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Under review as a conference paper at ICLR 2027

PLARE: Feature Replacement with a Mixture of Experts for Self-Supervised ECG Representation Learning

Abstract

Self-supervised models learn electrocardiogram (ECG) representations from unlabeled recordings. ECG waveform shapes vary within and across recordings: an isolated beat may differ from its neighbors, whereas a distinctive shape may recur across beats. This variation motivates selecting feature-processing parameters according to the content of each short waveform segment (patch). To this end, we introduce PLARE (Patch-Level Adaptive Replacement with Experts), a self-supervised ECG model with a patch-level mixture-of-experts (MoE) module. Content-dependent routing (CDR) selects experts based on each patch's convolutional features, and patch feature replacement uses their outputs in place of the original features before token projection. A temporal Transformer then models relationships among the resulting patch tokens to produce a record-level ECG representation. Across four PTB-XL label sets and CPSC2018, PLARE achieved higher AUROC and AUPRC than the evaluated baselines on four of the five tasks under both linear probing and fine-tuning. In ablations, feature replacement achieved a higher average of AUROC and AUPRC than residual addition on four of five tasks under each protocol. Content-dependent routing improved this average over fixed random expert assignment on all five tasks under both protocols. Inference costs were lower than those of larger baselines. Using INCART's beat-level annotations, we found that expert selection distributions in the frozen pretrained model differed between contexts surrounding normal beats and premature ventricular contractions. These findings support content-dependent feature replacement for ECG representation learning. Code is available at https://anonymous.4open.science/r/PLARE-5FC6.

Primary area:
unsupervised, self-supervised, semi-supervised, and supervised representation learning
Keywords:
ECG representation learning, self-supervised learning, mixture of experts, content-dependent routing, patch-level feature replacement

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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_EbLaOpenReview ↗
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Paper summary

PLARE uses a patch-level mixture of experts to process fixed-length 12-lead ECG patches according to their waveform content. Content-dependent routing selects experts based on each patch's convolutional features. Retained expert outputs replace the original features before token projection and a temporal Transformer, with the originals kept if capacity filtering removes all of a patch's assignments. Pretraining combines masked reconstruction, same-patient contrastive learning, and routing regularization. The authors evaluate linear probing and fine-tuning on four PTB-XL label sets and CPSC2018. PLARE has higher AUROC and AUPRC than the compared baselines on four of five tasks under both protocols. INCART is used to examine expert allocation.

Critical strengths
  1. Patch-level experts are well motivated by ECG morphology variation. Placing conditional feature transformations between convolutional feature extraction and the temporal Transformer gives the experts and temporal model complementary local and cross-patch roles.
  2. The ten baselines share the same unlabeled pretraining pool, with downstream procedures aligned where architectures permit. PLARE achieves higher AUROC and AUPRC than the compared baselines on Sub, Rhythm, Form, and CPSC under both linear probing and fine-tuning, providing convincing evidence of overall effectiveness.
  3. The replacement and routing ablations generally favor the proposed choices. INCART permutation tests also show different router-selection distributions for normal-beat and premature ventricular contraction contexts, supporting an association between signal content and expert allocation.
Critical weaknesses
  1. The residual control sums original features and expert outputs with unit weights, keeping the expert and router architectures unchanged. Replacement gives a higher mean C (the average of AUROC and AUPRC) on four of five tasks under each protocol. Without adjustable weights or gated fusion, this does not establish whether discarding the original features is preferable to a flexible combination.
  2. In w/o CDR, each patch position uses one fixed expert across all ECGs. The comparison therefore combines content-dependent selection with removal of a positional constraint, limiting attribution of the routing gains. All-expert aggregation provides another control, but also changes the number of experts used per patch.
Questions for authors
  1. Figure 5 analyzes routing before capacity filtering. Do the differences between normal-beat and premature ventricular contraction contexts persist in the retained expert assignments actually used for patch feature replacement?
  2. How would the model perform if all patches used one shared expert of the same architecture? This would approximately match the cost of a single feature transformation, complementing all-expert aggregation, which already matches total expert parameters but uses more computation per patch.
  3. Why do contextual experts within the temporal Transformer fail to improve results consistently? Could existing training or routing statistics clarify how their use differs from that of patch-level experts?
2 comments
AuthorsOpenReview ↗

Scope of the Component Comparisons and Routing Analysis

Thank you for recognizing the complementary local and temporal roles and the overall transfer results. We address the two weaknesses and three questions below.

