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Under review as a conference paper at ICLR 2027

Having It Both Ways: Personalization and Generalization in Federated EHR Generation

Abstract

Patient privacy regulations restrict the sharing of electronic health records (EHRs), limiting their use for clinical machine learning. While sharing realistic synthetic data can bypass these legal restrictions, EHR generation approaches trained on a single hospital's data generalize poorly to patient populations elsewhere, and their quality is often limited by the quantity of patient data available. To address these issues of data sparsity, federated learning enables training on data across many hospitals by only sharing model updates, allowing hospitals to learn statistical features of other hospital populations without leaking protected health information (PHI). In this paper, we first identify a trade-off inherent to this setting between generalization and personalization: joint training improves transfer across hospitals but degrades performance on each hospital's local distribution. We characterize this trade-off across a range of federated methods and propose FedLIBRA, an approach that directly pushes the frontier of personalization–generalization, enabling the generation of high-quality patient data for any hospital.

Primary area:
generative models
Keywords:
federated learning, personalized federated learning, synthetic electronic health records, generative models, healthcare, data heterogeneity, invariant risk minimization

Reviews

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1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_Zda4OpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

Hospitals want to train models that generate synthetic patient records, but they cannot share their data. With federated training, there is a trade-off: a model can fit one hospital's patients well (personalization) or work well for all hospitals together (generalization). Training each hospital alone gives the best personalization; pooling all data gives the best generalization. The authors draw a straight line between these two extremes (the "frontier") and show that the standard approach (FedAvg plus fine-tuning) lands right on it.

Their method, FEDLIBRA, tries to beat this line. It (1) adds a penalty (IRM) so the shared model learns patterns that hold at every hospital, uses a best-of-K training trick so different parts of the model can specialize to different types of patients, and (3) fine-tunes a small adapter for each hospital. Experiments use eight hospitals from the eICU dataset and the HALO generator. Quality is mainly measured by how well the frequency of medical codes in synthetic data matches the real data.

Critical strengths
  1. The paper draws a line between training each hospital alone (best for that hospital) and pooling all data (best for everyone), and shows that the standard approach lands right on this line. This turns a vague trade-off into a clear, testable target that other work can adopt, and it is the main reason I would like to see the paper accepted once the problems are fixed.

  2. By reporting R-squared alongside Pearson correlation, the paper shows that several existing methods get the order of medical code frequencies right but the actual frequencies badly wrong. Pearson correlation alone hides this. This is a real lesson for how synthetic health data should be evaluated.

Critical weaknesses
  1. The abstract says the method improves both personalization and generalization, but this holds only on R-squared. On Pearson correlation it is worse than simpler methods on both axes. In addition, the pooled-data reference that defines the frontier was replaced with a modified version after the original performed very badly, which weakens the claim of going beyond the frontier. This is the main reason for my negative score.

  2. No repeated runs or confidence intervals are reported, so many of the differences between methods are too small to tell apart from noise. One result is also clearly wrong: training on each hospital’s own real data scores below random guessing (AUROC 0.420 vs. 0.500), which suggests a problem in the evaluation and reduces trust in the results.

Questions for authors
  1. Can the claim of improving both axes be restated as an R-squared-only claim?
  2. Why is upweighting used only for the pooled reference? Please retrain all methods with it.
  3. Please report multiple runs with intervals for FEDLIBRA, FedAvg+FT, FedRep and Ditto.
  4. Why does local-only training score below chance (AUROC 0.420)?
  5. Can you add a sequence-level quality measure (e.g. number of visits, code co-occurrence, likelihood on held-out data)?
  6. How do results and cost change with K? Is there evidence that different latents capture different patient types?
  7. Why does best-of-K hurt alone but help together with IRM?
  8. Did IRM actually work? Can a classifier still tell which hospital a sample comes from?
  9. Why these eight hospitals? What happens with more or fewer, or with another dataset such as MIMIC-III?
  10. Have you tested attacks on the model updates shared during training?
1 comment
AuthorsOpenReview ↗

Reply to Reviewer Zda4

Reply to Reviewer Zda4

We thank Reviewer Zda4 for recognizing the value of our personalization–generalization framing and the importance of $R^2$ alongside Pearson $r$.

