How can treatment effects be estimated in high-risk groups with unobserved status?

Why restricting to high-risk members loses precision

The paper targets a group average treatment effect (GATE): the average difference between treated and untreated potential outcomes among people whose disease risk D exceeds a threshold c, within a prespecified subgroup Z. Formally the estimand is the expected value of Y(1) minus Y(0) given D > c and Z = z. This is a different quantity from an average effect in the whole sample, and it is the quantity a prevention trial usually wants when it enriches for high-risk participants.

The straightforward approach, which the paper calls hard targeting, keeps only individuals observed to be high risk and estimates the effect inside that subset. The paper states the problem directly: when risk status is unobserved, or the target population is small, analyses restricted to high-risk individuals can be unstable or inefficient. Small high-risk-by-subgroup cells are exactly where a hard-targeting estimate has few observations to work with.

The paper's alternative keeps everyone in the analysis sample but gives each person a weight equal to their probability of high-risk membership. That probability is the high-risk membership score W(x, z), defined as the probability that the high-risk indicator H equals 1 given covariates X and subgroup Z. Individuals who are unlikely to be high risk still contribute, but only in proportion to how much they resemble the target population.

The membership score behaves like a propensity score

The score W(X, Z) satisfies a balancing property: within a subgroup Z = z, conditioning on the scalar score balances the distribution of the potentially high-dimensional covariates X between high-risk and lower-risk individuals. The paper notes this property follows from the definition of W and does not involve the outcome Y. That is what lets a single number stand in for a rich covariate profile when representing the target population.

The paper handles two settings. In Setting I, risk status D and therefore membership H are observed in the study, so W can be estimated within the analysis sample. In Setting II, D and H are unavailable, so W is computed from an externally reported model and transported to the analysis cohort. Setting II additionally assumes that the external model is transportable, meaning it represents the same conditional membership probability over the covariate support in the analysis population.

Identification rests on four assumptions. Three are standard for observational treatment effects: consistency, unconfoundedness given X and Z, and treatment positivity. The fourth is specific to this method. Treatment-effect sufficiency and risk-score validity require that, within levels of Z and W, observed high-risk status carries no additional information about the conditional treatment effect. The paper is careful about what this does not require: it does not need each potential outcome to be conditionally independent of H, only the treatment-effect contrast Y(1) minus Y(0).

How the estimator turns a doubly robust signal into a GATE

Estimation proceeds in three steps. First, the method fits outcome regressions for the treated and untreated and a treatment propensity, all using flexible learners with X, Z, and W as features. From these it builds a doubly robust orthogonal signal: the modeled treatment-effect difference plus a treated residual term weighted by the inverse propensity and minus an untreated residual term weighted by the inverse of one minus the propensity. At the true nuisance functions, the conditional mean of this signal given Z and W equals the treatment-effect surface.

Second, the treatment-effect surface is modeled as a linear combination of a prespecified basis in Z and W, with coefficients obtained as a best linear projection of the signal. The basis can include subgroup indicators and a series basis in W, so the surface can approximate nonlinearity. The paper requires either correct specification of the surface by this basis or, more generally, that the population projection preserves the risk-weighted target.

Third, the fitted surface is aggregated over the risk-weighted target distribution within each subgroup. This is the step that converts a low-dimensional treatment-effect surface into the high-risk GATE. The paper establishes pointwise asymptotic normality and an influence-function-based variance estimator, and it accounts for the fact that the membership score itself was estimated. In Setting II, where the score comes from a separate reference sample, the influence function has a two-sample form: one part from the analysis sample and one from the reference sample, with no cross-covariance term because the samples are independent.

Simulations show lower variance at comparable bias

The simulation study crossed two outcome types, continuous and binary, with two treatment-effect settings, linear and nonlinear in the membership score W, at sample sizes of 500 and 2,000, giving eight main scenarios. Each scenario used 500 replications. The truth was computed from an independent sample of one million draws from the same data-generating mechanism, averaging the individual conditional treatment effect among individuals with H = 1 and Z = z.