W1. Replacement versus flexible fusion. We agree that the reported result establishes a comparison with unit-weight residual addition, not with a flexible combination. PLARE and PLARE-Residual share the expert/router architectures, temporal Transformer, projection, preprocessing, and reconstruction/contrastive objectives; each variant has its own pretrained checkpoint (§4.2; D.1, Eq. 19). Replacement has higher mean C on four of five tasks under each protocol (Tables 3–4).

Learned scaling and gated fusion are not reported. We cannot conclude from the unit-residual comparison that discarding the original features is preferable to a learned combination.

W2. Fixed-position assignment. We agree that the fixed-assignment comparison changes both content dependence and the positional constraint. The mapping is approximately balanced and reused across recordings and epochs independently of waveform content (§4.2; D.1). CDR has higher mean C in all ten task–protocol comparisons using the same four-expert architectures and count, but the contributions of the two changes are not separated.

All-expert averaging retains the expert bank while increasing active computation; it also retains straight-through router learning and auxiliary losses (A.3; D.2). Each selection setting is pretrained separately. We agree that this is a complementary control rather than an isolation of content-dependent selection at matched active computation.

Q1. Retained expert assignments. Section 5.4 reports pre-capacity N/PVC selection–context association. Appendix G reports 16.056% rejected selections in the finite-capacity INCART analysis. With Top-1 selection, rejected patches retain their original features; tokens are not removed. The rate is not an estimate for downstream PTB-XL or CPSC.

We do not have a reported post-capacity analysis establishing whether the N/PVC difference persists in the retained assignments. The aggregate rejection rate cannot answer this. We acknowledge that the current analysis does not establish the corresponding association for executed expert transformations.

Q2. One shared expert. The submission does not report this model, so we cannot provide its performance. We agree that one shared expert would approximately match the active cost of one expert transformation while using fewer total expert parameters, complementing all-expert averaging. The current comparisons do not resolve whether the expert bank improves on that shared transformation.

Q3. Contextual experts. Section 5.5 and Appendix E (pp. 9, 24–25) report higher mean C for PLARE than PLARE-Joint on three of five tasks under LP and four under FT. Joint is higher on Super and Form under LP and CPSC under FT. This describes a lack of consistent improvement from the evaluated Top-1 contextual extension.

The submission does not provide module-level routing or training-statistic analyses that explain this pattern. We therefore cannot determine why contextual experts did not consistently improve performance. The reported comparison establishes the performance pattern, not its cause.

I thank the authors for their thoughtful and transparent response. While the rebuttal clarifies several experimental details, key controls, including flexible feature fusion and a shared-expert baseline, are still missing. The contributions of the core design choices therefore remain insufficiently isolated. I maintain my original score.

Reviewer_QBsxOpenReview ↗
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Paper summary

PLARE inserts a patch-level mixture-of-experts module between the convolutional patch feature extractor and the token projection of a masked-reconstruction plus contrastive ECG encoder. A content-dependent router selects an expert per patch, and the expert output replaces the original patch feature before a temporal transformer produces the record-level representation. The model is pretrained on MIMIC-IV-ECG, CODE-15% and IKEM and compared with ten baselines re-pretrained on the same pool, on four PTB-XL label sets (official folds) and CPSC2018, under linear probing and fine-tuning. PLARE is best on Sub, Rhythm, Form and CPSC and behind CREMA on Super; the largest gain is on Rhythm (+3.93 AUROC and +4.43 AUPRC under linear probing, Table 1). Ablations compare feature replacement with residual addition and content-dependent routing with fixed assignment (differences of 0.07 to 2.58 C points, Tables 3 and 4), vary the number of experts and the number selected per patch, and an INCART analysis shows that expert selection differs between normal and PVC beat contexts.

Critical strengths

1. The comparison is executed with unusual rigor.

All ten baselines are re-pretrained on the same unlabeled pool with a shared HPO space, PTB-XL uses the official patient-stratified folds, the controlled ablations use five downstream seeds per checkpoint, the routing analysis on INCART (Section 5.4) uses a permutation null with patient bootstrap, and the appendix adds patient-cluster paired bootstrap intervals for the CREMA comparison. The writing is careful not to over-claim.