"Both axes" claims should be restricted to $R^2$ (W1, Q1). Agreed! We revised the Abstract and Results so simultaneous improvement claims are stated explicitly in terms of $R^2$, with Pearson $r$ reported alongside (General Response §4). In our temperature sweep (Section 4, Appendix B.2), one knob moves $R^2$ by 2.94 while keeping Pearson $r$ within 0.03, showing the two metrics are nearly independent here.

Rare-code upweighting was applied only to the pooled reference (Q2). We retrained all baselines with rare-code upweighting and early stopping across three seeds (General Response §1, Table 1), with per-method effects in Appendix A.3.

Missing multi-seed intervals and below-chance Local-Only AUROC (W2, Q3, Q4). Table 1 now reports 3-seed mean ± SD for all methods. In Table 2, adding $\ell_2$-regularized logistic regression (0.606 AUROC) and gradient boosting (0.573 AUROC) confirms the 0.412 RNN score was small-cohort overfitting (142 training patients at the smallest hospital; General Response §3). RNN and logistic-regression entries report 3-draw averages (SD $\le 0.03$); gradient boosting is a single draw.

Missing sequence-level quality measures (Q5). We report codes per visit against the real rate (General Response §2) and added a full code co-occurrence and sequence structure evaluation in Appendix B.4. Co-occurrence is a much harder target than marginal prevalence—every method scores below zero on co-occurrence $R^2$—though FedLibra attains the best generalized co-occurrence $R^2$ ($-0.01 \pm 0.01$ unweighted, $-0.13$ reweighted) and codes-per-visit Wasserstein distance closer to real ($1.25$ vs. $1.60$ real training data, $3.74$ local-only, $3.11$ centralized). Visit counts are near-degenerate in this cohort (median 1 visit per patient at every client; Appendix A.2), so visit-length distributions carry little signal.

Unclear $K$ sensitivity and why best-of-$K$ hurts alone but helps with IRM (Q6, Q7). We use $K=4$, and sweeping $K \in {1, 2, 4, 8}$ (Appendix B.3) shows $R^2$ scores are flat within $0.007$ (inside seed-to-seed variance) while training time scales roughly linearly with $K$ ($3\text{m }34\text{s}$ at $K=1$, $8\text{m }07\text{s}$ at $K=4$

$≈2.3×$\$\approx 2.3\times\$

, and $14\text{m }05\text{s}$ at $K=8$

$≈4×$\$\approx 4\times\$

) and generation cost is unchanged ($\approx 4\text{m }11\text{s}$). Without IRM, best-of-$K$ over-generates codes (worsening with $K$); IRM anchors the shared representation (General Response §2, Appendix B.1–B.3).

No domain-classifier test for IRM invariance (Q8). Testing a hospital-origin discriminator on learned representations is a direct invariance probe that we plan to include in the camera-ready.

Hospital selection and lack of MIMIC-III results (Q9). The 8 eICU hospitals span a 13× cohort-size range (202–2,617 patients) across teaching and non-teaching centers, with 8× variation in documentation depth uncorrelated with size (Appendix A.2, Table 5). Compute limits prevented adding MIMIC-III during the rebuttal window, though the framework is generator- and dataset-agnostic.

No evaluation of attacks on shared model updates (Q10). This is an interesting direction! Our privacy evaluation focuses on output-level memorization (NNAAR and MIA on synthetic records), following prior synthetic EHR work. While formal differential privacy is often very punitive in clinical generation, evaluating empirical attacks on shared model updates ($\Delta \theta_k$) is a practical and important complement. In particular, we can consider update-inversion attacks (whether a server can reconstruct multi-hot visit vectors or rare diagnosis codes from client updates) or update-level membership inference (whether parameter deltas reveal individual patient participation, especially at small hospitals). We now note update-level attack evaluation in Section 6 (Limitations and future work) (alongside Section 1).

