A counterfactual explanation answers a patient-level question: "what would have had to change for this model to call this patient low-risk?" In intensive care data, the most credible version of that answer restricts the suggested changes to ones that real patients have actually gone through between two time points. If a creatinine value has never fallen by that much in three hours, the explanation should not propose it. This restriction to observed transitions fixes the absurd outputs of plain distance-based methods, such as reversing a patient's age. It also creates a quieter problem. The "observed transitions" have to come from someone's history. If they come from the patient's own demographic subgroup, two things go wrong at once. Small subgroups supply too few trajectories to estimate what is plausible. Their recorded care pathways also carry the access gaps and undertreatment that the fairness literature documents.
We propose to treat the source of the plausibility constraint as the object of study and design. The core claim has two parts. First, history-constrained counterfactual explanations for a fixed longitudinal risk model fail unequally across demographic subgroups: they are less often valid and more often tied to lower-intensity care for groups with fewer than about 100 patients. Second, a constraint that pools strength across groups, but pools differently for physiological variables and for care-process variables, removes most of that disparity without bringing back implausible suggestions. Physiological variables get partial pooling, meaning each group's estimate is shrunk toward the whole-cohort estimate. Care-process variables are things like orders, medications and measurement frequency, and for these the constraint is set by clinically matched patients regardless of group. Because subgroup-level validity rates are themselves unstable at these sizes, the evaluation includes a small-sample significance test, so that a "disparity" is not just counting noise.
What exists and where this sits
The method we build on is Using Longitudinal Data for Plausible Counterfactual Explanations. It scores candidate counterfactuals by the median absolute deviation of historically observed feature changes, for example between hour 1 and hour 4 for acute respiratory failure in MIMIC-III. This drove immutable-feature changes to 0%, against 73–84% for proximity baselines. On MIMIC-III, 74% of standard counterfactuals proposed changes never seen in the data. The same paper is also our main constraint. Enforcing plausibility cut the number of patients with any valid counterfactual from 229 to 120, and the authors never asked who the 109 lost patients were. We take that loss, broken down by subgroup, as our first measurement.
Three lines of work motivate the fairness concern. Quantifying Health Inequalities Induced by Data and AI Models uses an allocation-versus-deterioration analysis to show that recorded ICU care already encodes inequality: women showed up to 33% poorer deterioration markers at admission in HiRID. It also shows that models can amplify this, in one case more than nine-fold. History is therefore a biased reference. MIMIC-IF audits temporal deep models on MIMIC-IV and finds that attributions differ by subgroup, but it does so on 43,005 stays and offers no mitigation. A Counterfactual Fair Model for Longitudinal Electronic Health Records via Deconfounder makes predictions invariant to sensitive attributes on large registries. Our question is different: we change the explanation of an unchanged model, not the model, and we work at subgroup sizes where its VAE-LSTM confounder estimate would not be stable.
The small-sample side supplies an evaluation tool. Algorithmic Accountability in Small Data shows that subgroup metrics are jagged and sometimes undefined below roughly n = 100. It provides the MATCH test, which checks whether a group disparity exceeds sample-size noise, and Cross-Prior Smoothing, which shrinks small-group metrics toward a large reference group. That paper notes that smoothing toward a biased reference spreads the bias. This is exactly our setting, so we use MATCH as the primary test and report Cross-Prior Smoothing only as a secondary view. Fairness without Demographics on Electronic Health Records is a relevant negative result. Its gradient-graph reweighting fails when gradients are noisy at small n, which argues against learned adversarial fixes in this regime and toward simple statistical pooling.
Research Program
The work holds one longitudinal risk model fixed and varies only how plausible transitions are defined. The model is an LSTM or IMV-LSTM, the architecture family MIMIC-IF reports as strongest on MIMIC-IV mortality. We then ask, per subgroup, whether each patient gets a valid counterfactual and what it recommends.
The first step is an audit. We replicate the hour-1-to-hour-4 acute respiratory failure setup of the longitudinal counterfactual paper on MIMIC-III and extend it to MIMIC-IV. We stratify by ethnicity, sex, insurance and age band, and compute subgroup-specific plausibility constraints. To control subgroup size directly, we subsample each minority group's reference trajectories to n in {25, 50, 100, 200}, keeping the full majority group. This turns "small subgroup" into a manipulated variable rather than an accident of the dataset.
The second step is the proposed constraint. Each feature is tagged, by a clinician-reviewed rule, as physiological (vitals, labs) or care-process (orders, drugs, measurement frequency, ventilation settings). For physiological features, the per-group transition scale for feature $j$ is modeled as a group deviation around a cohort-wide value, with between-group spread $\tau_j$ estimated from the data. Large $\tau_j$ means real group differences, such as sex differences in creatinine, which are kept. Small $\tau_j$ means groups are shrunk toward the pooled estimate. For care-process features, plausibility is judged against patients matched on physiological state at hour 1, ignoring group membership. A recommendation such as "earlier escalation" then counts as plausible if clinically similar patients received it, even if this patient's group rarely did. This split is the key ingredient: it pools physiology because small groups cannot estimate it alone, and it decouples care from group because that is where historical access bias lives.
