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Under review as a conference paper at ICLR 2027

Multi-Slide Views and Clustering-Inspired Memory Retrieval for Weakly Supervised Whole-Slide Image Classification

Abstract

When multiple instance learning (MIL) is applied to whole-slide image (WSI) classification, the large, variable-length instance sequences prevent multiple slides from being combined within a single batch for training. The difficulty of simultaneously incorporating information from multiple independent samples is a characteristic of this field. Moreover, the pathological significance of cross-sample view associations has not been established. To address these issues, we propose MSVCR-MIL, a two-stage weakly supervised classification framework combining multi-slide views and clustering-inspired memory retrieval. In the first stage, the model learns instance representations and attention scores under slide-level supervision. Core Memory Construction (CMC) collects high-response instances from different training slides to establish morphological references from multi-slide views and constructs a compact memory through clustering-inspired K-center coreset sampling. In the second stage, Confidence-Aware Prototype Retrieval (CAPR) generates query-conditioned prototypes and retrieval confidence scores, while Backbone-Adapted Gated Fusion (BAGF) adaptively fuses the original features with the retrieved prototypes, allowing cross-slide references to contribute to slide-level prediction. During training, Dynamic Memory Refresh (DMR) updates the instance memory and periodically reconstructs the coreset, keeping the references up to date as task representations evolve. Results on three datasets covering breast cancer, lung cancer, and skin diseases demonstrate that MSVCR-MIL consistently improves WSI classification performance (mean ). Retrieval-distance-based prediction risk in MSVCR-MIL is consistently lower than that obtained using methods based solely on predicted probabilities (mean ), indicating that it can provide complementary information for identifying prediction errors. Overall, explicit cross-slide morphological references and clustering strategies offer a feasible approach to enhancing weakly supervised WSI classification and assessing prediction risk.

Primary area:
unsupervised, self-supervised, semi-supervised, and supervised representation learning
Keywords:
Weak supervision, Multiple instance learning, Whole-slide imaging, Multi slide view, Cluster based

Reviews

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1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
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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

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.

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).

Reviewer_1chiOpenReview ↗
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Paper summary

The paper proposes MSVCR-MIL, a two-stage framework for weakly supervised WSI classification. It builds a compact memory from high-response training patches using K-center sampling, retrieves query-dependent prototypes, and combines them with the original features through learned gating. It refreshes the memory during training. Across CAMELYON16, Skin-PEAN, and Lung-HSFLA with three MIL backbones, the authors report a mean AUC improvement of 1.14 percentage points.

Critical strengths
  1. The authors provide an explicit, retrievable memory of training-cohort patches and connect those references to prediction through query-dependent fusion. This is a useful direction for incorporating information beyond the current slide.

  2. Table 1 reports accuracy and AUC improvements across all nine dataset/backbone combinations, empirically demonstrating the method's effectiveness. The fixed-checkpoint retrieval-off experiments also provide evidence that the trained models do make use of the memory branch during inference.

Critical weaknesses
  1. The CAMELYON16 risk-ranking results require reconciliation. For binary classification, 1−MSP and standard predictive entropy should produce identical rankings and AURC when computed from the same slide-level probabilities with consistent tie handling. Table 2 reports TransMIL AURCs of 0.0691 for 1−MSP and 0.0280 for entropy. The manuscript does not explain this difference, which affects confidence in a central claim about retrieval-based risk assessment.

  2. The evidence does not yet establish that the gains justify the added design complexity and training. The paper does not clearly report the training budget and computational cost of the proposed method.

  3. Minor ones: DTFD-MIL's CAMELYON16 AUC of 82.77% is substantially below its published results. Statistical analysis support for Table 1 and Figure 3 also needs strengthening. These issues make the reliability and attribution of the gains difficult to assess.

Questions for authors

Please check the Critical Weakness section first.

