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Paper summary
This paper proposes MSVCR-MIL, a two-stage framework for weakly supervised whole-slide image classification that explicitly retrieves patch-level references from the training cohort during prediction. Stage 1 learns task-specific instance representations and relevance scores, after which Core Memory Construction builds a compact memory using high-response training patches and K-center coreset sampling. In Stage 2, CAPR constructs query-conditioned prototypes, BAGF fuses them with the original features, and DMR refreshes the memory during training. The framework is evaluated with ABMIL, CLAM, and TransMIL on CAMELYON16, Skin-PEAN, and Lung-HSFLA. Table 1 reports AUC improvements in all nine dataset–backbone combinations. Separately, retrieval distance yields lower AURC than 1−MSP in all nine combinations, while its comparison with predictive entropy is mixed.
Critical strengths
S1. The framework provides an explicit mechanism for incorporating training-cohort patch references into slide prediction. Its dimension-preserving fusion design is integrated into three different MIL backbones, demonstrating compatibility with different aggregation mechanisms.
S2. The evaluation covers breast, skin, and lung histopathology tasks. Table 1 reports AUC gains across all nine dataset–backbone combinations, with a mean improvement of approximately 1.14 percentage points. The fixed-checkpoint analysis in Figure 3 also provides useful evidence of inference-time use of the retrieval branch: disabling retrieval lowers AUC in eight combinations and leaves it unchanged in one.
Critical weaknesses
W1. The contribution is insufficiently positioned relative to closely related prototype-based MIL. Yu et al.’s PMIL, “Prototypical multiple instance learning for predicting lymph node metastasis of breast cancer from whole-slide pathological images” (Medical Image Analysis, 2023; DOI: 10.1016/j.media.2023.102748), discovers prototypes from training patches through unsupervised clustering and constructs slide representations by aggregating patch-to-prototype matching scores. The manuscript cites Rymarczyk et al.’s ProtoMIL but neither discusses nor compares with this separate PMIL study. MSVCR-MIL has identifiable differences, including query-conditioned prototypes, confidence-informed gated fusion, and dynamic memory refresh. However, the current evaluation does not establish the additional benefit of these differences over a closely related prototype-based alternative under comparable conditions.
W2. The experiments establish inference-time use of the retrieval branch but do not isolate the contributions of CAPR, BAGF, and DMR. Table 3(a) and Figure 3 intervene in a trained model by disabling memory or retrieval. These results demonstrate dependence on the branch at inference, while leaving its training-time benefits and the gains from individual components unresolved. Separately trained ablations against a simpler static-memory approach, with comparable features, backbones, memory capacities, and training budgets, would help establish which proposed designs account for the improvements.
W3. The memory-quality analysis does not yet connect feature coverage to downstream classification or diagnostic relevance. Table 3(b) shows that K-center selection improves feature coverage relative to random selection, but it does not report the corresponding classification comparison. Section 3.5 also describes an equal-capacity random-memory AUROC comparison whose result is absent from Table 3(a). Furthermore, Figure 2 presents within-slide contribution heatmaps rather than query–neighbor correspondences, leaving the pathological relevance of retrieved instances and the effects of incorrect matches insufficiently examined.
Additional Comment: Table 2 shows that Distance achieves lower AURC than 1−MSP in all nine combinations, but its comparison with Entropy is mixed: four better, four worse, and one tied. The abstract’s broader statement of consistent superiority over probability-based risk scores should therefore be narrowed to the comparisons supported by these results.
Questions for authors
Q1. What distinguishes MSVCR-MIL from Yu et al.’s PMIL, and what evidence under comparable evaluation conditions demonstrates the benefit of these differences?
Q2. What gains do CAPR, BAGF, and DMR provide over a simpler static-memory approach? Focused, separately trained ablations would help establish their contributions.
Q3. Please report the equal-capacity random-memory AUROC comparison described in Section 3.5. Does K-center’s feature-coverage advantage translate into better classification performance?
