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Under review as a conference paper at ICLR 2027

What Makes High-Magnification Knowledge Transferable? A Study of Cross-Resolution Distillation in Whole-Slide Imaging

Abstract

Cross-resolution knowledge distillation aims to improve low-magnification whole-slide analysis by transferring high-magnification representations, yet the conditions for useful transfer remain unclear. We develop a decomposition-based analysis of teacher access, representation loss, and model excess, motivating three questions: whether (a) teacher targets help the task, (b) low-magnification students can predict them, and (c) slide models benefit from those predictions. We investigate them through controlled experiments across ten pathology cohorts spanning classification, grading, and survival prediction. In the main comparison, providing teacher regional means alongside native low-magnification features improves downstream performance in all ten cohorts. Direct prediction achieves lower reconstruction error than residual prediction, yet the predicted features underrepresent variation in the teacher targets. Moreover, better reconstruction does not consistently improve downstream scores, and retaining native features changes performance even when the predicted teacher features are held fixed. Together, these findings expose a gap between reconstructing teacher representations and realizing their downstream value. They challenge the sufficiency of reconstruction error as a measure of cross-resolution transfer and provide a diagnostic framework for examining where that transfer breaks down. Future distillation designs must account for both what students can predict and how slide models use those predictions. Code is provided in supplementary material and will be publicly released after review.

Primary area:
transfer learning, meta learning, and lifelong learning
Keywords:
Computational Pathology, Whole-slide images, knowledge-distillation, cross-scale learning, computer vision

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.75 over 4 reviews, above 83% of the others.
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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
  1. 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.

  2. The experiments cover ten cohorts spanning classification, grading, and survival analysis. They include both frozen-feature prediction and encoder adaptation.

Critical weaknesses
  1. 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.

  2. 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
  1. 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.

  2. 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.

  3. 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.

  4. 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.

  5. 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

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.

CohortUNI2-h 5×UNI2-h 20× with poolingTime ratio
CAM161.56 s24.7 s15.8×
BRACS2.04 s18.8 s8.9×
PANDA0.0242 s0.219 s9.0×

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.

PipelineGFLOPs per 5× regionRelative cost
Our 5× package (UNI2-h + DINOv3)4051
UNI2-h at 20×5,76914.3×
ViT-B at 20×5391.3×
ViT-S at 20×1360.34×
ViT-T at 20×340.09×

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.

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 / metricMean added to native featuresMean 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.

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Paper summary

This paper investigates the transferability of high-magnification knowledge to low-magnification models for whole-slide image (WSI) analysis. Rather than proposing a new distillation algorithm, the authors aim to understand the conditions under which cross-resolution knowledge transfer is beneficial. The paper introduces a risk decomposition that distinguishes three aspects: the task relevance of high-magnification teacher information, the ability of low-magnification students to predict teacher representations, and the ability of downstream models to utilize the predicted features.

The authors conduct experiments across ten pathology cohorts covering classification, grading, and survival prediction. They investigate regional mean and spatial teacher representations, compare direct and residual prediction, and analyze the effects of reconstruction accuracy and native feature preservation. The results suggest that observed high-magnification teacher features can provide useful complementary information, but lower reconstruction error does not consistently translate into better downstream performance. The study highlights the importance of evaluating teacher usefulness, student predictability, and downstream utility separately.

Critical strengths

1. Meaningful problem formulation and valuable analytical perspective.

The paper addresses an important and insufficiently understood problem in cross-resolution knowledge distillation. By separating teacher usefulness, student predictability, and downstream utility, the authors provide a clear analytical perspective for understanding why better feature reconstruction does not necessarily lead to better task performance. This distinction is valuable because it challenges the common practice of relying primarily on reconstruction error to evaluate knowledge transfer.

2. Comprehensive and carefully designed empirical analysis.

The experiments cover ten pathology cohorts with diverse downstream tasks and include several informative controls, such as constant predictors, direct versus residual prediction, token repetition, predictor initialization, and native feature retention. These comparisons help distinguish the effects of teacher information, feature reconstruction, and downstream representation usage. I also appreciate that the authors report mixed or negative findings rather than focusing only on performance improvements. The resulting empirical observations provide useful insights for evaluating future cross-resolution distillation methods.

Critical weaknesses

1. Limited mechanistic explanation of the observed transfer behavior.

Although the proposed risk decomposition provides a useful framework for organizing the analysis, the theoretical results are largely based on established properties of risk decomposition and squared-error prediction. More importantly, the experiments do not fully explain the mechanisms behind the observed limitations of knowledge transfer. For example, the reduced variability of direct predictions may be partly attributed to the restricted capacity of the student network, which contains a 256-dimensional hidden bottleneck before producing 1,536-dimensional outputs. Therefore, it remains difficult to distinguish limitations caused by model architecture and optimization from those arising from insufficient information in low-magnification inputs. Further clarification would strengthen the interpretation of the empirical findings.

2. Sensitivity of empirical conclusions to experimental configurations.

While the study covers diverse datasets, some findings are sensitive to the representation and evaluation settings. For example, the teacher regional mean improves the average primary metric across all ten cohorts in the main comparison, but this pattern is less consistent in the full-channel experiments reported in the appendix. These experiments use different configurations and are not directly contradictory, but they indicate that the observed benefits may depend substantially on representation design and downstream training protocols. In addition, several task improvements are relatively small, and the overlapping evaluation splits and limited test support in certain datasets make it difficult to assess the statistical reliability of some conclusions.

