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Under review as a conference paper at ICLR 2027

A Concept-Based Interpretability Benchmark for Pathology Foundation Models

Abstract

Pathology foundation models are usually compared by downstream accuracy, which can hide differences in what their representations encode and what downstream predictors use. Existing concept-based methods often use concepts or explanations that depend on the model being analysed, which makes direct cross-model comparison difficult. We introduce a model-independent framework that compares foundation models using the same predefined pathology concepts. We derive 23 morphology factors from structured pathology reporting standards and ground them in 9,672 caption-asserted factor–panel examples from 4,586 open-access articles. Using factor-specific probes on 16 frozen encoders, we measure factor accessibility, or how well each factor can be linearly recovered from a representation. Encoders differ in both overall accessibility and their factor-level profiles, and models with similar overall accessibility can differ substantially in which factors are most accessible. We then remove factor-associated information using the corresponding factor directions and measure factor sensitivity, or how much downstream performance changes after removal. In melanoma relapse prediction, accessibility is only weakly related to sensitivity. Across three melanoma prediction tasks, sensitivity patterns are consistent across retraining but differ across encoders and tasks. Our framework therefore provides a common concept space for comparing both what foundation models represent and what factor-associated information downstream predictors are sensitive to, turning concept-based interpretability into a tool for comparative foundation-model analysis.

Primary area:
interpretability and explainable AI
Keywords:
concept-based interpretability, foundation models, computational pathology, linear probing, concept erasure, benchmarking

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_R5gJOpenReview ↗
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Paper summary

This paper addresses a meaningful problem by introducing a concept-based benchmark for interpreting pathology foundation models. The evaluation across 16 encoders is fairly comprehensive, but the reliability of the benchmark annotations and the limited novelty of the findings weaken the overall contribution.

Critical strengths

The paper addresses a meaningful problem, as conventional performance benchmarks provide limited insight into what pathology foundation models actually learn. The evaluation across 16 encoders is relatively comprehensive, and the distinction between factor accessibility and downstream sensitivity offers an interesting perspective on model interpretability.

Critical weaknesses

The reliability of the proposed benchmark is a major concern. The morphology labels are derived from figure captions without independent image-level validation by pathologists. The reported 99.1% agreement only reflects consistency between LLM-based caption annotations rather than the visual validity of the concepts.

The methodological novelty and significance of the findings are also somewhat limited. The framework mainly relies on existing linear probing and concept erasure techniques, while the conclusions are largely descriptive. Furthermore, the downstream sensitivity analysis is restricted to a single melanoma cohort, and the observed performance changes after concept removal are generally small.

Questions for authors

Could the authors provide image-level validation by pathologists to establish the reliability of the morphology annotations? It would also be helpful to validate the downstream sensitivity analysis on additional cancer types to demonstrate whether the findings generalize beyond melanoma.

6 comments
AuthorsOpenReview ↗

Response 1/2

Thank you for the careful review, and for recognizing the value of comparing pathology foundation models through interpretable morphology and of the distinction between factor accessibility and downstream sensitivity. The revised paper adds a human audit of benchmark construction, evaluates 21 encoders, including five vision–language models, across nine melanoma and colorectal settings, and introduces a factor concept bottleneck (FCB) predictor.

Image-level validation and benchmark reliability

We agree that expert image-level judgement would greatly enhance the value of the dataset. The 99.1% agreement was reported as a check on label extraction, and the revision complements it with a human audit of every construction step. Pathologist annotation at this scale was not available to us in this study. What we propose is a scalable way to build a partially verified dataset, so that later expert effort can be more targeted.

We divide the verification work into three parts. The first is machine-verifiable: automated extraction and consistency checks identify panels, assign caption spans, and label asserted presence or absence. The second is human-verifiable: a reader without pathology training checks that these steps reflect the source publication. The third is expert-verifiable: whether the named morphology is visually correct requires a pathologist. The first two parts rely on public reporting standards and published figures and captions, and we have completed both.

We conducted a 4,000-judgment human audit of the human-verifiable steps, which found 98.4% agreement for blinded histopathology-panel identification, 95.2% for cropping, 95.0% for caption decomposition, 97.0% for panel–caption binding, and 97.2% for blinded polarity labels (Section 3.3; Appendix A.2–A.3, Tables 5–6). Every example retains its source panel and caption, so a pathologist can begin from a focused, traceable set instead of unfiltered images. Figures 2–3 show the construction process with asserted and denied examples. The labels also originate from experts: the factors are defined by ICCR and RCPath reporting standards, and each caption is the publishing authors' own description of the panel.

