acceptodds
Under review as a conference paper at ICLR 2027

Do Vision-Language Models Use the Regions They Cite? A Step-Specific Intervention Test

Abstract

Vision-language models increasingly attach a bounding box to each reasoning step as the visual evidence for that step. Localization metrics measure whether such boxes match reference regions; they do not test whether the step is selectively sensitive to the region it cites. We introduce a step-specific intervention test that requires no region annotations: perturb each cited region in turn, record the change in every fixed step's mean per-token log-likelihood, and compare a step's sensitivity to its own region with its sensitivity to distinct regions cited by other steps of the same chain. Because every pair of distinct regions is compared in both directions, the expected own-region ordering probability is at most 50% under an additive step-and-region sensitivity model with row-exchangeable residuals, so a confidence interval entirely above 50% is evidence against that joint null. For Qwen3-VL-4B the own-region ordering probability is about 61% in each of three image-disjoint GQA cohorts and 72% on A-OKVQA. On the largest GQA cohort, every preregistered change of scoring context and intervention operator (removing the preceding steps, replacing blur with within-box patch permutation, or both) keeps the interval above 50% (lowest point estimate 58%). On a held-out cohort, under a protocol specified in advance, we regenerate each current step with the preceding steps held fixed. The fixed-text margin predicts the relative content change caused by blurring the step's own rather than a sibling step's region (Spearman's ρ = 0.504, 95% CI [0.402, 0.600]). The advantage is strong for GLM-4.6V-Flash on two image-disjoint cohorts, weak and cohort-variable for InternVL3.5-4B, and partial throughout: about 40% of Qwen3-VL-4B's comparisons in the three fixed-text GQA cohorts favor another step's region. A cited region is a testable claim about evidence use, not proof of it.

Primary area:
learning theory
Keywords:
Vision-language models, Localization, Grounding, Causality

Reviews

Among:
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1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_YwEnOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
3
Soundness
3
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Paper summary

The paper studies whether VLM reasoning steps are more sensitive to the image regions they cite than to distinct regions cited by other steps. It changes each cited image region and measures how that affects the likelihood of the model producing the same reasoning step. When each eligible region pair is compared in both directions, the paper’s null model predicts that a step’s own region will win no more than half the comparisons on average. Qwen3-VL-4B and GLM-4.6V-Flash show own-region advantages, while InternVL3.5-4B's results are weaker and cohort-variable. A held-out study links the sensitivity margin to relative content changes under own-region versus sibling-region blur when regenerating the current step with preceding steps fixed.

I lean toward acceptance because the evaluation is useful and the main findings have good experimental support. A more direct localization comparison and better guidance on scoring-sensitive comparisons would strengthen its practical value. Clarifying the behavioral timeline would also help me assess the study's prospective design.

Critical strengths
  1. The own-versus-sibling comparison is simple and meaningful. Using other regions from the same chain as controls is more informative than just showing that a perturbation affects the text. It needs no region annotations, and the authors are clear about its limits.

  2. The evidence spans several cohorts, and for Qwen the advantage survives preregistered changes to the scoring context and intervention operator. The held-out generation test is a useful addition. Planned and exploratory analyses are clearly separated, and the documented protocol freezes and re-implementation checks strengthen the reproducibility record (Appendix J).

Critical weaknesses
  1. The empirical relationship to localization remains underexplored. Appendix E uses best-object IoU, which need not establish overlap with the referent actually described by a step. The planned robustness-cohort localization breakdown was also not implemented (Table 12). On a subset of steps with an unambiguous object referent, comparing sensitivity with localization against that referent would help explain what the assay adds in practice, given Section 6's recommendation against reporting localization alone.

  2. Individual results depend on how the score is calculated. Scoring only the content tokens changes whether the cited region wins in 13–22% of comparisons in the Qwen robustness cohort, even though the overall advantage remains (Table 6). This makes individual results harder to interpret. The authors rightly avoid treating one loss as evidence that a step is unfaithful. Looking at how the generated text changes in cases where the two scoring methods disagree would help clarify how to use these scores in practice.

