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Paper summary
The paper studies knowledge transfer from 20× to 5× representations for whole-slide prediction. It separates three questions: whether actual teacher targets help the task, whether low-magnification inputs can predict those targets, and whether downstream models benefit from the predictions. Experiments cover regional mean and spatial targets, direct and residual prediction, native-feature retention, and teacher objectives during encoder adaptation. Across five classification/grading and five survival cohorts, the authors find that better reconstruction does not consistently improve task performance and that feature delivery affects the outcome.
Critical strengths
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The paper asks a meaningful question and provides a coherent diagnostic framework. Separating teacher usefulness, student predictability, and downstream benefit helps avoid attributing successful transfer to reconstruction accuracy alone.
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The experiments cover ten cohorts spanning classification, grading, and survival analysis. They include both frozen-feature prediction and encoder adaptation.
Critical weaknesses
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The analysis gives limited guidance on choosing a target, predictor, or strategy for supplying features to a downstream model on a new task. Teacher features come from one pathology encoder, and additional encoder evaluations would help establish which findings carry over. Measured end-to-end speed and memory use, and a comparison with compact encoders operating at 20×, would strengthen the efficiency motivation.
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The native-versus-teacher comparisons change both magnification and the feature-extraction pipeline (Appendix B.2), so the effect of magnification alone is unclear. Patient independence is also unverified for several slide/image-level partitions. The authors acknowledge that standard deviations across overlapping holdouts do not establish statistically reliable population improvements. Some test groups and event counts are small. These comparisons need targeted validation and more cautious claims about population-level gains.
Questions for authors
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To strengthen the practical motivation, please identify the deployment bottleneck motivating this work and position it against model compression, including compact pathology encoders such as [1]. On representative tasks, compare 20× and 5× pipelines, including a compact 20× encoder, under matched tissue coverage and hardware. Report predictive performance, end-to-end inference time, and peak memory, accounting for tile loading, feature extraction, and slide-level aggregation. Explain whether the savings materially improve turnaround time, throughput, or hardware requirements. Appendix B.4 already acknowledges that patch counts and feature dimensions alone do not establish a processing speedup.
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The study separates teacher usefulness, student predictability, and downstream benefit, which is useful. Please draw the findings together more clearly and explain which practical choices they inform when designing future transfer methods, including the limits of that guidance. Please also repeat one or two representative analyses with one or two additional pathology encoders, keeping the remaining protocol matched.
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Appendix B.2 documents feature discrepancies when identical regions are re-encoded through the earlier and newer extraction pipelines. Please repeat a representative native-versus-teacher comparison using consistent extraction at both magnifications and assess whether the findings persist. Please also replace "UNI-v2 ... for most experiments" in Section 4 with an explicit description.
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Please clarify whether patient independence was enforced for CAM16, Private-CRC, and PANDA, whose partitions use slide or image identifiers in Appendix B.1/Table 5. Provide uncertainty estimates for the key paired performance differences, accounting for patient grouping and dependence between holdouts. UCEC, for example, has only seven test events at seed 42. Appendix B.7 acknowledges the limits of the reported standard deviations; please qualify comparative claims accordingly.
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Please simplify Figures 1b and 4. A small annotated example linking one native feature, its regional teacher mean, and both predictions would help, together with fewer overlapping correspondence lines and a clearer distinction between dataset reference contours and the displayed slide. Please soften the claim on page 8, lines 378–384, that some information is "not predictable directly from the student." The results show information not recovered by the tested predictors; Appendix A.3 explicitly acknowledges that this does not establish an information limit in the 5× inputs.
[1] Cai, Yu, et al. "A deployment-friendly foundational framework for efficient computational pathology." arXiv preprint arXiv:2602.14010 (2026).
4 comments
W1/Q2. Practical guidance for designing a transfer method. Our findings suggest checking the target, the student and the downstream model separately before adopting a transfer method. Section 6 now gives four practical checks, each paired with its supporting result. Appendix F.10 collects the comparisons:
- Compare native features with and without the observed teacher target. Regional means give small average gains, while spatial components add no consistent benefit (Table 1).
- Check held-out prediction against the training-target constant. Earlier checkpoints and within-cohort fits improve reconstruction in our experiments, so poor transfer can reflect the training setup (Appendices F.4 and F.6).
- Compare trained predictions with the same network at initialization. Training gives no consistent downstream gain in our controls (Section 5.3).
- Test native retention with teacher predictions held fixed. Retention changes task performance without changing reconstruction error, and its benefit depends on the predictor and metric (Figure 6; Appendix F.5).
The teacher mean and native retention are useful starting points in our experiments, but neither is a guarantee for a new task. The guidance is limited to the tested magnification pair and predictor families, with TransMIL as the main task model and limited test support in several cohorts.
W1/Q2. Repeating the teacher comparison with another encoder. We repeated mean augmentation and replacement with Virchow2 on four cohorts. Both magnifications use the same extraction pipeline, and the task-training recipe is matched within each comparison. The table reports mean score differences over five runs with paired 95% intervals, grouped by patient or case where available and by slide or image otherwise. Positive values favour the teacher mean.
| Cohort / metric | Mean added to native features | Mean replacing native features |
|---|---|---|
| CAM16 (AUC) | +0.009 [−0.002, +0.025] | −0.023 [−0.054, +0.001] |
| BRACS (F1) | +0.018 [−0.037, +0.057] | −0.032 [−0.064, +0.003] |
| PANDA (κ) | +0.002 [−0.005, +0.010] | +0.003 [−0.005, +0.009] |
| KIRP (C-index) | −0.006 [−0.092, +0.074] | −0.026 [−0.073, +0.038] |
Adding the mean raises the average score in the three classification cohorts, while replacing native features lowers it in three of the four cohorts. All intervals include zero. These directions support testing the mean as a complement to native features, but do not establish a gain in each cohort. CAM16's replacement result reverses direction relative to UNI2-h, which limits how broadly we can generalize the original finding. Appendix F.7 gives the full results and explains the historical patch support used in this follow-up.
