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Paper summary
The paper investigates how the composition of pathology foundation-model representations affects downstream fusion. It analyzes 13 encoders on TCGA-UVM through linear CKA, cross-feature Spearman correlations, and mean-baseline encoder ablations. The reported results suggest that adding encoders does not consistently improve performance and that fusion-method rankings vary across encoder compositions.
Motivated by these observations, the authors propose CoR-Fuse. Encoder-specific projections are initialized through mean-fusion training, after which a shared MLP conditions on each encoder’s slide descriptor and the cross-encoder mean to generate slide-specific weights. These weights fuse coordinate-aligned patch embeddings before downstream aggregation.
Evaluation covers UVM D3/M3 classification and BLCA TP53 mutation prediction, using patient-level five-fold cross-validation, multiple encoder compositions, baseline comparisons, and component ablations. CoR-Fuse achieves competitive performance with low additional fusion overhead and lower observed dispersion across the evaluated UVM compositions.
Critical strengths
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Useful comparison across representation compositions. Evaluating 13 pathology encoders and comparing fusion strategies under three fixed-size compositions helps separate encoder count from encoder identity. The changes in method ranking caution against assuming that more encoders or more complex fusion automatically improves performance. This is useful evidence for practitioners selecting among available pathology representations.
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A simple fusion mechanism with low additional overhead. CoR-Fuse generates one set of weights per slide while retaining patch correspondence for downstream aggregation. In Table 1, its router adds approximately 0.06M trainable parameters over mean fusion and has lower reported downstream FLOPs than the evaluated attention alternatives. This makes the method practically attractive when foundation-model embeddings are already available; the reported costs exclude backbone feature extraction.
Critical weaknesses
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The mean-baseline LOO analysis does not sufficiently establish encoder utility or synergy. Equations (5)–(6) quantify a fixed classifier’s sensitivity to replacing an encoder representation with a mean baseline. This does not by itself establish uniquely supplied information or the predictive benefit of removing an encoder and retraining. Mean substitution may disrupt correlations among encoder representations, while classifier nonlinearity can produce nonzero interactions even for redundant information. The manuscript insufficiently specifies baseline estimation, replacement space, the reference predictor, and the target-class convention, and does not validate its conclusions against alternative baselines or reference models.
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The incremental contribution of consensus routing is not sufficiently isolated or demonstrated against closely related methods. The paper does not directly compare CoR-Fuse with the cited AdaFusion and Shazam, both of which investigate adaptive integration of pathology foundation models. Component ablations cover only one five-encoder composition and omit a full consensus-by-warm-start factorial comparison. The interpretation of the cross-encoder mean as semantic consensus also lacks direct validation. Moreover, the BLCA AUC gain over mean fusion is only 0.01, Table 1 reports dispersion across compositions rather than uncertainty in paired improvements, and the full-model BLCA results in Tables 2 and 3 are inconsistent. Parameters and downstream FLOPs support low fusion overhead, but unreported latency and peak memory leave practical efficiency incompletely substantiated.
Questions for authors
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Can the authors explicitly define the mean-baseline LOO protocol, including baseline estimation, replacement space, reference predictor, target class, and evaluation split, and substantiate its interpretation as encoder utility rather than intervention sensitivity? Supporting evidence could include robustness to alternative baselines/reference models or duplicated-encoder and removal-and-retraining controls. Please also provide held-out slide-level LOO distributions and signed pairwise interaction summaries with uncertainty, including the signed results mentioned in Figure 6.
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Can the authors explain and experimentally validate why the cross-encoder mean provides useful semantic consensus, using a capacity-matched nonlinear gate without cross-encoder context and a consensus-by-warm-start factorial ablation? Please match nonlinearities, encoder biases, initialization, and total optimization budgets, evaluate across the three composition regimes, and provide training curves or failure-rate evidence for the claimed optimization-stability benefit.
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Can the authors add direct experimental comparisons with both AdaFusion and Shazam on the evaluated tasks, using identical patient splits and matching encoder compositions, feature availability, downstream heads, and tuning budgets where applicable? Please document necessary method-specific adaptations and report predictive performance alongside computational cost, so that the contribution beyond existing adaptive pathology-foundation-model fusion can be assessed.
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Can the authors provide paired performance differences and uncertainty against mean/global fusion and an inner-validation-selected single encoder, clarify the aggregation of folds, seeds, and compositions, and reconcile the BLCA full-model results in Tables 2 and 3? Please also report per-slide latency/throughput, peak GPU memory, and total training time including warm start under matched hardware, precision, and patch counts, distinguishing cached-feature fusion from backbone extraction, to substantiate the practical lightweight claim.
4 comments
Response to W2
We thank the reviewer for the constructive and detailed comments. We have revised the manuscript and expanded the experiments accordingly.
We acknowledge the relevance of AdaFusion and Shazam, which also investigate the adaptive integration of multiple pathology foundation models.
Regarding implementation, the publicly accessible AdaFusion repository indicating that the code will be released in the future.
Shazam, in contrast, require extracting intermediate-layer representations from the teacher backbones and implementing its multi-scale aggregation and distillation pipeline, rather than simply replacing the fusion module while keeping the existing feature inputs and downstream protocol unchanged. We therefore distinguish Shazam as a complementary framework-level approach rather than treating it as a directly interchangeable fusion-head baseline.
