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Under review as a conference paper at ICLR 2027

Performance Without Evidence: A Placebo-Controlled Audit of Medical Foundation Model Adaptation

Abstract

In few-label adaptation of medical foundation models, AUC gain is routinely read as evidence that the model has learned the target pathology. We show that this inference is unsafe and argue that standard adapters frequently achieve high performance by covertly exploiting spurious artifacts rather than genuine lesions. Because purely observational metrics cannot expose this shortcut, we introduce a Placebo-Controlled Auditing framework to isolate true grounding by verifying that predictions degrade when the actual lesion is occluded, yet remain stable otherwise. The protocol first measures causal reliance with a paired counterfactual intervention that occludes the annotated lesion against a shape- and texture-matched control. It then validates that measurement with a lesion-free placebo: the identical comparison with no lesion present, which must stay silent for the intervention score to mean lesion reliance. Across eight public task beds and six frozen encoders per bed, standard adaptation raises AUC substantially, yet the trained adapter stays statistically indistinguishable from a prior-matched, gradient-free null in 44 of 48 cells. Because the capacity for grounded transfer cannot be reliably predicted by encoder provenance, it must be explicitly measured and enforced. To address this, we act via Counterfactual-Consistency Adaptation (CCA), which translates the validated causal contrast directly into a training constraint. CCA successfully forces reliance on genuine lesions, raising both causal evidence and external AUC on every CXR-domain encoder while outperforming six mask-matched baselines. Causal reliance is measurable, unpredictable, yet trainable once validated—positioning our measure–validate–act loop as the reporting standard for label-scarce clinical adaptation. The code is available: https://anonymous.4open.science/r/calm_official-08B4/README.mdhere.

Primary area:
interpretability and explainable AI
Keywords:
medical foundation models, few-shot adaptation, causal evaluation, interpretability, counterfactual intervention

Reviews

Among:
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1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_f6kCOpenReview ↗
Rating
1
Confidence
2
Informativeness
2
Presentation
1
Soundness
1
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Paper summary

The authors investigate whether downstream models trained from radiology foundation models with a few annotated data samples learn biologically reasonable features. Specifically, they measure the prediction score change of samples with a lesion when the lesion region is occluded and compare it to prediction score changes when arbitrary regions are occluded. They find that in most cases, these prediction score changes/focus on correct regions do not increase despite increasing prediction task AUC. They further find that trained adapters (linear probe, attentive pooling, LoRA) often do not outperform training-free centroid-based baselines. Finally, they formulate an auxiliary loss based on the samples with occluded regions that leads to an improvement in the model's focus on the correct regions.

