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- 3
- Confidence
- 3
- Informativeness
- 2
- Presentation
- 2
- Soundness
- 2
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Paper summary
The paper asks whether aggregate AUROC reliably reflects hallucination detection performance in vision-language models, or whether simple shortcuts in the benchmark labels dominate it. Rather than proposing a new detector, it introduces three diagnostics: implementation intervals, headroom over a trivial axis, and an exact decomposition of AUROC. It applies them to four signal families (cross-modal alignment, self-consistency, external classifiers, and token confidence) on chest X-ray and general-domain datasets.
Critical strengths
An important question, approached critically. The paper does not add another detector. Instead, it examines whether current evaluation practice supports the conclusions drawn from it, which I think is a valuable contribution.
A clear central finding with a clear explanation. On the chest X-ray datasets, claim polarity alone reaches an AUROC of 0.84–0.87, even though it never sees the image. That leaves only a few hundredths of AUROC for the best detector configurations to improve on. The pair decomposition explains why: polarity alone correctly orders most hallucinated–grounded pairs.
Useful implementation-sensitivity analysis Reasonable configuration choices substantially change both the performance and the ranking of detector families. The stratified analysis is especially informative. It shows that detectors with similar aggregate AUROC can behave quite differently once the shortcut is controlled for.
Breadth of evidence. Three features strengthen the study: (1) multiple generators and datasets; (2) classifier checkpoints trained on neither corpus; (3)additional analyses on existing benchmarks (POPE, AMBER, M-HalDetect).
Critical weaknesses
1. Validity of the medical labels underlying the main result. This is my main concern.
- The medical labels are obtained by comparing RadGraph parses of generated claims against the reference reports, under a rule that treats unmentioned findings as absent. This rule creates a strong association between claim polarity and the hallucination label.
- Identifying this association is part of the paper's contribution. However, it raises a question: to what extent does the observed shortcut reflect a general limitation of hallucination detection evaluation, rather than the specific labelling procedure adopted here?
- The authors' own sensitivity analysis makes this concern more pressing. In Appendix J.9, replacing the reference parses with reader consensus on a MIMIC-CXR sample changes a noticeable share of the claim labels and substantially lowers the AUROC of the polarity-only baseline. Since this baseline is the quantity at the centre of the paper's argument, its sensitivity to the reference interpretation is important.
- The labels have not been validated against radiologist judgements, and the paper itself documents incorrect labels caused by missing laterality and missing pathology mappings (Appendix H).
- The size of the reported headroom (the gap between the best detector configuration and the trivial polarity baseline) depends directly on label validity. The results convincingly demonstrate a shortcut in the evaluated labelling setup, but more evidence is needed before the quantitative conclusions can be extended to clinically meaningful hallucination detection.
- Suggestion: an independently validated subset of claims, ideally assessed by radiologists, with the headroom analysis repeated on the corrected labels, would considerably strengthen the paper.
2. Selection of detector configurations. The admissible configurations are fixed without consulting the labels, but the best one is then chosen by evaluation AUROC.
- This introduces an optimistic selection bias.
- Families have configuration spaces of different sizes, so the bias may also differ between families and affect comparisons between them.
- Suggestion: selecting configurations on a separate validation split would address this.
3. Interpretation of headroom. A small gap between a detector's AUROC and a trivial baseline does not necessarily mean that the detector contributes little visual information. The authors themselves show that two detectors can reach similar aggregate performance while relying on different evidence and making different errors. The conclusion that small headroom rules out ranking by aggregate AUROC should therefore be stated with more qualification.
4. Few positive examples within the stratum. The absent-polarity analysis rests on relatively few hallucinated claims, especially on IU X-ray. Confidence intervals are reported, but broader evidence would help establish whether the observed ranking reversals are stable.
5. Comparability across configurations. Some classifier checkpoints can only score a subset of the claims, so parts of the implementation intervals compare performance on different evaluation populations. Suggestion: Reporting comparisons restricted to a common set of claims would make this clearer.
Questions for authors
Questions and suggestions for the authors
- Could you validate a subset of the specialist labels independently, ideally with radiologists, and repeat the headroom analysis on the corrected labels?
- How do the headroom estimates change when the best configuration for each family is selected on a separate validation split rather than on the evaluation data?
- How do the implementation intervals change when every configuration is evaluated on a common set of claims?
- Could you qualify the claim that small headroom rules out ranking by aggregate AUROC, in line with your own stratified results?
3 comments
Reply to Reviewer fNWT (2/2): ethics
Ethics — MIMIC-CXR data use.