2. The improvements on the harder label sets are consistent across both protocols.

PLARE leads on Sub, Rhythm, Form and CPSC under both LP and FT, with the largest gain on PTB-XL Rhythm (Table 1: +3.93 AUROC and +4.43 AUPRC under LP over the best baseline); the paired bootstrap interval in the appendix confirms that this gain excludes zero.

Critical weaknesses

I recommend rejection, although this is close to the borderline, for the two reasons below: the mechanism the paper proposes is not shown to be the source of the gains, and the inference protocol has a batch-dependence that is not addressed. I state in the Questions what would change my recommendation.

1. The novelty is thin, the mechanistic evidence for the two design choices is weak, and the experiments do not test the motivation.

The module is a standard sparsely-gated MoE (noisy Top-k, capacity filtering, load-balancing, z-loss, LIMoE entropy penalty) placed before token projection. The paper's contribution reduces to two configuration choices: placement, and replacement versus residual addition.

The effects attributed to them are small and inconsistent. Replacement beats residual addition by 0.07 to 2.17 C points with sign flips on Super-LP and CPSC-FT, and content-dependent routing beats fixed assignment by 0.33 to 2.58 points (both from Tables 3 and 4). Neither more experts (P = 8) nor more selected experts helps consistently (Figures 3, 4), and all-expert averaging (k = P, i.e., no content-dependent selection) is within noise of Top-1 on several tasks.

The control that would separate routing from capacity is missing. PLARE has 69.528M parameters versus 18.041M for CREMA (Table 5), with about 29.5M in the four experts (four 1920-1920-1920 MLPs, per the appendix architecture specification), and no variant with a single dense MLP of matched parameter count at the same position (or a no-MoE model with PLARE's patch extractor) is reported. Without it, the headline gains cannot be attributed to routing or to replacement.

The experiments also never test the motivation itself. Figure 1 motivates content-dependent routing with two cases: (i) a sporadic change within a recording (an isolated PVC among normal beats) and (ii) a morphology that recurs on every beat of one recording but differs from other recordings (persistent LBBB). Both cases establish only that waveforms differ, within and across recordings, which any input-dependent feature extractor already accommodates (the paper itself notes that shared patch processing "produces input-dependent features"). Neither case argues that different parameters, rather than one shared function of sufficient capacity, are needed; that is an empirical question, and it is exactly what the missing parameter-matched dense control would answer. Case (ii) in particular does not call for patch-level routing at all: if every patch of a recording goes to the same expert, the choice is a record-level one that the shared extractor and the transformer already make. Only case (i) requires different experts within one recording.

Even for case (i), no experiment stratifies the gain by local heterogeneity (recordings with versus without ectopic beats), no beat-level task is evaluated although INCART provides beat annotations, and the INCART analysis in Section 5.4 shows only that routing responds to beat context, not that it helps. Because the main text offers no such test, I checked the per-label comparison with CREMA in the appendix: under linear probing on CPSC2018 the gain is large for PVC (+8.651) and PAC (+5.926) but absent for LBBB (+0.084), which fits case (i) and not case (ii); the paper does not draw this connection. The label set most aligned with case (i) is PTB-XL Form, which contains PVC and PAC, yet it shows the smallest gain of the four tasks PLARE wins (Table 1: +0.69 AUROC and +2.02 AUPRC under linear probing), and the per-label comparison with CREMA is reported for Rhythm and CPSC but not for Form. The main text does not describe what the four label sets contain, so a reader cannot see which task tests the motivation.

2. Protocol concerns limit how much the comparisons can be trusted.

Section 3.2 states that capacity filtering discards excess expert assignments without reassignment, but does not say how the capacity is set. Because this determines what a patch's feature is, I checked the appendix: the capacity is computed from the number of patches in the routing batch (cap = ceil(n k alpha / E)), so a single ECG's representation depends on which other ECGs share its inference batch, and the appendix routing analysis reports 16.056% of selections rejected even at batch size 1, with the original feature passed through instead. This is undesirable for a representation encoder, and neither the downstream batch size nor the sensitivity to batch composition is reported anywhere.

