Why Missing Baseline Biomarkers Matter
Enrichment decisions and subgroup claims depend on knowing which participants have the biomarker of interest. If a baseline assay is unavailable for some randomized participants, their subgroup membership is unknown. An analysis restricted to observed assays can therefore describe a selected subset rather than all biomarker-positive participants. The key question is not simply how many assays are missing, but whether the participants with observed assays support the intended subgroup comparison.
Let \(B_i=1\) indicate that participant \(i\) is biomarker-positive at baseline, and let \(R_i=1\) indicate that the biomarker measurement is observed; \(R_i=0\) means it is missing. Let \(A_i\) denote randomized treatment assignment, with \(A_i=1\) for the treatment and \(A_i=0\) for control, and let \(Y_i\) be the outcome. For a higher-is-better outcome, one target is the mean treatment effect among all biomarker-positive participants in the trial:
Here \(Y_i(a)\) is the outcome participant \(i\) would have under assignment \(a\). Randomization supports a causal treatment comparison, but it does not by itself reveal \(B_i\) for participants whose assay is missing. This tutorial concerns missing baseline biomarker measurements, not errors in an observed assay result. Assay misclassification is a distinct problem.
Complete-Case Subgroup Analysis
A complete-case analysis includes only participants with an observed biomarker, then compares randomized treatment groups among those observed to be biomarker-positive. Its main attraction is transparency: each included participant’s subgroup is known, and the outcome comparison follows the randomized assignment. Its main limitation is that the resulting effect may apply to observed-assay biomarker-positive participants rather than to all biomarker-positive participants.
A strong sufficient condition for the complete-case comparison to represent the target subgroup effect is that, among biomarker-positive participants, assay observation does not select participants with different potential outcomes: \(R_i\) is independent of \(Y_i(1),Y_i(0)\) conditional on \(B_i=1\). MCAR is one sufficient, though often stronger than necessary, condition. If missingness depends on measured prognostic factors, a complete-case estimate can still be useful when the treatment effect is constant across those factors, but that is an additional assumption—not a consequence of randomization.
Worked Example: A Complete-Case Estimate
Suppose a hypothetical randomized trial has an outcome measured in points at 12 weeks. Biomarker status is observed for 160 of 200 participants. Among the observed biomarker-positive participants, 40 were assigned treatment and 35 control. Their mean outcomes are 8.2 and 6.4 points, respectively. Assume the randomized groups are intact within the observed biomarker-positive subset.
The complete-case treatment-effect estimate is the difference in subgroup means:
Thus, in this hypothetical observed-assay subgroup, the treatment group’s mean outcome is 1.8 points higher. Randomization supports the comparison for this selected subset. To interpret 1.8 points as the effect for all biomarker-positive participants, however, missing assay status must not have selected a subgroup with a different treatment effect, or an appropriate adjustment must be made under defensible assumptions.
Inverse-Probability Weighting
Inverse-probability weighting (IPW) gives more influence to observed biomarker measurements that represent participants with similar observed characteristics but a lower probability of having an assay recorded. Let \(X_i\) be observed baseline variables used to model assay availability, and let \(\pi_i=P(R_i=1\mid X_i,A_i)\). The treatment assignment may be included in this model if assay availability differs by assignment, although baseline collection before randomization makes such a difference less expected. For estimation of the biomarker-positive mean outcome in arm \(a\), an IPW estimator is:
The indicator \(I(\cdot)\) equals 1 when its condition holds and 0 otherwise. The probability \(\pi_i\) is the probability that the biomarker is observed, conditional on modeled variables. IPW requires a correctly specified or sufficiently accurate observation-probability model, conditional independence of observation from the unobserved subgroup and relevant outcomes given those variables, and positivity: every covariate pattern in the target population must have a nonzero probability of an observed assay. Very small \(\hat{\pi}_i\) values create large weights and unstable estimates.
