AI-driven clinical systems increasingly support high-risk decisions such as readmission prediction, diagnosis, and treatment prioritization [1,2]. However, substantial evidence shows that these systems can perform unevenly across groups defined by race, sex, socioeconomic status, age, or insurance status [3-9]. Such disparities raise concerns about safety, fairness, and regulatory accountability, particularly under emerging requirements for transparent governance of high-risk AI systems [10-12].

Bias in clinical AI is rarely produced by one mechanism alone. Historical health care data can reflect unequal access to care, differential documentation, changing coding practices, missingness patterns, and proxy variables that encode social disadvantage [4,5,8,9]. Representational imbalance can amplify proxy relationships, temporal drift can change subgroup prevalence, and data integrity anomalies can distort both model fitting and fairness estimates. These interactions motivate a coordinated data-centric framework rather than a single downstream fairness constraint.

This study specifies a multistage audit framework and reports a fresh reproducibility reconstruction of the components that could be implemented from the available public data. The empirical comparison focuses on representation weighting and missingness-aware modeling. Proxy residualization and temporal-shift correction are retained as prespecified framework components but are not claimed as executed in the fresh run because final thresholds and encounter-year or site variables were unavailable. The Centers for Medicare and Medicaid Services (CMS) SynPUF is evaluated as a separate, compatible readmission task, while the National Health and Nutrition Examination Survey (NHANES) is used only for stage-level auditing.

The framework complements, rather than replaces, established approaches. Reweighting addresses representation imbalance, adversarial debiasing and fairness constraints act primarily during model fitting, causal fairness methods formalize assumptions about pathways and interventions, model cards and datasheets support transparent reporting, and TRIPOD+AI (Transparent Reporting of a Multivariable Prediction Model for Individual Prognosis or Diagnosis Plus Artificial Intelligence) and trustworthy-AI guidance specify reporting and governance expectations. The present contribution is a data-centric orchestration layer that links these concerns through sequential, source-aware preprocessing and evaluation.

The main contributions are as follows:

Table 1 summarizes the research gaps addressed by the proposed framework and maps them to the corresponding “Methods” section used in this study.

We apply poststratification weighting w(a) = P_target(a)/P_obs(a) [14-16]. Before weighting, the target distribution is audited for geographic, temporal, and coverage mismatch. If a reference source is misaligned with the study population, the target distribution is blended with internal empirical priors, and uncertainty is evaluated in sensitivity analysis. Weights are clipped at the 95th percentile unless otherwise selected in nested cross-validation (Textbox 2).

The prespecified framework proposed mutual-information and correlation screening for proxy concepts. The new reconstruction did not implement these thresholds because the final prespecified values were unavailable. Accordingly, no empirical claim about proxy residualization is made. Instead, income_proxy and n_prior_visits were examined in stratified sensitivity analyses, as reported in the reproducibility package (Textbox 3).

The fresh predictive pipeline used median imputation for numeric variables, most-frequent imputation for categorical variables, training-only one-hot encoding with unknown categories ignored, and random forest classification. All preprocessing was fitted within the training split. Claims concerning k-nearest neighbors imputation, ridge or spline nuisance models, generalized additive models, or random forest residualization were removed because those procedures were not executed in the fresh run.

Race was used for auditing and poststratification weighting and was excluded from the predictive feature vector. Sex and age group were used for secondary subgroup audits. Admission type remained a contextual predictor. income_proxy and n_prior_visits were retained for sensitivity stratification; neither was claimed to have undergone residualization in the fresh reconstruction.

The operational integrity screen flagged records when missingness was at least 25% or n_prior_visits exceeded the 99th percentile (Textbox 4). Bounded laboratory variables such as glycated hemoglobin were assessed using missingness and distributional checks rather than the Benford Law. The complete concept-level missingness report is provided in Table S2 in Multimedia Appendix 1.

The exploratory mixture of experts (MoEs) used M2 as the main expert and M3 as the missingness-aware quality expert (Textbox 5). The rule gate selected M3 for integrity-flagged records and M2 otherwise; it did not use demographic labels, a learned softmax gate, or test labels.