3 comments
AC. Scope of the risk-ranking claim. We agree that the original claim of consistent superiority over probability-based risk scores was too broad. We have removed that superiority statement from the abstract and introduction and replaced it with a neutral description of the risk-ranking evaluation. Because the binary-score consistency issue remains unresolved, we have also withheld the original nine-setting claim against 1−MSP alone. We apologize that the complete AURC recomputation is not yet available. Numerical entries in Table 6 and the associated aggregate comparisons are left unfilled. Appendix D specifies the checks to be completed: identical slide identifiers, labels, and fixed-model probabilities; consistent score definitions, normalization, precision, clipping, and tie handling; and verified column mappings and difference signs. We will supply the recomputed results in a subsequent revision and state the comparisons with 1−MSP and entropy separately, according to those results.
Q1. How MSVCR-MIL differs from PMIL. As explained in our response to W1, the distinction is how references enter prediction: the PMIL formulation described in your comment aggregates patch-to-prototype matching scores, whereas MSVCR-MIL constructs query-conditioned neighborhood prototypes and fuses them into the current MIL representation using a confidence-informed gate, with periodic memory refresh. The revised Table 1 adds a five-run comparison with PMIL, and the evaluated MSVCR-MIL model has higher mean AUROC on all three datasets. For Skin-PEAN and Lung-HSFLA, PMIL is a shared-feature multiclass adaptation; these results concern that implementation and do not constitute a reproduction of every setting in the original PMIL study. Table 2 separately examines design choices within MSVCR-MIL. Together these analyses distinguish the empirical complete-system comparison from the more limited evidence about individual mechanisms. The fuller manuscript positioning paragraph and implementation/protocol description remain planned, as acknowledged under W1.
Q2. Gains from CAPR, BAGF, and DMR. Table 2(b) reports five-run independently trained ablations on Skin-PEAN with CLAM-MB: disabling dynamic refresh, using uniform prototype weights, removing the gate’s confidence input, and fixing the patch and bag gates to their training-set means. These target DMR, CAPR weighting, and the confidence-dependent or adaptive aspects of BAGF, respectively. The full model achieves 93.43 ± 0.17% AUROC, compared with 92.88 ± 0.38% for each of the first three variants and 92.91 ± 0.35% for fixed mean gates. The corresponding paired gains are 0.55 [−0.10, 1.20] and 0.52 [−0.10, 1.14] percentage points. All intervals include zero, and fixed mean gates have slightly higher macro-F1 (65.41% versus 65.36%). We therefore present these as modest mean improvements, not proof that every component is individually necessary. The larger full-versus-static differences in Table 2(a), summarized under W2, concern the combined design.
Q3. Equal-capacity random memory and classification performance. Table 4(a) now includes the equal-capacity comparison. At fixed model weights, K-center versus random selection gives mean AUROC values of 88.05% versus 84.71% on CAMELYON16, 93.43% versus 92.88% on Skin-PEAN, and 92.32% versus 90.19% on Lung-HSFLA. The paired differences are +3.34 [0.03, 6.64], +0.55 [−0.10, 1.20], and +2.13 [−0.80, 5.07] percentage points, respectively. Thus, the mean direction is favorable in all three settings, but only the CAMELYON16 interval excludes zero. The measured mean nearest-neighbor distance is higher with K-center in all three settings. It is a mean distance, not a maximum covering radius, and the original candidate-bank coverage results in Table S2 use a separate protocol. We have therefore reported classification and distance outcomes separately: the current comparison supports a mean classification advantage, but does not establish that an improvement in the reported coverage measure caused it. Random-memory summaries are checkpoint-level summaries of three draws; the statistical sample size remains five checkpoints. We apologize that the distance-consistency audit is not yet complete. We will verify the distance definition, normalization, candidate pools, query sets, and aggregation procedure for both memories, and provide the audit outcome in a subsequent update. The currently observed direction is retained unless a verified calculation error requires correction.