Questions for authors

Q1. Distinguishing model capacity limitations from information limitations

The paper observes that direct predictions exhibit reduced variability compared with high-magnification teacher features. However, the direct predictor uses a relatively narrow hidden bottleneck. Could the authors further clarify to what extent this behavior may be caused by architectural capacity or optimization limitations rather than the intrinsic predictability of high-magnification information from low-magnification inputs? Would increasing the predictor capacity affect the observed conclusions?

Q2. Consistency of teacher usefulness across experimental settings

The main experiments show improvements from adding observed teacher regional means across all ten cohorts, while the full-channel experiments in the appendix show more mixed results. Could the authors clarify which differences in representation construction, dimensionality, or downstream training settings are most likely responsible for these changes? This would help determine how broadly the reported teacher usefulness conclusions can be generalized.

Q3. Statistical reliability of the main empirical findings

Several reported improvements are relatively small, and the five evaluation realizations may contain overlapping test samples. Could the authors provide additional paired uncertainty estimates or clarify which of the main empirical comparisons remain reliable when accounting for overlapping evaluation groups and limited test support, particularly for the smaller classification and survival cohorts?

4 comments

Thank you for the review. We answer your questions and concerns in the following posts.

W1/Q1. Does predictor capacity explain the reduced variation? We tested widths 256, 1,536 and 4,096 on all ten cohorts, with five runs per setting. Direct predictions remain less variable than the teacher targets when we widen the network, so this pattern can be generalized beyond the 256-unit bottleneck. The table shows the variance of trained predictions divided by teacher variance. Ranges span cohort means, each averaged over five runs. Values below one mean less variation.

Predictor (initialization)Width 256Width 1,536Width 4,096
Direct, zero-initialized0.25–0.540.25–0.550.29–0.59
Direct, random-initialized0.37–0.650.46–0.720.47–0.76
Residual, both initializations1.14–2.400.93–1.880.80–1.69

A linear ridge predictor without a hidden layer also produces less variable outputs (ratio 0.30–0.56). Even the ideal squared-error predictor can have less variation than its targets (Proposition 1), so reduced variation alone cannot establish an information limit in the 5× input.

Capacity and checkpoint selection still affect reconstruction accuracy. Wider networks generally reduce residual error, while direct prediction has lower error in ten cohorts at width 256 and eight at the larger widths after earlier selection. All 600 networks reach their lowest validation error at 64–256 updates, before the original first checkpoint at 512. Earlier selection lowers width-256 direct error by 5–20%, but ridge still has lower mean error than the neural predictors in every cohort. Appendix F.4 gives the ranges for both initializations and the protocol differences, including the cached teacher targets used in this follow-up. Tables 34–35 show the zero-initialized comparisons.

Section 5.2 separates observed prediction errors from claims about input information. The Introduction attributes reduced variation to direct predictions, and the Figure 1 caption explains its single-region example.

W2/Q2. Why does teacher usefulness differ between the two protocols? The teacher-mean benefit depends on the representation and training settings. Four factors change between Tables 1 and 10, so their results cannot identify a single cause. The table shows those differences and the number of cohorts whose average favours adding the observed mean to native features.

ComparisonMain comparison (Table 1)Full-channel comparison (Table 10)
Added teacher block768 coordinates; 3,072 total input6,144 coordinates; 8,448 total input
Mean representationOne 192-coordinate projectionFour copies of the 1,536-coordinate mean after decoding
ScalingPer coordinate, from training-data momentsOne scale for the block, set relative to native-feature energy
Task trainingNVIDIA, BF16AMD, FP32
Matched settingsComplete fields, bag cap, TransMIL recipe, five runsSame
Higher primary score10/10 cohorts4/10 cohorts
Lower NLL7/10 cohorts3/10 cohorts

We suspect that delivery contributes to the difference. In Table 2, repeating the same mean sixteen times changes primary scores by −0.015 to +0.044 without adding information. The full-channel protocol supplies four copies within a wider feature vector. We have not isolated delivery's contribution because width, scaling and training numerics also change.

Section 5.1 now states that mean augmentation raises the average score in all ten cohorts under the main protocol, but only four under the full-channel protocol. Appendix C.6 points to the full comparison in Appendix F.9 (Table 43). We therefore limit the teacher-mean claim to the settings that support it.

W2/Q3. Which findings are supported after accounting for uncertainty? Adding the observed teacher mean gives a small positive average in all ten cohorts (exact two-sided sign test over cohorts, p = 0.002), but only CAM17's paired interval excludes zero. We distinguish this observed direction from confidence in any single cohort. For an individual gain to count as supported, its 95% interval must exclude zero and at least four of five runs must agree in sign.

The table gives the five-run mean paired change from adding the observed mean to the same native input (Table 1). Positive values favour adding the mean.

Cohort (metric)Change [95% interval]Runs > 0
CAM16 (AUC)+0.0166 [−0.0241, +0.0589]4/5
CAM17 (macro-F1)+0.0397 [+0.0008, +0.0810]4/5
Private-CRC (macro-F1)+0.0105 [−0.0078, +0.0294]3/5
PANDA (κ)+0.0061 [−0.0012, +0.0132]3/5
BRACS (macro-F1)+0.0046 [−0.0278, +0.0453]2/5
KIRC (C-index)+0.0068 [−0.0374, +0.0462]4/5
KIRP (C-index)+0.0429 [−0.0380, +0.1085]2/5
LUAD (C-index)+0.0415 [−0.0095, +0.0905]4/5
STAD (C-index)+0.0008 [−0.0459, +0.0412]2/5
UCEC (C-index)+0.0294 [−0.0488, +0.0991]2/5

The survival-cohort intervals all include zero, and KIRP and UCEC have nine and seven test events at seed 42. The abstract states the direction across cohorts. Section 5.1 gives the small gains and their uncertainty, with the interval analysis in Appendix F.1.

