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Under review as a conference paper at ICLR 2027

Multimodal-CL-Bench: A Benchmark for Multimodal Context Learning

Abstract

Can multimodal large language models (MLLMs) learn new knowledge from multimodal context and apply it downstream, rather than merely perceiving and retrieving information already in their weights? We formalize this capability as multimodal context learning (MCL) and introduce Multimodal-CL-Bench to evaluate it. The benchmark contains 344 self-contained multimodal contexts—spanning text, images, and videos—with 1,080 tasks and 7,309 fine-grained rubrics. Rather than grouping cases by surface domain, we organize them by the form of contextual learning required, yielding four categories and 20 subcategories that support diagnostic, capability-level evaluation. Cases are built via expert design and a controlled agent-based synthesis pipeline that minimizes pretraining contamination. Evaluating eight frontier MLLMs uncovers three findings: (1) none of the original eight models exceeds 13% task-level success, with the best reaching only 12.8%; (2) context-tracking failures and modality misgrounding are the most frequent annotated error types; (3) scaling test-time reasoning does not reliably help—Thinking variants do not consistently outperform their base models. These results suggest that the central bottleneck of MCL is stable evidence-state organization across heterogeneous modalities, rather than perception capacity or reasoning length.

Primary area:
datasets and benchmarks
Keywords:
Multimodal Large Language Models, Multimodal Context Learning

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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_niY2OpenReview ↗
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Paper summary

This paper introduces Multimodal-CL-Bench to evaluate whether multimodal language models can acquire case-specific knowledge from context and apply it in subsequent tasks. The benchmark contains 344 contexts, 1,080 tasks, and 7,309 rubric criteria, organized into four capability categories and 20 subcategories. Cases combine expert construction and controlled synthesis. Evaluation uses strict all-criteria task success judged by GPT-5.2.

Critical strengths
  1. The benchmark targets a practically relevant capability: applying newly supplied local rules to heterogeneous evidence over multiple tasks. Its four-category taxonomy, combination of expert and synthetic cases, and detailed rubrics provide a substantial resource for studying failures that conventional perception-focused benchmarks may miss. The construction procedures explicitly address distractors, exceptions, and context-dependent rules, which are useful design features for this goal.
  2. The paper provides more than a single leaderboard. Appendix G performs a paired multimodal-evidence ablation on 551 tasks, with average success decreasing from 6.15% to 2.52% when visual evidence is removed. Appendix I extends the evaluation to two Kimi models, reporting 12.87% task success for K2.6 and 22.31% for K3. These analyses provide useful evidence that the inputs matter and that the benchmark can distinguish improvements, rather than placing all models at an identical performance floor.
Critical weaknesses

All-or-nothing scoring jointly evaluates semantic correctness, completeness, and format compliance, while rubric counts vary substantially across categories (Table 1). Consequently, low pass rates and category differences may partly reflect the number and strictness of requirements, complicating the capability-level conclusions drawn from these results.

Questions for authors
  1. What are the exact aggregation formulas and success counts for Table 2 and Figure 6? Are scores micro-averaged over tasks, macro-averaged over contexts, or based on a case-level pass criterion? Please reconcile these values and recompute comparisons using one consistent unit.
  2. What is human judge agreement on a stratified sample, particularly for responses rejected by a single criterion?
6 comments

Thank you for recognizing the value of local-rule tasks, evidence ablation, and distinguishing model improvements. Your questions concern the interpretation of complete-task success and the reproducibility of aggregation.

1. Why retain all-or-nothing scoring?

We adopt all-or-nothing scoring based on the characteristics and evaluation objectives of context-learning tasks. Beyond answering conventional knowledge questions, context learning requires models to understand new knowledge in the supplied context and accurately integrate and apply it to complex tasks with multiple constraints.

First, our primary objective is to measure whether a model can solve a task completely and reliably, rather than merely satisfy some requirements. In practical applications, task constraints are often interdependent: omitting or misapplying a key rule can make the final result incorrect. Simply averaging satisfaction across criteria may therefore overstate the model's ability to solve the task.

Second, all-or-nothing scoring provides a stricter test of the integrated application of contextual knowledge. A model succeeds only when it satisfies all predefined grading criteria. This avoids assigning a high task score solely for partial understanding or locally correct reasoning and better reflects the completeness and reliability required by complex tasks.

This setting is also consistent with CL-Bench (Dou et al., 2026), which uses binary task-level scoring: a task is considered solved only when the response satisfies all associated rubrics. We follow this evaluation principle to distinguish complete task success from partial requirement satisfaction. See the official CL-Bench evaluation description.

Rubric-level satisfaction complements this metric by showing partial correctness, while task success stratified by rubric count examines how requirement count relates to performance. Neither replaces complete task success. Rubric-level statistics are restricted to records with equal rubric and judgment-entry counts; model coverage differs, so these are not rankings on a common subset. Results are provided in Rubric-level diagnostics.

