patient benefit — Thompson sampling among them — typically cost power, because power is maximised near balanced allocation and RAR deliberately moves away from it. There is a real trade-off between the number of patients who receive the better treatment during the investigation and the precision with which the investigation answers its question.

Thompson sampling additionally has high variability in realised allocation. The expected allocation may favour the superior arm while individual realisations vary widely, and in a non-trivial fraction of investigations more patients end up on the inferior arm than the superior one. This variability is itself an operating characteristic that should be simulated and reported, not just the mean allocation.

The multi-arm case is more favourable to RAR than the two-arm case. Wason and Trippa (2014) compared Bayesian adaptive randomisation directly against MAMS designs and found that RAR procedures can achieve higher power than MAMS when a single experimental treatment is genuinely effective — the most directly relevant published comparison for the choice this guide addresses.

Device-Specific Statistical Considerations

Medical devices introduce mathematical challenges that pharmaceuticals rarely face.

Learning Curves

Learning curves create a particularly complex problem because early poor outcomes might reflect operator inexperience rather than device inferiority. As described by Berry and colleagues (2010), this can be modelled explicitly. If \theta_{ij} represents the success probability for surgeon i on case j, a hierarchical model might use:

\operatorname{logit}(\theta_{ij}) = \alpha_i + \beta_i \log(j) + \gamma Z_{ij} + \eta Z_{ij}\log(j)

where \alpha_i captures surgeon i‘s baseline ability, \beta_i represents their learning rate, \gamma is the true device effect, Z_{ij} is an indicator of device assignment (0 for control, 1 for experimental), and \eta allows the experimental device to be learned at a different rate from the comparator. The logarithmic term captures the typical learning curve shape where improvement is rapid initially, then plateaus. The hierarchical structure is completed with prior distributions:

\alpha_i \sim N(\mu_\alpha, \sigma^2_\alpha), \qquad \beta_i \sim N(\mu_\beta, \sigma^2_\beta)

It is tempting to conclude that this framework makes RAR safe for devices by preventing promising devices from being penalised during skill acquisition. The opposite is closer to the truth.

A learning curve is a temporal trend. It guarantees that early outcomes are systematically worse than later ones for reasons unrelated to the device. RAR adapts most strongly on exactly this early, operator-contaminated data, and its allocation decisions persist. Worse, the hierarchical model cannot rescue the situation in real time: reliable estimation of \beta_i requires sufficient cases per surgeon, and those cases do not exist at the point where RAR is making its most consequential allocation decisions. The model is a sound analysis strategy and a poor adaptation strategy.

For device investigations with meaningful learning curves, this argues for MAMS, or for RAR with a substantial equal-randomisation burn-in extending past the steep portion of the curve. It also argues for pre-specifying a minimum case volume per operator before that operator’s data contributes to adaptation at all.

Software Updates During Investigations

Software updates present another mathematical puzzle. Instead of treating device versions as completely separate entities, hierarchical Bayesian methods model them as related. If version 1.0 has parameter vector \theta_1 and version 1.1 has \theta_2, the model can specify:

\theta_2 \sim N(\theta_1 + \delta, \Sigma)

where \delta represents expected improvement and \Sigma captures uncertainty about how modifications affect performance. Where \theta represents probabilities, this relationship should be specified on the logit scale rather than the natural scale. This approach borrows strength from pre-update data while learning about post-update performance.

The statistical machinery, however, is downstream of a regulatory question that must be settled first: whether the updated device is still the device under investigation. A modification that changes intended performance characteristics may require a protocol amendment, a new risk assessment, or in some cases a separate investigation.

Statistical Challenges and Solutions

Data Maturity

Both MAMS and RAR amplify “garbage-in, garbage-out” problems because incorrect early decisions cascade through the entire investigation. The concern is more acute for RAR, which adapts continuously on immature data, than for MAMS, which typically adapts at discrete points against cleaner data cuts.

For delayed outcomes, adaptation should be based only on mature data. The principled options are time-to-event modelling, multiple imputation, or restricting the adaptation rule to outcomes that have been confirmed available by the time of the next allocation decision. Ad-hoc down-weighting of immature observations should be avoided: for a binary endpoint, an observation that has not yet reached its follow-up window is censored rather than a partially-informative zero, and weighting schemes applied to the numerator alone attenuate confirmed events while leaving not-yet-events untouched, biasing the estimate toward the null.

Estimation After Adaptation

Both MAMS and RAR produce biased naive treatment effect estimates because the adaptation depends on observed outcomes. This is frequently overlooked in favour of Type I error discussion.

The mechanisms differ. In MAMS, an arm surviving to the final analysis has been selected for having performed well at interim, so the naive estimate of its effect is biased upward; investigations stopping early for efficacy are similarly biased, because early stopping occurs disproportionately on random highs. In RAR, the allocation itself depends on accumulating outcomes, which breaks the independence assumptions underlying standard estimators.

Regulators care about this because the reported effect size drives labelling and clinical decision-making, not just the yes/no of the hypothesis test. Sponsors should pre-specify bias-adjusted estimation in the SAP: median-unbiased point estimates and confidence intervals based on an appropriate ordering of the sample space are standard for group sequential and MAMS designs. Correction methods for RAR are less standardised, which is itself an argument for simulation-based evaluation of estimator bias and mean squared error at the design stage, not only power.