For native retention, the original ten-cohort averages favour higher primary scores in 7–8 cohorts for direct prediction and four for residual prediction, while log loss favours retention in 7–9 cohorts for both forms. The paired intervals below come from the new CAM17/PANDA refits. They compare the same prediction with and without the native block, averaged over five runs. Positive values favour retention.

Cohort (metric)Predictor, widthChange [95% interval]Runs > 0
CAM17 (macro-F1)Direct, 256−0.020 [−0.070, +0.024]2/5
CAM17 (macro-F1)Direct, 1,536+0.018 [−0.020, +0.066]4/5
CAM17 (macro-F1)Residual, 256−0.013 [−0.048, +0.019]1/5
CAM17 (macro-F1)Residual, 1,536−0.032 [−0.072, +0.007]1/5
PANDA (κ)Direct, 256+0.021 [+0.012, +0.030]5/5
PANDA (κ)Direct, 1,536+0.013 [+0.004, +0.022]5/5
PANDA (κ)Residual, 256−0.005 [−0.012, +0.002]2/5
PANDA (κ)Residual, 1,536+0.001 [−0.006, +0.009]3/5

PANDA supports a κ gain from retaining native features with direct prediction at both widths. The other primary-score effects are uncertain. At width 1,536, that same PANDA comparison raises log loss by 0.40 nats, so the preferred choice also depends on the metric (Appendix F.5). These task differences occur with the prediction and its reconstruction error held fixed.

The replacement comparison in Table 2 is also sensitive to protocol: PANDA's positive effect persists when both scales use the earlier caches, while CAM16's gain shrinks from +0.056 to +0.010 AUC and its interval includes zero (Appendix F.7).

The intervals use one shared resampling weight for each group's appearances in the five overlapping holdouts and both arms, conditional on the saved models. They do not include retraining uncertainty. For all experiments, we group by patient or case where identifiers are available. Appendix F.1 gives the full procedure.

Thanks to the authors for running the width/ridge experiments, adding the paired 95% intervals, and clarifying the protocol differences between Tables 1 and 10. While individual cohort gains remain modest, the revised manuscript scopes its claims carefully and provides a useful diagnostic study, so I will keep my rating at 3.

Reviewer_esHoOpenReview ↗
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Paper summary

The paper studies knowledge transfer from a high magnification model to a low-magnification one for whole slide analysis. Specifically the authors dissociate knowledge transfer into three parts, viz, useful information from the teacher, performance of the low magnification student in predicting those and if accurate predictions benefit the downstream task. They show that if the student produces one prediction per region, teaching with multiple detailed features is has equivalent performance with that of teaching with their average. They further demonstrate that better teacher imitation does not translate to better downstream task performance. Thus they establish that distillation techniques should account for both, the student’s prediction qualities as well as performance in whole slide analysis.

Critical strengths

The paper introduces a systematic experimental design which studies teacher content, token count, teacher learning vs an additional transformation. These controlled comparisons are a step towards interpreting apparent transfer gains by testing alternative explanations for improved performance.

Critical weaknesses
  1. None of the decomposition terms mentioned in Theorem 1 is estimated in the manuscript. Appendix A1 also states that the primary metrics (AUC, F1, etc) are not identified with the terms of the decomposition. This limits the motivation for the theorem.
  2. The experiments do not establish that the teacher learning adds task value nor why the prediction fails. In most scenarios (5/10 in Table 10 and 7/10 in Table 22), the control with exact-initialization beats the trained predictor and the direct/residual and native-retention studies (Tables 23-25) lack this control. Thus the reconstruction failures may also reflect weak, early-stopped single-layer MLP students. In stage-1 the mean predictors’ poor performance on OOD data signifies a cross-cohort shift rather than a limitation. Furthermore, the spatial-input student (which fails in-distribution) is not tested on spatial targets making it an unfair comparison.
Questions for authors
  1. Could the authors estimate atleast one of the decomposition terms from Theorem 1 on held-out data, for example, teacher access as the log-loss difference between task models with and without T on the classification cohorts?
  2. Could the authors train a spatial-input student on the spatial components, together with a Stage-1 prediction trained on the evaluation splits unlabelled split?
4 comments

Thank you for the review. We answer your questions and concerns in the following posts.

W1/Q1. Connecting the theorem to held-out task loss. Table 8 (Appendix C.5) estimates the fitted-model counterpart of the teacher-access term from held-out losses with and without the observed teacher mean. We made its link to Theorem 1 easy to miss. For your convenience, we reproduce the two relevant columns below for all ten cohorts. Both models retain the same native input, one of which also receives the observed teacher mean.

Values are mean ± SD over five runs. The first five cohorts use classification log loss, and the five survival cohorts use censored negative log-likelihood (NLL). Compare the models within each row: a positive reduction favours adding the teacher mean.