Thank you for adding the PMIL comparison and the separately trained ablations. The reported gains over the evaluated PMIL implementation and the static-memory baseline strengthen the evidence for the full method. The PMIL implementation and multiclass adaptation still need more detail to assess comparability. The individual component ablations cover one dataset–backbone setting, and all four paired 95% confidence intervals include zero, leaving the gains attributable to each design choice uncertain. These results address important parts of my original review, and my overall rating remains 2 (Weak rejection).
We thank the reviewer for the constructive assessment and for identifying the need to position MSVCR-MIL against PMIL, separate training-time component evidence from inference-time dependence, and connect memory selection to classification and pathological correspondence. Below, we address each weakness and question, distinguish completed revisions from remaining work, and use the numbering in the current revised manuscript. W1. Positioning and comparison with PMIL. Thank you for identifying this closely related work. We have added Yu et al.’s PMIL to the baseline list and Table 1. Following the distinction raised in your comment, PMIL constructs slide representations by aggregating patch-to-clustered-prototype matching scores. MSVCR-MIL instead forms a prototype for each query from its retrieved neighborhood, incorporates neighborhood confidence into feature fusion, and refreshes the training-cohort memory as representations evolve. These are the intended distinctions; the complete-system comparison alone does not identify the contribution of each design. The five-run mean ± SD AUROC values for PMIL versus MSVCR-MIL with CLAM-MB are 0.775 ± 0.069 versus 0.881 ± 0.012 on CAMELYON16, 0.705 ± 0.016 versus 0.934 ± 0.002 on Skin-PEAN, and 0.777 ± 0.032 versus 0.923 ± 0.003 on Lung-HSFLA. The multiclass comparisons use a shared-feature adaptation of PMIL, so our conclusion is limited to that evaluated implementation. We apologize that the manuscript’s PMIL discussion remains brief; we will add a concise positioning paragraph and further implementation and adaptation details in a subsequent revision.
W2. Training-time comparisons and component attribution. We agree that disabling retrieval after training establishes inference-time dependence but does not isolate training-time contributions. We have therefore added separately trained static-memory comparisons and component ablations in Section 3.3 and Table 2. The static system uses fixed memory and a fusion coefficient of 0.5. Relative to this control, the full framework increases mean AUROC by 1.57, 2.98, and 3.90 percentage points for CLAM-MB on CAMELYON16, Skin-PEAN, and Lung-HSFLA, and by 8.14 points for ABMIL on CAMELYON16. Three of the four paired 95% intervals exclude zero; the CAMELYON16 CLAM-MB interval does not. Table 2(b) further examines independently trained variants of refresh, prototype weighting, and gating, as detailed in our response to Q2. These comparisons provide evidence beyond post-training removal, while the static-system contrast changes several design choices jointly. We therefore distinguish evidence for the complete framework from evidence for individual mechanisms, rather than assigning the complete gain to any single component. Training and resource measurements in Table 3 are reported separately and do not establish exact compute matching for every ablation.
W3. Memory quality, classification, and pathological correspondence. We have added the missing equal-capacity classification comparison in Table 4, using 1,200-entry K-center and random memories with fixed model weights over five checkpoints per dataset. The full results and intervals are discussed in our response to Q3. K-center has higher mean AUROC, but also higher mean nearest-neighbor distance; we therefore do not interpret these results as showing that smaller distances explain the classification benefit. The original coverage experiment is retained separately in Table S2. Table 5 now reports lesion/non-lesion neighbor agreement and verified-mismatch masking. Original retrieval yields 87.80 ± 1.24% AUROC versus 84.40 ± 1.55% after masking; lesion agreement changes from 34.39 ± 46.01% to 60.32 ± 29.11%. Masking verified mismatches is not replacement of correct neighbors with random mismatches, and the AUROC decrease does not establish pathological validity. We apologize that actual query–neighbor image panels are not yet complete. We will add real, annotated matched and mismatched examples in a subsequent revision; Figure 2 remains a within-slide localization visualization. The corresponding consistency checks are also pending. We apologize for this incomplete verification. We will check the per-slide continuous prediction scores, the mismatch definition, and the denominators used for neighbor agreement, and report the completed checks alongside the real neighbor examples. Any identified implementation or aggregation error will be corrected before the affected result is updated.