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Under review as a conference paper at ICLR 2027

HEAL-Net: Heterogeneous Evidence-Adaptive Learning for Multi-Task Clinical Prediction

Abstract

Electronic health records contain heterogeneous clinical evidence, including diagnoses, procedures, medications, laboratory measurements, and longitudinal encounter histories. Integrating these sources is challenging because they differ in semantic structure, clinical relevance, and reliability, while downstream prediction tasks require different uses of current and historical information. We introduce **HEAL-Net**, a **H**eterogeneous **E**vidence-**A**daptive **L**earning **Net**work for clinical prediction. HEAL-Net models patient records as visit-aware heterogeneous graphs with typed concepts, severity-aware labs, and knowledge-based relations. Its relational attention encoder and learnable temporal kernel integrate heterogeneous evidence across visits. Task-specific heads support mortality/readmission prediction, medication recommendation, and length-of-stay estimation through tailored historical fusion and output adjustments. Experiments on MIMIC-III/IV across four tasks show that HEAL-Net achieves the best reported mortality and readmission AUPRC/AUROC, improves AUPRC over GraphCare by 2.40–4.06 points, and attains the highest length-of-stay AUROC and medication sample-F1. Ablations validate graph structure, temporal encoding, and laboratory representation.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
AI4Med, Heterogeneous Graphs, Longitudinal EHR, Clinical Prediction

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 5 reviews, above 27% of the others.
Reviewer_LJCoOpenReview ↗
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Paper summary

This work proposes a heterogeneous graph neural network for multi-task clinical prediction using electronic health records (EHR). The model constructs intra-visit medical entity edges by leveraging an LLM, combined with UMLS medical knowledge edges, to build patient-level heterogeneous graphs. A core design is a unified time decay kernel shared across graph message passing, visit-level attention, and cross-visit history aggregation, which imposes a consistent inductive bias for modeling the temporal decay of clinical evidence. The architecture uses history masking to naturally accommodate patients with only a single admission. The authors evaluate the model on four clinical prediction tasks: in-hospital mortality, length-of-stay (LOS) classification, readmission risk, and medication recommendation, and compare against several EHR prediction baselines on the MIMIC dataset.

Critical strengths

1.The paper addresses a pervasive pain point in EHR modeling: imbalance between single-visit and multi-visit patients, plus heterogeneous prediction tasks with distinct demands on patient history. It provides detailed dataset statistics in Appendix D to justify design choices, which strengthens the motivation. The architecture uses history masking to naturally handle patients with only one admission and avoids performance degradation on this large subgroup. 2. A key inductive bias is introduced: sharing one unified time decay kernel across graph message passing, visit-level attention and cross-visit history aggregation. While time decay weighting exists in prior EHR literature, prior models typically maintain separate time parameters for graph and sequence modules. This design enforces consistent modeling of temporal evidence decay across all model components. Task-adaptive prediction heads are carefully tailored for binary, ordered and multi-label clinical targets, enabling one shared backbone to serve diverse clinical prediction tasks.

Critical weaknesses

1.Ambiguous prediction cutoff definition creates substantial risk of look-ahead leakage and weakens experimental validity. Although standard cutoff conventions exist for MIMIC clinical benchmarks, the paper only gives abstract mathematical constraints and does not explicitly document the index time, observable input window, and label window for mortality, LOS, and drug recommendation tasks. It is not clearly specified whether post-cutoff events inside the target admission are excluded from graph construction. Even if the authors follow common benchmark rules, this omission creates ambiguity: readers cannot verify whether full within-stay codes/labs are used to predict LOS or in-hospital mortality, which would produce overoptimistic metrics. This opacity threatens the credibility of empirical results. 2. Core architectural claims cannot be fully validated due to missing ablation experiments and mismatched input modalities across baselines. First, LLM-generated intra-visit edges are a major component of the constructed graph, yet there is no ablation that removes these LLM edges to quantify their contribution. It remains unclear whether performance gains arise from UMLS medical knowledge or potentially hallucinated LLM relational edges. Second, input features are not matched across compared methods: HEAL-Net uses SapBERT embeddings and severity-aware lab features, while competing baselines do not receive these enriched inputs. The reported SOTA advantage may partially come from stronger preprocessing rather than the proposed heterogeneous graph attention architecture itself.