CohortNLL without teacher meanNLL with teacher meanReduction
CAM160.6110 ± 0.16050.6717 ± 0.3244−0.061
CAM170.8392 ± 0.43040.8605 ± 0.3460−0.021
Private-CRC0.6230 ± 0.05510.5563 ± 0.0356+0.067
PANDA1.4584 ± 0.58171.1328 ± 0.4491+0.326
BRACS1.8613 ± 0.54051.7576 ± 0.5130+0.104
KIRC2.0562 ± 0.48781.6173 ± 0.4347+0.439
KIRP1.2932 ± 0.24031.2128 ± 0.2770+0.080
LUAD2.7670 ± 0.60572.5482 ± 0.4887+0.219
STAD2.4675 ± 0.38912.5468 ± 0.5305−0.079
UCEC1.0027 ± 0.16320.9424 ± 0.1180+0.060

Adding the teacher mean lowers average NLL in seven of ten cohorts: three of five classification cohorts and four of five survival cohorts. This is the held-out comparison suggested in Q1, and it estimates how much the trained task models benefit from access to the teacher mean.

The theorem's teacher-access term compares the lowest possible population losses with and without teacher features, over all prediction rules. Held-out evaluation estimates the losses of our trained models, but those two estimates do not reveal how far either model is from its unknown optimum. Their population loss difference equals teacher access plus the difference in their excess risks (Appendix F.2). Matching the architecture and training procedure does not guarantee that those excess risks cancel. Isolating teacher access from these two losses alone would require additional assumptions or bounds on that difference. We therefore report the requested comparison as a fitted-model counterpart of teacher access where negative values can be observed.

Section 3 now makes this connection explicit (p. 4, l. 162–165 of the revised PDF), using the risk definitions in Appendix A.1. For the classification cohorts, Appendix F.2 (Table 31, p. 63) adds paired intervals. Private-CRC's reduction is +0.067 [+0.004, +0.127], with four of five runs agreeing. PANDA's larger average is mainly driven by two runs, so we report its variability alongside the mean.

W2a. Does training help beyond the exact initialization? The initialization controls show mixed task benefits. We now report the saved comparisons for the direct and residual predictors used in Tables 23–25. With a random final layer, training improves the primary score in 104 of 200 paired runs and lowers log loss in 101 of 200. With a zero final layer, the counts are 80 of 150 and 83 of 150 after excluding the all-zero-input reference.

These descriptive counts support the paper's distinction between a useful teacher target and a useful learned prediction. Together with Tables 10 and 22, they show that Stage-1 training does not consistently improve on the same network before training. Section 5.3 now reports this finding, and Appendix F.3 (Tables 32–33, pp. 63–64) gives the comparisons by cohort and input representation.

W2b. How much do capacity and checkpoint selection matter? Earlier checkpoint selection improves reconstruction. In the new sweep, all 600 networks reach their lowest validation error at 64–256 updates, before the first checkpoint considered by the original rule at step 512. Selecting earlier lowers width-256 direct error by 5–20%. Widening the networks also helps residual reconstruction, although direct prediction still has lower error in eight of ten cohorts at widths 1,536 and 4,096.

The linear ridge predictor has lower error than the neural predictors, so there is room to improve these students. Direct outputs are less variable than the teacher at every tested width, and ridge shows the same pattern. Reduced variation is therefore not specific to the 256-unit bottleneck. Appendix F.4 (Tables 34–35, p. 65) gives the width and checkpoint results and explains the follow-up protocol, including its cached teacher targets.

When we replayed training of the spatial predictors from Appendix C.6 on different hardware, their best checkpoints occurred at steps 48 or 64. Earlier selection brings their error close to that of the training-target constant on unseen groups from the training cohorts, but no spatial predictor beats its constant on the excluded cohort. Appendix F.11 (pp. 68–70) reports this replay separately from the original saved predictors.

W2c/W2d/Q2. Spatial prediction with within-cohort training. We have now run the combined experiment you requested. Within-cohort training with spatial inputs gives the lowest average spatial reconstruction error among the four trained conditions on both PANDA and BRACS.

We compared within-cohort and other-cohort training, each with global or quadrant inputs from the same 5× field (five runs per condition; 40 fits). All predictors learn the three nonconstant spatial components, with matched architectures and sample budgets. Within-cohort fitting and checkpoint selection use unlabeled groups from the task-training split. Task validation and test groups are excluded.

The table gives mean raw spatial MSE × 1,000 (lower is better). The last row is the training-target constant, which returns the within-cohort average training target.

Training dataInput / referencePANDA MSEBRACS MSE
Other cohortsGlobal16.0859.797
Other cohortsQuadrants16.6639.610
Within cohortGlobal12.3658.530
Within cohortQuadrants10.7428.112
Within cohortTraining-target constant13.2727.488

Compared with other-cohort training and global input, the combination reduces average error by 33.2% on PANDA and 17.2% on BRACS. Adding quadrants after within-cohort training gives a further 13.1% and 4.9% reduction, with all five runs agreeing in each cohort. The paired changes for this latter comparison are below, in the same MSE × 1,000 units.

CohortMSE change [95% interval]Runs lower
PANDA−1.623 [−1.771, −1.475]5/5
BRACS−0.418 [−0.498, −0.342]5/5

The combined predictor beats its training-target constant in all five PANDA runs, but in none of the BRACS runs. PANDA's improvement supports our revised interpretation that the earlier spatial failures depend partly on the input and training setting. Our main distinction between reconstruction and downstream usefulness still applies. Given the current time frame and scope, the downstream task value of these improved predictions remains untested for now, but will be tested in the camera-ready version.