Critical strengths
  • (S1) CCA attribution performance. The authors provide evidence that the CCA auxiliary loss seems to make the model focus on correct regions and improve model generalization performance (improved evidence peak inside the localization). This indicates that the method is actually useful for its intended purpose.
Critical weaknesses
  • (W1) Effect of counterfactual intervention. The authors compute counterfactuals by overwriting a region of interest or sampled control region with a “local ring-mean fill”, which seems to result in a monotonous grey pixel area (see Figures 1, 3). I believe that this likely introduces unnatural image artefacts. Therefore, the counterfactual generation method may easily take an image out of the training distribution, which makes the representation of the image produced by the image encoder unpredictable and potentially unstable. Therefore, it is unclear if the resulting representation is still suitable for making a reasonable prediction. Similarly, any adapter trained from the unmodified medical images has not seen any of these grey patches at training time, so that an image with a grey patch at test time may result in unpredictable behavior. Overall, the resulting model prediction scores may not be interpretable. This renders any derived downstream measure (such as the evidence, the placebo scores, the win rates) potentially unreliable. To my understanding, the choice of the local ring-mean fill method is not discussed, and there is no evidence provided that the resulting images lead to reasonable representations/predictions, despite the availability of alternative occlusion methods and literature studying the effects of them (see, e.g, [1]). Without additional discussion and/or validation, I believe that there may not be sufficient evidence for the derived claims.
  • (W2) Broad framing. The abstract and introduction frame the study as a general approach targeting medical foundation models. However, to my understanding, the main evidence is purely focused on binary detection tasks in radiology. How would this framework extend to, for example, multi-class classification, regression, time-to-event prediction, or other medical modalities beyond 2D chest radiography (and retinal fundus photographs)?
  • (W3) Reliance on region-of-interest annotations. To my understanding, both the measuring framework and the CCA method rely on region-of-interest annotations for positive samples. For the latter, these are used as additional labels in the training process. In this sense, the improved external AUC and localization performances may also just be a result of using additional labels compared to the adapters that are trained purely on the classification labels. An additional baseline that uses the annotations as a direct supervision signal, if available, would be helpful to clarify the added benefit of the CCA loss formulation.
  • (W4) Presentation. Personally, I struggled to understand many parts of the paper, as I found it difficult to read. The authors use plenty of previously unintroduced terminology that made it hard for me to follow the train of thought and to understand the details. For example:
    • “Table 1 reports partial Spearman correlations against external AUC” -- This is the first mention of external AUC, and it is unclear to me how it is computed and why it is correlated to the introduced metric.
    • “Calcification lesions carry higher edge energy than their paired controls (d = +0.80; Appendix D.5), so absolute win-rates are instrument-relative” -- What does “edge energy” mean? What “instrument” do the authors refer to in “instrument-relative”?
    • “Because the scope condition lacks a priori predictability, CCA serves as an empirical test of whether the audited quantity is causally actionable” -- What is the “scope condition”? What is the “a priori predictability” in this context?

[1] Bluecher et al.: "Decoupling Pixel Flipping and Occlusion Strategy for Consistent XAI Benchmarks." TMLR, 2024.

Questions for authors
  • (Q1) Outperforming the gate-0 method. The authors claim regarding the gate-0 method that “outperforming it is therefore a mathematical necessity, not a mere target. Failing to beat gate-0 implies the adapter extracts no novel features beyond first-order class statistics, regardless of its absolute AUC.” However, to my understanding, the features used to compute this gate-0 are deep representations from the feature encoders. Why are these considered “first-order class statistics”? A reason why an adapter may not outperform this baseline could be that the encoder produces strong representations that make positive and negative class samples easily separable in feature space. In this case, would this not be a strength of the encoder rather than a failure mode of the adapter?
  • (Q2) Adapter evaluation. The authors mention that they compare “three adaptation depths (linear probe, attentive pooling, LoRA)”. How were the results presented in Table 1, Figure 2, Table 2, and Table 3 computed? Which adaptation method was used here? Or are they aggregated results across adapters? Or are those results from the gate-0 / gate-0b baselines?
Reviewer_2JFwOpenReview ↗
Rating
2
Confidence
3
Informativeness
3
Presentation
3
Soundness
2
Read review
Paper summary

This paper investigates whether performance gains from few-label adaptation of medical foundation models reflect genuine reliance on the target pathology or instead arise from spurious correlations. It proposes a Placebo-Controlled Auditing framework with three components: (1) a prior-matched, gradient-free baseline (gate-0) to contextualize the gains of learned adapters; (2) a paired counterfactual occlusion test comparing score drops for an annotated lesion and shape- and intensity-matched control regions; and (3) a lesion-free placebo test intended to identify cases in which the measured evidence may reflect generic sensitivity to occlusion rather than lesion-specific reliance. The paper further introduces Counterfactual-Consistency Adaptation (CCA), which incorporates the lesion-versus-control score contrast into the training objective.

The evaluation spans eight public task beds, six frozen encoders per bed, multiple adaptation strategies, few-shot budgets, and external evaluation cohorts. The authors report that standard adapters are statistically equivalent to the gate-0 baseline within a 0.03 AUC margin in 44 of 48 cells, despite improvements in classification AUC. They also show that causal intervention scores and saliency-based localization can disagree substantially. CCA improves intervention-based evidence and external AUC for the evaluated chest-radiography-domain encoders, while its benefits are not consistent for natural-image encoders. Overall, the paper argues that classification performance alone is insufficient to establish pathology grounding and advocates measuring and validating grounding before attempting to enforce it during adaptation.