AuthorsOpenReview ↗

Response 2/2

Methodological novelty and significance

We see the contribution as the construction and reuse of a shared, externally defined morphology space rather than a new probing or erasure operator: the same 23 factors support cross-encoder comparison, post-hoc diagnosis of trained predictors, and a predictor built from the factors themselves.

On the comparison of encoders, we find that models with similar aggregate scores differ at the factor level. UNI2 and Virchow2 have polarity macro AUCs of 0.702 and 0.694, but UNI2 is stronger on invasive component (0.785 versus 0.651) and Virchow2 on mitotic activity (0.820 versus 0.761). Encoder–factor interactions explain 31.7% of explicit-polarity AUC variation (Section 4.3, Tables 8–9). Among the five added vision–language models, CONCH v1.5 has the highest broad and polarity accessibility of all 21 encoders (0.860 and 0.776; Section 4.1, Table 2).

On the concern that the conclusions are largely descriptive, we added a 23-factor concept bottleneck (FCB). It maps patch embeddings to named morphology scores, pools them with gated attention, and predicts only from that factor representation, so each logit is a bias plus one contribution per morphology score (Section 5.3, Figure 6). In the UNI2 COAD lymphatic-invasion model, for example, mitotic activity has the largest mean absolute contribution (0.356 logit units), and the profile changes for nodal-status prediction. A pathologist can inspect the tissue behind a contribution and question the interpretation. Predicting from only 23 named scores, the FCB reaches mean AUCs of 0.767, 0.845 and 0.881 across the 21 encoders on the three melanoma tasks (Table 11).

Additional cancer types and the size of the effects

Following your suggestion, we expanded the downstream study from melanoma to TCGA-COAD (405 slides) and TCGA-READ (141 slides), evaluated separately and pooled (546 slides). Lymphatic-invasion and nodal-status prediction add six colorectal settings to the three VisioMel tasks, giving nine settings across 21 encoders and three training seeds (Section 5.1; Appendix C.2).

With 21 encoders and nine settings, the effects are larger than in the original table. Targeted erasure reduces AUC by more than one percentage point in 291 encoder–factor–setting combinations, and the largest reductions are 4–8 points. Five random-direction erasures per encoder and setting change AUC by at most 0.624 points (Appendix C.3).

The effects also differ between predictors with nearly the same accuracy. Phikon and Phikon-v2 reach melanoma relapse AUCs of 0.791 and 0.794, but removing the mitotic-activity direction reduces them by 0.56 and 4.26 points, respectively (Section 5.1, Figure 7; Table 13). Mitotic rate is an established prognostic factor in melanoma (Thompson et al., Prognostic significance of mitotic rate in localized primary cutaneous melanoma, J. Clin. Oncol. 29(16):2199–2205, 2011), and mitotic activity has the largest encoder-averaged erasure loss of the eight factors on relapse prediction, 1.03 points compared with 0.10–0.70 for the others (Table 13).

Accessibility and sensitivity also remain largely decoupled in the new settings, as in the original submission, with a median correlation of +0.096 across all nine (Appendix C.8, Table 12).

Thank you again for the constructive feedback.

Thank you to the authors for the response. These newly added contents indeed largely address my concern, but regarding the pathologist validation, I understand that it is unrealistic to have pathologists verify such a large volume of data. However, I suggest that a small subset could be sampled for pathologists to conduct an evaluation, to see whether the overall setting is reasonable and what the overall accuracy of the captions is. However, this may not necessarily need to be completed in this rebuttal.

Additionally, this benchmark has a certain inherent bias: vision-language models will inevitably outperform vision-only models. Therefore, there is a certain gap between the conclusions drawn from this concept-based benchmark and the application to specific downstream tasks. So what does the author think is the practical significance of this benchmark?

Reviewer_9zgoOpenReview ↗
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Paper summary

The authors collect a novel benchmark for pathology foundation models, which contains representative patch data for 23 morphological factors extracted from public pathology reporting standards and PubMed image-caption pairs. With this, they expose considerable performance differences across 16 frozen encoders in predicting these morphological concepts, and also considerable differences across the morphological factors. The benchmark data is further used to determine concept components in the embedding space and to investigate the effect of removing them on downstream endpoint prediction in melanoma slides.