The third step is evaluation. Per subgroup we measure five things. Validity is the share of patients with a counterfactual that flips the prediction. Immutable-change rate is the share of counterfactuals that alter fixed traits. Held-out plausibility is the share of proposed physiological deltas that fall inside the range actually realized by held-out patients of the same group over the same window. Care lock-in is the share of recommended care-process values below the median intensity given to physiologically matched patients in the best-represented group. Sparsity is the number of features changed. Subgroup differences in each metric are tested with MATCH, with bootstrap intervals reported alongside.
Baselines
The naive reference is the unconstrained proximity counterfactual: the nearest point under L1 distance that flips the fixed model's prediction. This is the comparison point in Using Longitudinal Data for Plausible Counterfactual Explanations. It should show near-complete validity and high immutable-change rates. For it, the paper reports 73–84% immutable changes on Adult-Income and 74% never-seen changes on MIMIC-III.
The strongest existing method is that paper's longitudinal MAD constraint, run in two forms. One is its original form, a single cohort-wide history. The other is a stratified form with a per-subgroup history, which is the natural "fairness-aware" adaptation and the one we expect to fail at small n. Its reported strength is 0% immutable changes, with validity of 120 out of 229 MIMIC-III patients. We found no reported subgroup-level validity or lock-in figures on Lacuna for this method. Beating it means two things. First, the MATCH test must show no significant subgroup validity gap at n = 50 where the stratified version shows one. Second, immutable changes must stay at 0% and held-out plausibility must stay within a small margin of the stratified version.
All methods run on the same genetic-algorithm search with the same population size, number of generations and candidate budget per patient. They share the same fixed risk model, the same train/test patient split, and the same feature-tagging rule. Hyperparameters such as the plausibility threshold get an equal tuning budget, chosen on a validation split to match overall validity across methods. Differences then show up in who gets valid recourse rather than in how many.
Two ablations isolate the ingredient. One applies partial pooling to every feature, with no physiological/care split. The other applies the split but uses unpooled per-group physiology. If either ablation matches the full method, the extra machinery is not needed.
Why not just…?
Why not just use the whole-cohort history and ignore subgroups? This is the real threat, because the original method already does this and pooling solves the small-n problem for free. Our expectation is that full pooling has a different flaw: physiological transitions that are normal for the majority may be implausible for a group with different baselines. That would show up as lower held-out plausibility on the minority group's own realized trajectories, and a small $\tau_j$ is exactly the case where full pooling is fine. The experiment settles this directly. If whole-cohort history matches our method on held-out plausibility for every subgroup, the conclusion is that the physiological pooling is unnecessary. The contribution would then reduce to the audit and the care-process decoupling, and we would report it that way.
Why not just bootstrap the subgroup validity rates instead of using MATCH? Bootstrap intervals are cheap and familiar. But Algorithmic Accountability in Small Data shows that below about 100 samples, metric distributions are discrete and have holes, which makes resampling intervals unreliable. We report both, and we use simulations with known zero disparity at n = 25 and n = 50 to measure each test's false-positive rate.
Why not just debias the risk model and leave explanations alone? A counterfactually fair model such as the deconfounder approach changes the model's predictions. The recourse constraint, however, still reads biased histories, so lock-in can persist even under a fair predictor. We test this by rerunning the stratified-history baseline on top of a reweighted model trained with group-inverse-frequency weights. If lock-in falls to parity there, the explanation-side fix is redundant.
Proposed Experiments
The main experiment crosses five methods with four minority reference sizes, on MIMIC-III acute respiratory failure and MIMIC-IV in-hospital mortality. The five methods are proximity, cohort-wide MAD, stratified MAD, the two ablations, and the full method. Subgroups are ethnicity, sex and insurance. Each cell is repeated over 20 resamples of the minority reference set, so that the effect of reference size is estimated rather than inferred from one draw.
A transfer check applies constraints estimated on MIMIC-IV to HiRID, where sex-linked deterioration differences are documented by the allocation-deterioration study. This tests whether care-process decoupling reduces lock-in for women under shifted documentation practices.
A small clinician review rates counterfactuals from each method for physiological plausibility and actionability, with the method blinded. It covers 60 counterfactuals per method, stratified by subgroup, with two intensivists. This checks whether the held-out plausibility metric agrees with clinical judgment.
The decisive result has three parts. Stratified history must show a MATCH-significant validity or lock-in gap at n ≤ 50 that disappears at n ≥ 200. The full method must close that gap at small n while keeping 0% immutable changes. The method must also beat whole-cohort pooling on held-out minority plausibility. If the first part fails, the motivating problem is not real at these sizes. If the third part fails, the simpler pooled constraint is the recommendation, and we would say so.
References
- Using Longitudinal Data for Plausible Counterfactual Explanations
- Quantifying Health Inequalities Induced by Data and AI Models
- MIMIC-IF: Interpretability and Fairness Evaluation of Deep Learning Models on MIMIC-IV Dataset
- A Counterfactual Fair Model for Longitudinal Electronic Health Records via Deconfounder
- Algorithmic Accountability in Small Data: Sample-Size-Induced Bias Within Classification Metrics
- Fairness without Demographics on Electronic Health Records