Do Subgroup Risk Factors Survive Chain-Referral Sampling?

Health researchers who study hidden populations, such as people who inject drugs, undocumented migrants, or youth outside formal institutions, cannot draw random samples because no list of these people exists. They therefore recruit through social networks. A few initial participants refer peers, those peers refer their own peers, and so on, a design called respondent-driven sampling (RDS). The same studies increasingly report that risk factors differ between subgroups, and sometimes reverse direction. Parental closeness protects community adolescents against marijuana use but predicts higher use among child-welfare adolescents (Negriff et al.). In another study, food and housing insecurity drive hypertension risk for Black patients, while marital status drives it for White patients (Hu et al.). This proposal asks whether such subgroup-specific findings can be trusted when the sample was assembled by peer referral. The difficulty is that the health outcome and social circumstances shape each other, and both of them also shape who knows whom.

The core worry is a loop that no existing method closes. Drug use builds drug-using friendships. Friendships determine how many people a participant knows (their "degree"), and degree determines who gets recruited. Standard RDS corrections reweight people by inverse degree. When degree is partly a consequence of the outcome, and housing loss both follows from and feeds the outcome, two things can go wrong. A model fit to the recruited sample can manufacture or erase subgroup sign reversals. It can also be falsely certified as better than a pooled model, because recruits in the same referral chain are not independent. We propose to measure this failure on real social networks where the full population is known. We then build a fix with two parts: recruitment-model weights whose blocks are defined jointly by subgroup and outcome, and a chain-aware test for when separate subgroup models are actually warranted.

Core Claim

We make two claims. The first is that on chain-referral samples, inverse-degree weighting recovers population prevalence reasonably well but recovers subgroup-specific associations poorly, and the error grows with the strength of the feedback from outcome to network ties. The second is that the standard procedure for deciding whether to give each subgroup its own model over-certifies those separate models under RDS. That procedure is a McNemar test on held-out individuals in the decoupled classifiers of Ustun et al.. It over-certifies because splitting by individual leaks within-chain correlation and overstates the effective sample size.

Both claims are falsifiable through one control. When the simulated outcome does not affect tie formation, our method should offer no advantage over simple degree-weighted regression. If it still does, our explanation is wrong. If the advantage does not grow with feedback strength, the mechanism we propose is not the one at work.

Where This Sits

Three lines of prior work motivate the question without answering it. Negriff et al. and Hu et al. find subgroup-divergent or sign-inverted risk factors. Both treat these as static one-way associations, and both use fixed cohorts or hospital records rather than network-recruited samples. Hospital records miss exactly the people who avoid institutions out of fear of stigma or legal exposure (Jovanović et al.; vaccine equity review). Understanding challenges to the interpretation of disaggregated evaluations warns that subgroup comparisons mislead when the sample does not represent each group, which is the situation in every RDS study.

The RDS literature supplies our methods but targets a different estimand. Fox et al. show that block-structured network models, in the form of feasible generalized least squares on a degree-corrected stochastic blockmodel, can be learned from referral chains and beat inverse-degree weighting for estimating a mean. Work on seed bias (asymptotic seed bias; block transition probabilities) shows that clustered networks keep samples tied to the initial recruits. Indirect inference (Hidden Population Estimation) uses auxiliary covariates such as treatment status, but only to refine headcounts and graph structure. None of these papers fits a model of how outcomes relate to covariates within subgroups.

Model-Based Inference for Interference Using Partial Network Data is the closest work methodologically. It averages over unobserved edges with a random-graph model to estimate treatment effects from partial network data, including RDS-style data. We borrow its strategy of integrating over a fitted blockmodel. Unlike that paper, we target subgroup-specific outcome models rather than a global treatment effect, and we let node outcomes cause edges rather than only flow along them.

From the decoupling literature we take the notion of rationality from Ustun et al.: a group should get its own model only if it prefers that model over the pooled one. We also accept their negative result, which constrains our design. Decoupling hurts small groups unless the data support it, and RDS subgroups are small.

Research Program

Testbed. The first component is a semi-synthetic testbed built on the Add Health and Colorado Springs Project 90 networks. These are the same real networks Fox et al. used for RDS simulation, and their full structure is known. On each network we assign node covariates and a two-period structural model. Social conditions at period one affect the outcome at period two, and the outcome at period one affects social conditions and the formation of new ties at period two. Subgroup-specific coefficients include planted sign reversals modeled on the Negriff finding.

Three knobs vary across settings: the strength of feedback from outcome to ties, homophily on the outcome, and referral intensity. Referral intensity matters because Fox et al. show that inverse-degree weighting breaks down above a critical referral rate. We then simulate RDS with coupon limits and seeds on the period-two network. Because the whole population is generated, the population-level subgroup coefficients and the population-optimal choice between pooled and separate models are known exactly.

Estimator. The second component is the estimator. We fit a recruitment model in which blocks are cells of subgroup crossed with outcome status, not subgroup alone, and estimate each participant's inclusion probability $\hat\pi_i$ by integrating over the fitted blockmodel. This follows the iterated-expectation approach of the partial-network paper and the block-transition idea from the seed-bias work. The subgroup model $f_g$ for subgroup $g$, either pooled or separate, minimizes

$$\sum_{i \in S} \frac{\ell\big(f_{g(i)}(x_i), y_i\big)}{\hat\pi_i},$$

where $S$ is the recruited sample, $x_i$ are participant $i$'s covariates measured before the outcome, $y_i$ is the outcome, and $\ell$ is the prediction loss. Restricting $x_i$ to pre-outcome covariates and fitting the reverse direction, from the outcome to later social conditions, as a second weighted model lets us report, for each subgroup, which way the loop runs. Field use therefore requires an RDS design with one follow-up visit. Web-based RDS deployments show such designs are feasible (Sweden; Vietnam).