Critical strengths
  • (S1) Utility of the benchmark. The work is well-motivated: existing pathology benchmarks focus on coarse-grained downstream task performance, but do not measure the ability of foundation models to encode fine-grained morphological concepts. Therefore, I believe that the benchmark is a valuable contribution for assessing and improving pathology foundation models.
  • (S2) Interesting insights from foundation model evaluation. The model rankings and factor comparisons (Section 4) provide useful novel insights. Specifically, many of the evaluated models achieve very comparable performance in standard pathology benchmarks, which are likely close to saturation. In contrast, the morphological concept benchmark in this work exposes considerable model differences and also identifies factors that no model seems to encode well yet.
Critical weaknesses
  • (W1) Issues in the downstream experiments. I think that the results on concept effects on downstream model performance presented in Section 5 suffer from various limitations:
    • (i) The downstream effects reported in Table 5 are consistently small (<1pp in AUC change). For a complex target like relapse prediction, it is not clear to me that these changes are meaningful.
    • (ii) Since the prediction targets evaluated are comparably complex (esp. relapse prediction), they have many potential influencing factors. It is conceptually unclear if deleting any single morphological factor from the representations can be expected to have any outstanding effect at all. Is there any factor that, based on medical literature, the authors would have expected to have a strong influence?
    • (iii) The evaluation is only focused on one cohort and three prediction targets. Other effects may be observed for other cohorts and prediction targets, especially for simpler ones where a clear expectation about the connections between morphology and downstream target can be formulated.
    • (iv) Representations may be entangled and/or redundant: removing a specific part of the representation based on one cohort could (a) also remove other relevant information unrelated to the targeted factor that then causes some performance drop or (b) not remove all the factor information in the embedding on the other cohort.
  • (W2) Limited scope and insights. While the insights from the benchmark analysis are interesting, my impression is that the current scope of the study and therefore the resulting insights are relatively narrow and possibly too limited for publication in ICLR. I believe various interesting questions could be approached with the benchmark, e.g., further analysis on how the factors are encoded in the feature space of different models, how the representations of vision-only models differ from models trained with other data and/or targets, or if the benchmarked morphological factors can be used to discover connections between morphologies and prediction endpoints.
  • (W3) Benchmark data quality and LLM-based labeling. The benchmark is extracted from PubMed image-caption data using LLM-based pipelines, and to my understanding, no pathologist verification was performed. Despite high LLM agreement on the caption-label matching, this may introduce some label noise into the benchmark. Furthermore, the image quality (such as resolution, staining quality, artefacts, etc.) may also vary strongly. The level of noise can further vary per morphological factor, which makes comparing how well they are encoded across models more difficult. Specifically, the accessibility for a concept like “lymphovascular invasion” may also be low because of particularly high noise in this class. While I believe that the possibility of noise does not invalidate the benchmark or the results, I would still encourage the authors to explicitly discuss this possibility and the potential implications, and to qualify comparison claims accordingly.
  • (W4) [minor point] Breadth of the concept benchmark. There are likely many more relevant morphological concepts than the 23 covered. Therefore, the benchmark is still quite narrow. At the same time, I find that the benchmark is still a valuable step, as I am not aware of a comparable public dataset at this point.
Questions for authors
  • (Q1) The number of available patches per morphological factor is quite imbalanced (Table 1). How is this imbalance accounted for in the reported metrics? For example, how exactly is the AUC in Figure 1 computed? Is it balanced across classes or dominated by the most prevalent classes?
  • (Q2) How are the “context-matched” performances computed (Figure 2b)? Specifically, how did the authors obtain the relevant information about disease, organ, stain, and magnification, if the patch data were automatically extracted from image-caption pairs? And how exactly was the matching done?
  • (Q3) The authors noted that the “factor-level comparisons are sensitive to the evaluation setting” (l. 274). Why did the authors subsequently choose to report the “explicit polarity” setting for the factor-level analysis? What makes it more reliable than the “broad” setting for this type of analysis?
  • (Q4) An interesting addition (possibly for future work) may be to also evaluate models that have been trained with language supervision (i.e., pathology-specific vision--language models like CONCH). As these models may have been exposed to some degree of morphological supervision at training time, they may have stronger or more distinct encodings of the morphological concepts than vision-only models, which I believe could be an intriguing question to address.
5 comments
AuthorsOpenReview ↗

Response 1/3

Thank you for the detailed and constructive review, and for recognizing the value of a morphology benchmark that separates encoders beyond standard task performance. The revised paper evaluates 21 encoders, including the five vision–language models you proposed, across nine melanoma and colorectal settings, adds controls for the intervention and a human audit of benchmark construction, and introduces a factor concept bottleneck (FCB) predictor.