Questions for authors
  1. Appendix I (p. 24) mentions "earlier behavioral attempts" separately from the technical set and describes one pre-generation runtime abort. Were these attempts all part of the run that stopped before generating any output, or were there other runs? If additional runs produced outputs, when did this occur relative to the protocol freeze, and did those outputs inform the endpoint or analysis plan?

  2. On the held-out behavioral cohort, how often do full-token and content-only scoring disagree on the win/non-win outcome? If there are enough cases, does either margin predict the relative content-change contrast within that subset? Reporting the subset size and uncertainty would help; Table 10's overall correlations do not resolve this question.

  3. Could you include the fourth GQA cohort's fixed-text ordering estimate in Table 1, labeled descriptive: 0.557, 95% CI [0.498, 0.616] (Section 4.3; Appendix I)? It was not a prespecified replication, and its interval is compatible with the earlier estimates. Showing the four cohorts together would make the overall evidence easier to assess.

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

The paper asks whether a VLM's reasoning step depends more on the image region it cites than on regions cited by other steps. It perturbs each region and compares the resulting changes in the likelihood of the fixed step text. The paired design gives a conditional reference for interpreting this comparison. Experiments find a partial, repeatable advantage for Qwen3-VL-4B, with different results across checkpoints. A separate study shows that the likelihood margin also predicts relative content changes when the current step is regenerated.

Critical strengths

1.The comparison within each chain is carefully designed. Earlier region-masking work such as CRM already examines changes in reasoning after removing annotated evidence. This paper tests the model's own region claims against sibling claims while holding the target text fixed. Proposition 1 makes the assumptions behind the reference level explicit, and the paper acknowledges that a positive result does not establish semantic evidence use or identify an internal reasoning mechanism.

2.The main finding is supported by more than one favorable evaluation. Qwen's ordering probability is around 0.61 across three image-disjoint GQA cohorts, and the advantage survives both removing the preceding steps and changing the perturbation operator. The held-out behavioral correlation of 0.504 [0.402, 0.600] gives the score a concrete connection to generated content. These checks support the reproducibility of the reported effect under the specified assay.

Critical weaknesses

1.While the proposed assay differs from the grounding and intervention-based evaluations cited in the paper, I am less convinced of the additional insight it provides. Prior work, including FPVG, counterfactual editing, and CRM, has already examined whether visual answers or explanations depend on the proposed evidence. The own-versus-sibling comparison offers a more specific test, but it remains unclear to me what substantive understanding we gain from its findings beyond those earlier studies. This limits my assessment of the paper's significance, despite the care taken in designing and validating the assay.

2.Two gaps limit how directly the observed advantage informs us about the originally generated reasoning. First, in Table 3 the joint diagnostic passes in all 300 synthetic cohorts under a conflicting mixture of additive and proportional effects, despite there being no matching term. This is acknowledged and does not contradict Proposition 1, but the anchor-weighted and anchor-stratified analyses do not establish how much such a mixture could explain the real-data advantage. Second, Appendix A removes the bounding-box fields from preceding steps, and the behavioral study uses this edited prefix as well. Only 369 of 548 behavioral comparisons have an unperturbed regeneration matching the stored step's content units (Appendix I). The stronger correlation on this aligned subset is reassuring, but the persistence of the ordering advantage under the original generation prefix remains untested. These concerns qualify the interpretation of the effect rather than invalidate its measurement under the specified protocol.

Questions for authors

1.Beyond the anchor-weighted diagnostic and anchor-stratified results, can the measured whole-image sensitivities and regions' effects on other steps help assess how much of the observed advantage could arise from the mixed nuisance structure in Table 3? For example, does the advantage persist after matching or explicit adjustment using these quantities, with the target comparisons excluded from nuisance estimation where feasible? Please clarify the assumptions needed to interpret the resulting comparison.