Reviewer_dob9OpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
2
Soundness
1
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Paper summary

This paper studies federated generation of electronic health records, focusing on the tension between fitting each hospital’s local distribution and fitting the pooled distribution of participating hospitals. The proposed FedLibra combines an IRMv1 penalty, latent best-of-K training, and local LoRA adaptation of a HALO generator. Experiments on eight eICU hospitals evaluate diagnosis-code prevalence, downstream predictive utility, and distance-based privacy attacks.

Critical strengths
  1. The application is relevant, and using natural hospital partitions captures meaningful heterogeneity in population and sample size. Evaluating both local and pooled distribution fidelity is useful for understanding personalized generators.
  2. The paper considers prevalence fidelity, downstream utility, and empirical privacy risk separately. The observation that competitive downstream prediction can coexist with poor prevalence fidelity is informative.
Critical weaknesses
  1. The claimed frontier is not established. Figure 1 defines the frontier by connecting two selected baseline results. Neither an analysis nor a systematic exploration of achievable trade-offs justifies treating this line as a performance boundary. Improving over this line therefore does not establish that an inherent personalization–generalization trade-off has been overcome.
  2. Severe baseline failures undermine the central comparison. Centralized training yields (R^2) values of −53.1/−44.3, and several federated baselines also show extreme miscalibration. The centralized reference is then modified using both rare-code weighting and early stopping. Appendix A.3 acknowledges that their effects are confounded and each condition was run once. These unresolved training failures make the reported gains difficult to interpret.
  3. The contribution of the proposed combination is not isolated. Table 4 shows that best-of-K alone worsens both (R^2) scores, contradicting the accompanying description. More importantly, the crucial IRM-plus-LoRA baseline is missing. The experiments therefore do not establish whether best-of-K contributes to the final method beyond the simpler combination of IRM and restricted local adaptation.
  4. The main mechanism claims lack direct validation. Agreement in marginal code frequencies does not establish recovery of multimodal patient populations, clinical co-occurrence structure, or hospital-invariant features. The experiments provide little direct evidence for these explanations, which are central to the motivation for IRM and best-of-K.
Questions for authors
  1. What causes the extreme centralized and federated baseline miscalibration? Do the main comparisons remain favorable under validation-based checkpoint selection, with the effects of weighting and early stopping evaluated separately?
  2. How does IRM followed by the same local LoRA adaptation perform without best-of-K? Please compare this alternative with FedLibra across independent training runs and reconcile the discussion of best-of-K with its deterioration in Table 4.
2 comments
AuthorsOpenReview ↗

Reply to Reviewer dob9

We thank Reviewer dob9 for the detailed critique.

The claimed frontier was not established as a performance boundary (W1). We clarified in Section 1 (Figure 1) and Sections 3–4 that the dashed line represents the best trade-off the baselines reach—set by FedAvg with and without full local fine-tuning—as an intuitive reference rather than a formal theoretical boundary. Under uniform tuning, standard federated methods (FedAvg, Ditto, PerAda, FedProx) cluster around ~0.50 personalized and ~0.84 generalized $R^2$, while FedLibra improves substantially on personalization (0.724 vs. 0.522) without sacrificing generalization (0.762), which is a Pareto improvement on the weaker axis. We also now draw the frontier to include the set of core baselines in Figure 1.

Baseline miscalibration and confounded tuning undermined comparisons (W2, Q1). All baselines now use rare-code upweighting, early stopping, and validation-selected $\tau$ across three seeds in Table 1 (General Response §1; Section 4, Appendix A.3, and Appendix B.2).

Missing IRM + LoRA baseline and Table 4 contradiction (W3, Q2). Table 4 now includes both FedAvg + IRM + full fine-tune (0.321 / $-0.858$) $R^2$, showing that full fine-tuning overwrites the shared model and collapses generalization) and FedAvg + IRM + LoRA (0.587 / 0.244) alongside full FedLibra (0.716 / 0.704), confirming that best-of-$K$ improves $R^2$ on both axes when paired with IRM and restricted local adaptation (General Response §2).

