HIV Trial Outcomes After Treatment Discontinuation

Trial question and analysis setup

In an HIV trial, some participants stop their assigned regimen before the planned week-24 assessment. Discontinuation may be related to worsening viral control, adverse effects, or other clinical circumstances. The week-24 viral load may nevertheless be measured after discontinuation; for other participants it is missing. These are distinct events: stopping treatment does not, by itself, mean that the outcome is unobserved.

Consider the treatment-policy question: what is the mean week-24 viral load in each randomized group, regardless of whether participants continued the assigned regimen? Let \(Y\) be week-24 log₁₀ plasma HIV RNA in copies per milliliter; lower values indicate less viral RNA. Let \(D=1\) indicate discontinuation of assigned treatment before week 24, and \(D=0\) indicate no such discontinuation. Let \(R=1\) if \(Y\) is observed and \(R=0\) if it is missing. Let \(Z\) collect randomized group and measured prognostic information, such as baseline and week-12 viral load. A useful analysis must represent \(D\), \(R\), and \(Y\) separately.

A reasonable starting point conditions on \(Z\), including relevant observed viral-load history and discontinuation status where appropriate. The missing-at-random (MAR) reference analysis assumes that, given those measured variables, the distribution of unobserved \(Y\) is the same as the distribution predicted for observed outcomes. Sensitivity analyses ask what follows if that reference assumption is not adequate. Neither model makes an unobserved viral load empirically known: each adds an assumption about it.

The treatment-policy outcome must be meaningful after treatment discontinuation, and the trial must have enough observed outcomes across relevant covariate and discontinuation patterns to estimate the reference models. The models also rely on adequate specification of the outcome distribution and covariate relationships. If week-24 viral load is undefined for a participant, rather than merely unmeasured, a different estimand is needed; imputing a value would not resolve that definitional problem.

Two ways to describe the unobserved outcomes

A selection formulation starts with an outcome distribution, such as \(f(Y\mid Z)\), and describes pattern probabilities conditional on the outcome. For example, one can model the probability of observing week-24 viral load as a function of \(Y\), \(D\), and \(Z\). To represent discontinuation itself as outcome-related, a joint formulation can also include \(P(D\mid Y,Z)\). Since \(Y\) may be unobserved for those who discontinued, the strength of this association is not learned from those outcomes directly. It is a sensitivity assumption, not a causal claim that a future viral load caused an earlier discontinuation.

A pattern-mixture formulation instead describes \(Y\) separately by pattern. For example, it models \(Y\) among discontinuers and continuers, then specifies how missing outcomes within each group relate to the observed outcomes with similar \(Z\). A convenient sensitivity parameter is an additive shift:

Here \(Y_{\mathrm{MAR}}\) is a draw or prediction from the MAR reference distribution conditional on the measured information and pattern. The parameter \(\delta_D\) is in log₁₀ copies/mL. A positive \(\delta_D\) assumes higher, therefore worse, viral loads among missing outcomes than the MAR reference predicts. The shift can differ for discontinuers and continuers. This location-shift specification is a practical sensitivity model, not a claim that every missing value differs by exactly the same amount.

The same observed data can be represented by either factorization, but the assumptions used to extrapolate to missing outcomes need not be equivalent. A selection parameter describes how response odds vary with latent \(Y\); a pattern-mixture shift describes how an unobserved outcome distribution differs within a pattern. Results should therefore be compared by their implied missing-outcome distributions, not just by the names of the models.

Worked examples

Why the selection and pattern-mixture assumptions differ

The contrast can be made precise for a simple selection model. For fixed covariates and pattern, Bayes' rule gives:

The last ratio does not depend on \(y\). If the response model is logistic with linear term \(\gamma(y-y_{\mathrm{ref}})\), then the response odds are proportional to \(\exp\{\gamma(y-y_{\mathrm{ref}})\}\). The missing-to-observed density ratio is consequently proportional to \(\exp\{-\gamma(y-y_{\mathrm{ref}})\}\). Thus, when \(\gamma<0\), higher values receive greater relative weight in the missing distribution. The result follows directly from the response-odds ratio in Bayes' rule; it also shows why the sign of \(\gamma\) matters.

Neither \(\gamma\) nor a pattern-mixture \(\delta_D\) is generally identified from observed outcomes alone when the outcome is missing for some participants. The observed data can support the response rates and observed outcome distributions, but they do not reveal how the missing outcomes differ after conditioning on measured history. A defensible analysis therefore reports results over scientifically plausible sensitivity values and explains their clinical meaning.

Diagnostics, alternatives, and limitations

Begin by describing discontinuation and outcome observation separately in each randomized group. Compare observed viral-load histories and baseline predictors across the \(D\) and \(R\) patterns. Check whether the reference model predicts observed outcomes adequately, whether fitted probabilities are extreme, and whether there are enough observed outcomes among discontinuers to support the conditional models. These checks can reveal poor overlap or model misspecification; they cannot verify an assumption about outcomes that were never observed.

For the sensitivity analysis, inspect the implied distributions and summaries of missing viral loads, not only the final treatment contrast. A large selection coefficient can yield extreme implied outcomes or very low response probabilities. A large positive pattern-mixture shift can imply viral loads beyond a clinically plausible range. Also check whether conclusions change sharply with small parameter changes, whether model fits fail, and whether estimates are driven by a small discontinuation stratum. Such behavior signals sensitivity or instability rather than a reason to select the most favorable result.

A common mistake is to treat treatment discontinuation as synonymous with missing outcome and then assume every discontinuer has an unobserved week-24 viral load. The correction is to record \(D\) and \(R\) separately: a participant can discontinue and still contribute an observed outcome, while another can continue treatment but miss the visit. A second pitfall is to call a positive \(\delta_D\) a treatment effect. It is an assumed difference in unobserved outcomes relative to a reference distribution, measured in log₁₀ copies/mL; it does not establish a causal effect of discontinuation.

The two approaches are complementary sensitivity parameterizations, not automatic substitutes for clinical judgment. Selection models make outcome-related response assumptions explicit through response odds; pattern-mixture models make assumptions about outcomes within observed patterns explicit through distributions or shifts. Both depend on a credible MAR reference model, adequate observed-data support, and sensitivity values that can be explained in clinical units. Neither can remove uncertainty about unobserved viral loads.