Hospitals now screen patients with short questionnaires about unmet social needs such as housing, food, and transportation. Machine learning models then use the answers to predict outcomes like uncontrolled hypertension, often training a separate model for each racial group. These models report striking differences between groups. Structural barriers appear to drive risk for Black patients, while personal factors appear to drive it for White patients. The difficulty is that a questionnaire answer is a disclosure, not a measurement. If one group under-reports food insecurity more than another, out of stigma, distrust, or a different sense of what is "worth mentioning," then a group-specific model will learn that food insecurity matters less for that group. It will learn this even when the true biology and social mechanics are identical. Two different stories, different need and different willingness to disclose, can produce the same pattern of feature importances.
This note proposes to tell those stories apart. Each patient's true social-need status is treated as a hidden variable. We observe it through several imperfect channels whose errors arise from different sources: the patient's own survey answer; social-need mentions extracted by a language model from clinical notes; passive administrative traces such as repeated address changes, shelter addresses, or missed appointments; and neighborhood deprivation indices. Under standard conditions from the diagnostic-test literature, the probability that each channel reports a need that truly exists can be estimated separately for each subgroup. With those estimates, we can fit subgroup-specific outcome models on the corrected social-need variable instead of the raw answer. We then ask which of the published "divergent risk fingerprints" survive the correction.
Core Claim
Our central claim is that between-group differences in the learned weight of self-reported social determinants of health (SDoH) are confounded by differences in reporting sensitivity between groups, and that this confounding can be estimated and removed when at least two non-survey indicators of the same need are available. The claim is falsifiable in both directions. If the corrected subgroup models keep the divergence that Hu et al. reported, with food, transport, and housing dominant for Black patients and personal factors for White patients, that strengthens their etiological reading. If the divergence shrinks, part of what has been read as differential etiology is differential disclosure. That distinction matters for any intervention designed from those fingerprints.
The core mechanism comes from self-report bias. Subgroup-specific modeling is the application regime whose conclusions are at stake. The SDoH-capture literature supplies the extra indicators that make the correction identifiable.
What Prior Work Establishes and Leaves Open
Several studies supply the evidence that motivates the problem. Hu et al. trained race-specific XGBoost, random forest, and logistic models on 164,041 Boston Medical Center patients. Their 40 non-clinical features included the eight-domain THRIVE social-needs survey. They found divergent top predictors by race and then tuned group thresholds to equalize false negative rates. They treat survey answers as ground truth, and that assumption is what we test. The self-report literature shows that stigmatized behaviors are systematically under-reported (Yue et al.) and that current states distort recall (Vernon et al.). None of these studies estimates how such distortion varies across the demographic groups that subgroup models split on. Negriff et al. found a social feature whose predictive sign inverts across groups. That is a reminder that real divergence exists, so the goal is to measure divergence correctly, not to remove it.
Other studies constrain the design. Guevara et al. showed that fine-tuned Flan-T5 extraction from notes identified 93.8% of patients with adverse SDoH, against 2.0% for diagnostic codes. That makes notes a viable second channel. However, notes record what patients told clinicians, so their errors are not independent of survey errors. Their extractor also showed a 10–14% demographic discrepancy rate under demographic injection, which means the channel's own error differs by group. MIMIC-SBDH found that an extractor with 0.96 F1 still failed 44.5% of negation tests and 70.9% of attribution tests. Extraction errors must therefore be modeled, not assumed away. Yang et al. and Tang et al. show that zip-level indices improve calibration but mask individual heterogeneity. We therefore use them only as a prior on prevalence, never as an indicator of the individual's need.
Two lines of work supply methods. Ustun et al. give decoupled classifiers with "rationality" and "envy-freeness" guarantees, verified by held-out hypothesis tests. Rationality means each group prefers its own model to a pooled one; envy-freeness means each group prefers its own model to any other group's. We reuse their preference checks. Their method assumes clean features; ours does not. Shang et al. reweight SDoH edges in a knowledge graph to make predictions invariant to SDoH subgroup. We take the opposite stance: we allow group-specific weights but correct the measurement underneath them.
Research Program
For each patient $i$ in group $g$ and social-need domain, let $Z_i \in \{0,1\}$ be the true unmet-need status. We observe indicators $S_i$ (survey), $N_i$ (note extraction), and $A_i$ (administrative trace). Each indicator $k$ has group-specific sensitivity and specificity:
$$P(X^k_i = 1 \mid Z_i = 1, g) = \mathrm{se}_{k,g}, \qquad P(X^k_i = 0 \mid Z_i = 0, g) = \mathrm{sp}_{k,g}.$$
The prevalence $\pi_{g,r} = P(Z=1 \mid g, \text{region } r)$ is allowed to vary with neighborhood deprivation. With three indicators that are conditionally independent given $Z$, a latent class model is identified within each group. With two indicators, identification follows the classic two-tests, two-populations argument: two imperfect tests applied in populations with different prevalence pin down both prevalence and test accuracy. Here, deprivation strata play the role of the populations.
The quantity of interest is the disclosure gap $\mathrm{se}_{S,\text{Black}} - \mathrm{se}_{S,\text{White}}$, together with its counterparts for other groups. Survey and note indicators share the patient as a common source, so we add a pairwise dependence term between $S$ and $N$. We bound its effect with a sensitivity analysis rather than assuming it is zero. The administrative channel, which is built from address-history churn, shelter or care-facility addresses, transportation-assistance records, and appointment no-show patterns, does not pass through patient disclosure. It is the anchor that keeps the model honest.