Critical strengths
  1. A carefully structured audit that goes beyond conventional classification metrics.

The paper makes a useful distinction between predictive performance, intervention-based lesion reliance, and saliency-based localization. The combination of a prior-matched baseline, paired lesion/control occlusion, and a lesion-free placebo is a meaningful methodological contribution. In particular, the placebo addresses an important failure mode: an apparent intervention effect may reflect generic sensitivity to regional perturbations rather than specific reliance on the target finding. The experiments showing disagreement between classification, intervention, and localization metrics make a compelling case for evaluating these properties separately.

  1. Broad empirical evaluation and an actionable extension to training.

The evaluation covers eight public task beds, multiple frozen encoders, different adaptation strategies, and external cohorts. The authors also examine statistical dependence across seeds and conduct several sensitivity analyses. Beyond proposing a diagnostic protocol, the paper introduces CCA and compares it against mask-matched baselines. The reported improvements in intervention scores and external AUC for chest-radiography-domain encoders suggest that the proposed audit can inform a practical training intervention, rather than serving only as a post-hoc explanation metric.

Critical weaknesses
  1. The causal interpretation of the occlusion contrast depends on assumptions that are only approximately satisfied.

The central claim is that subtracting the score drop from a matched control region isolates lesion-specific reliance. However, Proposition 1 assumes that the nuisance component of the occlusion effect depends on region shape and local texture statistics. The implementation matches region shape exactly but primarily screens controls using local mean intensity; the authors themselves report a substantial residual difference in edge energy for calcification lesions (paired Cohen’s d = +0.80). More fundamentally, occlusion with a local ring-mean fill is an out-of-distribution intervention, and matching local statistics may not control for anatomical context or interactions between the lesion and its surroundings. The placebo is a useful diagnostic, but a quiet placebo does not by itself establish that the remaining contrast is a causal effect specific to the pathology. This limits the strength of the paper’s central causal claims and the interpretation of the resulting score as validated lesion reliance.

  1. The generality of the proposed training method is not yet established beyond a relatively narrow set of settings.

CCA requires spatial annotations for the positive training examples, so it addresses a more supervision-intensive setting than image-label-only adaptation. Although the paper includes six mask-matched baselines, its strongest external-AUC results are concentrated in chest-radiography-domain encoders, whereas the natural-image controls exhibit negative external-AUC changes despite improved intervention scores. The evaluation also relies heavily on chest radiography, with only one fundus task bed for cross-modality evidence. These results support CCA as a promising, conditional intervention, but do not yet establish that increasing the proposed grounding score reliably improves transfer across modalities or encoder families. The paper acknowledges some of these limitations, but the broad framing of the method as a general solution to ungrounded adaptation should be more carefully qualified.

Questions for authors
  1. How strong is the evidence that the proposed contrast measures lesion-specific causal reliance rather than residual artifacts of the intervention?

The theoretical cancellation argument assumes that nuisance effects are determined by region shape and local texture statistics, yet the implementation does not fully match higher-order texture and anatomical context. Could the authors provide a more direct validation against an independent reference, such as controlled lesion insertion/removal or a synthetic setting in which the true causal signal is known? In particular, how often does the audit produce a positive result when the model relies on contextual features that are correlated with, but not contained in, the annotated lesion?

  1. How should the placebo-based reporting rule be used when external labels are unavailable?

The paper defines reportable cells using the relationship between evidence scores, placebo scores, and external AUC. However, estimating these correlations requires external labels, which appears to limit the audit's use as a practical model-selection rule in genuinely label-scarce transfer settings. Can the authors clarify which components of the proposed protocol can be applied without external labels and what guarantees, if any, remain when the evidence–transfer relationship cannot be estimated?

  1. How sensitive are the main conclusions to the choice of the gate-0 equivalence margin and the use of spatial supervision?

