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Withdrawn from ICLR 2027

Measuring and Auditing Rubric-Induced Confabulation in VLM-Based Assessment of Human Procedural Skills

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

Procedural skills constitute core practical capabilities with pivotal importance across K-12, vocational, and higher education systems. Nevertheless, their assessment has long relied on experts scoring students' live demonstrations against standardized rubrics, which is hardly scalable. Vision-language models (VLMs) enable scalable expert-grade observation via long-video understanding. However, we find that VLMs fail to target graded operations and frequently misjudge critical devices without rubric guidance; conversely, equipped with rubrics, the models falsely mark planned procedural steps as completed actions. We name this rubric-induced confabulation a machine analogue of rater expectation bias, and trace it to recitation: the model repeats the rubric instead of reading the clip. We therefore audit each claim: deciding whether each claimed step came from the video or the rubric, formalized as conditional pointwise mutual information (CPMI) under two counterfactual interventions (removing the rubric procedure; swapping the video), and estimated either white-box from token log-probabilities or black-box from how often each claim reappears under resampling. As an outcome-validity check, higher white-box visual grounding corresponds to lower sampled support for absent steps on all four open-weight models (Spearman , ). Computed from sampled claim recurrence alone, the trust signal needs no internal probabilities and extends to closed-source models. We release a benchmark of four domains spanning K-12 science practicals and vocational skills (874 sixty-second clips, 14k step-level occurrence labels) and evaluate nine VLMs, four open-weight and five closed-source. On the four open-weight models, the rubric raises step coverage from 22% to 68% while 60–86% of the claimed steps never happened, and the false-claim rate rises from no to full rubric for every open-weight model–domain pair (+20 points on average), with an increase in 15 of 20 closed-source model–domain cells. Rubric-recited false claims recur almost as reliably as true ones, limiting detection by cross-sample consistency; under severe imbalance where true-claim prevalence is 13–27% by domain, our trust signal achieves AP at 2.0–4.0 times the corresponding prevalence baseline on the four domain averages.

Primary area:
applications to computer vision, audio, language, and other modalities
Keywords:
vision-language models, procedural skill assessment, rubric-induced confabulation, visual grounding, long-video understanding

Reviews

Among:
Shape:
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_XoxLOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper investigates rubric-induced confabulation in vision-language models (VLMs) applied to procedural skill assessment. The authors argue that providing detailed assessment rubrics can cause VLMs to report procedural actions that are not actually observed in the video.

The study introduces four input conditions (zero, weak, strong, and leak) to investigate the influence of rubric information and visual evidence. It further proposes white-box counterfactual measurements based on token log-probabilities and a black-box trust score based on repeated claim generation.

Experiments cover nine VLMs and 874 video clips across four domains. The results suggest that detailed rubrics improve the coverage of procedural steps but also increase unsupported claims. The proposed auditing method shows promising performance in identifying visually grounded claims.

Critical strengths
  1. Important and practically relevant problem.

The paper investigates a meaningful limitation of VLMs in educational and vocational assessment. The finding that detailed rubrics can improve procedural coverage while simultaneously increasing unsupported claims is interesting and potentially relevant to reliable multimodal AI systems.

  1. Counterfactual experimental design.

The strong, weak, zero, and leak conditions provide a useful framework for investigating the relative influence of task information and visual evidence. In particular, replacing the original video while retaining the same rubric is an interesting approach to identifying claims driven by textual rather than visual information.

  1. Broad empirical evaluation.

The evaluation includes nine VLMs across four domains, covering both open-weight and closed-source models. The authors also provide human validation of the claim-extraction pipeline, reporting an F1 score of 0.942. These efforts strengthen the empirical contribution.

Critical weaknesses
  1. Limited connection between the proposed evaluation and actual procedural skill assessment.

Although the paper is motivated by human procedural skill assessment, the actual evaluation primarily concerns the factual accuracy of VLM-generated procedural descriptions.

The pipeline generates captions and structured action descriptions from video inputs, extracts rubric-related claims using LLM judges, and compares those claims against binary action-occurrence labels.

This does not directly evaluate whether a learner performed an action correctly, the quality of execution, or the reliability of final skill assessment scores.

I recognize that claim-level factual grounding is a meaningful intermediate problem. Nevertheless, the paper should more clearly distinguish the proposed auditing task from comprehensive procedural skill assessment. Additional evidence connecting the auditing method to downstream assessment quality would strengthen its practical claims.

