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Paper summary
This paper proposes a post-training audit that measures how well a medical image classifier's output follows an ordered clinical factor within the same diagnostic label. The proposed metric 'F' uses partial Spearman correlation between model outputs on a clinically selected spatial-frequency band and an ordinal clinical factor withheld from training. The authors evaluate 96 checkpoints across four medical imaging tasks and 11 public Breast US checkpoints. They show that models with similar diagnostic performance can have different alignment scores and report associations with robustness under image perturbations.
Critical strengths
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The paper raises an interesting evaluation question: models with similar diagnostic performance may respond differently to clinically ordered factors. The proposed audit requires only frozen-model outputs and does not need retraining or access to internal representations, which makes it applicable to existing models.
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The experimental evaluation is fairly extensive, covering four imaging tasks and multiple architectures. I particularly appreciate the statistical controls, including permutation tests, seed stability, normalization sensitivity, and patient-disjoint cross-fitting. The association with clinical-order retention after image perturbations (Table 9) is also an interesting finding.
Critical weaknesses
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I am not convinced that higher clinical-signal alignment necessarily indicates a better or more clinically meaningful model. All models are trained for binary classification, so they are not explicitly expected to produce monotonically increasing probabilities across severity grades within the same diagnostic class. More importantly, agreement with an established clinical grading system is not necessarily equivalent to better diagnosis. A model may capture useful information that is not represented by the grading system. For example, Pierson et al. (Nature Medicine, 2021, An Algorithmic Approach to Reducing Unexplained Pain Disparities) showed that deep learning could capture pain-related information from knee radiographs that conventional radiographic grades did not fully explain. The paper needs to clarify why higher alignment should be preferred and what it tells us about model quality. I also have concerns about the clinical interpretation of the anchor bands in Section 3 and Table 1. The authors select spatial-frequency bands based on clinical literature, but do not directly verify that these bands capture the intended findings, such as joint-space narrowing, lesion morphology, or microaneurysms. A high correlation with KL grade or BI-RADS does not necessarily mean that the model is responding to those specific imaging findings rather than other image characteristics.
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The practical contribution beyond existing evaluation methods remains unclear. Table 6 shows that the relationship between the proposed alignment metric and corruption vulnerability almost disappears after controlling for anchor-band AUROC ((\rho=-0.035)). In Table 15, anchor-band AUROC performs as well as or better than the proposed metric for stress-testing prioritization. The association with clinical-order retention in Table 9 is interesting, but retention is also defined using the same clinical factor rather than an independent clinical outcome. I therefore find it difficult to identify a concrete situation where this metric would lead to a better model selection or evaluation decision. The experimental design also lacks comparisons with models explicitly trained to learn ordinal relationships. Methods such as CORAL (Cao et al., 2020) and CORN (Shi et al., 2023) seem particularly relevant. Although these methods use additional ordinal supervision and are not direct replacements for a post-training audit, they would provide useful reference models for checking whether the proposed metric captures the intended behavior. Currently, the paper mainly reports differences among binary classifiers without showing whether those differences reveal a meaningful limitation or something that can be improved.
Questions for authors
1. What is the intended use of higher clinical-signal alignment?
Does it indicate better clinical reasoning, greater robustness, or simply stronger agreement with an existing grading system? If a model has better diagnostic performance but lower alignment, how should we interpret that result?
2. Could the authors validate the clinical anchor bands using actual imaging findings?
For example, in Knee X-ray, evaluating the relationship with quantitative joint-space width rather than KL grade alone would help establish whether the coarse-band response reflects the intended finding. Similar finding-level or lesion-region analyses would be useful for the other tasks.
3. What does the proposed metric add beyond anchor-band AUROC?
Given Tables 6 and 15, could the authors provide an example where models have similar full-image and anchor-band AUROC but different alignment scores, and show that this difference corresponds to an independent and meaningful behavioral or clinical outcome?
4. Why were only binary cross-entropy classifiers evaluated?
Could the authors include multiclass or ordinal classification models, such as CORAL or CORN, as supervised reference models? It would be useful to see whether explicitly learning the clinical ordering increases the proposed metric and whether that improvement is associated with other desirable model properties.
5. Could the authors report class-specific alignment rather than only the pooled partial Spearman correlation?
The current implementation residualizes global ranks on the binary label, which is not equivalent to computing Spearman correlation separately within each class. Reporting (y=0) and (y=1) results, along with their uncertainty and grade distributions, would make the interpretation clearer.
6. How should the large model differences in Table 2 be interpreted?
For example, Liver US ResNet18 has a full-image AUROC of 96.2 but an anchor-band AUROC of only 32.3 and negative anchor alignment, while its full-image alignment is positive. Could this reflect sensitivity to the band-restricted input rather than clinically undesirable behavior? The Liver US evaluation also contains only 17 independent patients, so uncertainty around this example is particularly important.
7. Could the authors clarify the numerical stability and model selection in the supplementary analysis?
Some stored softmax outputs appear to be saturated, which may affect rank-based statistics. Comparing probabilities with logit margins would be helpful. The supplementary caches also appear to include ResNet50 results outside the reported eight-backbone panel; clarification of the architecture inclusion criteria and treatment of undefined alignment scores would improve
3 comments
Thank you for your detailed response and additional analyses. After reading your response, I have been waiting for the new results to be incorporated into the manuscript, but I haven't seen an updated version over the past several days.