Questions for authors

1.The paper only provides abstract mathematical cutoff constraints and does not explicitly document index time, input event window and label window for mortality, LOS and drug recommendation. Readers cannot verify whether post-cutoff events inside target admission are excluded from graph construction. Please clearly answer: what is the exact index time, allowed input window and label window for each task? Confirm whether all events occurring after the cutoff time in the target admission, including graph nodes, UMLS edges and LLM-generated edges, are excluded. 2. LLM-generated intra-visit edges are a major part of the graph construction, yet no ablation removes these edges to quantify their contribution. Please clearly answer: can you report full task performance when removing all LLM-generated intra-visit edges and keeping only UMLS edges? What is the performance drop across all four tasks? 3. The title and abstract frame this work as a multi-task clinical prediction model. However, the description on page 4 states that task encoders and prediction heads are trained independently per task. This creates ambiguity about whether the shared backbone parameters are jointly optimized across all tasks or trained separately for each task with no cross-task gradient interaction. Please clearly answer: Are the shared backbone parameters updated jointly across all tasks in a single training run, or is a separate model instance trained for each prediction task? If trained separately, how do you justify framing this as a multi-task learning contribution rather than a single-task architecture reusable across multiple prediction objectives? 4.The input modalities are mismatched across baselines: HEAL-Net uses SapBERT embeddings and severity-aware lab features while competing baselines do not use these enriched inputs, which makes the SOTA comparison unfair. Please clearly answer: can you run the strongest baseline (GraphCare) with exactly identical input preprocessing (SapBERT embeddings + severity-aware lab features) and report its metrics? How much performance advantage remains for HEAL-Net under fully matched input features? 5.The paper proposes sharing one unified time decay kernel across graph message passing, visit-level attention, and cross-visit history aggregation as a core inductive bias. Please clearly answer: can you provide an ablation where graph and visit attention modules use separate learnable τ\tau parameters? What empirical performance benefit comes from sharing this kernel across modules? 6. For the LOS prediction task, macro-F1 of the proposed model is worse than some compared baselines. Please clearly answer: which bins of stay-length samples produce the majority of prediction errors for the LOS task?

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AuthorsOpenReview ↗

Response to Reviewer LJCo

Thank you for pressing us to specify what the model can observe for each task and which comparisons isolate the proposed design choices.

Q1. Index, inputs, and labels. The implementation does not impose an admission-time or first-24-hour cutoff. The effective observation point is the end of the index stay for the binary tasks and the end of the target stay for LOS and medication. The actual settings are:

TaskObserved inputsOutcome and eligibility
MortalityCompleted index stay’s diagnoses, procedures, drugs, and labs; eligible earlier historyDeath indicator in the next recorded admission. A following admission is required.
ReadmissionSame inputs as mortalityLess than 15 days from the index admission to the next recorded admission. A following admission is required.
LOSCompleted target stay’s structured record; eligible earlier historyThe completed stay’s LOS category (ten classes).
MedicationFull target stay’s diagnoses, procedures, and labs; eligible earlier history. Target-stay drug nodes and current medication tokens are removed.Target-stay ATC-3 set. Patients have at least two eligible admissions; first-admission samples can be included.

Graph encoding excludes subsequent admissions; static and scored knowledge edges attach only to eligible concept occurrences. Within the observed stay, events after admission may still be used, and medication-task labs may be collected after treatment. The revised manuscript makes no prospective early-prediction or prescribing claim. The conditional readmission endpoint also differs from discharge-to-readmission risk in an unselected cohort.

Q2. Removing the LLM-scored edges. The table gives mean ± sample SD over seeds 42, 123, and 456. The removal variant keeps static UMLS and observed clinical edges. Patient-context scoring is disabled in both configurations.

ConfigurationMortality AUROCReadmission AUPRCLOS Cohen’s κMedication sample-F1
Full model71.03 ± 2.4986.44 ± 3.6037.04 ± 0.7464.62 ± 0.32
Without scored knowledge edges72.61 ± 1.8987.41 ± 0.7537.17 ± 0.4364.64 ± 0.36

There is no observed drop in the initialization-matched mortality comparison. For readmission, LOS, and medication, the full model initializes its learnable scale at 140, 20, and 80 days, respectively, while the removal variant starts at 60 days for all three. The scales are learned during training, but the different starting values mean these comparisons do not isolate an edge effect. The removal also changes connectivity, leaving the effect of semantic content unresolved.

Q3. Joint optimization. We train a separate encoder and head for each task, with no shared trainable weights or cross-task updates. We have withdrawn the multi-task learning claim and removed the joint objective. The revised runs evaluate the newly specified readout, including a softmax LOS head. The four slot names are type-prior-guided latent variables; we have not validated them as clinical explanations.

Q4. Matched-input GraphCare. We do not have a verified GraphCare run with the same patient partitions, task definitions, inputs, SapBERT features, and severity-aware lab representation. We have withdrawn the original GraphCare entries and the superiority claims based on them. As a result, we cannot quantify an advantage after matching the inputs. The revised results are limited to MIMIC-III.

Q5. Separate time scales. With matched initialization and the same three seeds, separate learnable scales give mortality AUROC 71.57 ± 2.68, versus 71.03 ± 2.49 with one shared scale. This does not establish a performance benefit from sharing. The other task comparisons have the initialization difference noted above. The method now distinguishes the training-time kernel from fixed construction decay and edge pruning.