W1(i). Are the downstream effects meaningful?

With 21 encoders and nine settings, the effects are larger than in the original table. Targeted erasure reduces AUC by more than one percentage point in 291 encoder–factor–setting combinations, and the largest reductions are 4–8 points. Five random-direction erasures per encoder and setting change AUC by at most 0.624 points (Appendix C.3).

The effects also differ between predictors with nearly the same accuracy. Phikon and Phikon-v2 reach melanoma relapse AUCs of 0.791 and 0.794, but removing the mitotic-activity direction reduces them by 0.56 and 4.26 points, respectively. From UNI to UNI2, the cytologic-atypia loss increases from 1.11 to 2.07 points and the invasive-component loss decreases from 1.10 to 0.08 (Section 5.1, Figure 7; Table 13).

We also added a patch-deletion experiment, which compares deleting the patches with the highest factor scores against deleting attention-matched patches. At a 5% budget the two deleted sets differ in mean factor score by at least 0.87, while their attention mass differs by less than 0.01. The additional change in predicted probability is positive in every setting at every budget, increasing from 0.06–0.14 percentage points at 1% to 0.31–0.62 at 5% and 1.32–3.38 at 30%. At 5%, paired case-bootstrap intervals exclude zero for 141 to 168 of the 168 encoder–factor contrasts in each setting (Section 5.2, Table 4).

W1(ii–iii). Expected factors, endpoints and other cohorts

In melanoma, mitotic rate is an established prognostic factor for melanoma-specific survival after accounting for tumour thickness (Thompson et al., Prognostic significance of mitotic rate in localized primary cutaneous melanoma, J. Clin. Oncol. 29(16):2199–2205, 2011), so we would expect it to matter for relapse prediction. Our results are consistent with this: mitotic activity has the largest encoder-averaged erasure loss of the eight factors, 1.03 points compared with 0.10–0.70 for the others (Table 13).

Following your suggestion, we added lymphatic-invasion and nodal-status prediction in TCGA-COAD and TCGA-READ, which correspond more directly to the benchmark vocabulary (Section 5.1; Appendix C.2). Erasing the lymphovascular-invasion direction reduces AUC by 4.0 points for CONCH v1.5 in COAD and by 4.3 points for Lunit ViT-S/8 in READ, and erasing invasive component reduces AUC by 4.4 points for CONCH v1.5 in COAD (Table 3). CONCH v1.5 is also the encoder in which lymphovascular invasion is most accessible (0.669, Table 8).

The size of these effects varies by encoder. The profiles are reproducible across independent training seeds: eight-factor profile correlations within the same encoder and setting average 0.734 ± 0.235 (0.857 ± 0.172 in melanoma, 0.673 ± 0.238 in colorectal settings; Section 5.1; Appendix D). Accessibility and sensitivity also remain largely decoupled in the new settings, as in the original submission, with a median correlation of +0.096 across all nine (Appendix C.8, Table 12).

W1(iv). Entanglement and residual information after erasure

We added experiments for both cases.

For (a), we erase random directions with the same operator and rank as a control. The largest resulting AUC change across all encoders and settings is 0.624 points, compared with 4–8 points for the largest targeted losses (Appendix C.3), so the targeted effects are unlikely to reflect a general loss of information.

For (b), the erasers are fitted on patches from the downstream cohort, not on the literature panels. On a separate evaluation half of those patches, the median absolute correlation between the targeted factor score and its linear reconstruction falls from 1.000 to 0.024, close to the permutation reference of 0.012 (Appendix C.3). We also tested a nonlinear reader on article-disjoint literature panels. Mean MLP AUC falls from 0.642 to 0.547 after targeted erasure, compared with 0.632 after random-direction erasure, and a refitted linear probe reaches 0.493 (Appendix C.4, Table 10).

In the revised paper we describe the findings as sensitivity to factor-associated information.

AuthorsOpenReview ↗

Response 2/3

W2. Broader insights and contribution

We see the contribution as the construction and reuse of a shared, externally defined morphology space rather than a new probing or erasure operator: the same 23 factors support cross-encoder comparison, post-hoc diagnosis of trained predictors, and a predictor built from the factors themselves. We have tried to address each of the three questions you raise.