Further questions:

  1. The abstract motivates MSVCR-MIL by stating that variable-length WSI bags prevent multi-slide mini-batch training. However, sampling the same number of patches from each WSI produces equal-length bags, allowing multiple slides to be processed together in a single training batch, for example, in [1]. What unresolved limitation motivates the proposed framework beyond this existing batching solution, and how does explicit cross-slide retrieval address it? Please also consider evaluating the existing baselines by sampling the same number of patches from each WSI and training with multiple WSIs per batch, then comparing their classification performance and computational cost with MSVCR-MIL.

  2. What evidence supports the necessity of the overall design? Please clarify the proposed method's training budget, computational cost, and memory requirements.

[1] Zhang, Tianyi, et al. "PathRWKV: Enhancing Whole Slide Image Inference with Asymmetric Recurrent Modeling." IEEE Transactions on Medical Imaging (2026).

3 comments

We thank the reviewer for the constructive assessment and for identifying concerns about risk-score consistency, computational cost, and statistical reliability. We have added repeated-run classification results, controlled comparisons, and resource measurements. Below, we distinguish these completed additions from the protocol checks and repeated-run analyses that remain to be completed.

W1. Consistency of binary risk scores and AURC We agree with this observation. For binary probabilities (p, 1−p), predictive entropy is a strictly increasing function of 1−MSP in exact arithmetic; identical slide predictions and consistent tie handling should therefore yield identical rankings and AURC. We apologize that the discrepancy in the original CAMELYON16 results has not yet been reconciled. We have removed the numerical risk-ranking entries from the revised Table 6 and withdrawn the aggregate superiority statement from the abstract and introduction. Section 3.7 now explicitly marks the results as pending recomputation. Appendix D specifies the planned checks: identical slide identifiers, labels, and predictions; probability normalization, precision and clipping; consistent handling of tied scores; score-to-column mappings; and the sign of Distance-minus-1−MSP differences. It also specifies the AURC calculation and expected random ordering within ties. These are planned checks, not completed validation. We will provide the recomputed values and revise the interpretation after reconciliation; no superiority over either probability-based score is claimed from the currently withheld results.

W2. Whether the gains justify additional training and complexity We agree that the benefit must be assessed together with its cost. Section 3.4 and Table 3 now report the sampled CLAM-MB baselines and MSVCR-MIL, including classification statistics, training time, GPU memory, parameter counts, and forward latency. The recorded 40-epoch stage takes 25.82 minutes for MSVCR-MIL, versus 3.04 and 2.21 minutes for batch-1 and batch-4 CLAM-MB; warm-up and initial memory construction are additional. These resource records are separate from the five classification runs. The results indicate a trade-off: MSVCR-MIL has higher mean accuracy and macro-F1, whereas batch-1 CLAM-MB has higher mean AUROC, lower log loss, and lower measured cost. The paired AUROC difference from batch 1 is −0.67 percentage points, with a 95% interval of [−3.54, 2.20]. Section 3.4 states this trade-off explicitly. Because the sampled baselines and full model differ in input configuration, and batch sizes imply different update counts, this comparison does not establish an advantage at equal computational budget or isolate a pure batching effect.

W3. DTFD-MIL reproduction and statistical support for Table 1 and Figure 3 (i) DTFD-MIL. The updated five-run CAMELYON16 AUROC is 0.816 ± 0.004 in Table 1; the original 0.8277 result is retained separately in Table S1. Repetition measures variability under our current implementation but does not explain the discrepancy with the published result. We apologize that this protocol-level explanation is incomplete. We will supplement the available implementation details and identify documented differences in features, splits, patch processing, training, and evaluation. We do not present the new mean as an exact reproduction of the published score. (ii) Table 1. The benchmark now reports five-seed means and SDs, with unavailable statistics marked by dashes. Table S4 additionally reports four paired comparisons and unadjusted 95% t-confidence intervals (df = 4). The CAMELYON16 CLAM-MB interval excludes zero; the Skin-PEAN and Lung-HSFLA intervals include zero. Table S4's CAMELYON16 ABMIL interval uses a different set of baseline records from updated Table 1 and must not be transferred to that benchmark comparison. (iii) Figure 3. This remains the original fixed-checkpoint intervention, not a new five-run statistical analysis. We apologize that repeated-checkpoint uncertainty estimates for its AUROC and NLL changes are not available. We retain the figure as descriptive evidence that the trained model uses retrieval at inference. The repeated-run classification statistics and separately trained ablations address different questions and do not replace uncertainty estimates for this intervention.