We provide full details in Appendix F.13, which gives the protocol, component results and all paired comparisons. The earlier separate checks remain in Appendices F.6 and F.12.

I thank the authors for updating the manuscript with the findings and conducting the experiment with spatial-input student evaluation. The justification and connection to Theorem 1 is more explicit in the manuscript now. The clarifications and the new results address my concerns. Thus, I am increasing my score.

Reviewer_qNp8OpenReview ↗
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Paper summary

This paper studies when high-magnification supervision benefits low-magnification whole-slide image analysis. It separates three questions: whether teacher targets are useful for the downstream task, whether low-magnification inputs can predict those targets, and whether the downstream model benefits from the predictions. A population-risk decomposition and squared-error identities motivate controlled comparisons of teacher summaries, direct and residual prediction, and native-feature retention. Experiments cover ten pathology cohorts spanning classification, grading, and survival prediction, generally with five realizations. The main findings are that observed teacher means can complement native features, lower reconstruction error does not consistently imply better downstream performance, and retaining native features can change task performance without changing the teacher predictions. The contribution is primarily an empirical analysis and an evaluation framework rather than a new distillation method.

Critical strengths

1.The paper separates questions that are often conflated in distillation evaluations. Testing observed teacher targets, learned predictions, and downstream delivery separately helps distinguish a useful teacher representation from a successful transfer procedure. The comparison between [x; q] and [0; q] is particularly informative: it holds the prediction and its reconstruction error fixed while testing the effect of retaining native features. This provides concrete evidence that reconstruction quality alone is insufficient to evaluate the resulting task representation.

2.The experimental controls make the study useful beyond its individual performance results. The training-target mean tests whether a predictor learns more than a constant, while comparisons against the exact initial network help distinguish the effect of distillation from that of adding a feature transformation. These controls are examined across classification, grading, and survival cohorts. The authors also document important qualifications, including overlapping holdouts and differences between experimental protocols. Together, these choices offer a useful starting point for more informative evaluations of cross-resolution transfer.

Critical weaknesses

1.The prediction experiments do not sufficiently distinguish limitations of the chosen predictors from limitations of the available information. Appendix E.4 uses a 3072 → 256 → 1536 predictor. The direct output therefore lies in an affine subspace of dimension at most 256, whereas the residual output retains a native-feature path around this bottleneck. The authors acknowledge that the finite function classes differ, but this leaves the interpretation of their reconstruction and downstream differences strongly dependent on the architecture. Moreover, all 200 predictors select the first eligible checkpoint, at update 512, leaving sensitivity to earlier checkpoint selection unresolved. These limitations do not invalidate the observed disagreement between reconstruction and task performance. They do, however, weaken the broader explanation of what is transferable. In particular, the statement in Section 5.2, lines 378–384, that the visualized results show information is not predictable from the student is stronger than the evidence supports; Appendix A.3 correctly explains why prediction failure alone cannot establish such a limit.

2.The robustness of the main empirical conclusions remains insufficiently established. The improvements in Table 1 are averages over five overlapping holdouts, and some are small, for example, STAD changes from 0.5104 to 0.5112. Appendix B.1 also reports only nine and seven test events for KIRP and UCEC, respectively, at seed 42. The authors appropriately acknowledge these limitations, but the reported standard deviations do not establish the uncertainty of the paired performance differences. There is also a gap in connecting reconstruction to downstream utility: Appendix C.6 explicitly states that independent component errors are unavailable for the full-channel predictors used downstream, while the projected diagnostic evaluates different predictors. For a paper whose contribution is primarily empirical understanding, stronger evidence for the key paired effects and a direct link between the evaluated predictors and their downstream outcomes would materially strengthen the case for acceptance.

Questions for authors

1.Should the statement in Section 5.2 about information being unpredictable be understood only as a limitation of the evaluated predictors? Do you have evidence that the direct/residual findings persist with a wider hidden layer or checkpoints before update 512? A focused check on representative cohorts would help assess how much of the observed behavior depends on the bottleneck and selection procedure.

2.Can you evaluate the saved full-channel mean and spatial heads from Appendix C.6 on groups excluded from both their training and checkpoint selection, using the corresponding training-target constants as references? This would directly connect their reconstruction behavior to the downstream results in Table 10.

3.Can you provide paired effect estimates and uncertainty for the teacher-mean augmentation and native-retention comparisons, using the appropriate patient or case grouping where available and accounting for overlap across realizations? I am interested in which conclusions remain supported once this uncertainty is considered, rather than in significance tests that treat the five seeds as independent samples.

The unresolved dependence on predictor architecture and selection, together with uncertainty around the key task effects, leaves me below the acceptance threshold. Focused validation addressing the questions above could change my assessment.

5 comments

Thank you for the detailed review. We answer your questions and concerns in the following posts.

W1/Q1. Predictor capacity, checkpoint selection and interpretation. The Section 5.2 statement applies only to the tested predictors. We replaced the claim that "some information is not predictable directly from the student" with: "The figure shows what the tested predictors recovered, not what the 5× input contains" (p. 8, l. 406–407 of the revised PDF). We also removed the information-limit claim from the Introduction and replaced the Figure 1 caption's diversity claim with an explanation of its single-region example.