The claim that 44 of 48 cells are equivalent to gate-0 depends on a 0.03 AUC equivalence margin. Could the authors clarify the rationale for this margin and report whether the main conclusion persists under alternative practically meaningful margins? Additionally, since CCA requires masks or boxes for positive training samples, how does its benefit compare with image-label-only adaptation when annotation costs are accounted for explicitly, rather than only against mask-matched baselines?

The first two questions are the most consequential for my assessment; the third would help clarify the practical scope of the claims.

Reviewer_GAecOpenReview ↗
Rating
3
Confidence
2
Informativeness
3
Presentation
3
Soundness
3
Read review
Paper summary

This paper investigates whether performance gains from few-label adaptation of medical foundation models are accompanied by reliance on the target lesion. The authors propose a Placebo-Controlled Auditing framework organized around measure–validate–act: gate-0 and gate-0b provide prior-matched controls based on class centroids; a paired counterfactual intervention compares lesion and matched-control occlusion score drops; and a lesion-free placebo compares non-lesion control regions within the annotated positive images. Counterfactual-Consistency Adaptation (CCA) then incorporates the paired contrast into the training objective.

The experiments cover eight task beds, multiple frozen encoders, and several external datasets. The results demonstrate dissociations among classification AUC, intervention win-rate, saliency localization, and external AUC. CCA improves both intervention win-rate and external AUC in some configurations. The authors also report configurations with negative external AUC changes and unsuccessful evidence-gated selection experiments.

The main contribution is the auditing perspective and its systematic empirical validation. CCA further tests whether the audited quantity can guide a useful training intervention.

Critical strengths

S1. The research question is important, and the method provides a clear connection between auditing and intervention.

The paper directly examines whether improved classification performance implies reliance on the target region, and then studies the effects of explicitly increasing that reliance. Paired controls, the placebo, and CCA form a coherent experimental framework that offers a useful perspective on the interpretation of adaptation gains in medical imaging.

S2. The experiments are extensive and examine alternative explanations across diverse tasks and representations.

The authors include label shuffling, off-target adapters, control-region resampling, alternative occlusion operators, perturbed training masks, and supervision-matched baselines. Experiments across tasks, encoders, and external sites reveal substantial heterogeneity. The explicit reporting of unsuccessful configurations and model-selection failures helps readers assess the scope of the findings.

Critical weaknesses

W1. CCA's effects beyond the selected controls remain unexamined. Figures 4, 8, and 12 and Appendix H.3 show changes in lesion and control responses, but do not compare these changes with those for eligible candidate regions excluded from selection. Whether CCA strengthens lesion reliance relative to this broader set remains unresolved.

W2. The contribution of control count and aggregation remains unclear. Equation (3) compares the lesion score drop with the mean of three controls, allowing individual controls to exceed the lesion. Appendix D.6 varies candidate-pool size for λ=0 probes, but does not test these training choices in CCA.

Questions for authors

Q1. Does CCA increase lesion reliance beyond the selected control comparisons? Please use the existing CCA and optimizer-matched λ=0 models to compare changes in occlusion score drops on held-out images for lesion regions, the three selected controls, and additional eligible candidate regions. Report the proportion of additional candidates with smaller score drops than the lesion, alongside external AUC gains.

Q2. How do control count and aggregation affect CCA? To separate their contributions, I suggest comparing the original three-control mean with a larger-control mean and, using the same larger set, separate hinge penalties for each lesion–control contrast or a penalty against the control with the largest score drop. Keep other settings fixed and report external AUC and intervention win-rate.

Minor corrections:

  1. Figure 14, page 56, lines 2991–2993: The caption states, “The scatter visual plots Δles directly against Δctl,” and subsequently refers to points “above the diagonal.” The figure actually shows overlaid histograms.
  2. Figure 17, page 58, lines 3128–3130: The caption states, “The grid spans six public beds, six encoders, and their corresponding public external sites.” The figure displays the primary calcification bed across six encoders and two external sites.
  3. Page 7, line 357: A closing parenthesis is missing in “all encoders (Tables 31, 33. The two pneumothorax beds…” Please change this to “all encoders (Tables 31, 33). The two pneumothorax beds…”

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