Q1. Motivation beyond fixed-size patch sampling and multi-slide batching We agree that fixed-size sampling enables multi-slide batching. Our intended motivation is to make training-cohort morphological references explicitly retrievable and usable by the current slide, beyond processing several slides in one batch. Query-conditioned retrieval and gated fusion provide that mechanism. The abstract still contains the earlier overgeneralized batching statement, and we apologize for this inconsistency. We will replace it with: “Fixed-size patch sampling enables multi-slide batching; our aim is to make cross-slide morphological references explicitly retrievable and usable for prediction.” Section 3.4 and Table 3 now evaluate CLAM-MB with 4,096 sampled patches per slide and batch sizes of 1 and 4. Both sampled baselines share a 10-epoch warm-up checkpoint and continue for 40 epochs, producing 10,800 and 2,720 updates. Their mean AUROCs are 88.72% and 84.62%, versus 88.05% for MSVCR-MIL; resource measurements are also reported. PathRWKV has been added to Table 1 and the references. We do not infer equal-budget superiority or a pure batch-size effect: the full model retains its original input configuration, and optimization counts differ. The current evaluation concerns explicit retrieval of training-cohort references; ordinary multi-slide batching is feasible with fixed-size sampling.

Q2. Necessity of the overall design, training budget, and memory requirements We have added separately trained static-memory comparisons and component ablations in Section 3.3 and Table 2. Relative to fixed memory with 0.5 fusion, the full system has higher mean AUROC in all four evaluated settings; three paired intervals exclude zero. On Skin-PEAN, disabling refresh, using uniform prototype weights, removing gate confidence, or fixing gates to training-set means yields full-minus-control AUROC differences of 0.52–0.55 percentage points, with all four intervals including zero. These results distinguish a system-level comparison from individual-component evidence; they do not establish that every component is indispensable. Table 3 provides the cost accounting: the 25.82-minute second stage includes eight refreshes totaling 175 seconds, while the 5.76-minute warm-up and 45-second initial memory construction are additional. MSVCR-MIL has 0.923 million trainable parameters, 5.170 GiB peak allocated GPU memory, a 28.71 MiB retrieval buffer, and a 2.34 MiB initial 1,200-entry coreset file. These quantities describe different resource categories. Timing records are separate from the five classification runs, with one recorded full-model training measurement. These measurements describe the evaluated configurations and allow the classification gains to be considered alongside their recorded cost.

I thank the authors for the additional comparisons, ablations, and cost reporting. The reported results strengthen the evidence for the full method. However, I remain uncertain whether the adaptive retrieval design offers sufficient benefit over simpler, comparably trained alternatives to justify its added complexity and computational cost. I therefore maintain my original score.

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Paper summary

This paper proposes MSVCR-MIL, a two-stage framework for weakly supervised whole-slide image classification that incorporates explicit cross-slide instance retrieval. The method first trains a conventional MIL backbone and constructs an external memory bank from high-response patches across training slides. K-center coreset sampling is used to maintain compact and representative memory. During the second stage, query-conditioned prototypes are retrieved from memory and integrated with the original patch features through confidence-aware gated fusion. A dynamic memory refresh mechanism updates the stored representations during training.

The framework is evaluated with ABMIL, CLAM, and TransMIL on three pathology datasets. The authors report consistent but generally modest classification improvements, alongside additional analyses of retrieval-based risk ranking, memory selection, and inference dependency.

Critical strengths
  1. The paper addresses a meaningful limitation of conventional MIL by enabling explicit retrieval of morphological references from other training slides. The proposed framework is compatible with multiple MIL backbones, and the consistent improvements across three datasets suggest that cross-slide retrieval can provide complementary information beyond within-slide aggregation.

  2. The paper provides useful empirical evidence that the retrieved memory contributes to prediction. The fixed-checkpoint retrieval intervention and memory selection analyses support the practical utility of external references. Additionally, the retrieval-based risk ranking experiments offer an interesting secondary application beyond classification accuracy.

