Adjusting Assurance for Attrition and Nonadherence

Why Retention and Adherence Belong in Assurance

An assurance calculation describes the probability that a planned trial will meet its success rule across the design scenarios and trial outcomes considered plausible. Its simulation should therefore represent not only the randomized sample size, but also what may happen after randomization. Dropout can reduce the information in the data; nonadherence can change the treatment effect that the randomized comparison is intended to estimate. These are different mechanisms, and a single “inflation factor” does not generally capture both.

The essential planning question is: what data would the proposed trial actually produce, and what effect would its success rule assess? In a simulation, the answer depends on the assumptions about retention, adherence, outcomes after nonadherence, and the analysis of missing outcomes. Those assumptions should be explicit before estimating assurance.

A Planning Model and Its Assumptions

Consider a two-arm trial with \(n\) participants randomized to each arm. Let \(r_T\) and \(r_C\) be the probabilities that a randomized participant in the treatment and control arms, respectively, has an analyzable endpoint. Let \(\delta\) denote the treatment effect under full adherence, measured in endpoint units. In a simple dilution model, a fraction \(q\) of treatment-assigned participants does not adhere, and their mean outcome is assumed to be the same as it would have been under control. The mean contrast by randomized assignment is then \(\theta=(1-q)\delta\).

This model is useful for illustration, but it is not a universal description of nonadherence. It assumes a common adherence probability, no effect of nonadherence other than foregoing the treatment effect, and no additional effect of treatment discontinuation on outcomes. For the examples below, endpoint outcomes are modeled as independent normal observations with a common known standard deviation \(\sigma\); the likelihood uses the diluted mean contrast and treats the residual variance as unchanged. This working approximation does not include extra outcome variability from individual-level mixtures of adherers and nonadherers. A realistic design may need to simulate adherence for each participant and include the resulting variability and analysis model.

For attrition, the simplest model draws observed counts independently as \(n_T\sim\operatorname{Binomial}(n,r_T)\) and \(n_C\sim\operatorname{Binomial}(n,r_C)\). This assumes endpoint availability is independent across participants and does not depend on their unobserved outcomes, conditional on the modeled variables. If dropout depends on prognosis, response, or treatment experience, complete-case analysis can be biased; reducing the sample size alone does not repair that bias.

How the Bayesian Success Rule Changes With Observed Sample Size

For a transparent calculation, suppose the analysis prior for the treatment-policy mean contrast \(\theta\) is \(N(0,\tau^2)\), and the observed difference in sample means is \(D=\bar{Y}_T-\bar{Y}_C\). With independent normal outcomes and known standard deviation \(\sigma\), the likelihood is \(D\mid\theta\sim N(\theta,v)\), where \(v=\sigma^2(1/n_T+1/n_C)\). The posterior is normal, with mean \(\tau^2D/(\tau^2+v)\) and variance \(\tau^2v/(\tau^2+v)\).

Suppose success requires posterior probability greater than 0.975 that \(\theta>0\). Since the posterior is normal, this is equivalent to the posterior mean divided by posterior standard deviation exceeding the standard-normal quantile at 0.975. For a positive \(D\), the resulting data threshold is:

The exact cutoff is \(\Phi^{-1}(0.975)\); its familiar value 1.96 is a rounded approximation. The threshold increases as \(v\) increases, so fewer observed participants can make the success rule harder to meet. In an assurance simulation with random observed counts, the threshold should be recalculated using each replicate’s \(n_T\) and \(n_C\), rather than using the planned randomized count as if everyone supplied an outcome.

Worked Examples

Simulation Workflow, Diagnostics, and Alternatives

A practical simulation keeps the sources of uncertainty visible. In each replicate, draw the true effect from the chosen design distribution, generate adherence and endpoint availability, generate the outcomes conditional on those events, fit the planned Bayesian analysis, and apply the prespecified success rule. If the design distribution itself includes uncertainty about retention or adherence, draw those rates as well. The final estimate is the number of simulated successes divided by the number of replicates; Monte Carlo uncertainty should be assessed using the methods for simulation error and rare-event assurance.

Useful diagnostics include checking simulated retention and adherence rates against their specified probabilities, verifying that observed counts vary as expected, and confirming that the analysis uses those counts correctly. Plotting success rates across effect sizes or retention scenarios can reveal unexpected patterns. If lowering the sample size appears to improve assurance, inspect the success boundary and outcome generation: added noise can sometimes increase threshold-crossing probability in a particular high-effect scenario, so the pattern should be understood rather than assumed impossible. Compare simulated results with a simpler fixed-count calculation when its assumptions apply.

Expected-count inflation is a convenient alternative for a quick enrollment approximation, but it ignores the distribution of retained counts and any interaction between counts and the success rule. A fixed dilution factor is similarly convenient, but can miss participant-level heterogeneity and differential adherence. Full simulation is more flexible and can represent random retention and adherence, but it is only as credible as its assumptions and implementation. It does not correct a misspecified missing-data model or justify an inappropriate analysis.

Common Pitfall and Limits

A common mistake is to divide the required sample size by the retention rate and then divide again by the adherence rate, treating both as if they were the same kind of loss. Attrition reduces the number of observed outcomes; nonadherence need not remove observations at all and may instead change the treatment contrast. The correction is to model each mechanism in its proper place: retention in the data-availability process, and nonadherence in the outcome-generating process and the effect being analyzed.

The examples use a simple normal model and a particular success rule. In practice, dropout may be informative, adherence may vary over time, and outcomes after discontinuation may differ from either assigned treatment condition. The model should reflect the trial’s intended interpretation and analysis; the detailed choice of estimand and handling of intercurrent events requires careful specification. Sensitivity analyses are especially important when retention or adherence assumptions are uncertain.