Why Covariate Choice Is a Causal Decision
A propensity model estimates treatment probabilities from observed covariates, but its inputs should not be chosen simply because they predict treatment well. The central question is whether conditioning on a covariate set makes treated and untreated units comparable with respect to the potential outcomes relevant to the analysis. That question depends on how treatment was assigned and how the outcome arose, so it requires subject-matter knowledge as well as data.
Let \(D\) indicate treatment, with \(D=1\) for treated and \(D=0\) for untreated. Let \(Y(1)\) and \(Y(0)\) denote the potential outcomes under those two treatment states, and let \(X\) be a vector of covariates measured before treatment. The propensity score for a chosen covariate set is \(e(X)=P(D=1\mid X)\). The introductory material on the propensity score establishes its role as a balancing score; here the focus is how to decide which variables belong in \(X\).
A standard sufficient condition for identifying causal effects by adjustment is conditional exchangeability: \(Y(d)\perp D\mid X\) for each treatment state \(d\in\{0,1\}\). It is used together with consistency (the observed outcome equals \(Y(D)\)) and positivity, \(0<P(D=1\mid X=x)<1\) for covariate values in the target population. These assumptions are not established just by fitting a propensity model. Covariate selection is an attempt to make exchangeability plausible while retaining useful overlap.
Classify Variables by Their Causal Role
A causal diagram can help organize the decision. An arrow from one variable to another represents a causal influence. Before fitting a model, map plausible causes of treatment and outcome, and check when each candidate was measured. The same variable name can play different roles in different studies, so classification requires the study design and clinical or policy context.
| Candidate variable | Typical role | Usual implication for the propensity model |
|---|---|---|
| Baseline cause of treatment and outcome | Confounder | Include when measured and sufficiently well-defined. |
| Baseline cause or strong predictor of outcome, not treatment | Prognostic variable | May improve precision or reduce residual outcome variation; inclusion is not needed solely to control treatment confounding. |
| Baseline cause of treatment, with no effect on outcome except through treatment | Treatment-only predictor; sometimes an instrument | Do not include automatically. It may weaken overlap and can increase sensitivity to unmeasured confounding. |
| Common effect of two variables, one related to treatment and the other to outcome | Collider | Conditioning on it can create a noncausal association; avoid unless a valid adjustment argument supports its inclusion. |
| Variable caused by treatment | Post-treatment variable; possibly a mediator | Do not use as a baseline propensity covariate for a total treatment effect. |
Confounders are the priority because leaving one out can leave treatment groups different in causes of the outcome. Baseline prognostic variables can be useful even when they do not cause treatment: controlling them may improve precision, and a variable that is associated with both treatment and outcome should be considered even if the association is modest. In contrast, a variable that predicts treatment but has no outcome relevance is not automatically helpful.
An instrument is a variable that changes treatment assignment but, under the instrumental-variable assumptions, has no effect on the outcome except through treatment and is independent of unmeasured causes of the outcome. Those assumptions are demanding and cannot be inferred from a treatment-assignment association alone. For propensity adjustment, a strong instrument can concentrate treated observations in some covariate regions and untreated observations in others. If important confounding remains unmeasured, adjustment for the instrument can make the remaining treatment variation more dependent on that unmeasured confounding.
A mediator lies on a pathway from treatment to outcome. Adjusting for it generally removes part of the total treatment effect and can introduce additional bias. A post-treatment measure should therefore not be included simply because it is associated with the outcome or improves the apparent fit. Eligibility criteria, time zero, and treatment initiation must be specified so that “baseline” has a consistent meaning.
A Justification for Prioritizing Common Causes
Suppose \(U\) is an observed baseline cause of both \(D\) and \(Y\), and that treatment groups differ in \(U\). Then an unadjusted comparison mixes treatment effects with outcome differences attributable to \(U\). If adjustment for a measured set \(X\), including \(U\), makes the potential outcomes conditionally exchangeable, then within levels of \(X\), treatment assignment no longer carries information about those potential outcomes:
Under consistency, the observed outcome among units with \(D=d\) is their \(Y(d)\). The conditional outcome distribution for treatment state \(d\) can therefore represent the corresponding potential-outcome distribution at the same \(X\) values. Averaging over the target distribution of \(X\) then identifies a causal contrast, provided positivity holds. This argument explains why choosing covariates is about removing treatment-outcome differences, not maximizing a treatment classifier’s accuracy. It does not prove that a proposed set is sufficient: unmeasured causes, poor measurement, or incorrect timing can still violate exchangeability.