Mechanism claims lacked direct validation beyond marginal frequencies (W4). We acknowledge that we do not have direct mechanistic probes verifying multimodal latent specialization or hospital-invariant representations, and we have softened our wording in the revised draft (Sections 4 and 6) so we do not overclaim these mechanisms. At the same time, we still observe clear empirical benefits from our best-of-$K$ + latent and IRM formulation in Figure 2 and across our main $R^2$ and Pearson $r$ fidelity results (Tables 1 and 4), as well as in downstream utility across three model families (Table 2). Beyond marginal frequencies, we also report emission rate directly (real: ~3.3 codes/visit, FedAvg: 3.5, FedLibra: ~3.3, whereas best-of-$K$ alone rises to 4.2 at $K=2$ and ~115 at $K=8$); visit counts are near-degenerate in this cohort (median 1 visit/patient at every client; Appendix A.2), so prevalence and emission-rate agreement carry most of the distributional signal.

Thank you for the detailed rebuttal and additional experiments. I appreciate the efforts to address my concerns, particularly the inclusion of the missing ablation. However, significant concerns remain regarding the consistency of the baseline results, the actual contribution of best-of-K (Table 9), and the validation of the proposed mechanisms. Therefore, I maintain my rating of 1 and confidence of 3.

Reviewer_RS1VOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
3
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Paper summary

This paper studies federated training of generative models for synthetic EHRs. The authors describe a trade-off between personalization and generalization. They argue that standard federated methods, including FedAvg with local fine-tuning, only move along a line between a local-only model and a centralized model. They propose FedLibra, a two-level approach combining IRM and a best-of-K latent selection objective during federated global pretraining, followed by lightweight local LoRA fine-tuning. Experiments show that FedLibra has the best balance of R² on each hospital’s own test set and on the pooled test set.

Critical strengths
  1. The paper addresses an important, practical problem: generating synthetic patient data across hospitals that cannot share records.
  2. Evaluating each model on its own hospital’s test set and on the pooled test set is a clear, useful way to frame what a federated generator should achieve.
  3. The method is simple and adds no communication cost.
  4. The evaluation covers fidelity, downstream utility and privacy.
Critical weaknesses
  1. The IRM gains may come from calibration rather than from learning invariant features.
  2. The ablation text doesn’t match the table, and the final method still makes a trade-off.
  3. Downstream utility shows no advantage. FedLibra’s AUROC (0.702) is on par with FedRep (0.709) and LG-FedAvg (0.700).
  4. The abstract implies federated learning avoids leaking patient information, but the evaluation uses only simple distance-based tests on synthetic records. There is no formal guarantee such as differential privacy, and no test of attacks on the shared model updates, which the paper itself notes can leak data. The claim that synthetic data “can bypass” privacy laws is also too strong.
Questions for authors
  1. Does the IRM gain remain if FedAvg and the other baselines get a simple calibration step, such as tuning the sampling temperature per hospital?
  2. Why does the centralized model fail so badly on the pooled test set? And why does a classifier trained on real local data score below chance in Table 2?
  3. How were the 8 hospitals chosen, and do the results hold across random seeds and different hospital subsets?
  4. What value of K is used for best-of-K, and what is its actual compute cost compared with the baselines? Why does best-of-K alone hurt fidelity?
  5. Why should each hospital’s personalized model also perform well on the pooled test set, instead of using the shared model for system-wide data?
1 comment
AuthorsOpenReview ↗

Reply to Reviewer RS1V

We thank Reviewer RS1V for the positive assessment and constructive questions. Please see our General Response for the full summary of revisions; we address specific points below.

IRM gains could come from simple temperature calibration (W1, Q1). Table 1 now selects $\tau$ per run on validation performance for all methods (Section 4, Appendix B.2; General Response §1). Temperature scaling is monotone per code, moving Pearson $r$ by $\le 0.03$ while moving $R^2$ by nearly 3. Even with per-run $\tau$ tuning and rare-code upweighting, FedAvg (0.497 personalized $R^2$) and all personalized baselines ($\le 0.522$) still trail FedLibra (0.724).