Critical weaknesses
  1. The methodological novelty is limited, as the framework mainly combines established techniques, including attention-based patch selection, K-center coreset sampling, nearest-neighbor retrieval, gated feature fusion, and memory updating. The experiments do not sufficiently isolate the benefits of the proposed components. Comparisons with static memory, simple nearest-neighbor feature fusion, and training without dynamic memory refresh would be important to establish the necessity of the complete framework.

  2. The classification improvements are relatively modest, and their statistical reliability is insufficiently established. Several AUC gains in Table 1 are below one percentage point, while the confidence intervals for memory removal in Table 3(a) include zero on two of the three datasets. Repeated-run results and statistical comparisons are needed to demonstrate that the improvements are robust and not primarily attributable to additional training or model capacity. The risk-ranking results should also be interpreted more carefully, since retrieval distance does not consistently outperform predictive entropy.

Questions for authors
  1. Were the baseline MIL models trained for the same total number of epochs and with comparable parameter budgets as the two-stage MSVCR-MIL models? Are repeated-run performance statistics available for the classification results in Table 1?

  2. Do the authors have results that independently disable Dynamic Memory Refresh or replace confidence-aware gated fusion with a simpler retrieval-based aggregation? Such results would materially clarify whether the improvement originates from the proposed mechanisms or from generic memory retrieval.

  3. How should the reported retrieval-based risk-ranking improvement be interpreted relative to predictive entropy? Table 2 shows several settings where entropy performs better than retrieval distance. Is the intended claim an improvement over maximum-softmax-probability ranking rather than consistently superior performance over both conventional uncertainty measures?

2 comments

We thank the reviewer for recognizing the value of explicit cross-slide references and for identifying the need for component controls, repeated-run evidence, and a more careful interpretation of risk ranking. We have expanded the experimental reporting and distinguish mean improvements from statistical support. The planned risk-score verification remains incomplete and will be supplied in a subsequent update.

W1. Methodological contribution and controls for the complete framework Thank you for identifying the need to separate the contribution of the complete retrieval framework from that of its established building blocks. Our contribution concerns their integration into query-conditioned cross-slide retrieval and adaptive fusion; we do not claim that coreset sampling or nearest-neighbor retrieval is itself new. Section 3.3 and Table 2(a) now compare the full model with a separately trained static-memory system using fixed 0.5 fusion. The mean AUROC gains are 1.57, 2.98, and 3.90 percentage points for CLAM-MB on CAMELYON16, Skin-PEAN, and Lung-HSFLA, and 8.14 points for ABMIL on CAMELYON16. Three paired 95% confidence intervals exclude zero; the CAMELYON16 CLAM-MB interval includes zero. Table 2(b) additionally reports independently trained Skin-PEAN ablations of dynamic refresh, prototype weighting, the gate's confidence input, and adaptive gating. Their 0.52–0.55-point mean AUROC differences all have intervals containing zero, so we do not present every component as individually established as necessary. We apologize that the current revision does not include a dedicated simple single-nearest-neighbor fusion experiment. The static-memory comparison and independently trained simplifications provide a partial response to this request; we have limited the component-level conclusions to those evaluated controls.

W2. Repeated-run reliability, inference interventions, and risk-ranking scope We agree that mean improvements alone do not establish reliability. Table 1 now reports available five-run means and standard deviations, with unavailable statistics explicitly marked. Original-protocol results are retained separately in Table S1. Appendix E and Table S4 provide four paired-run comparisons with unadjusted 95% t-confidence intervals. The AUROC gains are +3.07 [0.97, 5.17] and +6.64 [1.59, 11.68] percentage points for CAMELYON16 CLAM-MB and ABMIL, respectively, and +0.52 [−0.11, 1.15] and +1.56 [−0.22, 3.34] for Skin-PEAN and Lung-HSFLA CLAM-MB. The latter intervals include zero. The CAMELYON16 ABMIL interval applies only to the paired records in Table S4, whose baseline differs from the updated Table 1 benchmark. The original memory-removal results remain in Table 4(c), including the intervals containing zero. We interpret them as fixed-model interventions, not as uniform evidence of training-time gains. Resource measurements and partial training controls are provided in Table 3, but do not fully exclude budget or capacity effects across all settings. Unavailable five-run statistics remain explicitly marked in Table 1. We apologize that the planned risk-score verification is not yet complete; we will supply the recomputed results in a subsequent update. As detailed in R1-Q1 and R1-Q3, we clarify the available budget information and have withdrawn the previous numerical risk-superiority claim.