Q6. Which LOS bins drive errors? The 4-, 5-, 6-, and 7-day bins account for approximately 52.7% of all misclassifications across the five saved test sets, with mean error counts per split of 317.6, 288.2, 311.4, and 298.2. Class F1 is especially low for the 6- and 7-day bins (10.27 ± 6.03% and 2.91 ± 2.41%). The 8–14-day bin also contributes 318.4 errors per split on average, from a mean of 1,142.8 examples. Appendix A3 gives the support and error count for every bin; overall macro-F1 is 36.04 ± 0.59%.

Reviewer_yJXMOpenReview ↗
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Paper summary

This paper proposes HEAL-Net, a heterogeneous evidence-adaptive learning framework for clinical prediction using electronic health records (EHRs). The framework constructs visit-aware heterogeneous graphs incorporating diagnoses, procedures, medications, and laboratory measurements, together with biomedical knowledge and temporal relationships. A relational graph attention network integrates heterogeneous clinical evidence, while a learnable temporal kernel captures dependencies across patient visits. Task-specific prediction heads adapt historical information for four clinical prediction tasks: mortality prediction, readmission prediction, length-of-stay estimation, and medication recommendation. Experiments on MIMIC-III and MIMIC-IV demonstrate competitive performance against existing clinical prediction models, particularly for mortality, readmission, and length-of-stay prediction. Ablation studies further investigate the effectiveness of heterogeneous graph construction, temporal encoding, and severity-aware laboratory representations.

Critical strengths

S1. The proposed framework integrates multiple clinical information sources, including diagnoses, procedures, medications, laboratory measurements, and biomedical knowledge, within a unified graph representation. S2. The design of different historical integration mechanisms for binary, multi-label, and ordinal prediction tasks is well motivated by their distinct output structures. S3. The experiments demonstrate improvements over competitive baselines, particularly GraphCare, across mortality and readmission prediction. The model also achieves strong results for length-of-stay prediction and medication recommendation. S4. The paper evaluates the framework on two widely used clinical datasets and four prediction tasks. The ablation studies provide additional evidence supporting the proposed graph structure, temporal modeling, and laboratory encoding.

Critical weaknesses

W1. Several components, including heterogeneous graph attention, exponential temporal decay, gated historical fusion, and ordinal prediction, are established techniques. The main contribution appears to be their integration rather than a fundamentally new learning mechanism. The paper could better distinguish its methodological novelty from existing graph-based EHR models.

W2. The framework involves heterogeneous graph construction, biomedical knowledge retrieval, LLM-assisted evidence extraction, and relational attention. However, the paper does not provide sufficient quantitative analysis of preprocessing costs, training time, inference latency, or memory consumption relative to simpler baselines.

W3. Although the paper includes ablation studies, these primarily compare broad architectural configurations. More targeted experiments are needed to isolate the contributions of shared attention normalization, knowledge-based edges, the learnable temporal kernel, and task-specific historical correction mechanisms.

Questions for authors

Q1. Section 3.1 states that the encoder and prediction head are trained independently for each task. However, Section 3.5 describes a joint weighted objective with shared parameters updated across task batches. These descriptions suggest different training strategies. The authors should clarify whether HEAL-Net uses independent task-specific models or a jointly trained multi-task architecture.

Q2. The experimental analysis refers to dir_I, dir_G, and a Markovian prediction head. However, these terms are not defined in the methodology, which instead introduces bounded historical corrections and an ordinal prediction head. The relationship between these terms and the proposed mathematical formulations should be clarified.

Q3. The discussion claims that DemoGraph achieves the highest sample-AUPRC/AUROC but performs poorly on F1/Jaccard. However, DemoGraph does not appear among the reported models in Table 3. Furthermore, the claim that HEAL-Net achieves the best sample-Jaccard on both datasets is inconsistent with Table 3: CNN+Lab achieves 51.69 on MIMIC-IV, compared with 50.21 for HEAL-Net. These discrepancies should be corrected.

Q4. Section 3.2 describes temporal relationships using a learnable exponential decay kernel, whereas Appendix C discusses a strict temporal cutoff and specifies a decay parameter of 180 days. It is unclear whether temporal edges are removed beyond a predefined threshold or continuously downweighted. The authors should explain how these mechanisms interact.

Q5. The same temporal decay parameter is used for graph-level relationships, visit-level attention, and historical aggregation. Although this provides architectural consistency, these components may operate at different temporal scales. The paper does not establish whether sharing a single decay parameter is preferable to learning separate parameters.

Q6. The graph-topology ablation attributes the degradation in medication recommendation performance to label leakage caused by homogeneous graph construction. However, the reported performance difference alone does not establish label leakage as the underlying cause. Additional analysis is needed to support this explanation.

Q7. The paper attributes improvements in AUROC, Cohen’s κ, and accuracy to better ordinal calibration. However, these metrics do not directly measure probability calibration. Dedicated calibration metrics or additional analysis would be necessary to substantiate this interpretation.

2 comments
AuthorsOpenReview ↗

Response to Reviewer yJXM

Thank you for pointing out where the method description, table labels, and interpretation diverged. We have corrected each of those points in the revision.

