ADAPTABLE Bayesian Monitoring Of Aspirin Doses

Why Bayesian Monitoring Fits a Dose-Comparison Case

ADAPTABLE compared two daily aspirin doses among people with established atherosclerotic cardiovascular disease. The practical question was not only whether one dose might prevent more cardiovascular events, but also whether the evidence gathered during the trial would justify changing course before planned follow-up was complete. Bayesian monitoring makes that decision explicit: it updates probabilities about treatment effects as data accumulate, then compares those probabilities with decision thresholds set in advance.

Monitoring is not a license to stop whenever an interim result looks persuasive. The endpoint, treatment contrast, model, timing of reviews, and stopping rules need to be specified before the data are examined. The resulting decision is conditional on those choices, and the performance of the full design should be assessed by simulation under plausible treatment effects and trial operations.

ADAPTABLE’s Question and Its Null Comparison

ADAPTABLE was an open-label, pragmatic randomized comparison of aspirin 81 mg and 325 mg daily in people with established cardiovascular disease. Its primary composite outcome was death from any cause, hospitalization for myocardial infarction, or hospitalization for stroke. The trial enrolled 15,076 participants. The published primary comparison reported a hazard ratio of 1.02, with a 95% confidence interval from 0.91 to 1.14 and a p-value of 0.75. The estimate did not show a statistically significant difference between assigned doses.

For interpretation, define the hazard ratio as the hazard under assignment to 325 mg divided by the hazard under assignment to 81 mg. On this scale, a value below 1 favors 325 mg for the primary outcome, while a value above 1 favors 81 mg. The reported point estimate is close to 1, but the interval includes values on either side. It does not establish that the doses are equivalent, nor does the p-value give the probability that the null hypothesis is true.

The primary comparison concerns randomized assignment, not simply the dose a participant took at every point in follow-up. That distinction matters here: participants assigned to 325 mg were more likely to switch doses or discontinue their assigned regimen than participants assigned to 81 mg. Assignment-based results preserve the randomized comparison; comparisons based on dose actually taken can lose that protection.

A Simple Bayesian Model for Interim Evidence

Let \(\theta=\log(HR)\), where \(HR\) is the hazard ratio for 325 mg versus 81 mg on the primary outcome. Thus \(\theta=0\) corresponds to equal hazards, \(\theta<0\) favors 325 mg, and \(\theta>0\) favors 81 mg. For illustration, suppose an interim analysis provides an estimate \(y\) of \(\theta\) with standard error \(SE\), and use the approximate likelihood \(y\mid\theta\sim N(\theta,SE^2)\). A normal prior \(\theta\sim N(\mu_0,\sigma_0^2)\) gives a normal posterior.

This approximation assumes that the estimate is approximately normally distributed on the log-hazard-ratio scale, that its standard error adequately describes its sampling uncertainty, and that the prior was specified independently of the interim result. It also abstracts from the details of a time-to-event analysis, such as censoring and the proportional-hazards assumption. A real monitoring plan would need a likelihood appropriate to its endpoint and would account for the design and timing of interim looks.

The update follows by multiplying the prior density by the likelihood. Terms in the exponent that depend on \(\theta\) are \(-\frac{1}{2}\{(\theta-\mu_0)^2/\sigma_0^2+(y-\theta)^2/SE^2\}\). Collecting the coefficient of \(\theta^2\) gives posterior precision \(1/\sigma_0^2+1/SE^2\); collecting the linear term gives posterior mean \(\sigma_1^2(\mu_0/\sigma_0^2+y/SE^2)\). Completing the square yields the stated normal posterior.

Stopping Criteria: Direction, Magnitude, and Timing

A superiority rule should express what evidence would be persuasive enough to stop early for benefit. For example, a protocol might require \(P(\theta<0\mid\text{data})>0.99\). A futility rule asks whether the chance of achieving a worthwhile result is too small to justify continuing. One possible rule is based on the posterior probability of a clinically important effect, such as \(P(HR\leq0.85\mid\text{data})\); another uses the predictive probability that the completed trial will satisfy its success criterion. These rules answer different questions and should not be treated as interchangeable.