2. Aggregation formulas and success counts

Thank you for highlighting the need to clarify the aggregation scope. The original Overall values in Table 2 cover the first-turn tasks of 344 cases, whereas Figure 6 covers all tasks within each source track. We will consistently use task-level micro-averaging: the number of successful tasks divided by the corresponding total number of tasks. The denominators are 1,080 for the full benchmark, 325 for the expert-collected subset, and 755 for the synthetic subset. Per-model success counts and reproducible aggregation records are provided in the supplement.

For any task set SS, the metric is Am(S)=∑t∈Ssm,t/∣S∣A_m(S)=\sum_{t\in S}s_{m,t}/|S|, where sm,ts_{m,t} is the stored binary task score and missing scores count as end-to-end failures. Figure 6 uses the source-specific denominators of 325 and 755, rather than averaging case-level scores. Full-benchmark success counts are:

ModelSuccessful tasks / 1,080
Opus Thinking135
Opus114
Sonnet Thinking141
Sonnet140
Gemini-3.1104
GPT-5.2116
Doubao82
Gemini-2.579

Reproduction retains stored scores. One Gemini-2.5 record has a score/status conflict; status normalization gives 78/1,080, and the supplement reports this sensitivity result separately. Full reproduction and source-track records are in Task-level scores and reproduction materials.

Our core observations remain under consistent aggregation: complete task success remains challenging, and the gains from Thinking are not consistent across models. The Thinking variant improves Opus by 1.94 percentage points, while the gain for Sonnet is only 0.09 percentage points. These results indicate that additional reasoning does not automatically translate into more reliable learning and application of contextual rules. We will clarify the original statement as “Thinking does not consistently improve performance” and update the numerical results and rankings accordingly.

3. Author review and single-requirement failures

We have an existing targeted author review of 100 responses, covering unanimous passes, unanimous failures, and disagreements among the three judges. The review examines whether responses actually satisfy explicit task requirements and whether partial or implicit satisfaction is incorrectly accepted as complete satisfaction. Disagreement examples and their grading rationales are included in the anonymous supplement.

For responses failing because of a single rubric, we focus on the substantive role of that requirement. Violating a case-local rule, citing evidence that does not support the conclusion, or omitting a necessary state update can prevent correct task completion even when all other requirements are satisfied. Conversely, synonymous wording, formatting differences not explicitly constrained, or harmless additions that do not change the evidential basis should not automatically cause failure. All-or-nothing scoring should therefore enforce explicit task requirements rather than mechanically match wording.

To make these boundary cases inspectable, we provide per-requirement satisfaction, counts of single-requirement failures, and representative responses with grading rationales. The existing review does not separately report human agreement for this stratum. We distinguish the available qualitative review from stratum-specific quantitative statistics and do not substitute three-judge agreement for judge–human agreement.

Materials: Single-requirement failure records and inspection guide and Three-judge judgments and review materials.

Thanks for quick reply, My questions have been answered with the calculation formulas and human evaluation. I hope you can correct the numerical results and rankings in the manuscript based on the clarifications before the discussion deadline. I recommand you to show these changes and additional discussions in paper using different color. It will be clearer for AC and us to check! After the corrections, I will consider raising my score.

Reviewer_un37OpenReview ↗
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Paper summary

The paper introduces multimodal context learning (MCL), the ability to acquire case-specific knowledge (local rules, procedures, symbol mappings, temporal patterns) from multimodal context and reuse it across sequential tasks. It also introduces Multimodal-CL-Bench to evaluate this ability:

  • Scale: 344 contexts, 1,080 tasks, and 7,309 binary rubrics, spanning 18,740 images and 304 videos.
  • Organization: cases are grouped by the form of learning required rather than by domain, giving four categories and 20 subcategories.
  • Construction: cases come from an expert-collected track (155 cases, 325 tasks; fictional, adapted, or niche contexts) and an agent-based synthesis track (189 cases, 755 tasks).
  • Scoring: each task is scored all-or-nothing against its rubrics, with GPT-5.2 as the judge.

The paper evaluates eight frontier MLLMs and makes three main claims:

  1. No model exceeds 13% task-level success (GPT-5.2 is best at 12.8%).
  2. Context Tracking Failure (34.5%) and Modality Misgrounding (26.7%) are the dominant error types.
  3. Thinking variants do not consistently beat their base models.

Supporting analyses include a Without-MM ablation on a 138-case synthetic subset, breakdowns by media configuration and image count, a reasoning-style analysis, and supplementary Kimi K2.6/K3 results (K3 reaches 22.31%).