  1. Insufficient methodological detail and reliability analysis for ground-truth annotations.

The reported false-claim rates and coverage depend critically on the reliability of the ground-truth action-occurrence labels.

Appendix A.3 reports raw inter-annotator agreement ranging from 87.4% to 94.6%, but several details remain unclear, including the number and qualifications of annotators, the independent annotation procedure, the handling of temporal boundaries, and the adjudication process.

Given the substantial imbalance between occurred and absent steps, raw agreement alone may not adequately characterize annotation reliability. Chance-corrected agreement and positive-class agreement would provide useful complementary evidence.

Additionally, the Kitchen domain uses video-level annotations propagated to individual 60-second clips. As acknowledged by the authors, this may underestimate false-claim rates and overestimate coverage. The potential impact of this approximation on the reported findings deserves further investigation.

  1. Dependence on a single LLM backbone for claim extraction.

All three judging roles (lenient, strict, and reverse) use the same gpt-oss-120b model. Although different prompting strategies are employed, the judges are not independent model families.

The human validation results are encouraging. However, the robustness of the main conclusions to the choice of judge model remains unclear.

Different LLM judges may interpret ambiguous procedural descriptions differently, affecting extracted claims, assertion frequencies, false-claim rates, and the proposed trust-score rankings.

A sensitivity analysis using at least one alternative judge-model family would help establish whether the findings are specific to gpt-oss-120b or generalize across evaluation models.

  1. Insufficient justification of the number of repeated generations.

The black-box method relies on only five generated captions per input condition. As a result, claim-frequency estimates have a resolution of 0.2.

Moreover, the sampling protocol combines one generation at temperature 0 with four generations at temperature 0.5 when supported. Consequently, these observations do not necessarily represent identically distributed samples from a single decoding configuration.

While this approach is computationally understandable, the paper does not sufficiently establish whether five generations are adequate for stable trust-score rankings.

This concern is particularly relevant because some improvements over individual-input baselines are relatively modest, and the proposed method does not outperform the strongest single-input baseline in every model-domain combination.

A sensitivity analysis with larger sample sizes, such as N = 10 or N = 20, would help establish the robustness of the reported ranking performance.

  1. Potential sensitivity to video preprocessing and counterfactual video selection.

The video-processing procedures differ across model families. For example, GPT models receive only 20 uniformly sampled frames per 60-second clip, whereas other models use their respective video-processing interfaces.

Short procedural actions may be missed by sparse frame sampling, potentially affecting whether a model can visually verify an action.

I acknowledge that the authors appropriately focus their counterfactual comparisons within each model. Nevertheless, the effective visual information available to each model should be characterized more explicitly.

Furthermore, the leak condition uses an unrelated real video as the counterfactual visual input. It remains unclear whether the resulting differences reflect evidence for specific procedural steps or broader semantic compatibility between the video and the rubric.

A within-domain video-replacement analysis, or a sensitivity analysis involving alternative replacement videos, would strengthen the interpretation of visual grounding.

Questions for authors
  1. Can the authors provide additional details about the human annotation protocol, including the number of annotators, annotation independence, temporal-boundary rules, and chance-corrected agreement statistics?

  2. How robust are the claim-extraction results and downstream trust-score performance to the choice of LLM judge? Have alternative judge models or single-judge configurations been evaluated?

  3. Why was N = 5 selected for repeated generation? How do average precision and claim rankings change when larger numbers of samples are used?

  4. How sensitive are the results to the effective frame-sampling rate and the selection of counterfactual replacement videos?

  5. To what extent can the proposed auditing method improve downstream procedural skill assessment, beyond detecting unsupported claims in generated descriptions?

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

This paper investigates rubric-induced confabulation in VLM-based procedural skill assessment. While rubrics help VLMs identify more relevant actions, they may also cause models to report expected steps that did not actually occur. The authors propose counterfactual interventions on the rubric and video to measure rubric reliance and visual grounding.

Critical strengths
  1. An interesting and practically important problem. The paper studies a meaningful systematic error in VLM-based assessment.

  2. Careful consideration of potential confounding factors. The authors make efforts to control potential confounding factors. For example, they use consistent prompting across experimental conditions and explicitly instruct models to avoid hallucinations and describe only visually observable actions. This makes the experimental findings more convincing.