Ablation text mismatched Table 4 and trade-offs remain (W2). We aligned the ablation text with Table 4 (General Response §2) and clarified that FedLibra pushes the Pareto frontier between local-only and centralized training rather than dominating every single-objective baseline on generalization alone (upweighted centralized reaches 0.917 generalized $R^2$ vs. FedLibra's 0.762; no other method is strong on both axes).

Downstream utility showed no advantage and Local-Only scored below chance (W3, Q2). Table 2 compares real-only (Local-Only) against real + synthetic (augmenting each hospital's private records with generated data, matching realistic deployment). Adding $\ell_2$-regularized logistic regression (0.606 AUROC) and gradient boosting (0.573 AUROC) confirms the 0.412 Local-Only RNN score was small-cohort overfitting (142 training patients at the smallest site; General Response §3, Table 2), and augmenting with FedLibra improves over Local-Only across all three families. Table 2 also shows that FedRep's high RNN AUROC (0.714) masks severe miscalibration ($-33.17$ personalized $R^2$), whereas FedLibra achieves both strong utility (0.708 RNN / 0.669 GB AUROC) and calibrated fidelity.

Privacy claims were too strong without DP or update-attack tests (W4). We revised the Abstract, Section 5 (Privacy), and Section 6 (Limitations and future work) to state that synthetic data reduces direct record sharing without guaranteeing differential privacy or regulatory compliance, and noted gradient-level attacks as a limitation and future direction (General Response §4).

Hospital selection lacked justification and MIMIC-III is missing (Q3). We selected these 8 eICU hospitals to span a 13× range in cohort size (202 to 2,617 patients) across 3 teaching and 5 non-teaching sites in two census regions, capturing realistic heterogeneity in volume and documentation depth (Appendix A.2, Table 5). Documentation depth varies 8× and is uncorrelated with site size—the deepest-coding site is the smallest—matching the spurious variation our invariance penalty targets. Table 1 now includes 3-seed intervals; extending to MIMIC-III is left for future work given compute limits.

Missing $K$ value, compute cost, and explanation for best-of-$K$ alone (Q4). We use $K = 4$. Sweeping $K \in {1, 2, 4, 8}$ for FedLibra in Appendix B.3 shows $K$ makes no measurable difference to fidelity—all four values lie within $0.007$ on $R^2$ (inside seed-to-seed SD of $0.004$–$0.006$). Training time scales roughly linearly with $K$ ($3\text{m }34\text{s}$ at $K=1$, $5\text{m }03\text{s}$ at $K=2$, $8\text{m }07\text{s}$ at $K=4$

$≈2.3×$\$\approx 2.3\times\$

, and $14\text{m }05\text{s}$ at $K=8$

$≈4×$\$\approx 4\times\$

), while generation time is unchanged ($\approx 4\text{m }11\text{s}$–$4\text{m }15\text{s}$ for 8k patients/hospital). See General Response §2 for why best-of-$K$ fails without IRM.

Personalized models should not need to generalize to the pooled test set (Q5). While system-wide generation can use a shared model (where centralized and FedAvg excel), evaluating personalized models on the pooled distribution tests whether local adaptation causes catastrophic forgetting of rare conditions absent from a small hospital's own sample.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Summary of revisions + general comment

General Response: Summary of Revisions and New Experiments

We thank all reviewers for their constructive feedback and for recognizing the value of evaluating federated synthetic EHR generation along both personalization and generalization axes. We have uploaded a revised manuscript (new text and tables in blue) addressing the shared methodological, empirical, and framing concerns.