External comparisons use a single downstream seed and no pretraining-seed variation (Section 4.3); only the CREMA comparison has intervals, and only in the appendix. Section 4.2 marks the three foundation-model baselines with superscripts, and the appendix confirms they are reimplementations with altered objectives (e.g., ECGFounder with the PU objective replaced by InfoNCE); they nevertheless appear under the original names in Tables 1 and 2.

PLARE is behind CREMA on PTB-XL Super, the most common benchmark, and the cost advantage in Table 5 holds only against the two largest baselines; relative to CREMA it has 69.528M versus 18.041M parameters and 4.611 versus 2.190 ms latency (Table 5).

Questions for authors

The paper's novelty is a placement choice for a standard module, so my recommendation rests on whether the empirical finding is real. I would raise my score only if Q1 shows that content-dependent routing beats a parameter-matched dense model by a margin that survives pretraining-seed variation (Q4); Q2 and Q3 would then determine how much of that finding is attributable to the motivation and whether the encoder is usable as a representation model.

  1. Please add two rows to Tables 3 and 4: (i) a dense variant with a single MLP of the same total parameter count as the four experts at the same position (no router), and (ii) a no-MoE variant (PLARE's patch extractor and transformer without the module). This is the minimal evidence that the gain comes from content-dependent routing rather than from added capacity.

  2. Please connect the results to the motivation of Figure 1: stratify the gain over CREMA and the loss from removing content-dependent routing by whether a recording contains ectopic beats (or by label groups such as PVC and PAC versus LBBB), and evaluate a beat-level task on INCART with frozen features. Please also report the per-label differences from CREMA on PTB-XL Form, in particular for PVC and PAC, and describe in one line each what the four PTB-XL label sets contain so that readers can see which task tests the motivation. If the benefit is confined to case (i), the paper should say so and drop case (ii) from the motivation.

  3. What batch size was used for downstream LP/FT inference, and how do the test metrics change when the batch composition or ordering changes, or when capacity filtering is disabled at inference? Please report the fraction of rejected assignments on the PTB-XL test set.

  4. Please provide at least two or three pretraining seeds for PLARE and CREMA on Rhythm and Sub so that the reported differences can be compared with pretraining variability.

  5. With lambda_con = 0.005 (appendix training settings), does the contrastive term contribute at all? An ablation with lambda_con = 0 would clarify what the objective actually is.

  6. Clarifications that do not affect the score: Figure 1 is hard to read (the nine thumbnails on the right are not recognizable as separate recordings, and "recurrent morphology across beats" and "variation across recordings" label the same panel); please label the adapted foundation-model baselines explicitly in Tables 1 and 2 (e.g., "ECGFounder-arch, InfoNCE"); please offer an interpretation of why gains concentrate on label sets with many rare classes (Rhythm, Sub) and vanish on Super; and please note in Section 5.4 that the INCART effect (delta JS = 0.0114 bits) shows selection differs by context but not that it helps.

1 comment
AuthorsOpenReview ↗

Architectural Evidence and Remaining Gaps in Attribution and Robustness

Thank you for recognizing the common-data comparison and transfer results. We address Q1–Q6 below.

Q1. Architectural evidence. The contribution is content-dependent patch-feature replacement before temporal modeling (§3.1). Tables 3–4 report higher mean C for replacement than unit-residual addition on 4/5 tasks per protocol, and for CDR than fixed assignment in all ten comparisons. More experts or selections are not consistently better (Figs. 3–4). Fixed assignment also imposes a positional constraint; all-expert averaging preserves the expert bank but increases active computation, with separate pretraining for each setting.

The requested same-backbone no-MoE and parameter-matched dense controls are not reported. CREMA-Max is a larger comparator (Table 5), not a substitute for these controls. We therefore cannot fully separate the expert bank’s benefit from added capacity relative to a shared dense transformation.

Q2. Motivation and labels. Local transformation precedes temporal modeling; A.4 excludes frequency estimates and rarity-dependent weights. Recurring morphology need not produce identical patches, but we have not isolated benefits from sporadic versus recurring morphology. The cited CPSC LP contrasts are correct. Table 13 also reports LBBB FT ΔC = +5.548 [0.846, 12.040], versus +0.084 [−3.486, 3.499] under LP, and PVC FT ΔC = +0.539 [−2.197, 3.286] despite its larger LP gain. These pointwise intervals are conditional on fitted models. FT should also be considered before concluding that gains are confined to sporadic ectopic beats; this does not establish a morphology-specific mechanism.