Worked Example: Selecting Candidates for a Medication Study
Consider a hypothetical observational study of whether initiating a preventive medication reduces a one-year cardiovascular event. Investigators define treatment at a common eligibility date and record candidate variables before that date. Their clinical review suggests that prior cardiovascular disease and current disease severity influence both prescribing and the event risk. In a hypothetical sample, 60 of 100 patients with severe disease initiate treatment, compared with 20 of 100 patients with mild disease.
The observed treatment proportions are \(60/100=0.600\) for severe disease and \(20/100=0.200\) for mild disease. The difference is \(0.600-0.200=0.400\), or 40 percentage points. These crude proportions do not establish a causal effect; they show that severity is related to treatment assignment and support treating it as an important candidate confounder when the clinical account also links it to the outcome.
The candidate list is classified using timing and causal role. Prior cardiovascular disease and baseline severity are priority candidates because they plausibly affect both prescribing and outcome risk. Age and baseline kidney function should also be considered if clinical knowledge indicates they affect either treatment selection and outcome risk, or outcome risk sufficiently to improve precision. Clinician prescribing preference may predict initiation strongly, but if it has no outcome effect except through treatment, it is treatment-only and should not be added automatically. Medication adherence after initiation occurs after treatment assignment; it is not a baseline propensity covariate and may mediate the treatment effect.
The choice is not “include every measured variable.” It is to include the well-measured, pre-treatment causes needed to make the exchangeability assumption credible, and consider other baseline outcome predictors when they serve the analysis. The investigators should document why each variable is included or excluded and then examine whether treatment groups overlap and are balanced on measured baseline covariates after the chosen propensity-score procedure.
Worked Example: A Treatment Predictor Is Not Automatically a Confounder
Suppose a hypothetical health system has two groups of clinicians. A clinician’s preference for a new treatment, \(Z\), affects whether an eligible patient receives it. Among patients treated by high-preference clinicians, 80 of 100 receive treatment; among those treated by low-preference clinicians, 20 of 100 receive it. Thus the treatment proportions are \(80/100=0.800\) and \(20/100=0.200\), a difference of 0.600.
This strong association makes \(Z\) a treatment predictor. It does not by itself make \(Z\) a confounder. Suppose, based on the hypothetical design, preference has no direct effect on the outcome, is not a proxy for patient prognosis, and affects the outcome only by changing treatment. On those stated assumptions, it is a treatment-only variable rather than a cause of the outcome.
If a prognostic factor \(U\) is unmeasured and affects both treatment and outcome, including \(Z\) can make the treatment comparison rely more heavily on differences in treatment within preference groups. Those differences may be particularly tied to \(U\). Strong treatment prediction can also produce fitted probabilities near zero or one, leaving few comparable treated and untreated patients in some regions. Thus \(Z\) should not be included just because it increases treatment prediction. If preference also captures differences in care quality that affect outcomes, however, the causal classification changes: that outcome pathway must be considered, and a blanket exclusion would not be justified.
The decision requires examining what clinician preference represents, whether it affects outcomes through other care, and whether adequate overlap remains. A large treatment-assignment association is evidence about prediction, not proof about the causal role of the variable.
Worked Example: Why Conditioning on a Collider Can Mislead
Consider a deliberately simple hypothetical baseline setting. Let \(H\) denote high clinician concern, which influences later treatment, and let \(U\) denote an underlying disease condition, which affects the outcome. Suppose \(H\) and \(U\) are initially independent, each with probability 0.5. A baseline screening flag \(C\) is recorded if either \(H=1\) or \(U=1\). Thus \(C\) is a common effect of \(H\) and \(U\), a collider. In this example, treatment is determined by \(H\) and the outcome by \(U\), solely to isolate the association created by conditioning.