We tested hidden widths of 256, 1,536 and 4,096 on all ten cohorts, with both final-layer initializations and five runs per setting. Table 34 in Appendix F.4 (p. 65) shows the reconstruction results. We present the width comparison in the table below, where each cell gives direct/residual held-out MSE, averaged over five runs with zero final-layer initialization (lower is better). All widths use the same validation-based selection rule. Ridge has no hidden layer.

CohortWidth 256Width 1,536Width 4,096Ridge
CAM160.0604 / 0.09270.0577 / 0.08050.0586 / 0.07450.0573
CAM170.0672 / 0.09810.0641 / 0.08440.0645 / 0.07850.0634
Private-CRC0.1538 / 0.17770.1566 / 0.17370.1684 / 0.18190.1505
PANDA0.1292 / 0.12960.1251 / 0.12140.1298 / 0.12560.1210
BRACS0.0926 / 0.11180.0895 / 0.10060.0891 / 0.09490.0860
KIRC0.1269 / 0.12820.1209 / 0.12060.1194 / 0.11900.1150
KIRP0.0992 / 0.10830.0929 / 0.09900.0936 / 0.09610.0896
LUAD0.0927 / 0.14010.0872 / 0.12120.0910 / 0.11690.0867
STAD0.0819 / 0.10870.0772 / 0.09310.0773 / 0.08800.0742
UCEC0.1187 / 0.13420.1121 / 0.12100.1129 / 0.11710.1076

Increasing width from 256 to 4,096 reduces residual error in nine cohorts. Direct error changes by less than 6% in nine cohorts and increases from 0.1538 to 0.1684 in Private-CRC. Direct prediction still has lower error in eight of ten cohorts at both wider widths. Table 35 (Appendix F.4, p. 65) shows that direct outputs stay less variable than the teacher at every width. Ridge also produces less variable outputs, so this pattern is not specific to the narrow network.

Checkpoint selection also matters. Every network in the sweep reaches its best validation error at 64–256 updates, before the original first checkpoint at 512. Earlier selection lowers width-256 direct error by 5–20% over the two initializations. Table 34 includes the original selection rule for comparison. Ridge still has lower error than the neural predictors, so there is room to improve these students. Appendix F.4 (pp. 64–65) documents the protocol differences, including the use of cached teacher targets in this follow-up.

For downstream performance, Tables 36–37 in Appendix F.5 (p. 66) report the CAM17 and PANDA refits at widths 256 and 1,536. On PANDA, direct and residual prediction have nearly equal reconstruction error. When predictions are used alone, residual prediction gives higher κ and direct prediction gives lower log loss. Retaining native features also helps direct prediction, as detailed in Q3 below. Width 4,096 was evaluated for reconstruction only.

W2/Q2. Reconstruction and task results for the same saved predictors. We ran the evaluation you requested on the exact 100 saved mean and spatial predictors behind Tables 10 and 11, without refitting them. We used groups excluded from both training and checkpoint selection, and compared each predictor with a training-target constant equal to the average of its training targets.

The mean predictors beat this constant on unseen groups from their training cohorts and on eight of ten excluded cohorts. Private-CRC and PANDA are the exceptions. The spatial predictors never beat it on either set.

The table shows the percent reduction in reconstruction error relative to the constant, averaged over five runs per cohort. Positive values mean lower error. The training-cohort columns use groups unseen during fitting and checkpoint selection.

CohortMean: training cohortsMean: excluded cohortSpatial: training cohortsSpatial: excluded cohort
CAM16+48.1+22.3−30.0−67.5
CAM17+49.1+19.4−29.5−44.7
Private-CRC+46.2−19.1−35.4−112.4
PANDA+48.1−8.5−37.2−71.5
BRACS+47.6+20.0−29.5−49.2
KIRC+48.3+20.5−30.0−52.1
KIRP+49.8+15.4−29.7−59.4
LUAD+50.0+12.7−29.3−62.8
STAD+50.7+14.4−29.1−46.9
UCEC+50.4+2.6−29.2−69.1

Training often reduced spatial reconstruction error without improving the task score. The following counts compare each trained spatial predictor with its exact initialization on the excluded cohort, using the corresponding task results from Table 10.

Change after spatial-predictor trainingRuns
Lower reconstruction error40/50
Higher primary task score22/50
Higher task score among runs with lower reconstruction error16/40

Only 16 of the 40 runs with better reconstruction also have a higher task score. These counts are descriptive because the runs share training data.

We provide details in the appendix. Appendix F.11 (pp. 68–70) gives the independent reconstruction results and their connection to Table 10. Appendix C.6 (p. 33) now points to this evaluation. For the regional-mean predictors, the submission already linked independent reconstruction results in Appendix D.1 to the task results in Tables 23–25; Appendix E.4 (p. 54) now makes that link explicit.

W2/Q3. Which task effects remain supported after accounting for uncertainty? We distinguish the direction of the observed cohort averages from the uncertainty of each individual effect. We now report paired 95% intervals that account for evaluation groups appearing in more than one holdout. For a gain to count as supported within an individual cohort, we require its interval to exclude zero and at least four of five runs to agree in sign.

Adding the observed teacher mean gives a small positive average in all ten cohorts (exact two-sided sign test over cohorts, p = 0.002), but only CAM17 supports a gain on its own. The table compares task models given the same native features, with either the observed mean or zeros appended (Table 1). Changes are averaged over five runs. Positive values favour adding the mean.