On how factors are encoded in different models, we find that models with similar aggregate scores differ at the factor level. UNI2 and Virchow2 have polarity macro AUCs of 0.702 and 0.694, but UNI2 is stronger on invasive component (0.785 versus 0.651) and Virchow2 on mitotic activity (0.820 versus 0.761). Encoder–factor interactions explain 31.7% of explicit-polarity AUC variation (Section 4.3, Tables 8–9).

On models trained with other data or targets, we added five vision–language models. CONCH v1.5 has the highest broad and polarity accessibility of all 21 encoders (0.860 and 0.776; Section 4.1, Table 2). We give more detail under Q4.

On connections between morphology and prediction endpoints, we added a 23-factor concept bottleneck (FCB). It maps patch embeddings to named morphology scores, pools them with gated attention, and predicts only from that factor representation, so each logit is a bias plus one contribution per morphology score (Section 5.3, Figure 6). In the UNI2 COAD lymphatic-invasion model, for example, mitotic activity has the largest mean absolute contribution (0.356 logit units), and the profile changes for nodal-status prediction. A pathologist can inspect the tissue behind a contribution and question the interpretation. Predicting from only 23 named scores, the FCB reaches mean AUCs of 0.767, 0.845 and 0.881 across the 21 encoders on the three melanoma tasks (Table 11).

W3–W4. Annotation validity, image quality and coverage

We agree that expert image-level judgement would greatly enhance the value of the dataset. Pathologist annotation at this scale was not available to us in this study. What we propose is a scalable way to build a partially verified dataset, so that later expert effort can be more targeted.

We divide the verification work into three parts. The first is machine-verifiable: automated extraction and consistency checks identify panels, assign caption spans, and label asserted presence or absence. The second is human-verifiable: a reader without pathology training checks that these steps reflect the source publication. The third is expert-verifiable: whether the named morphology is visually correct requires a pathologist. The first two parts rely on public reporting standards and published figures and captions, and we have completed both.

A 4,000-judgment human audit found 98.4% agreement for blinded histopathology-panel identification, 95.2% for cropping, 95.0% for caption decomposition, 97.0% for panel–caption binding, and 97.2% for blinded polarity labels. A separate model family agreed with 99.1% of 1,000 caption-derived labels (Section 3.3; Appendix A.2–A.3, Tables 5–6). Every example retains its source panel and caption, and Figures 2–3 show the construction process with asserted and denied examples.

On per-factor noise and image quality, Section 6 now states that factor-level AUCs reflect supervision quality and example composition as well as representation accessibility. Comparisons between encoders should be less affected, since all encoders are evaluated on the same panels and labels. The encoder ordering is also largely preserved when comparison panels are matched on organ, stain and magnification, with mean AUC decreasing by 0.059 at the strictest level (Section 4.1, Figure 4b). For lymphovascular invasion specifically, accessibility ranges from 0.437 to 0.669 across encoders (Table 8), so the labels do carry signal that some encoders recover better than others.

On coverage, we agree that more concepts would be valuable. The 23 factors are the result of a strict filtering process. To reduce false positives, we keep a label only when repeated labelling runs agree and discard search terms that retrieve normal anatomy or non-diagnostic material. To keep factor-level estimates reliable, we then exclude three higher-order tasks and retain only factors with at least 100 positive examples, which reduces 35 histologically assessable candidates to 23 (Section 3.1; Appendix A.1).

AuthorsOpenReview ↗

Response 3/3

Q1. How is class imbalance handled?

ROC AUC is invariant to class prevalence, so a factor's score is not inflated or deflated by how many examples it has. We compute one out-of-fold ROC AUC per factor using article-grouped five-fold cross-validation, then macro-average across factors so each contributes equally regardless of prevalence; Figure 4 reports that macro average, with error bars giving the s.e.m. over the 23 factors. Explicit-polarity probes use class-balanced training weights; broad probes use unweighted logistic regression (Appendix B.1; Table 2).

Q2. How is context matching performed?

We use context proxies: article-level MeSH disease and organ-system headings, panel-colour-derived stain categories, and caption-derived magnification. Of 11,564 source panels, organ resolves for 8,774 (75.9%), stain for all, and magnification for 7,331 (63.4%). The nested sequence selects one exact-key-matched negative per positive without replacement, matching successively on organ; organ and stain; and organ, stain and magnification. Unmatched positives are excluded. Disease matching is evaluated separately, using MeSH disease groups and up to four negatives per positive. The unmatched baseline is recomputed for each eligible subset (Appendix B.2; Section 4.1, Figure 4b, Table 2).

Q3. Why explicit polarity for factor-level comparisons?