A numerical threshold is meaningful only together with its definition of benefit, prior, likelihood, interim schedule, and action. The following thresholds are purely illustrative, not ADAPTABLE’s reported protocol boundaries: stop for superiority if \(P(\theta<0\mid\text{data})>0.99\), and stop for futility if \(P(HR\leq0.85\mid\text{data})<0.05\). The futility boundary asks about a reduction of at least 15% in the hazard, rather than merely any reduction.

In ADAPTABLE, Bayesian interim monitoring was part of the adaptive-trial context, but the published primary comparison is reported with a hazard ratio, confidence interval, and p-value. Those summaries cannot be converted into a unique posterior probability without specifying a prior and likelihood. In particular, do not claim a particular posterior probability or reconstruct a stopping boundary from the reported confidence interval alone. The trial did not stop early for superiority or futility.

Adherence, Assignment, and the Estimand

A randomized dose assignment is not the same as sustained dose exposure. In ADAPTABLE, switching and discontinuation were substantial, especially among participants assigned to 325 mg. This can dilute an assignment-based contrast: outcomes under the two assigned strategies may look similar even if taking the doses consistently would produce a different contrast. But switching does not by itself prove that the doses have different biological effects. Reasons for switching may relate to health, tolerability, clinician advice, or other factors that also predict outcomes.

The intention-to-treat comparison estimates the effect of assignment to the two dose strategies, under the trial’s actual pattern of adherence and follow-up. An as-treated comparison instead groups participants by the dose they received; because dose received is not generally randomized throughout follow-up, confounding can arise. A per-protocol question about sustained adherence needs additional assumptions and methods. Changing the analysis after seeing switching patterns does not restore randomization.

What a Null Result Does—and Does Not—Say

A non-significant result is not proof of no effect. The ADAPTABLE hazard-ratio interval, 0.91 to 1.14, is compatible with a range of possible effects in either direction under the analysis used. It is evidence against neither every clinically relevant benefit nor every clinically relevant harm. To conclude equivalence or noninferiority, a trial needs a prespecified margin and an analysis designed to assess that margin; simply failing to reject a no-difference hypothesis does not supply either.

A null comparison also has to be read against adherence and the treatment strategy being estimated. With considerable switching, the randomized result remains informative about assignment to the dose strategies as implemented. It may be less informative about the effect of sustained use under perfect adherence. Those are different questions, and the second requires assumptions beyond the original randomized comparison.

Diagnostics and Common Pitfalls

Before acting on an interim posterior, check that the endpoint and treatment contrast match the protocol, the data cut is complete enough for the planned analysis, and the likelihood’s assumptions are plausible. For a time-to-event model, inspect whether proportional hazards is credible and whether censoring or outcome ascertainment differs across groups. Examine dose switching and missing follow-up by assignment. If adherence or data capture departs from assumptions used in design simulations, the calculated posterior may still be mathematically available, but its decision meaning can be compromised.

A further diagnostic is simulation of the entire monitoring design. Simulate under no effect, clinically important benefit, and harm, including the planned interim looks and realistic adherence patterns. Estimate how often each stopping rule fires and how long trials run. Bayesian thresholds do not automatically control frequentist error rates at a desired level; simulation shows the operating characteristics of the specific design.

• Mistake: “The p-value is 0.75, so there is a 75% probability that the doses have no difference.” Correction: A p-value is calculated under a null model; it is not a posterior probability that the null is true.
• Mistake: “The confidence interval includes 1, so the two doses are equivalent.” Correction: Equivalence requires a prespecified margin and suitable inference; a non-significant difference alone is insufficient.
• Mistake: “Switching makes the randomized result invalid, so we should use the dose actually taken.” Correction: The randomized result estimates the assignment strategy. An as-treated analysis answers a different question and may be confounded.