The basic justification is that, under the stated conditional independence assumption, weighting by \(1/\pi_i\) reverses the over- or under-representation caused by assay observation. For any quantity \(g\) whose value is available when \(R_i=1\), conditional on \(X_i,A_i,B_i,Y_i\), if \(P(R_i=1\mid X_i,A_i,B_i,Y_i)=\pi_i\), then:
Thus weighted totals recover the corresponding full-data totals in expectation. In practice, the probability is estimated and the ratio estimator is used; uncertainty in the estimated weights should be reflected in the standard error.
Worked Example: Weighting Observed Biomarker-Positive Participants
Consider a hypothetical trial with two observed baseline covariate strata, low-risk and high-risk. A fitted assay-observation model gives probabilities \(\hat{\pi}=0.80\) in the low-risk stratum and \(\hat{\pi}=0.50\) in the high-risk stratum. The table below summarizes observed biomarker-positive participants and their outcome totals in each randomized arm.
| Arm | Stratum | Observed \(B=1\), n | Outcome total |
|---|---|---|---|
| Treatment | Low-risk | 10 | 80 |
| Treatment | High-risk | 2 | 12 |
| Control | Low-risk | 4 | 24 |
| Control | High-risk | 8 | 32 |
For treatment, the weighted outcome total is \(80/0.80+12/0.50=100+24=124\), and the weighted denominator is \(10/0.80+2/0.50=12.5+4=16.5\). Therefore:
For control, the weighted outcome total is \(24/0.80+32/0.50=30+64=94\), and the weighted denominator is \(4/0.80+8/0.50=5+16=21\). Thus:
The estimate is 3.039 points, conditional on the observation model and missingness assumptions. It differs from the unweighted contrast because weighting changes the representation of low- and high-risk participants. The small hypothetical dataset makes the weights and arithmetic visible; it does not establish that the model assumptions hold.
Multiple Imputation
Multiple imputation (MI) replaces each missing biomarker value with a draw from a predictive distribution, producing \(m\) completed datasets. Each completed dataset is analyzed using the planned subgroup model, and the estimates and variances are combined. For a baseline biomarker, a suitable imputation model may include observed baseline predictors of biomarker status and assay availability, randomized assignment, and outcome information. Including treatment and outcome information can preserve the associations needed to estimate treatment effects within the biomarker subgroup. The imputation model should also represent relevant nonlinearities and interactions, including treatment-by-biomarker structure when needed.
MI relies on a MAR assumption conditional on variables included in the imputation model, together with a sufficiently well-specified imputation model. A binary biomarker is generally imputed using a model appropriate for a binary variable, such as logistic regression. Imputed values are draws, not deterministic classifications from a predicted probability. Treating a probability above an arbitrary cutoff as a known biomarker status discards uncertainty and can distort subgroup estimates.
Let \(Q_j\) be the subgroup effect estimate and \(U_j\) its estimated variance in imputed dataset \(j\). Rubin’s combining rules use the mean estimate \(\bar{Q}\), the average within-imputation variance \(\bar{U}\), and the between-imputation variance \(B\):
The combined standard error is \(\sqrt{T}\). The between-imputation component represents uncertainty from the missing values; simply averaging subgroup estimates without it understates uncertainty.
Worked Example: Combining Imputed Subgroup Effects
Suppose five hypothetical imputed datasets yield treatment-effect estimates, in points, of 1.8, 2.0, 1.9, 2.1, and 2.2. For simplicity, suppose each analysis has within-imputation variance \(U_j=0.64\) points squared. The mean estimate is:
The squared deviations from 2.0 are \(0.04,0,0.01,0.01,0.04\), which sum to 0.10. Hence \(B=0.10/(5-1)=0.025\) points squared, while \(\bar{U}=0.64\). The total variance and standard error are:
Using a large-sample 1.96 multiplier for illustration, the interval is \(2.0\pm1.96(0.8185)\), or approximately 0.396 to 3.604 points. This interval describes uncertainty in the estimated mean treatment effect under the imputation and analysis assumptions; it is not a probability statement about the fixed effect. With few imputations, a degrees-of-freedom adjustment and corresponding \(t\) critical value are preferable to the large-sample multiplier used here.