§1. Baseline tuning, validation selection, and multi-seed runs

(Table 1, Section 4, Appendix A.3 & B.2; RS1V, dob9, Zda4)

Baseline miscalibration and asymmetric tuning made comparisons unclear. We re-ran all baselines with rare-code upweighting and early stopping enabled under a matched 100-epoch ceiling, selecting the sampling temperature $\tau$ per run on validation performance (Section 4, Appendix B.2). Broadly, tuned baselines improve $R^2$, but still sit below FedLIBRA. We omit upweighting for FedLibra because its cross-site objective already models code rarity by design; adding it lowers FedLibra's $R^2$ by 0.09 personalized and 0.15 generalized (Appendix A.3).

Single-seed results lacked uncertainty estimates. Table 1 now reports mean ± SD across three independent training seeds for every method. Even against fully tuned baselines, FedLibra achieves the highest personalized $R^2$ (0.724 ± 0.006 vs. 0.522 ± 0.014 for the strongest baseline, FedProx) while maintaining strong generalization (0.762 ± 0.003).

The $-53.1 / -44.3$ centralized collapse was a single-run artifact. With three seeds and early stopping, unweighted centralized training reaches 0.128 personalized / 0.857 generalized $R^2$, instead the $-53 / -44$ reported previously from a single full-budget run. Upweighting improves it to 0.497 / 0.917, and we have revised the Abstract, Section 5, and Appendix A.3 accordingly. We apply early stopping and reweighting to all baselines, taking the best configuration on each..

§2. Isolating component contributions and IRM+LoRA ablations

(Table 4; dob9, RS1V, Zda4)

Best-of-$K$'s contribution was not isolated from IRM + LoRA. We added FedAvg + IRM + LoRA/full FT to Table 4. Comparing it (0.587 personalized / 0.244 generalized $R^2$) against full FedLibra (0.716 / 0.704) confirms that best-of-$K$ adds substantial gains on both axes beyond IRM and LoRA alone.

Best-of-$K$ alone degraded $R^2$ in Table 4, contradicting the text. Trained on the best of $K$ candidate draws but evaluated on a single draw, best-of-$K$ without IRM systematically over-generates codes, collapsing prevalence fidelity. Pairing it with IRM anchors the shared representation and keeps emission rates aligned with real data. We updated the ablation text to match Table 4.

§3. Downstream utility and the below-chance Local-Only score

(Table 2, Appendix C; RS1V, Zda4)

Below-chance Local-Only AUROC (0.412) reflected RNN overfitting on small cohorts. The smallest hospital has only 142 training patients (202 total). Expanding Table 2 with $\ell_2$-regularized logistic regression (0.606 AUROC) and gradient boosting (0.573 AUROC) shows both score above chance on Local-Only, confirming 0.412 was specific to RNN overfitting. Table 2 compares real-only against real + synthetic (augmenting each hospital's private local records with synthetic data, reflecting realistic deployment where a site uses all available local and generated data). Across all three classifier families, augmenting with FedLibra improves over real-only, directly serving hospital systems with small, unevenly sized sites.

Downstream AUROC parity masked severe prevalence miscalibration. FedRep (0.714 RNN AUROC) and LG-FedAvg (0.707) match FedLibra's RNN AUROC (0.708), yet Table 1 shows severe miscalibration for both ($-33.17$ and $-0.829$ personalized $R^2$). FedLibra matches their downstream utility while preserving calibrated prevalence fidelity (0.724 / 0.762 $R^2$). We now frame our utility claim accordingly.

§4. Scoping $R^2$ vs. Pearson $r$ and privacy claims

(Abstract, Sections 3 & 5; RS1V, Zda4)

Simultaneous improvement on both axes held for $R^2$, not Pearson $r$. We revised the Abstract and Results to state explicitly that FedLibra pushes the personalization–generalization frontier under $R^2$ (exact prevalence calibration), while reporting Pearson $r$ (rank ordering) alongside it.

Privacy wording overstated formal guarantees and regulatory exemption. We softened the Abstract and added a Limitations and future work paragraph in Section 6 (alongside Section 5 Privacy) to clarify that NNAAR and MIA measure empirical memorization resistance on synthetic outputs rather than providing formal differential privacy or testing gradient-level attacks.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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