Simulation Requirements and Operating Characteristics

Before implementing any adaptive design, extensive simulation studies are required — typically 10,000 or more simulated investigations under multiple scenarios. These simulations must explore the null hypothesis (where all treatments are equivalent), realistic alternative hypotheses with plausible effect sizes, mixed scenarios where some treatments work while others do not, delayed response scenarios, and explicit temporal drift scenarios including operator learning curves. For each simulated investigation, patient outcomes are generated from appropriate probability distributions, adaptation rules are applied, and final sample sizes, allocation ratios, and conclusions are recorded.

The resulting operating characteristics are what regulators scrutinise most closely. Under the null, the Type I error rate must remain controlled — conventionally two-sided \alpha = 0.05, or one-sided \alpha = 0.025 for superiority investigations. Under realistic alternatives, the design must achieve adequate power, typically at least 80%, to detect clinically meaningful differences. Adaptive designs typically require a larger maximum sample size than a fixed design while delivering a smaller expected sample size, and both quantities inform operational planning. The allocation distribution should be reported with its variability across simulations, not only its mean, including the proportion of investigations in which more patients are allocated to an inferior arm. The early stopping probability quantifies how often the investigation would terminate for efficacy or futility, and estimator bias and mean squared error should be reported for both naive and bias-adjusted estimates of the primary treatment effect.

Sample size determination proceeds iteratively. The design is simulated across a range of total sample sizes under the alternative hypothesis, and the smallest N that achieves the desired power is selected, provided Type I error remains controlled under the null.

Sensitivity analyses test robustness to violations of assumptions: varying effect sizes, endpoint timing for RAR, accrual rates, dropout rates, and the magnitude of temporal drift. Simulation results themselves have sampling error. With 10,000 simulations, the Monte Carlo standard error for a 5% Type I error rate is approximately:

SE = \sqrt{\frac{0.05 \times 0.95}{10{,}000}} \approx 0.0022

giving a 95% confidence interval of roughly 4.6% to 5.4%. For power estimation, use more simulations if the target is close to a regulatory threshold.

Where the purpose of the simulation is to choose between MAMS and RAR rather than to characterise a single chosen design, the comparison should be run head-to-head under a common set of scenarios and a common maximum sample size. Reporting each design’s operating characteristics in isolation makes the trade-off invisible.

Pre-Specified Simulation Scenario Table

The following scenarios should be pre-specified in the SAP:

Scenario	Description	Purpose
Global null	All treatments are equally effective	Assess Type I error control
Superiority	One treatment is superior to all others	Assess power and expected sample size
Mixed	Some treatments work, others do not	Assess ability to drop inferior arms
Delayed response	Outcomes take time to confirm	Test RAR delayed response handling
Temporal drift	Population or operator skill changes over time	Test confounding of allocation with time
High dropout	Significant patient dropout rate	Test robustness to missing data

Pre-specifying scenarios prevents “data dredging” by selecting scenarios that make the design look good post-hoc.

Regulatory Considerations

Regulators globally have become increasingly supportive of adaptive designs, provided they are grounded in mathematical rigour. Support is not uniform across adaptation types, however, and RAR occupies a more contested position than MAMS.

Across all regions, regulators require evidence that Type I error remains controlled at the pre-specified significance level under the global null, that the investigation achieves adequate power to detect clinically meaningful differences, and that the design yields efficiency gains when clear winners exist (Pallmann et al., 2018). Regulators increasingly expect simulation code to be submitted for independent verification. Sponsors should ensure simulation code is well-documented and commented, that random number seeds are set for reproducibility, and that the code can be run independently by regulators or their statistical reviewers.

United States

The FDA’s 2016 guidance Adaptive Designs for Medical Device Clinical Studies is the governing document, with Guidance for the Use of Bayesian Statistics in Medical Device Clinical Trials (CDRH/CBER, 2010) as the relevant companion for Bayesian approaches including RAR. CDRH has historically been more receptive to Bayesian methods than FDA’s drug centres, which is a genuine advantage for device sponsors.

The FDA expects adaptation algorithms, whether MAMS stopping boundaries or RAR probability updates, to be detailed in the Statistical Analysis Plan. The SAP must be finalised and locked before any unblinded data are reviewed, ensuring that adaptive features are truly prospective and algorithmic rather than subjective. Pre-specification before the study begins is the regulatory standard. The guidance’s central principle is that modifications are scientifically valid when made without knowledge of outcome results by treatment group, which places the emphasis on firewalls and controlled information flow as much as on the algorithms themselves.

European Union

In the European Union, clinical investigations are governed by the EU Medical Device Regulation (MDR 2017/745) and ISO 14155:2026. Under the MDR, the study protocol is officially designated as the Clinical Investigation Plan (CIP). The CIP must outline the high-level adaptive methodology and justify how the design protects human subjects and minimises risk (Article 62), with statistical design and analysis content specified per ISO 14155:2026 Annex A. The exact statistical algorithms, simulation parameters, and \alpha-spending functions are then specified in a separate, detailed SAP.