W1–W3: Positioning, efficiency, and component evidence. The contribution is the encounter-indexed representation and its integration with explicit recurrence and history masks. We acknowledge prior work on relation-aware attention, incoming-edge normalization, exponential decay, and gated fusion. The evaluated graph rebuild reuses cached scores without new LLM calls, but we have no controlled comparison of preprocessing cost, training time, inference latency, or memory. We have removed claims of efficiency superiority. The component table includes the scored-edge and time-scale comparisons; it does not isolate incoming-edge normalization or the clinical-state readout.

Q1–Q2: Training and configuration labels. Training is independent per task, with no joint weighted objective. dir_I and dir_G are legacy model implementations retained for reproducibility. They do not denote graph edge direction, and neither was used to produce the final reported results. Those results come from the final HEAL-Net configuration, which uses the shared training-time kernel and clinical-state readout. We have excluded the legacy head descriptions from the final configuration and from the interpretation of its results. LOS uses ten-class softmax with weighted, smoothed cross-entropy; there is no Markovian head or set of cumulative thresholds. The revised readout bounds the mixing coefficient (ε ≤ 0.35); it does not bound the resulting logit corrections as described in the original manuscript.

Q3: DemoGraph and Jaccard. We removed the DemoGraph discussion because it had no verified result row. The original MIMIC-IV table also contradicted our Jaccard claim: CNN+Lab was listed at 51.69, above HEAL-Net at 50.21. We withdraw the claim that HEAL-Net led on both datasets and remove the unverified medication baseline rows. The revised five-seed MIMIC-III sample-F1/Jaccard are 64.50 ± 0.36 / 49.08 ± 0.46 at threshold 0.3 and 64.50 ± 0.35 / 49.11 ± 0.44 with validation-selected thresholds.

Q4–Q5: Construction, learned decay, and time-scale sharing. The 180-day value is a decay scale, not a hard cutoff. Graph construction assigns evolution edges exp(−Δd/180) and same-concept edges 0.7 exp(−Δd/360), and prunes weights below 10⁻³. The learned kernel reweights retained evolution and same-concept edges; it cannot recover pruned edges. META-chain weights keep their fixed construction decay. Visit attention and historical mixing use the training-time kernel subject to their history masks and windows. In the initialization-matched mortality comparison, shared versus separate scales give 71.03 ± 2.49 versus 71.57 ± 2.68 AUROC. Other tasks also differ in initialization, so the results do not establish an advantage from sharing.

Q6: Leakage interpretation. We agree that the topology ablation cannot diagnose label leakage and have removed that explanation. Target-stay drug nodes and current medication tokens are excluded from the medication inputs, but the remaining full-stay records may include observations made after treatment. We therefore interpret this as retrospective medication reconstruction. Appendix A1 gives the actual observation and label windows for all tasks.

Q7: Calibration. We withdraw the calibration interpretation of AUROC, κ, and accuracy. Across the five saved LOS prediction sets, top-label ECE with ten equal-width bins is 0.0434 ± 0.0226 on a 0–1 scale. Quadratic-weighted κ is 0.8303 ± 0.0108 and MAE is 0.9582 ± 0.0264 category indices. The latter two describe ordinal error, and MAE here is not measured in days. These diagnostics are descriptive; there is no matched calibration comparison. Ordinary Cohen’s κ, accuracy, and macro-F1 are 36.97 ± 0.59%, 47.81 ± 0.55%, and 36.04 ± 0.59%, respectively.

Thank you for the detailed responses and for acknowledging and correcting the inconsistencies identified in my review.

The clarifications regarding independent task training, legacy prediction heads, temporal decay mechanisms, evaluation protocols, and unsupported performance interpretations satisfactorily address several of my concerns.

However, some substantive issues remain unresolved:

  • Methodological contribution: The proposed framework primarily integrates established techniques, and its distinctive contributions are still insufficiently validated through controlled experiments.

  • Component effectiveness: The reported ablations do not establish clear benefits from shared temporal decay or scored knowledge edges. Important components, including historical integration and attention normalization, remain insufficiently isolated.

  • Empirical validation: The withdrawal of the original GraphCare comparisons, together with the absence of matched-input baselines and revised MIMIC-IV results, substantially weakens the experimental evidence.

  • Computational efficiency: Quantitative comparisons of preprocessing cost, training time, inference latency, and memory consumption remain unavailable.

I appreciate the authors' transparency and the improvements in methodological clarity. Nevertheless, the revised evidence does not yet sufficiently substantiate the proposed framework's methodological advantages or comparative effectiveness.

Reviewer_adzaOpenReview ↗
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Paper summary

This paper introduces HEAL-Net, a graph-based approach for clinical outcome prediction from electronic health records (EHRs). The model organizes longitudinal patient records into visit-aware heterogeneous graphs, incorporates biomedical knowledge and laboratory severity information, and employs relation-aware attention and exponential temporal decay to integrate clinical evidence across visits. Separate prediction heads are used for mortality, readmission, medication recommendation, and length-of-stay (LOS) prediction. The authors evaluate the approach on MIMIC-III and MIMIC-IV and report competitive results against existing methods.