Could you please let me know when the revised manuscript will be available, or where I can access the additional results? I would like to review them before reconsidering my assessment.
Dear Reviewer PRSz,
Thank you for your patience, and we sincerely apologize for the delay. As this is our first experience with the ICLR discussion process, we did not realize that the revised manuscript should be uploaded together with our response. We have now uploaded the revised PDF, in which all revised or added text is shown in teal.
The additional results described in our response can be found as follows:
- Measured lesion morphology (Response 2): §6.5 and Appendix D.5 (Figure 6, Tables 20–21)
- Retraining with the fine band removed from half of the training images (Response 1): §6.6 and Appendix D.8 (Figures 8–9, Tables 28–31)
- Class-specific alignment and grade distributions (Response 5): Appendix D.1 (Table 19) and Appendix C.1 (Table 18)
- Saturation ties and the ResNet50 exclusion (Response 7): Appendices B.1 and C.2
We also added a concept-level analysis of Knee X-ray concept bottleneck models (§6.5, Appendix D.6) and probe-design sensitivity analyses (Appendix D.7), and updated the abstract, contributions, and conclusion accordingly. The original tables and figures keep their numbers, so the references in our response remain valid.
Thank you again for your careful review.
Response to Reviewer PRSz
Thank you for examining our supplementary caches and code so carefully.
1. On Why Within-Label Alignment Matters (Weakness 1 & Question 1)
We did not explain clearly enough why higher alignment is preferable. Binary models are indeed not trained to follow the grade order, which is why we check it after training. In three tasks the label is a threshold of the clinical factor (§3.1), so a model that decides from the finding responds more strongly to more severe findings. Alignment is not a quality score but a flag for models that do not follow this order. Pierson et al. (2021) trained on patient-reported pain, a subjective experience, whereas our labels and clinical factors are physicians' image-based grades or biopsy results (Table 1). Here, departing from the order means judging the same finding from other cues.
Question 1. Liver US ResNet18 has the highest full-image AUROC (96.2) but alignment −0.24, and loses 41.2 AUROC points without the fine band and 37.7 under blur, JPEG, and downsampling (Table 10). Retraining with the fine band removed from half of the training images preserved performance (97.4) and cut the corruption loss to 8.2 points, as it did for all 18 checkpoints of the two low-alignment backbones (28.2 to 9.7 points).
2. On Validating the Anchor Band with Measured Imaging Findings (Weakness 1 & Question 2)
Of our four cohorts, only Breast US (BUS-BRA) has expert lesion annotations (masks), so we measured the lesion morphology you mention there, without model outputs or BI-RADS (1 − solidity, depth/width ratio). The prespecified coarse band followed the measured findings best (6 of 8 models), alignment against the measured findings ranked the models almost identically to F_anchor|y (hereafter F; +0.976), and within the same BI-RADS grade the response still followed the findings (7 of 8). The other three cohorts lack such annotations (including knee joint-space width) and are left to future work.
3. On the Contribution beyond Anchor-Band AUROC and the Retention Endpoint (Weakness 2 & Question 3)
The covariance with A_anchor (Tables 6, 15) is correct. A_anchor might seem to substitute for F, but alignment examines whether the response follows the clinical order within a label, not the discrimination outcome; we did not explain this sufficiently. The audit's purpose is to judge black-box models using only clinical scales and forward passes (§6.4; 11 public checkpoints). A model that decides from the clinical finding responds to the anchor band much as to the full image, so both are high, which is what the audit is designed to check (Table 2).
Question 3. We did not emphasize this enough in the main text. If two models have equal full-image and anchor-band AUROC, the remaining difference is the clinical ordering within a label, and it predicts retention of that ordering under corruption (+0.475 [+0.17, +0.71] after controlling for A_anchor and clean full-image alignment, Table 9). Retention is the property itself, measured the way robustness is measured by accuracy under corruption (Hendrycks & Dietterich, 2019).
4. On Binary Training and Ordinal Reference Models (Weakness 2 & Question 4)
We should have stated this rationale. The audit is a post-hoc check of trained models, not a method for training ordinal models, so the reference factor c is withheld from training and checkpoint selection (§3.1) and grades are thresholded into binary labels (Table 1; Breast US: label pathology, factor BI-RADS). CORAL, CORN, and multiclass models use c as training supervision and cannot be audited this way; for the same reason, public Fundus models trained on the DR grade were excluded (C.6).
5. On Class-Specific Alignment (Question 5)
We computed class-specific alignment with intervals and grade distributions for all 32 cells; the conclusions are unchanged (no significantly negative cell), and the tables will be added to the appendix.
6. On Liver US ResNet18 (Question 6)
The two measurements in Response 1 reach the same conclusion without band inputs (Table 10), and alignment was negative under all three normalizations (B.3). The 17-patient limitation is stated in §5.3 and D.1.
7. On Saturation, Logit Margins, ResNet50, and Undefined Scores (Question 7)
The positive-class probability is a strictly increasing function of the logit margin, so all rank-based audit quantities are identical (B.1), and worst-case re-ordering of float32 saturation ties changed F by at most 0.039, with no sign change. No panel checkpoint has an undefined F (B.4). ResNet50 was excluded because its Liver US anchor-band output is constant, leaving F undefined.
Revisions. Lesion-finding measurements (§6.3); class-specific alignment and the scale correction (D.1); saturation and the ResNet50 exclusion (B.1, C.2).
Thank you again for the careful review. We hope this addresses your concerns and would appreciate your reconsideration of the score.