Cohort (metric)Change [95% interval]Runs > 0
CAM16 (AUC)+0.0166 [−0.0241, +0.0589]4/5
CAM17 (macro-F1)+0.0397 [+0.0008, +0.0810]4/5
Private-CRC (macro-F1)+0.0105 [−0.0078, +0.0294]3/5
PANDA (κ)+0.0061 [−0.0012, +0.0132]3/5
BRACS (macro-F1)+0.0046 [−0.0278, +0.0453]2/5
KIRC (C-index)+0.0068 [−0.0374, +0.0462]4/5
KIRP (C-index)+0.0429 [−0.0380, +0.1085]2/5
LUAD (C-index)+0.0415 [−0.0095, +0.0905]4/5
STAD (C-index)+0.0008 [−0.0459, +0.0412]2/5
UCEC (C-index)+0.0294 [−0.0488, +0.0991]2/5

The abstract now states the direction across cohorts. Section 5.1 gives the small gains and their uncertainty. No survival cohort supports a gain on its own, including KIRP and UCEC with only nine and seven test events at seed 42. Appendix F.1 (pp. 62–63) gives the full analysis.

For native retention, Section 5.3 reports a directional pattern: primary scores more often favour retention for direct prediction, and log loss often improves for both prediction forms. The original ten-cohort comparisons give the following counts of favourable five-run averages (Tables 24–25). All predictors were trained. Zero and random describe their final-layer initialization before training.

Predictor (initialization)Cohorts with higher primary scoreCohorts with lower log loss
Direct (zero)8/108/10
Direct (random)7/107/10
Residual (zero)4/108/10
Residual (random)4/109/10

These counts describe a tendency in the evaluated cohorts, without establishing a reliable gain in every cohort. The paired intervals below assess individual effects in the new CAM17/PANDA fits. Retention improves PANDA κ for direct prediction at both widths, with all five runs agreeing, while the residual-prediction and CAM17 effects are uncertain. Each prediction is held fixed, and the native block is either retained or replaced by zeros. Changes are averaged over five runs. Positive values favour retaining native features.

Cohort (metric)Predictor, widthChange [95% interval]Runs > 0
CAM17 (macro-F1)Direct, 256−0.020 [−0.070, +0.024]2/5
CAM17 (macro-F1)Direct, 1,536+0.018 [−0.020, +0.066]4/5
CAM17 (macro-F1)Residual, 256−0.013 [−0.048, +0.019]1/5
CAM17 (macro-F1)Residual, 1,536−0.032 [−0.072, +0.007]1/5
PANDA (κ)Direct, 256+0.021 [+0.012, +0.030]5/5
PANDA (κ)Direct, 1,536+0.013 [+0.004, +0.022]5/5
PANDA (κ)Residual, 256−0.005 [−0.012, +0.002]2/5
PANDA (κ)Residual, 1,536+0.001 [−0.006, +0.009]3/5

The log-loss results also depend on prediction form and width, so we do not claim that retention always helps. The supported finding is that task performance can change even when the teacher prediction, and hence its reconstruction error, stays fixed. Appendix F.5 (pp. 64–66) gives all retention comparisons.

The resampling uses one shared weight for each evaluation group's appearances in the five holdouts. The intervals hold the trained models fixed, so they do not include retraining uncertainty. Appendix F.1 gives the full procedure and grouping limitations.

Comments on the paper

4 comments
AuthorsOpenReview ↗

General response and summary of changes

We thank the four reviewers for their careful reading. Reviewers qNp8 and VUcM highlighted the separation of teacher usefulness, predictability and downstream benefit. Reviewers esHo and uRiW valued the controlled comparisons and the reporting of mixed outcomes. We have added analyses and clarified the passages raised in the reviews.

1. Predictor capacity and checkpoint selection (qNp8, uRiW, esHo). Wider networks and earlier checkpoint selection improve reconstruction, but direct predictions still vary less than their teacher targets. We tested hidden widths 256, 1,536 and 4,096 on all ten cohorts, and added a linear ridge predictor without a hidden layer. Every neural predictor selected an earlier checkpoint than the original rule allowed. Direct prediction has lower error than residual prediction in eight to ten cohorts, depending on width, and ridge has lower error than the neural predictors.

These results show that capacity and optimization affect accuracy, while reduced variation is not specific to the narrow bottleneck. The Introduction now describes reduced variation as a finding about direct predictions. Figure 1b explains the gap from the matched teacher target, and Section 5.2 states that prediction errors do not establish an information limit. Section 5.3 now places the task refits alongside the native-retention results. They support retention for direct prediction on PANDA's κ. Appendices F.4–F.5 give the results and protocol differences.

2. Paired uncertainty and the scope of task gains (qNp8, uRiW, VUcM). We now report paired 95% intervals that account for the overlapping holdouts. Each evaluation group keeps one resampling weight wherever it appears. We use patient or case identifiers to create training, validation and test splits when available, and report limitations when they are not.

The teacher mean raises the average primary score in all ten cohorts, by +0.001 to +0.043 (two-sided sign test over cohorts, p = 0.002). Only CAM17's paired interval excludes zero. The abstract states the direction across cohorts. Section 5.1 gives the small effect sizes and their uncertainty. The native-retention comparisons are also directional: the effect depends on the prediction form and task metric. Appendix F.1 gives the uncertainty procedure, and F.5 reports the new task comparisons.

3. Spatial prediction and the training setting (qNp8, esHo, uRiW). We evaluated the original spatial heads on groups excluded from both fitting and checkpoint selection. They do not beat their training-target constant, which returns the average training target for every input. Lower reconstruction error also does not always give a higher task score (Appendix F.11).