Textbox 6 summarizes the fixed rule-gated exploratory inference procedure. This exploratory rule-gated analysis was evaluated separately from the primary M2-M3 comparison. It was included to test whether routing the 203 (1.00%) flagged test records improved outcomes. Bootstrap contrasts compared the rule-gated MoE with M3. Because the gate and experts differed in more than one component, the analysis cannot isolate a pure architecture effect.

The exploratory gate retained every record but did not outperform M3 on fairness, Brier score, or macro F1. It should therefore be interpreted as a negative sensitivity analysis rather than evidence supporting subgroup-specific clinical models.

Temporal-shift mitigation was not empirically evaluated in the new Diabetes reconstruction because encounter year and site were unavailable. CMS calendar information was used only descriptively. The temporal procedure remains a prespecified framework component requiring a dataset with reliable event time and site identifiers (Textbox 7).

The Diabetes 130-US Hospitals dataset contained 101,766 encounters. A patient-level 80/20 split yielded 81,563 training encounters and 20,203 test encounters from 14,304 test patients; the test set contained 2254 (11.16%) thirty-day readmissions. The split prevented repeated-patient leakage. Race was the primary fairness attribute, with sex and age group used for secondary subgroup reporting.

Two primary random forest configurations were evaluated in the fresh run: M2 used the source-specific predictors with median or mode imputation, whereas M3 added missingness-count or rate indicators, column-level missingness masks where applicable, and poststratification sample weights. Both used 200 trees, max_depth=12, min_samples_leaf=10, class_weight=balanced_subsample, and seed 20250117. Earlier manuscript-only baselines without reproducible predictions were removed from the empirical comparison.

CMS SynPUF was analyzed as a separate claims-based readmission task, not as zero-shot transport of the Diabetes model. NHANES was used only for stage-level concept-coverage, missingness, proxy, and bounded-laboratory audits.

CMS inpatient claims were grouped by beneficiary and ordered by discharge and subsequent admission dates. A readmission was defined as the next inpatient episode beginning 1 to 30 days after index discharge; same-day, overlapping, and contiguous claims were collapsed. Episodes without 30-day observable follow-up and records with invalid chronology were excluded. Predictors were restricted to information available by index discharge. The resulting analysis contained 63,996 eligible episodes from 37,702 beneficiaries; the test set contained 12,801 episodes from 7541 beneficiaries, including 1232 (9.62%) readmissions.

The fresh analysis used Python 3.10.9, NumPy 2.2.6, pandas 2.3.3, SciPy 1.15.3, and scikit-learn 1.7.2. The master seed was 20250117. The local reproducibility package contains record-level predictions, overall and subgroup metrics, calibration outputs, bootstrap intervals, split counts, missingness tables, sensitivity analyses, scripts, and SHA-256 checksums. No external repository URL or DOI is claimed until an archival deposit is completed.

The computational environment, reproducibility settings, and model hyperparameters are summarized in Table 3.

Overall 95% CIs were estimated using 500 bootstrap replicates stratified jointly by outcome and race; subgroup intervals used 300 outcome-stratified replicates. Metrics included AUC, macro F1, Brier score, sensitivity, specificity, positive predictive value, negative predictive value, DPD, EOR, calibration intercept, calibration slope, and expected calibration error. At the prespecified probability threshold of 0.50, the EOR was calculated across race groups as EOR = min_g(TPR_g)/max_g(TPR_g), where TPR_g is the group-specific true-positive rate; values closer to 1 indicate greater true-positive-rate parity. Equalized-odds difference was calculated separately as max[max_g(TPR_g) – min_g(TPR_g), max_g(FPR_g) – min_g(FPR_g)]. A group was omitted from a component only when it had no observations in the corresponding true-outcome class. Because ratios can be unstable when small groups contain few positive outcomes, EOR was interpreted with subgroup counts, CIs, calibration, and equalized-odds difference. DPD was the primary fairness end point; EOR and subgroup analyses were secondary. No multiplicity-adjusted confirmatory inference was performed.