Critical weaknesses
  1. I have concerns about the experimental setup. GPT-5.4 only sees 20 frames from a 60-second video. I think it encourages the VLM to guess that there are more actions because it is only exposed to a very small set of frames. I know the model should not hallucinate anyway. But still, I think maybe the high false-claim rate is partly because it doesn't have enough visual information. The authors should test more frames before making general conclusions about rubric-induced confabulation.

  2. I think the paper needs more baselines. One is to directly give the video and rubric to a VLM and ask which steps happened. Another is to use another VLM to check whether the claims in the generated captions are supported by the video. These seem like some simpler solutions, and I want to know whether the proposed pipeline is actually worth it.

  3. In Appendix Table 13, removing visual grounding barely changes AP in most domains. This makes me think that most of the improvement may come from combining Strong and Weak, rather than using video replacement. Also, video replacement requires 5 more generations, but the improvement seems very small. I think the authors should compare with a simpler Strong + Weak method using a similar budget (e.g., 7+7 generations in total) without the video replacement. Another concern is that the replacement video comes from a completely different task. For example, if the original video is about a physics experiment and the replacement is about cooking, the model can easily tell they are different. This may not be a good way to test whether the model really sees a specific action.

Questions for authors
  1. Is 20 frames from a 60-second video a common approach/setting? If not, could the author try to have a test on a larger sampling rate even on a small set?
Reviewer_RDnyOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper looks at what happens when a VLM is asked to describe a 60-second clip of a procedural task while being given the scoring rubric for that task. The rubric helps the model find the steps that matter, but it also makes the model report steps that are not in the clip. The authors call this rubric-induced confabulation. To separate recited claims from observed ones, they compare the same caption under three inputs: full rubric, nouns only, and full rubric with the video swapped for an unrelated one. On open models they use token log-probabilities; on closed models they sample five captions per input and compare how often each claim recurs. The recurrence counts are combined into a trust score for ranking claims. The authors release a four-domain benchmark with step-level present/absent labels, and evaluate nine models.

Critical strengths

Expert-labeled step occurrence at the clip level across four domains is useful and will be used by others. The rubric-removal and video-swap interventions are a sensible way to ask where a claim came from. The limitations (Kitchen label broadcast, within-model comparisons only, uncalibrated score) are stated rather than hidden.

Critical weaknesses
  • The video input is too poor to tell “rubric-induced” apart from “could not see it.” Clips are downsampled to 640×360, and GPT models get 20 frames per 60 seconds, one every three seconds. The authors say themselves that the scorable evidence in the physics domains is small instrument readings and fine wiring motions. At this resolution and frame rate, a one-second switch closure or a needle deflection is not in the input at all, so the model fills the gap with the rubric. Several results in the paper fit this reading better than the rubric story. Kitchen, where actions are large and visible, is the one domain where video dominates the rubric in three of four models. GPT-4.1 on Resistance claims 97% of steps with a 72% false rate, which is what a model that cannot see would do. Gemini, which gets native video, shows almost no rubric effect on Resistance or Auto-repair. The leak test has the same problem: a claim that survives a video swap may mean the model ignored the video, or that the evidence was never visible in either video. Without an experiment that varies frame count and resolution, the attribution to the rubric is not established. The frame rate and frame count for the open models are not stated anywhere.
  • The counterfactual terms add very little over the strong-input frequency, at three times the cost. Table 13 puts the trust score at +0.02 to +0.07 AP over “strong input only”; in Table 2 several cells are flat or lower (both InternVL models on Resistance). The “2.0–4.0× prevalence” figure in the abstract therefore comes mostly from the strong frequency alone. The trust score also uses 15 generations against 5 for every baseline, and there is no budget-matched comparison (strong only, 15 samples).
  • The strong prompt makes recitation likely. It gives the full ordered procedure as “the standard correct procedure includes...” and then asks for a description. The prompt a practitioner would actually write, “for each step, is it visible in this clip, yes/no, with evidence,” is not tested. Until it is, the phenomenon may be a prompt-design artifact.
Questions for authors
  • What frame rate and frame count did Qwen3.6 and InternVL3.5 receive? Please state them.
  • Please rerun at least the two physics domains at 1 fps and higher resolution for one model, and report how the false-claim rate and the CPMI recitation signature change. If the effect shrinks substantially, the framing of the paper needs to change.
  • Please report a strong-only baseline with 15 samples so the trust score is compared at equal budget.
  • Please test a per-step yes/no prompt with the rubric. Does it show the same false-claim rate?

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

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