Critical strengths
  1. The proposed architecture considers structured clinical concepts, biomedical relations, laboratory measurements, and temporal dependencies. This provides a reasonable starting point for studying how different sources of clinical evidence contribute to prediction.
  2. The experiments cover MIMIC-III and MIMIC-IV and include component-level ablations. Evaluating different outcome types offers a broader assessment than studying a single prediction task.
Critical weaknesses
  1. The proposed architecture comprises heterogeneous graph construction, relation-aware attention, laboratory severity encoding, exponential temporal decay, and task-specific prediction heads. Each component is individually plausible, but the paper does not sufficiently explain what fundamental limitation of existing methods is overcome by their particular combination. For example, merely allowing different clinical relations to receive different weights does not establish a new attention mechanism. A learnable exponential decay function provides a compact inductive bias for longitudinal data, but its inclusion does not, on its own, constitute a novel temporal modeling strategy.
  2. The paper presents HEAL-Net as a unified solution for multiple clinical prediction tasks, including binary classification, multi-label prediction, and LOS prediction. However, the stated training procedure in Section 3.1 indicates that the encoder and prediction head are optimized independently for each task.
Questions for authors
  1. What specific technical capability does HEAL-Net provide that cannot be achieved by existing heterogeneous graph attention and temporal modeling methods? In particular, beyond assigning relation-specific attention weights and introducing a learnable exponential decay function, does the proposed architecture offer a distinct modeling or optimization mechanism?
  2. Section 3.1 indicates that the encoder and prediction head are trained independently for each task. Given this training procedure, does HEAL-Net involve any joint parameter optimization or cross-task knowledge transfer? If not, what distinguishes the proposed formulation from applying a shared architectural design to independently trained task-specific models?
  3. The proposed method shares a learnable exponential decay kernel across graph-level temporal features, visit attention, and historical aggregation. What evidence supports the assumption that these operations benefit from a common temporal decay function? More importantly, does this parameter-sharing strategy outperform independently parameterized decay functions or standard temporal attention under otherwise comparable settings?
  4. What is the incremental contribution of LLM-generated relations beyond the information already provided by biomedical knowledge and observed clinical relationships? Can the reported improvements be attributed to the semantic content of the generated edges, rather than changes in graph size or connectivity?
1 comment
AuthorsOpenReview ↗

Response to Reviewer adza

Thank you for asking us to distinguish the design rationale from the evidence for individual mechanisms.

1. What the model contributes. HEAL-Net keeps separate nodes for the same clinical concept in different admissions. This allows the graph to preserve local evidence around each occurrence and to represent recurrence explicitly. Masked encounter aggregation and a latent-slot readout combine that evidence for prediction. We use established heterogeneous attention and exponential decay and do not claim a new operator, optimization mechanism, or capability unavailable to existing heterogeneous temporal models. The revision presents the specific representation and evaluates its implementation.

2. Training across tasks. Each task uses a separate encoder, readout, optimizer, and checkpoint. The tasks reuse the architecture and may reuse fixed preprocessing artifacts; there is no cross-task gradient update or learned transfer. We have removed the joint objective and clarified this in the abstract and method. The new runs use the revised readout described in the common response.

3. Shared temporal scale. With the same 60-day initialization, three-seed mortality AUROC is 71.03 ± 2.49 with a shared scale and 71.57 ± 2.68 with separate module scales. A fixed 180-day scale gives 71.66 ± 2.17. Tying the scales reduces the number of time-scale parameters, but these results do not show a predictive benefit. In the full HEAL-Net configuration, the shared learnable scale is initialized at 60, 140, 20, and 80 days for mortality, readmission, LOS, and medication, respectively. These are starting values; the scale is optimized during training. The learnable scales in the component runs start at 60 days, so for readmission, LOS, and medication the comparisons change both initialization and the design under test. The variant formerly called uniform_attention removes elapsed-time weighting only in visit attention; content attention, graph decay, and historical mixing remain. We have not completed a comparison against standard temporal attention.

4. What scored edges add. The scored edges use cached concept-relation priors supported by UMLS triples; patient-context scoring is disabled. With static knowledge and observed clinical edges retained, removing scored edges gives mortality AUROC 72.61 ± 1.89, versus 71.03 ± 2.49 for the full model. This comparison does not show a benefit from the scores. For readmission, LOS, and medication, the removal variant gives 87.41 ± 0.75 AUPRC, 37.17 ± 0.43 Cohen’s κ, and 64.64 ± 0.36 sample-F1, subject to the initialization difference above. Removing edges also changes connectivity. Without a degree-matched or score-shuffling control, we cannot attribute any differences to the semantic content of the edges.