The new combined experiment requested by esHo gives a more specific picture. Within-cohort training with quadrant inputs lowers spatial error on PANDA and BRACS, and beats the training-target constant on PANDA but not BRACS. The earlier failures therefore depend partly on the input and training setting. These new fits evaluate reconstruction, but their downstream task value is still untested given the current time frame and scope. Appendix F.13 reports the comparison, and Section 5.2 now states this qualification alongside the original results.

4. Broader checks and practical guidance (VUcM, uRiW). We repeated teacher-mean augmentation and replacement with Virchow2 using one extraction pipeline. The mean is more promising as an addition than as a replacement in these four cohorts, but all primary-score intervals include zero (Appendix F.7). Our learned-predictor findings remain limited to UNI2-h.

Section 6 now gives four practical checks, each linked to our findings on target choice, prediction, initialization and native retention. Appendix F.8 reports measured processing time and memory and explains how lower magnification differs from encoder compression. The compact-encoder benchmark and learned Virchow2 comparison are planned for the camera-ready version.

Revision. Changes are marked in blue. Post 2 lists their locations in the revised PDF. The original section, table and figure numbers are retained, and Appendix F collects the additional analyses.

Changes in the revised PDF. Changes are marked in blue. The table lists the targeted additions and corrections, with locations in the compiled anonymous revision. F.1–F.13 are subsections of the new Appendix F.

WhereLocationChangeRaised by
Abstractp. 1Teacher-mean direction and direct/residual variation clarifiedqNp8, uRiW, VUcM
Introductionpp. 1–2Information-limit sentence removed; direct-prediction finding scopedqNp8, uRiW, VUcM
Figures 1b and 4pp. 2, 8Matched-region example explained, fewer lines and clearer reference contoursVUcM
Figure 5p. 9Training-target constant identified and definedqNp8, esHo
Related workp. 2Compact pathology encoder citation and cost distinctionVUcM
Section 3p. 4Fitted-model teacher-access comparison and excess-risk qualificationesHo
Section 4pp. 5–6Encoder and baseline definitions, patch-count costs and spatial scopeVUcM, qNp8, esHo, uRiW
Section 5.1, Table 1p. 7Small gains, protocol limits and extraction historyqNp8, uRiW, VUcM
Section 5.2pp. 8–9Scoped interpretation, capacity/checkpoints and the combined spatial resultqNp8, uRiW, esHo, VUcM
Section 5.3pp. 9–10Native-retention task refits and the comparison with exact initializationqNp8, uRiW, esHo
Section 6p. 10Four practical checks linked to their supporting resultsVUcM
Appendix B.1, Table 5p. 22Patient/case grouping and missing-identifier limitsVUcM
Appendix B.2pp. 23–24Encoders by experiment and extraction checksVUcM
Appendix B.4pp. 24–25Compute, storage and measured processing timeVUcM
Appendix B.7pp. 27–28Wording corrected after submission–
Appendix C.6p. 33Exploratory scope and independent-group evaluationqNp8, uRiW
Appendix D.1p. 38Cohort-shift check for regional-mean predictionesHo
Appendix D.3p. 42Sampling details for the simplified Figures 1b and 4VUcM
Appendix E.4p. 54Task inputs linked to their reconstruction resultsqNp8
F.1pp. 62–63Paired grouped intervals for Tables 1, 2 and 4qNp8, uRiW, VUcM
F.2pp. 62–63Held-out log loss with and without the teacheresHo
F.3pp. 63–64Trained versus exact-initial predictionsesHo
F.4pp. 64–65Widths, earlier checkpoints and ridge predictionqNp8, uRiW, esHo
F.5pp. 64–66Task refits with the re-selected predictorsqNp8, uRiW
F.6pp. 66–67Stage 1 on the cohort's own unlabeled training slidesesHo
F.7p. 67Extraction checks and Virchow2 comparisonsVUcM, uRiW
F.8p. 68Compute, processing time and memoryVUcM
F.9pp. 68–69Differences between projected and full-channel protocolsuRiW
F.10pp. 68–69Practical checks linked to their evidenceVUcM
F.11pp. 68–70Independent reconstruction errors and checkpoint replayqNp8, esHo
F.12pp. 70–71Spatial inputs for the mean and spatial targetesHo
F.13pp. 71–72Spatial inputs combined with within-cohort trainingesHo

We are happy to answer further questions.

Area_Chair_fH9YOpenReview ↗

A Gentle Nudge: Let's Keep the Discussion Going!

Dear Reviewers,

The authors have now posted their responses, addressing your concerns and incorporating your suggestions. We are already halfway through the discussion period!

One of the distinguishing features of ICLR is its interactive review process, where constructive discussions not only help strengthen individual papers but also contribute valuable insights to the broader scientific community.

So, let's not let the discussion be a one-way street! I encourage you to revisit the authors' responses, acknowledge their efforts, and engage in further discussion where needed. After all, a good scientific discussion is often as valuable as the final verdict!

-AC

AuthorsOpenReview ↗

Gentle reminder on response feedbacks and discussions

Dear Reviewers,

Thank you for your time and feedback.

As the rebuttal discussion period is close to its end, we would be grateful for everyone to comment on our responses if you haven't done so, particularly any remaining concerns or questions, so that we can have an opportunity to address them before the deadline.

Thank you again for your consideration.

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