Explicit polarity compares captions that assert a finding with captions that explicitly deny the same finding. Broad evaluation compares positives with background panels, which may contain unmentioned positives or differ in context. Eight factors have enough explicit absences for polarity evaluation. Factor rankings differ markedly between the two settings (Spearman ρ = −0.357), while encoder rankings remain strongly aligned (ρ = 0.916). Section 4.2 now explains this choice (Tables 2 and 7; Appendix B.3).

Q4. Vision–language encoders

Thank you for this suggestion. We added CONCH, CONCH v1.5, BiomedCLIP, PLIP and general-purpose CLIP. CONCH v1.5 has the highest broad and polarity macro AUCs among all 21 models (0.860 and 0.776), followed by CONCH (0.840 and 0.737); both are ahead of every vision-only encoder on the broad benchmark. General-purpose CLIP reaches 0.673 and 0.582 (Section 4.1, Figure 4, Table 2). This is consistent with your expectation that pathology-specific language supervision helps. Since the checkpoints also differ in training data and architecture, we do not attribute the difference to language supervision alone.

Thank you again for the thorough review.

Reviewer_cHV4OpenReview ↗
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Paper summary

The paper proposes a concept-based interpretability benchmark for pathology foundation models using 23 morphology factors extracted from ICCR/RCPath reporting guidelines. These concepts are grounded in ~9.7k image panels from open-access scientific literature. Across 16 frozen encoders, the authors measure linear decodability (factor accessibility) and downstream impact via linear concept erasure on a melanoma cohort (factor sensitivity). The main takeaway is that linear accessibility correlates poorly with downstream task reliance (rho ~ 0.11), showing that high probe accuracy does not mean a downstream classifier actually uses that feature.

Critical strengths
  1. External concept grounding: Deriving morphology factors from established pathology guidelines before analyzing models provides a clean, model-agnostic reference space that allows fair comparison across heterogeneous encoders.
  2. Useful empirical insight: Demonstrating that linear decodability does not imply downstream model reliance is an important cautionary result for interpretability in computational pathology.
Critical weaknesses
  1. Proxy ground truth: The supervision comes from caption text matching rather than expert-annotated image regions. Negative examples are also very sparse for some factors (e.g. only 9 absent cases for dysplasia), which makes the polarity erasure directions noisy.
  2. Limited downstream scope: The concept erasure experiments only look at one clinical dataset (melanoma) and one aggregation model (ABMIL). It is unclear whether these sensitivity patterns generalize to major epithelial cancers (like breast or colon).
Questions for authors
  1. For factors with under 20 negative examples, how stable are the erasure directions across folds, and does resampling change downstream delta-AUC?
  2. Did you evaluate whether non-linear downstream models can recover the erased concept information?
  3. Does the decoupling between accessibility and sensitivity hold in another tissue type (e.g. TCGA breast cancer)?
4 comments
AuthorsOpenReview ↗

Response 1/2

Thank you for the careful review, and for recognizing the value of a model-independent morphology reference and of separating factor accessibility from downstream sensitivity. Your questions led to several substantial additions: a human audit of benchmark construction, article-level resampling, a nonlinear recovery test, and evaluation in colorectal cancer. We also expanded the comparison from 16 to 21 encoders.

W1. Caption-derived supervision and sparse negative examples

We agree that expert image-level judgement would greatly enhance the value of the dataset. Pathologist annotation of thousands of panels across 23 morphology factors was not available to us in this study. What we contribute instead is a scalable strategy for building a partially verified dataset, designed so that expert effort, when it is available, goes only where it is needed.

We decompose the annotation and verification burden into three components:

  • Machine-verifiable. Automated extraction and consistency checks identify candidate panels, bind them to caption spans, and label whether a factor is asserted present or absent.
  • Human-verifiable. A reader without pathology training can check whether the selected panel, crop, caption span and assertion match the published source.
  • Expert-verifiable. Whether the named finding is correctly visible in the image is the judgement that requires a pathologist.

The first two components reuse knowledge already documented in public reporting standards and scientific publications, before any costly expert annotation is requested. We have now completed both. A separate model family agreed with 99.1% of the caption-derived labels in a reweighted 1,000-example audit. A human audit of 4,000 judgments found 95.2% agreement for cropping, 97.0% for panel–caption binding, 97.2% for blinded polarity assignment, and 98.4% for blinded histopathology-panel identification (Section 3.3; Appendix A.2–A.3, Tables 5–6). Every example retains its source panel and caption, so a pathologist can begin from a focused, traceable set instead of unfiltered images. Figure 2 now illustrates the extraction process for asserted presence and absence, and Figure 3 shows examples for all eight polarity factors. These checks establish fidelity to the source.