Reviewer_znakOpenReview ↗
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Paper summary

The paper proposes HEAL-Net, a model for EHR-based clinical prediction on MIMIC-III/IV. Each prediction instance becomes a heterogeneous graph with encounter-specific nodes for diagnoses, procedures, drugs, and abnormal labs (severity-discretized; normal results dropped). Node features combine SapBERT, type, and severity embeddings.

Critical strengths
  • Coherent, availability-aware head design grounded in data analysis. The monotone-threshold ordinal head preserves ordinal consistency by construction.

  • The experiments are quite comprehensive. If they hold under a clean protocol, a consistent 2–4 point AUPRC gain on the binary tasks is of practical interest.

Critical weaknesses
  • Possible patient-level leakage. Table 7 describes an 8:1:1 split of visit-level samples, not patients. Visits of one patient can then land in both train and test.

  • Undefined cutoffs. Section 3.1 asserts task-specific cutoffs but never states them.

  • No variance information. Results come from a single split with no seeds or confidence intervals.

  • Lacks 2026 baseline.

Questions for authors
  • Is the 8:1:1 split in Table 7 patient-level or sample-level, and does it apply to all four tasks?

  • For each task, which current-encounter diagnoses, procedures, drugs, labs and text are inputs? Which LLM, prompt and patient context generated the LLM-induced edges, and were they generated for test patients? What are the cost and runtime relative to GraphCare?

  • All GraphCare values in Tables 1–3 have exactly one decimal (e.g., 15.80, 70.30). Were GraphCare’s numbers rerun on your splits or taken from the original paper?

  • Which row of Tables 1–3 is the final model, and how does it differ from the all-flags row? What are dir_I/dir_G and the hash-code embedding, and are tasks trained jointly or independently?

1 comment
AuthorsOpenReview ↗

Response to Reviewer znak

Thank you for asking us to specify the split, model configuration, and information available at prediction time.

Patient split and variability. The 80/10/10 split is by patient for all four tasks. We found no patient overlap across training, validation, and test sets in any of the 20 saved MIMIC-III task–seed partitions. Stratification uses whether a patient contributes multiple task samples. We withdrew the earlier single-run results affected by split selection; the current seed-42 partitions match the preserved originals. The five-seed results in the common response include variation in both the split and initialization.

Inputs and cutoffs. No task uses narrative text. Mortality and readmission use diagnoses, procedures, medications, and labs from the completed index admission, plus eligible earlier history. Their labels refer to the next recorded admission, as detailed in Appendix A1. LOS uses the completed target stay’s structured record and eligible history. Medication reconstruction uses full-stay diagnoses, procedures, labs, and eligible history, with target-stay drug nodes and current medication tokens removed; earlier medications remain eligible. Normal lab values are omitted from graph lab nodes, though normal lab tokens may remain in the code branch. The implementation does not enforce an admission-time cutoff.

LLM scoring and held-out patients. The revised graph rebuild reuses cached concept-relation scores. The scoring prompt contains the two concepts’ names, identifiers and types, a candidate relation, and supporting UMLS triples. It contains no patient notes, demographics, dates, or outcome labels. The saved configuration specifies deepseek-v4-pro, temperature 0, and a score threshold of 0.3; we could not independently confirm the provider version for every historical cache entry. Patient-context scoring (Stage 2) is disabled. A concept triple in a test graph can reuse a cached score; a cache miss adds no scored edge and triggers no new API call. We have no controlled cost or runtime comparison with GraphCare, including the cost of building the original cache.

GraphCare and recent baselines. We cannot verify the provenance of the original GraphCare values as either matched reruns or published results under the same protocol. We have withdrawn those rows and the claims based on them. A verified matched-input GraphCare comparison and the requested recent baseline remain unavailable.

Final model and old table labels. The revised full model uses graph-primary fusion, two graph layers over merged clinical, knowledge, and temporal relations, a softmax over incoming edges, shared training-time decay, historical mixing, and a clinical-state readout. It is trained independently per task. The original “all-flags” row is omitted from the revised table. dir_I and dir_G are legacy model implementations retained solely to reproduce earlier configurations; the names do not indicate graph edge direction. All final reported results were obtained with the HEAL-Net configuration described above. Neither legacy head was used in those runs, so neither forms part of the final configuration or supports the claims drawn from it. Hash32 is a deterministic SHA-256-derived concept identity feature. It encodes neither edge direction nor learned graph structure. Type and severity feature blocks are fixed.

Reviewer_BZViOpenReview ↗
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Paper summary

HEAL-Net proposes a unified framework for mortality, readmission, medication recommendation, and length-of-stay prediction from heterogeneous clinical records. It constructs visit-specific graphs of diagnoses, procedures, medications, and abnormal laboratory findings, connected through biomedical knowledge and temporal relations. Relation-aware attention and a shared exponential time kernel aggregate evidence across visits, while task-specific heads adapt historical information to binary, multi-label, and ordinal outcomes. Experiments on MIMIC-III and MIMIC-IV report leading mortality/readmission AUPRC and AUROC, LOS AUROC, and medication sample-F1 among the evaluated methods. Ablations examine graph structure, cross-visit encoding, and laboratory representation.