The SAP should be finalised and locked before the initiation of any adaptive algorithms. While not explicitly required by MDR Article 62 or ISO 14155, this is considered best practice and is expected by the Member State Competent Authorities that authorise clinical investigations.

The EMA’s Complex Clinical Trials Questions and Answers (2022) is the current reference point for novel design discussions. Sponsors considering RAR in the EU should engage early and be prepared to demonstrate robust control of temporal drift.

United Kingdom

In the United Kingdom, device clinical investigations are governed by the UK Medical Devices Regulations 2002 (revised version expected June 2027). The MHRA Innovation Office supports innovative trial designs across both medicines and devices, and MHRA guidance states that it supports complex innovative designs such as umbrella, basket, platform, and master protocol trials, requiring sponsors to justify the design choice, demonstrate that each adaptation and the investigation as a whole are safe and scientifically sound, and describe how the integrity of results will be maintained.

Sponsors should note a jurisdictional distinction that is easy to miss: much of the MHRA’s published adaptive-design engagement sits in the CTIMP (medicines) space. The methodological expectations transfer readily; the regulatory route does not. Early engagement with the MHRA Innovation Office is the appropriate mechanism for a novel device design.

Pre-Submission Engagement

Across all regions, pre-submission interactions (FDA Pre-Subs, MHRA Innovation Office or scientific advice meetings, or Expert Consultations with EU Competent Authorities) should include the proposed CIP and draft SAP, simulation results demonstrating operating characteristics under both stationary and drift scenarios, clear rationale for methodological choices, the firewall and information-flow plan, and detailed plans for Independent Data Monitoring Committee (IDMC) involvement.

Implementation Requirements

Implementing adaptive randomisation requires careful consideration of operational constraints. MAMS designs require \alpha-spending function calculations at discrete intervals, which can be performed on periodic clean data cuts.

RAR designs demand considerably more: real-time or group-sequential Bayesian updating, Monte Carlo sampling for Thompson sampling, and automated allocation probability updates. The system architecture flows from data entry through real-time databases to statistical engines that feed the randomisation system. Every link in that chain becomes a potential single point of failure that can silently corrupt allocation. RAR investigations inherently require greater statistical analysis plan complexity, increased programming effort for the creation and validation of simulation and allocation code, and heightened data management complexity. The randomisation system requires formal validation, and the audit trail must be sufficient to reconstruct why each allocation probability took the value it did at the time it was applied.

A further consideration is specific to devices: most device investigations cannot be fully blinded, which interacts badly with RAR. A visibly skewed allocation ratio leaks interim results to investigators and patients, potentially introducing performance bias and influencing which patients are approached, how they are consented, and how subjective endpoints are assessed. Maintaining allocation concealment is materially more challenging with RAR than with fixed randomisation or MAMS. The FDA’s 2016 guidance emphasises the importance of firewalls to prevent operational bias — measures that deserve more than a single passing IDMC mention in the protocol.

Decision Framework for Method Selection

The framework below should be read alongside the comparison table in the Fundamental Differences section.

Choose Multi-Arm Multi-Stage (MAMS) designs when:

• There are well-defined interim analysis timepoints (e.g., safety run-ins, planned efficacy looks)
• Primary endpoints require substantial follow-up time
• The investigation features multiple treatment arms where dropping inferior arms is preferred over skewing allocation
• Operator learning curves or other temporal trends are expected
• The investigation cannot be blinded
• There is a regulatory preference for pre-specified, discrete adaptation rules and fixed randomisation between looks
• Real-time data processing capabilities are limited

Choose Response-Adaptive Randomisation (RAR) when:

• Rapid endpoint assessment is possible (minutes to days), or group-sequential updating is operationally feasible
• There is a strong ethical imperative to minimise exposure to inferior treatments without dropping them entirely
• The patient population is homogeneous and stable over the enrolment period
• Robust, real-time data systems are available
• The investigation prioritises within-investigation patient benefit, and the associated power cost has been quantified and accepted
• Adequate mitigations against temporal drift are pre-specified: burn-in, control-arm protection, and drift-adjusted analysis

Consider hybrid approaches when:

• Different endpoints have different assessment timelines
• Both early safety signals (MAMS) and longer-term allocation efficiency (RAR) matter
• Regulatory discussions suggest openness to novel designs

While MAMS and RAR are often presented as alternatives, in practice they exist on a spectrum. I-SPY 2 and REMAP-CAP combine response-adaptive randomisation with arm graduation and dropping; STAMPEDE uses a pure MAMS framework. The choice is not binary but should reflect the specific operational and scientific context of the investigation.

RAR’s patient-level adaptation offers genuine ethical advantages but demands flawless data systems, a stable population, and acceptance of a power and estimation cost. MAMS provides more operational control and traditional regulatory familiarity but may miss opportunities for real-time optimisation. Both approaches require extensive simulation studies to demonstrate operating characteristics under realistic, including adverse, scenarios. The choice between them should be driven by which method best serves the specific combination of scientific questions, operational constraints, and regulatory pathway.

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