Among individuals with \(C=1\), the equally likely \((H,U)\) pairs are \((1,0)\), \((0,1)\), and \((1,1)\). Therefore \(P(H=1\mid C=1)=2/3\), \(P(U=1\mid C=1)=2/3\), and \(P(H=1,U=1\mid C=1)=1/3\). The conditional covariance is
Although \(H\) and \(U\) were independent before conditioning, they are associated among those with \(C=1\). Since \(H\) determines treatment and \(U\) determines outcome in this simplified setup, conditioning on \(C\) creates a treatment-outcome association. The example is intentionally stark: in the \(C=0\) group, both variables are fixed at zero, so positivity also fails there. The practical lesson is not to omit every screening variable, but to ask whether it is a common effect of causes related to treatment and outcome. Timing alone does not make a baseline variable safe to adjust for.
Selection, Diagnostics, and Alternatives
A disciplined selection process starts with the treatment-assignment mechanism and the outcome-generating process, rather than a sequence of statistical significance tests. Before fitting the score, establish a covariate measurement window and draw or describe the hypothesized causal structure. Then classify each candidate as a common cause, outcome predictor, treatment-only predictor, collider, post-treatment variable, or a variable whose role is uncertain. Include measured, pre-treatment common causes when justified; make reasoned decisions about prognostic variables and avoid automatic inclusion of treatment-only predictors or colliders.
After estimation and matching or other score-based adjustment, evaluate covariate balance for all relevant measured baseline candidates, not only variables retained in the final model. Check overlap by comparing the distributions of estimated scores across treatment groups and identifying regions with little or no counterpart. A chosen set can fail in practice if key confounders are measured poorly, omitted, or represented inadequately. Conversely, apparent lack of balance can signal that the adjustment procedure or model has not achieved its purpose. Good balance on recorded variables is reassuring but does not establish balance on unmeasured variables or prove exchangeability.
Common alternatives include outcome regression that adjusts directly for covariates, and doubly robust approaches that combine treatment and outcome models. These approaches change how covariates enter estimation, but they do not make causal knowledge irrelevant: confounders still need attention, post-treatment adjustment can still be problematic, and unmeasured confounding remains a limitation. A propensity model is especially useful when its score supports a transparent design-stage comparison, but a fitted score cannot compensate for a weak adjustment set.
Common Mistakes and Limitations
- Selecting by treatment p-values: A small p-value shows evidence of association with treatment under a statistical model; it does not establish that a variable is a confounder. A true confounder can be weakly associated in a limited sample.
- Including every available variable: This can add colliders, post-treatment variables, or strong treatment-only predictors. More model inputs do not guarantee less bias.
- Excluding variables that do not predict treatment: A baseline outcome predictor may improve precision or help account for outcome differences even if it has little treatment association.
- Using treatment prediction as the criterion: High predictive accuracy can coexist with poor overlap and a weak causal comparison.
- Assuming balance proves no confounding: Balance checks address measured variables. They cannot reveal whether important unmeasured causes remain.
Subject-matter judgment is not a substitute for evidence: researchers should state assumptions, timing, and the rationale for each important choice. The adjustment set may be uncertain, measurements may be crude, and several plausible causal structures may fit the available information. When reasonable alternatives exist, sensitivity analyses can show whether conclusions depend on those choices; no single covariate-selection rule resolves uncertainty about unmeasured causes.
Check Your Understanding
Answer each question, then compare your reasoning with the solutions below.
- A baseline variable predicts treatment and the outcome because it reflects disease severity. What role does it play, and what is the usual implication for selection?
- A clinic preference measure strongly predicts treatment but has no outcome pathway except through treatment. Is strong prediction alone enough to include it? Why or why not?
- Why should a post-treatment adherence measure generally not be included in a baseline propensity model for a total treatment effect?
- After matching, all included variables are balanced. What important conclusion cannot be drawn from that fact alone?
- In the collider example, calculate the conditional covariance of \(H\) and \(U\) given \(C=1\) from the displayed probabilities.
Solutions. (1) It is a baseline confounder, so it is a priority candidate for adjustment if measured adequately. (2) No. It is a treatment-only predictor under the stated assumptions; it may impair overlap and does not control confounding merely by predicting treatment. (3) Adherence occurs after assignment and may lie on the causal pathway; adjusting for it can remove part of the total effect or introduce bias. (4) Balance does not establish exchangeability or rule out unmeasured confounding. (5) The covariance is \(1/3-(2/3)(2/3)=1/3-4/9=-1/9\).