Decision procedure. The third component decides whether a subgroup gets its own model. We keep the rationality criterion from Ustun et al. but replace individual-level holdouts with holdouts made of whole referral trees, and replace the McNemar test with a weighted bootstrap over trees. A subgroup receives its own model only if it beats the pooled model on held-out trees after weighting.

Field application. Finally, we apply all estimators to the Kohtla-Järve data on people who inject drugs (Hidden Population Estimation), using its auxiliary health covariates. This has no ground truth. It serves as a field check of whether substantive subgroup conclusions change across weighting schemes.

Baselines

The naive reference fits pooled and per-subgroup logistic models directly to the recruited sample with no weights. This is what much applied RDS work does, and every other method must beat it on bias of subgroup coefficients against the population truth.

The strongest simple competitor is a single pooled model with subgroup-by-covariate interaction terms, weighted by the Volz-Heckathorn inverse-degree estimator described in the RDS overview. It is cheap, standard, and can in principle represent sign reversals through its interaction terms, so it is the real threat. Its per-subgroup variant, which fits separate models with the same weights, is run alongside.

For the decision question, the strongest existing method is TREE01-style decoupling from Ustun et al., with McNemar pruning on individual-level holdouts. Their reported figure is a maximum 30.8% accuracy gain on the apnea dataset without preference violations. That figure comes from independent, non-network data and is not directly comparable. We found no reported result on Lacuna for recovering subgroup coefficients or preference decisions under RDS.

For prevalence, the reference point is Fox et al.'s result that feasible generalized least squares with 500 recruits beats inverse-degree weighting with 1,000 in root mean squared error. We include their estimator for subgroup means as a sanity check. An oracle model fit to the full network population gives the ceiling.

All methods see the same simulated samples, the same covariates, the same model class (regularized logistic regression, plus gradient-boosted trees as a check), and the same tuning budget. Tuning uses tree-level cross-validation for every method, so that only the weighting and the decision rule differ.

Beating the competitors means two things in settings with moderate or strong outcome-to-tie feedback. Our estimator must cut subgroup-coefficient bias and sign-error rate relative to inverse-degree-weighted interactions, with confidence-interval coverage near nominal. Our decision rule must produce fewer population-level rationality violations than individual-level McNemar pruning.

Two ablations isolate the key ingredients. The first uses blocks defined by subgroup only, without outcome status, which tests whether outcome-defined blocks matter. The second applies our weights but individual-level splits, which tests whether chain-aware holdouts matter.

Why not just…?

Why not just fit a degree-weighted pooled model with interaction terms? This is a genuine threat, and the experiment is designed to settle it. The prior evidence against it concerns prevalence, not associations. Fox et al. show that inverse-degree weighting loses its usual $1/n$ variance decay above a critical referral rate, and the seed-bias papers show persistent bias under clustering. Neither speaks directly to subgroup coefficients. We predict the interaction model matches ours when the outcome does not shape ties and degrades as that feedback grows, because degree then carries outcome information that inverse-degree weights handle incorrectly. If it matches ours across all feedback levels, we will report that the simple method suffices and narrow our contribution to the chain-aware decision test.

Why not just extract social determinants from hospital records with NLP? Hospital records omit the people who avoid institutions, and extraction is itself unreliable. On MIMIC-SBDH, Bio-ClinicalBERT reaches 0.96 F1 on Community-Present yet fails 44.5% of negation tests and 70.9% of Education attribution tests. That pipeline cannot reach the populations studied here, so it is not a competitor on this question.

Why not just use instrumental variables or a standard cross-lagged panel to handle the two-way causation? Both address the causal direction but assume the sample is representative. In an RDS study, the sampling depends on the very outcome under study, so a correctly specified cross-lagged model fit to the raw sample is still biased. The unweighted two-direction model in our experiments makes this testable. Valid instruments for social conditions are also rarely available, as Section 1.1 of the research file notes.

Why not just recruit more people? Larger samples reduce variance but not the bias from outcome-dependent recruitment or seed dependence. Our simulations vary sample size from 300 to 2,000 to show whether that bias persists as samples grow.

Decisive Checks

Three results would establish the claim. First, the gap between our estimator and inverse-degree-weighted interactions must be near zero at zero outcome-to-tie feedback and grow monotonically with it. Second, removing outcome status from the block definition must remove most of that gain. Third, individual-level McNemar pruning must certify separate subgroup models that the full population rejects at a measurably higher rate than tree-level testing does. This effect should be largest in the small, high-referral subgroups where Ustun et al. already warn decoupling is fragile.

On the Kohtla-Järve data, a meaningful contribution would be a subgroup association that changes sign or loses support between inverse-degree and outcome-block weighting. That would show the simulation failure mode appears in practice. If no conclusion changes, the field risk is smaller than the simulations suggest, and we would report that.