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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 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?
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:
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.
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%.