On sparse negatives, we would like to clarify one count: dysplasia has 45 explicit absent examples (Table 1, unchanged from the submission). The polarity and erasure experiments use only the eight factors with at least 30 explicit absences; lymphovascular invasion has 31, the smallest eligible count. The remaining factors enter the broad benchmark only, not polarity-based erasure (Table 1; Appendix A.1).

W2. Additional cancer types and downstream scope

We expanded the downstream study from melanoma to TCGA-COAD (405 slides) and TCGA-READ (141 slides), evaluated separately and pooled (546 slides). Lymphatic-invasion and nodal-status prediction add six colorectal settings to the three VisioMel tasks, giving nine settings across 21 encoders and three training seeds. Factor-sensitivity patterns differ across encoders and endpoints, with cohort-averaged targeted AUC losses of up to 4.4 percentage points for individual encoder–factor combinations (Section 5.1, Table 3, Figure 7; Appendix C.2).

We also added factor-ranked patch deletion, which tests whether patches identified by factor scores affect predictions beyond approximately matched baseline attention. At a 5% deletion budget, factor-ranked removal produces an additional 0.31–0.62 percentage-point change in predicted probability across the nine settings (Section 5.2, Table 4).

The erasure and deletion studies use ABMIL as the aggregator. To extend beyond it, we introduce a 23-factor concept bottleneck (FCB), a different prediction design that predicts only from the shared morphology scores and decomposes each prediction into named contributions (Section 5.3, Figure 6).

AuthorsOpenReview ↗

Response 2/2

Q1. Stability with resampled literature examples

We tested stability by resampling the source articles 20 times and refitting the polarity directions and erasers, holding the VisioMel relapse predictors, folds and patches fixed. Each resample retains 3,752 distinct articles on average, and leaves as few as 12 distinct absent examples for lymphovascular invasion, which is below the 20-example level you asked about. The encoder-averaged mitotic-activity AUC loss is 1.03 percentage points in the original fit and 0.98 across resamples; the standard deviation of encoder-averaged effects ranges from 0.14 to 0.33 percentage points across factors.

The main model comparisons hold across these literature draws: the Phikon-v2 versus Phikon mitotic-activity contrast preserves its sign in 20/20 resamples, the UNI2 versus UNI cytologic-atypia contrast in 19/20, and the UNI2 versus UNI invasive-component contrast in 18/20 (Appendix C.9, Table 13).

Q2. Nonlinear recovery after erasure

We added a nonlinear recovery experiment using a one-hidden-layer MLP on article-disjoint literature panels. After targeted erasure, mean MLP factor-label AUC falls from 0.642 to 0.547, versus 0.632 after random-direction erasure; a refitted linear probe reaches 0.493. The targeted operation therefore removes most of the above-chance signal available to a nonlinear reader as well as to a linear one. The residual nonlinear recovery is reported in full in Appendix C.4 and Table 10.

On downstream tissue patches, the median absolute correlation between the targeted linear score and its reconstruction falls from 1.000 before erasure to 0.024 afterward, close to the permutation reference of 0.012 (Appendix C.3). The downstream predictor is frozen during erasure, so these results measure the sensitivity of the trained predictor.

Q3. Decoupling in another tissue type

Accessibility and sensitivity are also largely decoupled in colorectal cancer. Across 168 encoder–factor combinations, Spearman correlations are +0.051 and +0.124 for COAD lymphatic invasion and nodal status, and +0.144 and −0.139 for READ. The three VisioMel correlations are +0.209, +0.194 and +0.096. The median across all nine settings is +0.096 (Appendix C.8, Table 12).

The colorectal experiments support the paper's central conclusion beyond melanoma: how accessible a morphology factor is in an encoder does not, by itself, predict how sensitive the trained downstream model is to removing the corresponding direction. Measuring both gives a more informative comparison of foundation models.

Thank you again for the constructive questions.