Overall were estimated using 500 bootstrap replicates stratified jointly by outcome and race; subgroup intervals used 300 outcome-stratified replic Metrics included AUC, macro F1, Brier score, sensitivity, specificity, positive predictive value, negative predictive value, DPD, EOR, calibration intercept, calibration slope, and expected calibration error. At the prespecified probability threshold of 0.50, the EOR was calculated across race groups as EOR = min_g(TPR_g)/max_g(TPR_g), where TPR_g is the group-specific true-positive rate; values closer to 1 indicate greater true-positive-rate parity[17]. Equalized-odds difference was calculated separately as max[max_g(TPR_g) – min_g(TPR_g), max_g(FPR_g) – min_g(FPR_g)]. A group was omitted from a component only when it had no observations in the corresponding true-outcome class. Because ratios can be unstable when small groups contain few positive outcomes, EOR was interpreted with subgroup counts, CIs, calibration, and equalized-odds difference. DPD was the primary fairness end point; EOR and subgroup analyses were secondary. No multiplicity-adjusted confirmatory inference was performed.

This study used only deidentified, publicly available datasets: Diabetes 130-US Hospitals [18,19], NHANES [20], and CMS SynPUF [21]. No primary data involving human subjects were collected, and no personally identifiable information was accessed. Institutional review board or research ethics board approval was therefore not required.

On the Diabetes test set, M2 AUC was 0.648 (95% CI 0.637‐0.660), and M3 AUC was 0.640 (0.628‐0.652). Macro F1 improved from 0.514 (0.508‐0.521) to 0.546 (0.539‐0.553), and Brier score decreased from 0.231 (0.230‐0.232) to 0.213 (0.212‐0.214). Thus, M3 improved classification balance and probabilistic accuracy but reduced discrimination.

DPD decreased from 0.206 (95% CI 0.147‐0.268) for M2 to 0.124 (0.101‐0.185) for M3. EOR decreased from 0.444 (0.222‐0.685) to 0.291 (0.097‐0.545), indicating that the DPD improvement did not extend to equalized-odds parity. The findings therefore represent a trade-off rather than simultaneous improvement across fairness definitions.

The primary Diabetes test-set performance and fairness metrics are summarized in Table 4.

A stage-wise ablation analysis was not performed because proxy residualization and temporal-shift mitigation were not implemented in the fresh reconstruction. Consequently, the independent contribution of each proposed stage, including the previously reported 22.4% reduction attributed to representation-level correction, could not be reproducibly estimated and is not claimed in this analysis. The empirical comparison instead evaluates the combined missingness-aware and representation-weighted M3 pipeline against M2. In practical terms, representation weighting targets unequal subgroup coverage, missingness indicators address systematic differences in documentation, integrity flags identify records affected by unusual missingness or utilization patterns, and proxy and temporal stages remain prespecified components requiring future evaluation.

The reproducibility flow included 101,766 Diabetes encounters (20,203 in the patient-separated test set), 63,996 eligible CMS episodes (12,801 test episodes), and 71,058 NHANES records for stage-level auditing. Test or stage-level prevalence was 11.16%, 9.62%, and 8.42%, respectively. Full split counts, individuals, positive outcomes, and prevalence are reported in Table S4 in Multimedia Appendix 1.

Subgroup analyses showed heterogeneity by race. M2 race-specific AUC ranged from 0.631 to 0.782, and M3 ranged from 0.609 to 0.796; sex-specific AUCs were similar within each model. M3 subgroup Brier scores ranged from 0.193 to 0.214, while calibration slopes ranged from 1.48 to 3.90, indicating material miscalibration despite the lower overall Brier score. Full estimates and CIs are reported in Table S3 in Multimedia Appendix 1.

The evaluation sample sizes across the Diabetes, CMS, and NHANES analyses were as follows: n=20,354, n=12,732, and n=45,565, respectively. The observed outcome or high-risk prevalences across the Diabetes, CMS, and NHANES analyses were as follows: 11.2%, 9.4%, and 8.8%, respectively.

The operational integrity rules flagged 203 (1.00%) of 20,203 test records. The rule-gated MoE achieved an AUC of 0.648, a macro F1 of 0.514, a Brier score of 0.231, and a DPD of 0.205. M3 achieved an AUC of 0.640, a macro F1 of 0.546, a Brier score of 0.213, and a DPD of 0.124.