Super has 5 broad diagnostic categories, Sub 23 subclasses, Rhythm 12 rhythm labels, and Form 19 morphology labels including PAC/PVC (B.1; Table 10). Form’s absolute label results are reported, but Form–CREMA contrasts, recording-level stratification of CREMA-relative gains and CDR-removal losses, and frozen-feature INCART beat classification are not.

Q3. Inference. Actual LP/FT test-batch and capacity settings are insufficiently specified. A.3 disables inference routing noise, not explicitly capacity filtering. B.5’s training batch and F’s profiling batch do not identify the test-loader configuration. G’s 16.056% rejection rate applies to finite-capacity INCART analysis at batch size one, not downstream PTB-XL/CPSC. Batch composition/order sensitivity, capacity on/off comparisons, and PTB-XL test rejection rates are unreported. We cannot establish whether co-batching affected test predictions. Finite capacity can also reject assignments at batch size one.

Q4. Uncertainty. Controlled comparisons use five downstream seeds per fixed pretrained checkpoint (§4.3; B.5). Table 11’s CREMA-relative bootstrap intervals measure test-sampling uncertainty conditional on fitted models. External comparisons use one downstream seed; intervals do not cover all baselines. Evaluation of PLARE and CREMA on Rhythm/Sub across two or three pretraining seeds is unreported. Downstream repetitions and bootstrap do not establish robustness to pretraining variation.

Q5. Contrastive term. The objective includes three symmetric InfoNCE relations (§3.4; A.5), with λ_con = 0.005 (B.5). The coefficient alone does not quantify its effect. Architectural comparisons hold reconstruction and contrastive objectives fixed (§4.2), but λ_con = 0 is unreported, so the term’s incremental contribution is unknown.

Q6. Presentation and interpretation. We agree that Fig. 1 should distinguish within-record and across-record variation, and Tables 1–2 should use ECGFounder–CommonSSL, ECGFM–CPC, and ECG-FM–WCR. These are the adaptations described in §4.2/B.3, not reproductions of the complete original training regimes. Tables 1–2 also show higher AUROC/AUPRC than CREMA and CREMA-Max on Sub, Rhythm, Form, and CPSC under LP/FT.

Why gains vary across label sets, or whether rarity explains them, is not established. Sections 5.1/5.3 report the Super exceptions and that CREMA is smaller and faster; efficiency gains are relative to larger models. INCART ΔJS ≈ 0.0114 bits (§5.4; G) supports pre-capacity selection–context association, not its contribution to classification.

Reviewer_Uqn9OpenReview ↗
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Paper summary

This paper proposes PLARE, a patch-level MoE framework for self-supervised ECG representation learning, combining content-dependent routing (CDR) with feature replacement. The method reports promising results on PTB-XL and CPSC2018. However, concerns remain regarding baseline fairness, methodological novelty, and whether the experiments explain the observed improvements.

Critical strengths

The problem is relevant, and the reported improvements, particularly in AUPRC, are encouraging.

Both linear probing and fine-tuning are evaluated, with additional ablations and expert allocation analyses.

The architecture and implementation details are generally clear.

Critical weaknesses

Questionable SOTA comparisons. Although retraining baselines on a shared unlabeled corpus is reasonable, substantially modifying their original objectives raises concerns about baseline fidelity. How can the authors distinguish improvements attributable to PLARE from performance degradation caused by these adaptations? Could the authors additionally evaluate the original pretrained models on independent downstream datasets, or provide stronger parameter-matched comparisons?

Motivation–method mismatch. The paper motivates its design using sporadic PVCs and recurrent LBBB morphologies. However, routing decisions depend only on individual 240-ms patches, without explicitly modeling morphological recurrence or rarity. The proposed mechanism does not directly address the temporal characteristics highlighted in the motivation.

Insufficient ablation controls. The w/o CDR baseline uses fixed position-dependent random assignments, which is a weak alternative to learned routing. The replacement comparison only considers unit-weight residual addition, without adaptive scaling or gating. These experiments do not sufficiently isolate the benefits of the proposed design.