Critical strengths
  1. The underlying problem is important and the motivation has a useful empirical starting point. Clinical records combine different observation types and irregular histories, and patients without usable history require sensible predictions. Figure 1 and Appendix D document the uneven history distribution and recurrent clinical content. A framework that demonstrably improves how current and historical evidence are balanced across tasks would be valuable.

  2. The proposed integration is coherent and evaluated across several output structures. Encounter-specific nodes, explicit history-availability handling, and ordered cumulative LOS probabilities are sensible design choices. The reported binary-task improvements and the two-dataset, four-task evaluation are promising evidence of practical usefulness.

Critical weaknesses

1.The distinctive contribution is insufficiently established, and the experiments do not directly test the central motivation.

1(a). The clinical problem is important, but heterogeneous EHR graphs, temporal patient modeling, and knowledge integration are already addressed in relevant prior work, including MulT-EHR, TRANS, and GraphCare. Shared normalization across incoming relation types also has established precedents in RGAT/ARGAT (Busbridge et al., 2019) and HGT (Hu et al., 2020). The potential contribution therefore lies in the specific evidence representation, coordinated temporal modeling, and task-adaptive historical integration, whose benefits require clearer justification and isolation.

1(b). The current ablations do not provide that isolation. The simple-graph comparison simultaneously removes encounter-specific structure, relation typing, and knowledge augmentation. The laboratory comparison changes both discretization and normal-value filtering. Neither directly isolates the shared temporal kernel, contextual knowledge evidence, or historical prediction heads. Furthermore, aggregate performance does not establish that the method addresses the motivating problem of uneven history availability: results are not stratified by available history. Matched comparisons with standard relational or heterogeneous attention models would help distinguish architectural gains from benefits attributable to richer inputs and graph construction.

2.Inconsistencies in the evaluation and incomplete protocol descriptions prevent reliable assessment of the empirical claims.

2(a). Table 3 contradicts the medication metric definitions in Appendix B. With identical predictions, thresholding, and sample averaging, F1 must be at least Jaccard. However, AdaCare reports 11.91% F1 versus 46.97% Jaccard on MIMIC-III, with similar contradictions for ConCare and GRASP. These discrepancies require corrected results or an explicit explanation of which reported metric definitions are inaccurate. The LOS discussion also understates the MIMIC-III macro-F1 gap: Table 2 reports 36.17 for the full model versus 40.58 for MulT-EHR.

2(b). The implemented training and evaluation settings are also unclear. Section 3.1 states that models are trained independently for each task, whereas Section 3.5 describes a joint objective and shared parameter updates. Table 7 does not clearly establish whether patients are disjoint across splits. These omissions prevent verification that the inputs match the intended prediction setting. Finally, KARE and DemoGraph are listed as baselines without corresponding results, despite the discussion interpreting DemoGraph’s performance. Results also lack uncertainty estimates.

Questions for authors
  1. Could authors reconcile Table 3 with Appendix B’s metric definitions and provide corrected medication results? Please also correct the LOS macro-F1 comparison in Section 4.1.

  2. Were the reported results obtained through independent per-task training or joint multi-task training? Please reconcile Sections 3.1 and 3.5 and specify which parameters were shared.

  3. What improvements are attributable specifically to the shared temporal kernel, contextual knowledge evidence, and historical prediction heads? Component-specific ablations and a matched-input RGAT or HGT comparison would materially clarify the contribution. Do the gains persist separately for patients without prior visits and those with longer histories?

  4. Where are the KARE and DemoGraph results, and which reported results support the discussion of DemoGraph? Can you provide uncertainty estimates for the principal improvements, using repeated runs or an appropriate patient-level resampling procedure?

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Response to Reviewer BZVi

Thank you for identifying the gaps in the component comparisons and the inconsistencies in the original results. We address the two sets of concerns below.

1(a) Contribution relative to prior work. We now discuss MulT-EHR, TRANS, GraphCare, RGAT, and HGT in relation to the relevant design choices. Our focus is the encounter-indexed representation: a recurring concept has a separate node in each admission, preserving its local neighborhood while allowing explicit links across admissions. A history mask allows the current-encounter pathway to operate when prior history is absent. This is a specific modeling choice that existing heterogeneous temporal graph methods could also express. We have removed the novelty claim for shared incoming-edge normalization.

1(b) Component comparisons and history. In the three-seed mortality comparison, where the learnable decay scales start at 60 days, AUROC is 71.03 ± 2.49 for the full model, 72.61 ± 1.89 without scored knowledge edges, and 71.57 ± 2.68 with separate learnable scales. The fixed 180-day configuration gives 71.66 ± 2.17. These results provide no evidence that scored edges or a shared scale improve mortality AUROC. The readmission, LOS, and medication variants also differ from the full model in decay initialization, so those comparisons are exploratory. We do not yet have a matched-input RGAT/HGT comparison or isolated controls for the historical readout, laboratory representation, or graph topology.