The learned direct/residual comparison has not yet been repeated with Virchow2. Repeating its leave-one-cohort-out training requires features from all ten cohorts, while our Virchow2 cache covers four. We will add that comparison in the camera-ready version. Appendix B.2 now limits the learned-predictor findings to UNI2-h.
W2/Q3. Magnification and the extraction pipeline. The mixed results for replacing native features with the teacher mean persist in the follow-up checks, but individual cohort effects change. Using both scales from the earlier UNI2-h caches preserves PANDA's positive result, while CAM16's gain shrinks and its interval includes zero. The Virchow2 comparison above uses one recorded extraction pipeline at both scales and also gives mixed replacement results.
The UNI2-h check removes the earlier-cache versus new-extraction difference, although identical processing across its cache dates is not documented. Both follow-ups use historical patch support, so they do not isolate extraction as the sole cause of changed effects. Section 5.1 and Appendix B.2 now state that the submitted comparison combines magnification and extraction history; Appendix F.7 reports the checks.
Q3. Which encoders are used? Section 4 now names the encoders explicitly. Table 1 uses UNI2-h and DINOv3 for the native 5× input, with UNI2-h teacher features at 20×. Tables 2–3 use UNI2-h, and Table 4 adapts UNI2-h with LoRA. DINOv3 supplies low-magnification inputs. Appendix B.2 lists the encoders for every experiment, and Appendix F.7 reports the separate Virchow2 check.
W2/Q4. Patient independence and uncertainty. In all our experiments, we keep patients or cases separate between training, validation and test sets whenever identifiers are available. We verified this separation in BRACS and all TCGA cohorts. CAM17 follows its challenge patient groups. For CAM16, Private-CRC and PANDA, the available slide or image identifiers do not provide patient linkage. We updated Appendix B.1 and the Table 5 caption to state these limits.
The new paired intervals give each evaluation group one shared resampling weight across overlapping holdouts. They condition on the fitted models and exclude retraining uncertainty. In Table 1, the mean gain is positive across all ten cohorts, but only CAM17's interval excludes zero. The abstract describes the direction across cohorts, and Section 5.1 gives the small gains and their uncertainty. Sparse survival events further limit the UCEC and KIRP comparisons. Appendix F.1 gives the intervals and reporting rule.
Q5. Figures and the interpretation of prediction failures. We removed the information-limit interpretation from Section 5.2, the Introduction and the Figure 1 caption. The revised text states: "The figure shows what the tested predictors recovered, not what the 5× input contains (Appendix A.3)." Prediction failures alone cannot distinguish missing input information from limitations of the trained model.
Figures 1b and 4 are now simplified in the revised PDF. Figure 1b links one region's native feature, teacher mean and predictions. Its caption explains that both predictions move toward the teacher mean but remain separated from the matched target in the display. Figure 4 shows correspondence lines for a small random subset of regions, with reference contours distinguished from the displayed slide's points. Its caption states the takeaway: overlap with teacher features does not imply accurate prediction. Appendix D.3 gives the sampling details for both figures.
I thank the authors for their response. I will keep my score.
Thank you for the review. We answer your questions and concerns in the following posts.
W1/Q1. Deployment cost and the comparison with compact encoders. The deployment cost we address is encoding many high-magnification patches. At the same tissue coverage and patch size, 20× requires sixteen patches for each 5× patch. A compact encoder reduces the cost per patch, while lower magnification reduces the number of patches. The two savings can be combined.
Our matched-field measurements show that the UNI2-h 20× pipeline takes about 9–16 times as long as the 5× pipeline. We used the same GPU and tissue fields, including slide reading, preprocessing, feature extraction and the task model. The table gives per-slide median times, and ratios are medians of paired slide ratios.
The predicted-summary pipeline, which uses UNI2-h and DINOv3 at 5×, takes 1.3–1.6 times as long as plain UNI2-h at 5×. Peak allocated GPU memory is 2.9–3.6 GiB for the UNI2-h pipelines and 1.9–2.5 GiB for the predicted-summary pipeline. Thus, the time saving does not imply a proportional reduction in GPU memory. These timings cover the selected fields and exclude model loading and whole-slide tissue detection, so they do not measure complete slide turnaround. Appendix F.8 gives the protocol and measurements.
A compact 20× encoder can cost less than our two-encoder 5× pipeline. The estimates below make that trade-off explicit. They count forward compute for the same tissue area and do not measure task accuracy or runtime.
The requested compact-encoder comparison of accuracy, time and memory has not been run given the current time frame and scope for rebuttal, but we will add a compact encoder at both magnifications on representative cohorts in the camera-ready version. Section 4 and Appendix B.4 now distinguish patch-count savings from measured processing time, and the related work includes the compact pathology encoder study you cited. Our results support faster processing on the measured fields, but they do not establish a lower minimum GPU-memory requirement or the best accuracy–cost trade-off among encoders.