Across these scenarios, RSW had similar bias and lower variance than the two hard-targeting alternatives, labeled FS-HR and HR. The reported averages make the pattern concrete. In the binary-outcome Setting II table with a reference sample of size twice the analysis sample, at n = 500 with linear heterogeneity, average absolute bias was 0.004 for RSW, 0.009 for FS-HR, and 0.007 for HR, while average empirical standard deviations were 0.122, 0.184, and 0.234 respectively. At n = 2,000 in the same panel, average standard deviations fell to 0.057, 0.083, and 0.086.

The paper's discussion adds a condition that changes how much this gain matters. The precision advantage was largest when the observed high-risk-by-subgroup cells were small, and it decreased when almost the entire subgroup was high risk. That is consistent with the mechanism: soft targeting borrows information from people outside the realized high-risk group, and there is less to borrow when nearly everyone is already in it.

Violating treatment-effect sufficiency trades bias for variance

The key extra assumption is treatment-effect sufficiency, and the paper tests what happens when it fails. Sensitivity analyses showed that the variance gain persisted under violations, but RSW bias increased under strong violations. The discussion describes the result as a clear bias-variance trade-off: RSW remained the lowest-MSE estimator in the scenarios examined, while the hard-targeting estimators retained better bias and coverage under strong violations. The paper also notes the effect was modest in the binary-outcome scenarios considered.

This is the most decision-relevant boundary in the paper. A reader choosing between soft and hard targeting is not choosing between a biased and an unbiased method in general; they are choosing which error to prioritize in a specific setting. When high-risk cells are small and the sufficiency assumption is plausible, the variance reduction is the main story. When sufficiency is strongly violated, the hard-targeting estimators' better bias and coverage become the relevant comparison, even though RSW still had the lowest MSE in the scenarios examined.

The method also depends on accurate estimation of the membership probability W and, in Setting II, on its transportability. The paper states that misspecification may bias estimation of the high-risk GATE. This limitation sits directly on the weighting step, since every downstream estimate inherits whatever error the score carries.

An application to medication use and MCI-free time

The paper applies the method to the All of Us Research Program, estimating effects of non-GLP antidiabetic and antihypertensive medication use on mild cognitive impairment (MCI)-free time restricted at 48 months, within comorbidity-defined high-risk subgroups. The risk score was estimated in a nonoverlapping internal reference sample and then applied to the outcome-analysis sample, which the paper describes as emulating a genuine external sample and illustrates soft targeting in Setting II.

The authors are explicit about what this application can and cannot support. Medication use was measured only at baseline, without information on initiation or adherence, and the endpoint was the first recorded MCI diagnosis in the electronic health record rather than biological onset. Differences in enrollment timing or follow-up could affect risk-score transportability, although baseline high-risk prevalence was similar in both samples, which the paper says partially mitigates that risk. Flexible nuisance modeling and cross-fitting improve robustness to model specification but cannot address violations caused by unmeasured determinants of follow-up.

The paper frames the application as an illustration of how soft targeting can improve precision while retaining an interpretable high-risk target population, not as a definitive causal claim about these medications. The estimand is restricted to 48 months and to the comorbidity-defined high-risk subgroups, so the numbers do not transfer to other horizons or to populations defined by different risk criteria.

Where soft targeting earns its keep

The paper's own summary ranks three findings. RSW preserved small bias while improving precision relative to the two hard-targeting alternatives. The gain was largest when observed high-risk-by-subgroup cells were small and shrank when almost the whole subgroup was high risk. And violating treatment-effect sufficiency produced a bias-variance trade-off in which RSW kept the lowest MSE in the scenarios examined but hard targeting kept better bias and coverage under strong violations.

Read together, these point to a specific priority rather than a general endorsement. Soft targeting is most valuable when the target group is small enough that hard targeting is unstable, and when the analyst has reason to believe that, within levels of the subgroup and the membership score, high-risk status adds little information about the treatment effect. When that belief is weak and the high-risk cells are large enough to support hard targeting, the paper's evidence favors the hard-targeting estimators on bias and coverage.

The framework also extends beyond the low-dimensional subgroup setting studied here. The paper notes that replacing Z with a vector of treatment-effect modifiers and estimating the corresponding surface jointly with W yields conditional average treatment effects. That extension is stated as a natural direction, not as something the simulations or the All of Us application evaluated.

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