Thank you for asking this directly; it deserves a direct answer. How the model was accessed: the two readers in Appendix J.9 and the Figure 9 candidate check were instances of Claude reached through a third-party API relay service that forwards requests to Anthropic's API — not an enterprise deployment covered by a zero-data-retention agreement. Whether the conditions were met: use of online LLM services on credentialed data has become widespread in the field — PhysioNet issued guidance on it in April 2023 and tightened it in September 2025 — but prevalence is not compliance. We subsequently contacted the relay operator, who confirmed to us that the relay platform and its upstream Claude service do not retain submitted inputs or outputs, do not use submitted content for model training, and do not subject it to human review. These statements correspond to the three conditions in PhysioNet's 2025 guidance.
Exact scope. The audit itself sent the findings sections of 404 de-identified reports with their study identifiers, in batched runs; no images were part of that step. Because your question deserves a complete answer, we also audited every local session log post hoc: between July and September 2026 the same route additionally received findings-text fragments in roughly 25 development-time prompts, roughly 100 further study identifiers (mostly directory listings echoed while debugging), and 8 in-session openings of draft figures containing report excerpts. The full itemisation is in the revised ethics statement. The reports are de-identified (HIPAA Safe Harbor; the identifiers are dataset-internal pseudonyms), and no MIMIC-CXR record-level file was included in any released material — the supplementary material contains aggregates only.
Remediation, following your comment. (1) The parse audit and the Figure 9 check were re-run entirely offline with two different open-weight models (Qwen2.5-72B, Llama-3.3-70B) on local hardware under the archived reader instruction; the revised Appendix J.9 and Figure 9 rest only on these labels (reader–reader kappa 0.61, 23/485 labels change, polarity 0.855 → 0.759, headroom +0.035, Figure 9 pool 81/244), and no Claude-produced MIMIC-CXR label is used anywhere in the revision or will be shared. (2) We have asked both the relay operator and Anthropic to delete the affected requests and not to use their content for training, supplying the identifiers of every affected request (5,233 across four sessions, July–September 2026). (3) Our pipeline now processes credentialed data with local open-weight models only. The ethics and AI-use statements disclose the incident and this policy. The IU X-ray check (Appendix J.2) used public, de-identified Open-i data and is unaffected.
Gentle Follow-up on Our Rebuttal
Dear Reviewer,
Thank you very much for your time and effort in reviewing our paper. We sincerely appreciate your thoughtful comments and understand that you have a busy schedule.
As the discussion deadline is approaching, we would like to gently follow up on our rebuttal and the additional analyses we have provided. We would be very grateful if you could take a moment to review our responses and let us know whether any concerns remain that we could further clarify.
Thank you again for your valuable time and consideration.
Best regards, The Authors
Reply to Reviewer fNWT (1/2)
Thank you for a careful review whose main suggestion — a radiologist-validated subset with the headroom analysis repeated on corrected labels — we carried out. We answer your five weaknesses, four questions, and the ethics question in turn.
W1 / Q1 — validity of the medical labels (your main concern). Two board-certified radiologists (~25 and ~20 years of chest radiology) independently rated a stratified sample of 160 IU / LLaVA-Rad claims under an analysis plan fixed before any label was collected (images first, then the reference report; blinded to rule labels, strata and scores; 5 quality-control sentences each, 10/10 passed; final-judgement kappa 0.94). Results, weighted back to the population:
W2 / Q2 — configurations selected on the evaluation labels. Two selection-independent checks: (a) selecting each family's best configuration on one IU generator and evaluating on the other leaves every headroom unchanged (+0.025 and +0.013; the two strongest families select identical configurations on both); (b) the paper's transfer table: IU-selected configurations land within 0.004 AUROC of MIMIC-selected ones. The selection bias direction also only inflates the families' best, i.e. inflates headroom — conservative for the small-headroom finding.
W3 / Q4 — interpretation of headroom. We agree and have revised the wording: small headroom means aggregate AUROC alone cannot resolve a ranking under that rule; it does not mean the detectors carry no visual information (the stratified analysis, and now the radiologist labels, show they do — and differ). The conclusion no longer says "rules out".
W4 — few positives in the absent stratum. Across the three chest X-ray cells (215 hallucinated denials in total), the mean of the per-cell discriminative-minus-cross-modal differences within the stratum is +0.222 [+0.184, +0.265], positive in every cell (+0.241, +0.249, +0.177) with every interval excluding zero. The radiologist-label reversal above shows the same ordering at the aggregate level.
W5 / Q3 — comparability across configurations. Restricting the discriminative family to the checkpoint that scores every claim ('all'; n = 2,222 / 2,389 / 2,884, identical populations), its intervals are [0.833, 0.871], [0.807, 0.863], [0.596, 0.621]. The qualitative conclusions stand: 13 of 15 chest X-ray family pairs still overlap (the two that separate are classifier vs token confidence on the IU cells), and no family is implementation-inert. The revised appendix reports both versions.