Critical strengths
  • A timely and well-motivated evaluation target. The paper shifts evaluation from passive perception and retrieval toward acquiring and reusing case-specific knowledge from multimodal context. This capability matters increasingly as MLLMs are deployed with manuals, dashboards, and videos. Organizing cases as sequences of dependent tasks, where later tasks build on earlier conclusions, is a meaningful step beyond single-turn multi-image QA. This is the main reason I think the work is worth pursuing, even though the current execution has problems.
  • A large and diverse resource with substantial curation effort. The benchmark covers images, videos, documents, charts, forms, UI screenshots, and multi-turn histories at a scale well beyond most comparable benchmarks. The expert-collected cases are deliberately built from fictional, adapted, or niche material to reduce reliance on pretraining knowledge. If the evaluation issues below are addressed, the data itself could be a useful testbed for the community.
Critical weaknesses

W1. The evaluation protocol conflates instruction compliance with context learning, and the protocol itself is never validated.

Every score relies on GPT-5.2 as the primary judge. Apart from an unquantified mention of human audits on selected cases (App. A), the paper reports no judge–human agreement and no human baseline to check that tasks are solvable. This is combined with strict all-or-nothing scoring over ~6.8 rubrics per task, which likely deflates the headline "<13%" result and leaves the original eight models within a narrow, noisy 8.4–12.8% range where small differences are hard to interpret.

Fig. 15 shows the problem. Claude-Sonnet-4.6 gets the sample mapping and evidence citations fully correct, yet scores 0 under Rubric 7 only because it uses correct pathology terms (e.g., lamina propria, hyperchromatic). Here the "no outside knowledge" constraint conflicts with the model's instruction-tuned professional behavior, so the protocol rewards pedantic compliance rather than genuine multimodal learning.

The Refuse to Answer category has a similar issue. It absorbs budget exhaustion (Fig. 14, stop_reason='max_tokens'), so output truncation is counted as refusal, and no breakdown of this category is given. The authors should report rubric-level accuracy alongside task-level success, plus final-decision accuracy, rule-application accuracy, evidence coverage, and format compliance.

W2. The benchmark's construction and ablations do not isolate context learning.

Synthetic cases account for 70% of tasks (755/1,080), but they pass at 5.43%, compared with 22.42% on expert-collected cases (App. C.6). The case studies (Figs. 15, 18, 20) suggest that fixed templates impose obscure artificial labels and mechanical constraints that depart from natural context learning. A low pass rate alone is therefore not evidence of meaningful difficulty. The taxonomy also contains clear mislabeling: the 3×3 jigsaw in Fig. 21 is filed under Forms & Receipts. Beyond raw image and video counts (Table 1), the case-level modality breakdown (e.g., image-only, video, document, multi-turn) is not reported.

The Without-MM ablation (App. G) has three problems:

  • Limited coverage. It covers only 138 synthetic cases, and the same ablation on the 155 expert-collected cases is missing.
  • Remaining shortcuts. Some models keep more than half their score without images (Claude-Opus-4.6 Thinking drops only from 9.44% to 5.08%, Table 5), which points to text-rule shortcuts that survive.
  • Generic finding. A performance drop after removing images holds for any multimodal benchmark. App. G shows visual dependence, but it does not distinguish perception failures from failures to learn contextual rules.

W3. The diagnostics cannot localize failures, key MCL capabilities are untested, and closely related work is missing.

The scoring folds perceiving the material, learning the rules, maintaining state, executing correctly, and answering completely into a single outcome, without identifying where each failure originates. Error labels assigned from the final answer cannot recover the initial failure point. For example, a perception error may propagate into misgrounding and incorrect state updates, and the response is then labeled Context Tracking Failure. The prevalence of Context Tracking Failure therefore does not show that perception is not the main bottleneck.

The benchmark also leaves out two capabilities central to its own motivation:

  1. Multi-turn error recovery, i.e., overturning an earlier incorrect state when new evidence or feedback arrives. The multi-turn evaluation only uses same-model sequential history.
  2. Resolution of visual–textual conflicts.

Kimi K3 is in fact the best model (22.31%), yet it is relegated to the appendix with no analysis of where it outperforms the others.

Finally, the paper does not cite MMCL-Bench (arXiv 2605.12703). That work targets essentially the same problem: learning task-local rules, procedures, and patterns from multimodal context, scored with strict rubrics. The authors should clarify how their benchmark differs.

Questions for authors

Please take a look at the weaknesses. That’s all I wanted to ask.

8 comments

Thank you for recognizing the shift toward acquiring and sequentially reusing case-specific knowledge. We address your concerns through task semantics, inspectable materials, and experimental results.

1. Interpreting low success

The target is complete execution: acquiring case-local knowledge and applying it under evidence and task constraints. Low task success does not mean that all response content is wrong; the new rubric diagnostics make that distinction explicit.

