Inputs for MAMS Sample-Size Calculations

Why Sample-Size Inputs Need a Clear Specification

A MAMS design can stop early, drop individual treatment arms, or continue several comparisons using a shared control. Its sample-size assessment therefore depends on more than one number such as “the planned sample size.” The design must specify how many participants are assigned at each stage, how they are allocated across arms, which outcome model and treatment effects are assumed, what power objective is being targeted, and how likely the design is to continue under relevant scenarios.

These inputs serve different purposes. Allocation and stage sizes describe the design’s planned resource use. Outcome assumptions and the prespecified decision rule determine how likely each interim decision is. Continuation probabilities summarize those decisions under particular treatment-effect scenarios. If any of these pieces is ambiguous, a calculated maximum or expected sample size may answer a different question from the one intended.

Define the Design and Its Stage Sizes

A design specification should state whether stage sizes are fixed increments or are recalculated after interim decisions. It should also say whether all retained arms continue recruiting to the same planned stage and whether control recruitment changes when treatment arms are dropped. A stage size needs a unit: participants per arm, participants in a particular arm, or participants across all arms are not interchangeable descriptions.

For arm \(k\), define its stage-specific allocation ratio relative to control as \(\rho_{kj}=n_{kj}/n_{0j}\), when \(n_{0j}>0\). If allocation is intended to remain constant, state that \(\rho_{kj}=\rho_k\) at each relevant stage. If the ratio changes by stage or after dropping an arm, specify the full allocation schedule rather than reporting a single ratio.

State the Outcome and Treatment-Effect Assumptions

Power and interim continuation depend on the distribution of the outcomes, not just on allocation counts. Specify the primary endpoint, its units, the estimand for each treatment-control comparison, and the model used to describe its sampling distribution. State assumptions about nuisance parameters—such as variance for a continuous endpoint or event rate for a binary endpoint—and identify whether they are common across arms or allowed to differ. If the endpoint is measured repeatedly or participants contribute correlated observations, the assumed correlation structure must also be specified.

For example, with a continuous endpoint measured once per participant, an elementary planning model might assume independent observations within and between randomized groups, with \(X_{ki}\sim N(\mu_k,\sigma_k^2)\) for treatment arm \(k\), and \(X_{0i}\sim N(\mu_0,\sigma_0^2)\) for control. Under this model, the estimated treatment-minus-control difference has standard error \(SE=\sqrt{\sigma_k^2/n_k+\sigma_0^2/n_0}\) for the sample sizes being considered. A shared control makes the treatment-control statistics dependent: comparisons reuse control observations. The power calculation must reflect that dependence and the design’s actual multiple-testing procedure.

Define the treatment effect in a direction that makes the clinical interpretation unambiguous. For a lower-is-better endpoint, one might define \(\theta_k=\mu_k-\mu_0\), so beneficial effects are negative. State the clinically relevant effect for each scenario, along with the assumed nuisance parameters and any allowance for missing outcomes, nonadherence, or unusable measurements. Such allowances must be tied to the chosen analysis estimand and recruitment plan rather than added as unexplained multipliers.

Specify the Power Objective and Decision Rule

A power target is incomplete unless it names the event whose probability is being targeted and the treatment-effect scenario under which that probability is evaluated. The decision rule includes the prespecified efficacy and futility rules, the stagewise boundaries, and the method used to control the familywise error rate. Power should be evaluated for that complete rule, not for an isolated comparison if the intended conclusion concerns the MAMS procedure as a whole.

Common objectives answer different questions. Arm-specific power is the probability of rejecting the null hypothesis for a named treatment arm under its specified effect. Disjunctive power is the probability of rejecting at least one null hypothesis in a stated set of comparisons. Conjunctive power is the probability of rejecting every null hypothesis in a stated set. These probabilities can differ substantially when several arms are tested, so a plan should name the objective, the set of arms, the target level (for example, 90%), and the assumed true effects for every arm, including arms assumed to have no effect.

For an illustrative target, a protocol might require 90% disjunctive power when one of two treatments has the specified clinically relevant benefit and the other has no benefit. That is not the same target as 90% power for each arm separately, nor is it a claim that both active treatments will be detected with 90% probability. The power calculation also presumes the type-I error procedure has been set; changing the multiplicity strategy or decision boundaries can change power even when the allocation and outcome assumptions stay fixed.

Describe Interim Continuation Under Scenarios

A continuation probability is not an intrinsic property of the treatment effect alone. It depends on the outcome model, stage sizes, correlation between comparisons, interim boundaries, and the rule for dropping or retaining arms. It should therefore be reported alongside the scenario and design assumptions that produced it. If the design can drop arms separately, a single probability of “continuing” may hide important differences: specify probabilities for the relevant retained-arm states or transitions.

A Short Justification: Why Scenarios Must Be Named

Continuation probabilities, and therefore expected resource use, can change when the assumed effects change. The distinction follows directly from conditional probability. If \(R_j\) is reaching stage \(j\), the probability of reaching the next stage under scenario \(\theta\) is \[ P(R_{j+1}\mid\theta) =P(R_j\mid\theta)P(R_{j+1}\mid R_j,\theta). \] The second factor is \(q_j(\theta)\). Because the interim statistics have distributions that depend on the assumed effects and nuisance parameters, changing \(\theta\) can change \(q_j(\theta)\), even with an unchanged design. Consequently, an expected sample-size assessment needs an explicit scenario (or a specified weighting of scenarios); it cannot be reported as one universal value without qualification.

For a design that drops arms separately, the same logic applies to transitions between states. For example, “both arms retained,” “only arm A retained,” and “trial stopped” are distinct outcomes of an interim decision. Probabilities should be conditional on the state reached, and the enrollment cost associated with each state must be available. Treating all these possibilities as a single all-arms continuation event can misrepresent resource use.

Diagnostics, Alternatives, and Limitations

Before using the inputs, check that the design schedule and the probability model describe the same trial. The following are useful warning signs:

• Ambiguous stage sizes: a number is labelled “stage 2 sample size” without stating whether it is newly recruited or cumulative, or which arms it includes.
• Incompatible allocation ratios: treatment counts do not match the stated ratios, or the plan does not say what happens to control allocation after an arm is dropped.
• Incomplete scenarios: an active-arm effect is given but the assumed effects for other arms are omitted, even though the target is disjunctive or conjunctive power.
• Unstated model inputs: the endpoint, variance or other nuisance parameters, or the dependence among shared-control comparisons are left unspecified.
• Mislabelled probabilities: a conditional continuation probability is reported as a probability from the start of the trial, or a probability is given without naming the scenario.
• Mismatch with the decision rule: power or continuation is assessed using boundaries that differ from the boundaries planned for the MAMS design.

A fixed-sample-size design is a useful alternative when there are no interim decisions that affect recruitment or stopping. It may be easier to describe, but it does not capture the resource consequences of MAMS stopping rules. A simple calculation for one treatment-control comparison can be a useful check on the scale of an assumed effect and its standard error, but it is not a substitute for evaluating the joint, stagewise decision rule in a multi-arm design. When analytic calculations do not adequately represent the model or the decision process, simulation can evaluate the prespecified rule under explicitly generated scenarios; the simulation must still use defensible outcome, allocation, and missingness assumptions.

No set of inputs removes uncertainty about the true effects or nuisance parameters. Results should therefore be interpreted as conditional on the stated assumptions, and sensitivity analyses should examine plausible alternatives. In particular, expected sample size under a global null, under a specified alternative, and under partial activity are different scenario-specific quantities, not interchangeable summaries.