Compared with M3, the MoE-minus-M3 bootstrap contrast was +0.0078 for AUC (95% CI 0.0034‐0.0122), −0.0316 for macro F1 (−0.0372 to −0.0264), +0.0177 for Brier score (0.0175‐0.0180), and +0.0708 for DPD (0.0154‐0.1172). Thus, the exploratory gate improved AUC slightly but worsened classification balance, probabilistic accuracy, and demographic parity.

Because the rule gate selected between 2 differently processed experts, these contrasts cannot distinguish gating effects from differences between M2 and M3. The analysis does not support the previous claim that MoE provided the best fairness-performance combination.

The integrity-flagged MoE comparison is summarized in Table 5; race-specific subgroup discrimination and the exploratory MoE end point comparison are shown in Figures 1 and 2, respectively.

In the CMS test set, M2 versus M3 results were AUC 0.798 (95% CI 0.786‐0.808) versus 0.796 (0.785‐0.806), macro F1 0.575 (0.568‐0.583) versus 0.583 (0.575‐0.591), Brier score 0.187 (0.185‐0.189) versus 0.183 (0.181‐0.185), DPD 0.693 (0.655‐0.733) versus 0.730 (0.697‐0.771), and EOR 0.656 (0.500‐0.778) versus 0.625 (0.438‐0.742). M3 slightly improved macro F1 and Brier score but did not improve discrimination or fairness. The CMS external-validation metrics are summarized in Table 6.

NHANES contained 71,058 records with 5980 (8.42%) high-risk labels and was used only for stage-level concept-coverage, missingness, proxy, and bounded-laboratory auditing. No readmission AUC, model-level DPD, or direct transportability claim was estimated.

The fresh reconstruction did not reproduce the earlier manuscript’s claim of simultaneous improvement in discrimination and fairness. On the primary test set, M3 improved the macro F1, Brier score, and DPD but reduced the AUC and EOR. CMS showed similar discrimination and slightly improved Brier score but worse DPD. These mixed results demonstrate why multiple fairness and calibration end points, subgroup analyses, and uncertainty intervals are necessary.

The external evidence has 2 deliberately different levels. CMS SynPUF evaluates the readmission outcome after claims-to-concept harmonization. NHANES does not evaluate the readmission model or its AUC; it examines whether selected representation, proxy, and bounded-laboratory integrity procedures behave sensibly in a different data-generating environment. This distinction limits the transportability claim and should be preserved when interpreting Table 6.

Missingness-aware features and representation weights can change model selection rates and probability errors without improving ranking discrimination. In this reconstruction, a lower DPD coexisted with a worse EOR and heterogeneous subgroup calibration. The results therefore support an end point–specific interpretation rather than a general claim that data-centric mitigation improves both fairness and performance.

The reproducibility package provides an auditable starting point: record-level predictions, split flow, subgroup metrics, calibration, concept missingness, and bootstrap intervals. However, proxy residualization and temporal mitigation require separate, prespecified implementations before they can be evaluated as components of the workflow.

Accordingly, the 37-concept dictionary should be interpreted as a reusable semantic interface, not as a guarantee of immediate interoperability. Its application at a new institution requires local clinical review; data-quality validation; documentation of mapping decisions; and re-evaluation of discrimination, calibration, and subgroup fairness before use.

First, the results are retrospective and limited to structured public data. Second, the 37-concept dictionary was used for audit reporting rather than a single transported prediction model. Third, the fresh run did not implement mutual-information or correlation proxy thresholds, k-nearest neighbors imputation, or temporal-shift correction; earlier claims about these components were removed. Fourth, subgroup estimates were imprecise for small groups. Fifth, the exploratory MoE used a fixed rule gate and cannot isolate architecture effects. Sixth, CMS SynPUF is synthetic and may not reproduce real institutional calibration, subgroup relationships, or coding behavior. Finally, no external repository DOI is available until the local package is deposited.

This reproducible reconstruction found that M3 improved the macro F1, Brier score, and DPD on the primary Diabetes test set but reduced the AUC and EOR. CMS results did not show a fairness improvement, and the exploratory MoE did not outperform M3 on most end points. The evidence supports a nuanced fairness-calibration-discrimination trade-off, not uniform mitigation success. Prospective, institution-specific validation and prespecified implementation of the remaining proxy and temporal stages are required before clinical use.