2.On the same chains and region pairs, does the ordering advantage persist when the exact original generation prefix, including preceding step-and-box records, is retained and only the current step's text is scored? How much does the advantage change, and how does this affect agreement between unperturbed regeneration and the stored step?

Reviewer_mkKeOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
3
Soundness
3
Read review
Paper summary

This paper explores whether the image regions referred to by vllm during step-by-step reasoning are intervention-sensitive to the corresponding step outputs. The authors propose an evaluation method which requires no manual region annotations; they perturb regions referred to by different steps independently in the same reasoning chain and measure the change of the average token log-likelihood of each fixed step text. They compare the sensitivity to its own referred region for each step to the sensitivity to the regions referred to by other steps. The paper also derives a theoretical reference value for this comparative metric under a specific null hypothesis.

The experiments are conducted on GQA and A-OKVQA. The results suggest that among the analyzed samples, Qwen3-VL and GLM are more sensitive to their own cited regions, whereas InternVL has a weaker advantage that varies across samples. The authors evaluate the robustness of these findings by employing different perturbation operators, scoring contexts and using independent sample groups. They also find that the sensitivity difference measured on fixed text corresponds to changes in the content of the current step when it is regenerated with the preceding context held fixed.

Critical strengths
  1. I find the research question compelling and appreciate the motivation for your choice of controls. I especially appreciate the distinction you make between localization accuracy for regions that are correctly identified and sensitivity to interventions on those regions. Controlling for other steps that cite a particular region in the same reasoning chain seems more informative than simply measuring the impact of intervening on the region identified by a particular step. It also addresses the concern of regions that are generally important or steps that are generally sensitive to perturbations. Your paper presents an interesting take on evaluating vllms.

  2. The main empirical claim is supported by multiple validity tests. First, the results are consistent across different independent sample groups, and distinct perturbation operators and scoring contexts. Second, repeating individual steps with a varying preceding context allows linking the metric to model output variation through context. Finally, it is commendable how the authors highlight the limitations of statistical significance testing, sample filtering procedures, and what the metric does not say about the semantic use of evidence. All these validity tests and transparency about the approach’s limitations add up to a substantial level of support.

Critical weaknesses
  1. My main question is whether this metric can differentiate between a model actually being using a region for reasoning and just emitting a description that matches that region. For example, the model could generate an answer first, and then add a sentence describing an object in the image. Blurring that object would lower the probability of this sentence, but would not demonstrate that the model used this step to come up with its answer. The authors note this limitation in the metric, and in section 4.3, argue that the metric is tied to changes in regenerated content, but I would want to see a controlled experiment where known evidence dependencies would be used in order to see what sorts of meaningful reasoning behaviors this metric would actually capture beyond just measuring correspondence between text and image regions.

  2. The paper finds substantial differences across the models, but it is unclear what those differences are. The models have different reasoning steps and boxes, and the samples eventually chosen as part of the evaluation are also different. This makes it hard to tell if higher scores reflect more reliable use of evidence from the text or just differences in style of outputs and selection of samples. In section 4.7, the authors also show that removing JSON formatting tokens alone would change 13%–22% of individual comparison outcomes, albeit with stability in the aggregate. It is unclear to me how helpful this approach is in terms of diagnosing evidence-use issues at the level of individual steps rather than finding aggregate patterns. I would want the paper to make clear what problems this metric helps uncover or what insights it gives us about the behavior of these models.

Questions for authors
  1. If a model first settles on an answer, and then creates an explanation and evidence boxes of this answer matching with the image, would the suggested metric still show a big advantage for own-region? And how would the authors interpret the score, and its connection to using evidence during reasoning? Do the presented results give us anything that could differentiate between this case and when the cited regions were actually used to get to the answer?

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

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