I thank the authors for the significant effort and empirical rigor demonstrated in their rebuttal.The extensive new additions successfully address several of my main methodological questions:

  1. Stability under sparse negatives (Q1): The 20x article-level resampling experiment demonstrates that polarity directions remain stable even when negative examples drop to ~12 cases (e.g., mitotic-activity delta-AUC standard deviation of 0.14 to 0.33 pp), and relative model contrasts are preserved across draws.
  2. Non-linear concept recovery (Q2): The 1-hidden-layer MLP experiment shows that targeted erasure strips the majority of above-chance signal for non-linear readers as well (MLP factor AUC falls from 0.642 to 0.547), indicating that the erasure is not trivially bypassed.
  3. Generalization across tissue types (Q3 & W2): Expanding evaluation to colorectal cancer (TCGA-COAD/READ across 546 slides) provides further evidence that the decoupling between linear factor accessibility and downstream task sensitivity holds beyond melanoma (median ρ = +0.096 across all 9 settings).
  4. Architectural extension (FCB): Introducing the Factor Concept Bottleneck demonstrates a clear constructive application of the morphology vocabulary beyond ABMIL.

Remaining Limitation: As the authors transparently acknowledge, the benchmark fundamentally relies on caption-derived proxy supervision without expert pathologist image-level annotation. While the new human audits provide useful verification of the extraction and annotation pipeline, the lack of certified visual verification on image regions remains an inherent limitation of this literature-mined approach.

Given the solid empirical additions, and because proxy ground truth remains an important limitation, I maintain my overall Rating at 3.

Thank you for your thoughtful follow-up and for recognizing the additional experiments and analyses. We appreciate your constructive feedback, which has helped us strengthen the paper, and your time and care throughout the review process.

Comments on the paper

2 comments
AuthorsOpenReview ↗

Summary of contributions and revisions

We thank the reviewers for their constructive feedback. We have uploaded a revised manuscript and provided point-by-point responses to all three reviews. Here we summarise the main contributions and revisions.

Our work seeks to make pathology expertise more accessible to ML researchers, both for evaluating foundation models and for interpreting their predictions. We make three contributions.

First, we introduce a partially verified and model-independent morphology benchmark that reuses existing expert knowledge. Clinical reporting guidelines define the factors, while published figures and captions provide image examples. We separate verification into automated checks, non-specialist human review, and expert image-level assessment. By completing the first two stages, we aim to reduce the annotation burden for subsequent pathologist validation.

Second, the benchmark provides a shared morphology reference across foundation models. Using the same 23 factors and literature examples, we compare what different encoders represent and how trained predictors respond to factor-associated interventions.

Third, we introduce a factor concept bottleneck (FCB) that predicts directly from the morphology scores. Each prediction decomposes into named factor contributions, giving ML researchers and pathologists a common basis for investigating model behaviour.

The reviews raised three main concerns: the lack of independent pathologist validation, the limited downstream evaluation, and the scope of the methodological contribution. We made the following revisions:

  • Benchmark validation: Added a human audit with 4,000 judgments covering panel identification, cropping, caption decomposition, panel–caption matching, and polarity assignment. Agreement was 95.0–98.4% across the relevant checks (Section 3.3; Appendix A.2–A.3, Tables 5–6). Figures 2–3 now illustrate the construction pipeline and representative examples.
  • Encoder coverage: Expanded the comparison from 16 to 21 encoders, adding a second family of models (vision-language models): CONCH, CONCH v1.5, BiomedCLIP, PLIP, and CLIP (Section 4.1, Table 2).
  • Downstream generalization: Added TCGA-COAD and TCGA-READ with lymphatic-invasion and nodal-status endpoints. The analysis now spans nine settings across melanoma and colorectal cancer, where accessibility and sensitivity remain largely decoupled (Section 5.1, Table 3; Appendix C.2 and C.8).
  • Intervention validation: Added random-direction controls, nonlinear recovery experiments, and literature-resampling analyses (Appendix C.3, C.4, C.9), together with factor-ranked patch deletion (Section 5.2, Table 4).
  • Interpretable prediction: Introduced the 23-factor concept bottleneck, with case-level and population-level analyses of factor contributions (Section 5.3, Figure 6).

All references in our responses use the revised manuscript's table and figure numbering.

AuthorsOpenReview ↗

Update on the revised manuscript

We thank the reviewers for their continued constructive feedback. In response to the follow-up comments, we have uploaded a new revision. The manuscript is restored largely to its submitted wording, with rebuttal edits marked in blue.

The main changes are the vision–language results in Tables 2–5, the nine-setting comparison in Table 6, Section 5.2, which condenses the original Sections 5.2 and 5.3 (now in Appendix D), the factor concept bottleneck in Section 6, and the limitations in Section 7. Our earlier summary and responses refer to the previous revision, including its description of the contributions and its section and table numbers.

We thank the reviewers and the area chair for their time.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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