Our evaluation includes several categories of fusion baselines: Fixed aggregation: Mean fusion, Concatenation, Global learned weighting: Global weighting fusion Slide-specific weighting: Gated fusion and Attention-based fusion: Cross attention and Self attention.
We also compare CoR-Fuse with three pathology-specific methods: Meta-Encoder(Gaoetal.,2026), FuseCPath(Yangetal.,2025) and ELF(Luoetal.,2026) in pathology research field. To further extend the comparison to general multimodal feature fusion, we also compared EmbraceNet (Choi&Lee,2019).
Following the reviewer's suggestion, we add the baseline results in ablation study:
Table. Ablation study of CoR-Fuse components.
| Method | TCGA-UVM AUC | TCGA-UVM AUPRC | TCGA-BLCA AUC | TCGA-BLCA AUPRC |
|---|---|---|---|---|
| w/o Both | ||||
| w/o Consensus | ||||
| w/o Warm Start | ||||
| CoR-Fuse |
The cross-encoder mean is constructed by averaging the projected representations of different foundation models in a shared dimensional space. In our method, it serves as a reference representation that provides shared cross-encoder context to the routing network.
We agree that the AUC improvement over Mean Fusion on TCGA-BLCA is modest (0.01). We do not intend to claim that CoR-Fuse consistently produces large predictive performance gains over simple fusion strategies across all datasets.
Our main objective is to investigate whether lightweight consensus-conditioned routing can achieve competitive performance across different foundation-model compositions without introducing the substantial additional parameters and computational cost associated with more complex attention-based fusion mechanisms.
Response to Q1-Q4
We thank the reviewer’s questions.
Response to Q1
In our analysis section, the reference predictor is trained using the complete set of encoders and is kept fixed throughout the LOO evaluation. For each held-out slide, we replace the representation of one encoder with its corresponding encoder-specific mean baseline, while keeping the representations of all other encoders unchanged. The prediction difference is then evaluated using the target-class one-vs-rest logit margin, defined as the logit of the ground-truth class minus that of the alternative class. Importantly, no model retraining is performed after representation replacement.
Overall, we have narrowed the role of this analysis to an auxiliary diagnostic of sample-dependent predictor sensitivity, rather than using it as direct evidence of encoder-specific predictive utility.
Response to Q2
We clarify that the cross-encoder mean is computed by averaging the projected slide-level descriptors of all encoders and is used as a shared cross-encoder reference to condition the routing network. We do not claim that this arithmetic mean constitutes a semantically validated consensus representation. Rather, its purpose is to provide cross-encoder context when estimating sample-specific routing weights.
Regarding the component contributions, we have included a factorial ablation of consensus and warm-start, as detailed in our response to Weakness 2 and the revised ablation table.
Then we narrowed the corresponding claims and avoid interpreting the cross-encoder mean as intrinsically semantic or the warm-start strategy as a demonstrated optimization-stability guarantee.
Response to Q3
In response to W2, we discuss the reasons why we did not select these two methods for comparison.
In particular, we clarify that AdaFusion and Shazam operate under different fusion paradigms and feature requirements from CoR-Fuse. Consequently, reproducing these methods using only the final-layer patch embeddings employed by our current pipeline would not constitute a faithful implementation, particularly for Shazam, which requires additional intermediate features and its associated multi-scale training procedure.
Response to Q4
Regarding peak GPU memory, we agree that memory consumption is an important aspect of practical computational efficiency. However, our efficiency analysis is specifically designed to characterize the additional computational overhead of the cached-feature fusion stage, rather than the resource requirements of the entire multi-encoder pipeline.
The measured GPU memory usage would depend not only on the fusion module itself but also on the handling and residency of these shared input feature tensors.
I thank the authors for the response. The clarified LOO protocol and the narrowed interpretation of the LOO, interaction, and cross-encoder mean analyses make the claims more accurate, and I accept that AdaFusion's code is not yet public. However, the rebuttal adds little new empirical evidence. The factorial ablation table contains no numbers, and no capacity-matched gate without cross-encoder context is provided. Since the authors no longer interpret the mean as semantic consensus, such a comparison is needed to show that consensus conditioning adds anything over standard context-conditioned gating. With the contribution now framed as competitive, lightweight fusion and a 0.01 AUC gain on BLCA, paired fold-level differences with confidence intervals, a comparison against the best single encoder, and runtime measurements (fusion latency and total training time, excluding backbone extraction) are needed, but none were provided. The inconsistency in the BLCA results between Tables 2 and 3 was also not addressed. I therefore maintain my score.
Response to W1
We thank the reviewer for this important and technically well-founded comment. We agree that our original interpretation of the mean-baseline LOO and pairwise interaction analyses was too strong.
We now describe the LOO results as baseline-dependent, fixed-predictor sensitivity analysis, rather than as a direct measure of encoder-specific predictive utility. Similarly, we clarify that the pairwise inclusion–exclusion score captures the non-additive response of the fixed predictor to pairwise baseline replacement. We no longer interpret definitive evidence of intrinsic synergy or interference between encoders.
Importantly, we emphasize that this analysis is an auxiliary diagnostic rather than the principal evidence for the proposed fusion method. The motivation for adaptive routing is supported more broadly by the observed variation in fusion performance across FM compositions and by the sample-dependent behavior of the fixed-predictor sensitivity analysis. We have revised the manuscript to ensure that the LOO and pairwise interaction results are not used to make stronger claims than their experimental design supports.