The outcome model is then fit jointly. A subgroup-specific predictor uses the posterior $P(Z_i=1 \mid S_i, N_i, A_i, g)$, or multiple imputations of $Z_i$, in place of $S_i$. This propagates measurement uncertainty into the coefficients and the predicted risks. Decoupling across groups follows the recursive split-and-test logic of Ustun et al., with their preference tests run on held-out data. The deliverables are corrected subgroup feature-importance profiles with uncertainty, estimated disclosure gaps for each domain and group, and a test of whether rationality and envy-freeness still hold once features are corrected.
Baselines
The naive reference is a single pooled gradient-boosted model on raw survey answers, demographics, and clinical covariates, with one 0.5 threshold. This is the "do nothing" option. Hu et al. report that a model of this kind yields a false positive rate of 27.71% for Black and 5.92% for White patients, and a false negative rate of 43.11% versus 73.82%.
The strongest existing method on this question is the race-specific pipeline of Hu et al.. It uses separate XGBoost models per group on raw THRIVE answers, with thresholds tuned to equalize false negative rates at 25%. They report AUC 74.49% for XGBoost and 73.42% for logistic regression, with thresholds of 0.296 for Black and 0.245 for White patients. We will re-implement it on the same splits, features, and hyperparameter search budget as our method. Our model differs only in replacing the survey features with their corrected posteriors. Beating it means two things. First, held-out AUC must be within noise or better, and subgroup calibration error must be lower at matched false negative rates. Second, and more importantly, in the semi-synthetic setting described below, the error in recovered group-specific coefficients must be smaller than the coefficient error of the raw-feature model.
The decoupled-classifier baseline uses the tree-based method of Ustun et al. on raw features. Its strongest reported result is a 30.8% maximum accuracy gain for some groups on an apnea dataset. Running it on social-need features tells us whether clean-feature decoupling already satisfies preference guarantees, and whether those guarantees survive once measurement is corrected.
We also include a calibration-focused baseline: the same models with zip-level indices added, following Yang et al., who report in-hospital-mortality calibration error falling from 0.11 to 0.03.
Three ablations isolate the key ingredient. The first estimates sensitivities shared across groups instead of group-specific ones; it tests whether the subgroup-varying part matters. The second drops the administrative channel; it tests whether the non-disclosure anchor matters. The third removes the survey–note dependence term.
Why not just…?
Why not just combine survey and notes with an "any positive" rule? Treating a patient as in need if either the survey or the note says so recovers some under-disclosed cases. For pure prediction AUC it could plausibly match our method. This is a real threat, and we include it as a baseline. Its weakness lies in attribution. The OR rule raises sensitivity while lowering specificity, and it does both by different amounts per group, because note-extraction error itself differs by demographic group (Guevara et al.). It therefore substitutes one differential error for another. The semi-synthetic experiment settles the question: if the OR rule recovers the planted group coefficients as well as the latent model does, we will say so and recommend it.
Why not just a pooled model with race-by-SDoH interaction terms? Interactions let the weight of a feature differ by group, but they estimate exactly the confounded quantity, effect multiplied by reporting sensitivity. They therefore inherit the same ambiguity as separate models. They also average inverted signs toward zero when the interaction is mis-specified, the failure mode Negriff et al. warns about. We run this baseline, and the same coefficient-recovery test applies.
Why not just use neighborhood deprivation indices instead of surveys? They are free of patient disclosure, but they are not individual measurements. Tang et al. show large heterogeneity within groups across deprivation levels, and Yang et al. find them accuracy-neutral for discrimination. We use them only to shift prevalence, which is the role they can support. The ablation that replaces all individual indicators with zip-level indices shows the cost.
Why not just apply noise-robust training from the label-noise literature? Those methods correct noise in the outcome, not misclassification in input features that differs by group. They also produce no estimate of the disclosure gap, which is itself a scientific output here.
Proposed Experiments
The first experiment is semi-synthetic, because only there is the truth known. We take MIMIC-IV-SDOH (Yang et al.) and use MIMIC-SBDH (MIMIC-SBDH) annotations as stand-ins for true need. We generate outcomes with known group-specific coefficients, some equal across groups and some inverted. We then inject survey-like indicators with planted group-specific sensitivities, spanning gaps from zero to large, and a controlled survey–note dependence. Metrics are coefficient recovery error, accuracy of the estimated disclosure gap, subgroup calibration error, and the frequency of false "divergent fingerprint" findings when true effects are equal. The decisive check is that raw-feature subgroup models report spurious divergence at a rate that grows with the planted gap, while the corrected models stay near nominal. If the corrected models do not, the method fails.
The second experiment uses real data from a screening site with THRIVE-style surveys, notes, and address-history records, reproducing the Hu et al. cohort design. We estimate disclosure gaps for each domain and refit their race-specific models. The decisive check is whether the reported Black/White divergence in structural-barrier importance holds up. We report the corrected importance difference with intervals and test the preference guarantees of Ustun et al. on held-out patients. We also run a replication in All of Us, which the file describes as pairing EHR, community linkage, and passive wearable data. Using participant-reported social-need answers where available, it extends the analysis beyond two racial groups. Intersectional strata are flagged with the Maximum Subgroup Discrepancy (MSD) search of Nemecek et al., which finds the conjunction of attributes with the largest disparity.
The main identification risk is that administrative traces themselves depend on group-linked factors such as housing-registry practices. We handle it in two ways. First, we report results under a grid of assumed dependence strengths. Second, we check for consistent conclusions across two anchor sets, address-based and appointment-based.
The predictive ceiling we compare against throughout is Hu et al.'s reported AUC of 74.49%. For readmission on the Multimodal Clinical Benchmark for Emergency Care (MC-BEC), no reported result was found on Lacuna, so we will not claim a comparison there.
References
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