Relapse-Related Missing Reports in a Smoking Cessation Trial

Why Missing Smoking Reports Need Special Attention

In a smoking-cessation trial, an end-of-study self-report may be absent because a participant stopped responding, but it may also be absent because the participant relapsed and disengaged. Those explanations matter: if participants who do not report are less likely to be abstinent than participants who do report, treating the reporters as representative can overstate abstinence. The direction and size of that distortion can differ between trial arms.

The analysis below focuses on a binary endpoint at a fixed follow-up time: whether a participant is abstinent. The target is the abstinence proportion among all randomized participants in each arm, not only among those who supplied a report. This is a hypothetical worked case; the values are invented to illustrate the calculations, not results from a real trial.

The treatment contrast used here is the absolute difference \(\theta_T-\theta_C\), in percentage points, where \(T\) denotes the intervention arm and \(C\) the control arm. Positive values favor the intervention on the abstinence scale. Randomization supports comparing the arms, but it does not reveal \(q_a\): when smoking status is unreported, the observed data alone do not establish how many nonreporters were abstinent.

The Mixture Calculation and Its Assumptions

Within each arm, the full group consists of reporters and nonreporters. Partitioning on report status gives the identity

The identity is exact, but \(q_a\) is unknown when outcomes are missing. An assumption about \(q_a\), or information that helps estimate it, is needed to produce an all-randomized estimate. Under a missing-at-random assumption for this endpoint, conditional on the information being used in the analysis, missing reports do not carry additional information about abstinence. In a simple arm-only calculation this sets \(q_a=p_a\), and therefore \(\theta_a=p_a\). If baseline or other observed predictors are used, the corresponding assumption is that abstinence among nonreporters equals the predicted abstinence for otherwise comparable reporters; the simple formula should then be applied within predictor strata or through an appropriate prediction model.

A relapse-related sensitivity analysis instead allows \(q_a<p_a\). One convenient parameter expresses the abstinence odds among nonreporters relative to the abstinence odds among reporters:

The parameter is a sensitivity assumption, not an estimate obtained from the reports alone. Setting the same \(\gamma\) in both arms means assuming the same relative odds departure in both arms; it does not mean the same number of missed reports or the same abstinence probability among nonreporters. Setting different values allows the relationship between relapse and missing reporting to differ by arm. If every nonreporter is assumed to be smoking, set \(q_a=0\) directly; that is a strong boundary scenario, not a fact implied by a missing report.

Worked Analyses

Why the Mixture Result Holds

The key derivation is a partition of the abstinence event by whether a report was observed. Within arm \(a\), the events \(R=1\) and \(R=0\) are disjoint and cover all participants. Therefore,

Applying the multiplication rule to each term gives \(P(Y=1\mid R=1,A=a)P(R=1\mid A=a)+P(Y=1\mid R=0,A=a)P(R=0\mid A=a)\). Replacing these probabilities by \(p_a\), \(q_a\), \(1-m_a\), and \(m_a\) yields the mixture identity. No assumption that missingness is random is needed for this identity. The assumption enters only when assigning a value to the unobserved \(q_a\).

The odds transformation follows by setting the nonreporter odds equal to \(\gamma_a\) times reporter odds: \(q_a/(1-q_a)=\gamma_a p_a/(1-p_a)\). Multiplying through by \((1-q_a)(1-p_a)\) and collecting the \(q_a\) terms gives \(q_a(1-p_a+\gamma_a p_a)=\gamma_a p_a\), which yields the stated formula. For \(0<p_a<1\), its implied \(q_a\) increases as \(\gamma_a\) increases. The sensitivity parameter therefore moves the assumed missing-outcome distribution in a controlled, interpretable direction.

Diagnostics, Alternatives, and Limits

The observed data cannot directly prove whether relapse caused a report to be missed, because the smoking status of nonreporters is precisely what is unknown. They can, however, reveal warning signs and help discipline sensitivity assumptions. Examine missing-report rates by randomized arm, baseline smoking intensity, prior quit attempts, earlier abstinence reports, and recorded reasons for nonresponse. Check whether missingness clusters after visits at which relapse was reported or suspected. A pattern linking observed relapse indicators to later missingness makes an assumption of no relapse-related departure less comfortable, although it does not determine \(q_a\).

Where feasible, use contact attempts, biochemical verification, or other auxiliary information to estimate outcomes in a representative sample of nonreporters. Check whether verification participation and measurement quality plausibly support that use. Also inspect the implied \(q_a\) values: probabilities outside \([0,1]\), or values inconsistent with reliable auxiliary evidence, signal an invalid calculation or an implausible scenario. Extreme sensitivity values may still be useful as bounds, but should be identified as such.

The main alternatives answer different questions or rely on different assumptions. A complete-case comparison uses \(p_T-p_C\) and describes reporters; it is not the all-randomized contrast unless the missingness assumptions justify that interpretation. A missing-at-random analysis can use observed predictors to model outcomes, but it depends on adequately measured predictors and a credible conditional missing-at-random assumption. A relapse-related pattern-mixture analysis directly varies \(q_a\) or \(\gamma_a\), making the untestable departure explicit. Declaring every missing participant to be smoking provides a simple conservative scenario for abstinence, but it is not automatically conservative for every treatment contrast: its effect depends on the missing fractions in both arms.

A practical limitation is that sensitivity parameters are not identified by the observed self-reports alone. A range of plausible assumptions is more informative than presenting one chosen value as if it were known. These calculations also give point estimates; they do not account for sampling uncertainty in reported proportions or in a verification subset. Inference requires uncertainty calculations consistent with the chosen model and the trial design. Finally, an end-of-study report may not establish abstinence over the entire follow-up period; the endpoint definition and timing must match the clinical question.