Q1. Training and parameter budgets, and availability of repeated runs Repeated-run statistics are now available for the reported entries in Table 1: each populated performance cell gives a five-run mean and standard deviation, while missing statistics are marked explicitly. Appendix E preserves the four paired-run comparisons and their confidence intervals. These paired results are not interchangeable with every baseline record in the broader benchmark. For budget reporting, Table 3 specifies that the sampled CAMELYON16 CLAM-MB baselines share a 10-epoch warm-up and train for 40 additional epochs, with 10,800 and 2,720 updates for batch sizes 1 and 4. The reported trainable parameter counts are 0.791 million for CLAM-MB and 0.923 million for MSVCR-MIL. The sampled baselines use 4,096 patches per slide, whereas MSVCR-MIL retains its original input configuration. The resource measurements are separate from the five-run classification statistics. Consequently, these comparisons do not establish equal total optimization budgets or parameter-matched controls across every backbone and dataset. We apologize that the available documentation does not establish complete budget equivalence across all settings. We will supplement the description of the recorded training stages, optimizer updates, and parameter budgets. We retain the available repeated-run statistics and explicitly mark missing entries, without presenting the reported comparisons as fully parameter- or compute-matched.

Q2. Independent dynamic-refresh and simplified-fusion ablations Yes. Section 3.3 and Table 2(b) now report independently trained Skin-PEAN CLAM-MB variants that disable dynamic memory refresh, use uniform prototype weights, remove the gate's confidence input, or replace adaptive gates with their training-set means. The full model has mean AUROC 93.43%, compared with 92.88% for the first three variants and 92.91% for fixed mean gating. The corresponding full-minus-control gains are approximately 0.55 and 0.52 percentage points, but all four paired 95% confidence intervals include zero. We therefore describe favorable mean directions without claiming that each mechanism has an independently established benefit. Fixed mean gating also has slightly higher mean macro-F1, 65.41% versus 65.36%, which remains reported. Table 2(a) provides the complementary comparison against a separately trained static-memory system with fixed 0.5 fusion across four settings, as summarized in R1-W1. This addresses a simpler retrieval design but does not by itself isolate every component. A dedicated single-nearest-neighbor fusion control is not included; the current evidence concerns the static-system comparison and the four independently trained variants above.

Q3. Interpretation relative to predictive entropy and maximum probability Thank you for pointing out that the original statement was broader than the reported comparisons justified. We have withdrawn the previous numerical claim of consistent superiority and the aggregate AURC reduction. The abstract and Introduction now state only that retrieval distance is additionally evaluated as a reference-based score for prediction-risk ranking. We do not currently claim superiority over either predictive entropy or maximum-softmax-probability ranking. The revised Section 3.7 retains the evaluation definition, while Table 6 leaves the numerical entries pending recomputation. Appendix D specifies that all three scores will use identical slide identifiers, labels, and fixed-model predictions, with a common AURC definition and consistent handling of tied scores. The checks will cover probability normalization, numerical precision, score-to-column mappings, and the sign of the reported differences. In binary classification, the probability-based rankings should agree under consistent computation. We apologize that this verification is not yet complete. We will provide the recomputed AURCs and separate comparisons against both probability-based scores in a subsequent revision, and limit any resulting claim to those verified results.

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Title: Gentle Reminder: Discussion Closing Soon

Dear Reviewer,

As the discussion period closes soon, we kindly encourage you to engage in the discussion and share any remaining thoughts or feedback.

Thank you for your time and valuable contributions!

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