Incomplete mechanistic explanation. The INCART analysis establishes an association between expert selection and beat types, but does not demonstrate that this specialization improves classification. Furthermore, approximately 16% of assignments are rejected by capacity filtering, while the reported allocation statistics are computed before filtering.

Questions for authors

See weaknesses.

2 comments
AuthorsOpenReview ↗

ECG Transfer Gains Under a Shared Pretraining Protocol

Thank you for recognizing the transfer results and the relevance of ECG representation learning. We clarify what the comparisons test and address the four concerns below.

1. Baseline fidelity and the common-data comparison. Section 4.2 (p. 5) and Appendices B.2–B.3 (pp. 18–19) define the experiment as pretraining the methods on a shared unlabeled ECG pool. B.2 describes the shared HPO space, validation-based checkpoint selection, and method-specific input requirements. This provides a common evaluation setting, but it does not establish equivalence to the original models’ complete training regimes.

The adaptations differ in scope. ECGFM–CPC uses the original CPC objective alone, without the supervised classification and diagnostic text-generation objectives described in §2. ECG-FM–WCR follows the public pretraining example with the configuration and eligibility changes specified in B.3. ECGFounder–CommonSSL replaces diagnostic positive–unlabeled learning with two-view InfoNCE. Section 4.2 identifies these variants, and B.3 states that public checkpoints with known downstream-test overlap were excluded. The full adaptation names should also be explicit in Tables 1–2.

We agree that disclosing these adaptations does not measure their effect on performance. The submission does not compare them with the original pretrained checkpoints on independent cohorts or report the requested same-backbone, parameter-matched dense control. We therefore cannot establish that adaptation preserved the original models’ performance. Our comparisons are with the reported variants under the stated protocol.

The reported transfer gains also hold against CREMA and CREMA-Max: PLARE has higher AUROC and AUPRC on Sub, Rhythm, Form, and CPSC under LP and FT (Tables 1–2). CREMA-Max is larger than PLARE (177.601M versus 69.528M parameters, Table 5). These results provide evidence beyond the three adaptations, although they do not resolve the fidelity of those adaptations or replace a same-backbone capacity control.

2. Motivation and local routing. Sections 1 and 3.1 describe local, content-dependent feature construction followed by temporal contextualization. Sporadic PVCs and recurring LBBB morphology illustrate waveform variation within and across recordings. Appendix A.4 (p. 15) explicitly excludes morphology-frequency estimates and rarity-dependent weights; the router uses local patch features, while the Transformer models relationships among patch tokens.

This explains the intended division of labor, but the submission does not isolate benefits attributable to sporadic versus recurring morphology. We agree that the examples alone do not establish that conditional transformations are necessary or explain why they improve performance.

3. Component controls. PLARE and PLARE-Residual use the same expert/router architectures, temporal Transformer, projection, preprocessing, and reconstruction/contrastive objectives; the additive residual connection differs (§4.2; D.1, Eq. 19). Replacement has higher mean C, the average of AUROC and AUPRC, on four of five tasks under each protocol (Tables 3–4). This supports the comparison with unit-weight residual addition. Learned scaling and gated fusion are not reported, so the result does not establish superiority over a flexible combination.

CDR has higher mean C than the fixed-assignment control in all ten task–protocol comparisons using the same four-expert architectures and count (Tables 3–4). We agree that this comparison changes both content dependence and the positional constraint and does not separate their effects. All-expert averaging preserves the expert bank but increases active computation (D.2); it does not supply the missing shared-expert or parameter-matched dense comparison. Those results are not reported.

4. INCART analysis. Section 5.4 and Appendix G report an association between pre-capacity selections and beat context. Appendix G explicitly states that this does not establish a causal explanation for downstream performance. It also reports 16.056% rejected selections in the finite-capacity INCART analysis. Patches with no retained expert assignment keep their original features; tokens are not removed.

We agree that pre-capacity statistics do not establish whether the same N/PVC difference persists in the expert assignments actually retained. Those statistics are not reported, and the aggregate rejection rate cannot answer that question. The contribution of the observed specialization to classification gains is also not established.

Reviewer_Uqn9OpenReview ↗

Final Response

Thank you to the authors for their candid response. However, as the core experimental gaps remain unresolved, I believe the paper does not yet meet the soundness criteria for publication.

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

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