Across the five main runs, mortality AUROC is 72.03 ± 3.47 for samples with one eligible sequence position and 72.18 ± 3.87 for those with at least two. Medication sample-F1 is 64.92 ± 0.75 and 64.23 ± 0.41, respectively. The medication one-position group consists of first admissions in a cohort selected for multiple eligible admissions. The reported ≥2 and ≥3 groups overlap. These are within-model summaries; without a matched baseline in each group, they cannot establish a gain for patients with no prior history or for those with longer histories.

2(a) Medication metrics and LOS macro-F1. You are correct that sample-F1 must be at least sample-Jaccard when both are computed on the same thresholded prediction sets with the same averaging convention. We could not verify the affected baseline rows and have withdrawn them. The revised medication results are 64.50 ± 0.36 F1 / 49.08 ± 0.46 Jaccard at a fixed threshold of 0.3, and 64.50 ± 0.35 / 49.11 ± 0.44 with thresholds selected on validation data. We also understated the original MIMIC-III LOS macro-F1 gap: Table 2 reported 36.17 for HEAL-Net versus 40.58 for MulT-EHR, a gap of 4.41 points. We have removed the unsupported comparative claim. The revised macro-F1 is 36.04 ± 0.59.

2(b) Training, partitions, and baseline provenance. Section 3.1 was correct about independent per-task training. We have removed the contradictory joint objective from Section 3.5 and documented the configuration used for the new runs. The common response and Appendix A1 give the patient split checks and the actual input and label windows. We have removed KARE and DemoGraph from the comparison list and withdrawn the DemoGraph performance discussion because we do not have verified results for them. The five-seed SD summarizes variation across partitions and initializations; it is not a confidence interval for a gain over a baseline.

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AuthorsOpenReview ↗

Common response: evaluation protocol, revised results, and scope

We thank all the reviewers for their careful reading and thoughtful feedback. The original submission did not clearly specify when inputs were observed, and its description of the training objective and prediction heads did not match the implementation. We have corrected those descriptions, withdrawn comparisons we could not substantiate, and rerun the revised configuration on MIMIC-III. The new results apply to the configuration described in the revision. The changes are highlighted in the updated PDF for your review.

Evaluation protocol. The mortality and readmission tasks use the completed index admission and eligible earlier history. Mortality is the death indicator in the next recorded admission; readmission is an admission-to-admission interval of less than 15 days. Both analyses are restricted to index admissions with a subsequent recorded admission. Length of stay (LOS) is classified from the completed target stay. The medication task reconstructs the target stay’s ATC-3 set from full-stay non-drug inputs and eligible history, with current medications removed from the inputs. These settings do not establish performance at admission or at the time of prescribing. Appendix A1 specifies the input windows and cohorts.

Training and revised model. We train one encoder and prediction head per task, with separate optimizers and checkpoints. There is no joint objective or sharing of trainable weights across tasks. The revised results come from the final HEAL-Net configuration, which uses the temporal kernel and clinical-state readout now specified in the method. Within each task, the kernel shares one learnable time scale across modules. We initialize it at 60 days for mortality, 140 for readmission, 20 for LOS, and 80 for medication, and optimize it during training. The revised runs do not evaluate the originally described bounded historical logit corrections or cumulative ordinal thresholds; the revised LOS head uses a ten-class softmax.

Repeated results on MIMIC-III. The four tasks each use five seeds (42, 123, 456, 789, and 1024). We verified patient disjointness across the training, validation, and test sets in all 20 task–seed partitions and checked the reported values against the run logs. We withdraw the original single-run results affected by split selection. The revised seed-42 partitions match the preserved originals.

MetricMean ± sample SD (percentage points)
Mortality AUROC72.56 ± 3.27
Readmission AUPRC87.35 ± 3.25
LOS Cohen’s κ / macro-F136.97 ± 0.59 / 36.04 ± 0.59
Medication sample-F1 / sample-Jaccard64.50 ± 0.36 / 49.08 ± 0.46

The SD reflects variation across both patient partitions and model initializations. The revision also reports 60 task–configuration–seed runs in the component analysis. The cleanest comparisons are on mortality, where the relevant initialization is matched. They do not establish a benefit from the scored knowledge edges or from tying the temporal scales.

Scope of the contribution. HEAL-Net represents each occurrence of a clinical concept in its own encounter, so recurring concepts can be linked across admissions while retaining their local clinical context. The model combines that representation with masked aggregation across encounters and applies it to independently trained outcome models. We acknowledge relation-aware attention, incoming-edge normalization, and exponential decay as established techniques. We have removed claims of comparative superiority: the original GraphCare results could not be substantiated, and no completed matched-input comparison or revised MIMIC-IV evaluation is available. The revised evidence characterizes the model on MIMIC-III and makes the remaining comparisons explicit.

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

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