Choosing and Checking an Approach
| Approach | Useful when | Main vulnerability |
|---|---|---|
| Complete case | Assay observation is plausibly nonselective for the target effect, or the target is explicitly the observed-assay subgroup. | Selection can change subgroup composition and the effect being estimated. |
| IPW | Observed predictors explain assay availability, and observation probabilities can be estimated with adequate overlap. | Misspecified probabilities or extreme weights can cause bias or instability. |
| Multiple imputation | A credible MAR model can predict missing status using relevant predictors and preserve the analysis relationships. | Results depend on the imputation model; MNAR departures are not fixed by adding more imputations. |
These approaches are not interchangeable guarantees of validity. Complete-case analysis has the least modeling machinery, but can target the wrong population. IPW models assay observation and reweights measured cases; MI models the missing biomarker distribution and carries imputation uncertainty into the final estimate. Either model-based method can fail if its assumptions or models are poor. When reasonable, comparing methods can reveal sensitivity to modeling choices, but agreement does not prove that MAR holds.
Useful diagnostics include tabulating assay-observation rates by treatment arm and by observed baseline predictors; checking whether the observation model predicts those rates; and inspecting the distribution of estimated probabilities and weights. For IPW, report the range of weights and consider whether a few observations dominate the estimate. Weight truncation may reduce variance but changes the estimator and can introduce bias, so it requires justification and sensitivity analysis. For MI, inspect whether imputed biomarker prevalences and relationships with predictors are plausible, and use enough imputations for stable estimates. Neither diagnostic set can verify the unobserved values.
Assumptions, Sensitivity, and Common Mistakes
The most consequential limitation is that MAR cannot generally be confirmed from observed data alone. If assay failure depends on the unobserved biomarker value even after conditioning on measured variables, the data are MNAR. For example, samples with a particular unrecorded biomarker level might be more likely to fail for technical reasons. A primary MAR analysis should therefore be accompanied, when this concern is material, by sensitivity analyses that vary plausible assumptions about missing participants. The purpose is to show how conclusions change under departures from MAR, not to claim that one untestable assumption has been proven.
A common mistake is to reason, “Treatment was randomized, so the complete-case subgroup comparison is unbiased.” Randomization balances assignment at baseline in the randomized population; it does not ensure that the biomarker-observed subset represents all biomarker-positive participants. If assay availability selects participants differently by prognostic characteristics or treatment-effect modifiers, the observed subgroup can differ from the target subgroup. State the target population, examine selection, and justify the missingness assumption before interpreting the estimate.
Check Your Understanding
Answer each question, then compare with the brief solutions.
- In a complete-case analysis, 50 observed biomarker-positive treatment participants have a mean outcome of 7.0 points and 45 observed biomarker-positive controls have a mean of 5.5 points. What is the estimated contrast, and what population does it directly describe?
- Why can randomized treatment assignment fail to justify complete-case inference for all biomarker-positive participants?
- An IPW analysis has estimated assay-observation probabilities close to zero for some participants. What is the concern?
- What is the distinction between MAR and MNAR for a missing baseline biomarker?
- In MI, why is the between-imputation variance included in the total variance?
Solutions. 1. The contrast is \(7.0-5.5=1.5\) points. Directly, it describes the observed-assay biomarker-positive participants in the two randomized groups; extending it to all biomarker-positive participants requires additional assumptions. 2. Randomization does not prevent assay observation from selecting a subset whose biomarker-positive participants have a different distribution of prognostic factors or treatment effects. 3. The inverse weights become very large, so a few participants may dominate the estimate and produce high variance; near-zero observation probabilities also threaten positivity. 4. Under MAR, missingness is independent of unobserved biomarker status conditional on included observed variables; under MNAR, dependence remains after that conditioning. 5. Different completed datasets yield different effect estimates because the missing values are uncertain; \(B\) captures that additional uncertainty.