After consistent all-task aggregation, the original eight models obtain 7.31%–13.06%, and Kimi K3 reaches 22.31%. The original table's first-turn aggregation will be corrected together with the abstract and ranking. The substantive result is that the same benchmark registers substantial model improvements while most tasks remain unsolved by the strongest evaluated setting. The benchmark does not confine every model to the same low-score range.

2. Figure 15: pathology terminology and closed-context requirements

Our evaluation asks whether models can learn and follow knowledge and rules defined in the current context. To distinguish context learning from reliance on pretrained knowledge, cases can introduce new label mappings, decision criteria, and local rules that differ from familiar conventions. When the two conflict, the supplied context takes precedence within the task.

Figure 15 uses an explicit closed-context setting: both the system prompt and Rubric 7 require answers to rely on case materials without introducing outside medical knowledge. The evaluation therefore checks not only whether sample mappings are correct, but also whether the response respects the supplied evidence and rule boundaries. A medically plausible interpretation does not satisfy the task merely because it is professionally correct; otherwise, additions from pretrained knowledge could obscure whether the model actually followed the context.

This requirement concerns additional inferences unsupported by the materials, not technical terminology itself. Equivalent expressions that preserve the evidential basis should be accepted. Histopathological interpretations not provided by the case should instead be checked against its closed-context rules. We will clarify this distinction in the caption so the example separates domain correctness from compliance with the case context.

3. Truncation and refusal

Reaching max_tokens means the output has hit the generation-length limit and may remain incomplete because the budget was exhausted; this does not by itself indicate active refusal. It differs from an explicit decision not to carry out the task or answer the question. We will revise the category description to distinguish budget truncation from active refusal, avoiding conflation of the two failure sources. Task success will continue to depend on whether the actual response satisfies the rubrics, rather than on the termination reason alone.

4. Synthetic labels, templates, and Figure 21

Case-specific labels test whether models can learn new mappings from context, much like status codes in a new manual. What matters is that labels are clearly defined and require applying local rules to multimodal evidence. Our Self-Construct, Self-Evolve, and Self-Improve framework links evidence, rules, reference answers, and rubrics, with targeted repairs for ambiguity and inconsistencies. The design is supported by inspectable construction materials and reference derivations, rather than inferred from low pass rates. See the synthetic-framework materials.

Figure 21 involves establishing and reusing a target state. To illustrate local-rule learning more directly, we will replace the example and correct its category label. We will also clarify the media breakdown: documents can be represented as images, while multi-turn describes interaction; these should not be counted as mutually exclusive categories alongside images and videos.

5. What Without-MM establishes

The paired experiment retains textual rules and task structure while removing visual evidence, comparing 138 synthetic cases and 551 tasks per model. Mean success decreases from 6.15% to 2.52%, a 3.63-percentage-point difference with a paired case-bootstrap 95% CI of [2.02, 5.50].

This control answers a necessary question: whether models benefit from supplied multimodal evidence, or whether the same text structure suffices to recover their original performance. The result supports the former and quantifies the visual-evidence benefit in the evaluated subset. It therefore has a specific role in this benchmark.

The experiment does not separate perception from rule learning or cover the expert track; we position it as a bounded test of visual-evidence dependence. Residual success without vision also does not establish that every remaining pass uses a shortcut: tasks must be inspected to distinguish sufficient textual evidence from actual bypasses of required visual information.

6. Error distributions and initial causes

This analysis uses model-assisted diagnosis of individual failed turns. GPT-5.2 assigns one primary label using the original task prompt, model response, and rubric-level grading rationale. When multiple labels apply, the existing protocol uses the fixed priority Refuse to Answer, Rule/Format Error, Modality Misgrounding, Context Omission, and Context Tracking Failure. A single primary label avoids double counting; it does not identify the earliest failure in time.

Context Tracking Failure describes failure to maintain prior rules, states, or intermediate conclusions. Modality Misgrounding describes incorrect binding between textual conclusions and visual entities, pages, or temporal segments. These labels organize recurring output defects into inspectable types that can guide subsequent model improvements.

Thus, 34.5% and 26.7% describe output-error distributions under this procedure. A perception error can propagate into incorrect binding or state updates, so these proportions do not exclude perception as an upstream bottleneck. We will specify the operational definitions, inputs, and primary-label policy and use Figure 5 for this diagnostic purpose, rather than as a causal decomposition of internal failure mechanisms.

7. Multi-turn recovery and visual–textual conflicts

The sequential protocol includes the same model's actual earlier responses in subsequent history, testing whether it maintains and reuses intermediate states acquired from context. Earlier errors can affect later results, as in sequential interaction. Task success therefore measures end-to-end execution under actual model history, rather than independent solving with correct prior states supplied.

This differs from an intervention that injects an error, supplies new evidence or feedback, and tests correction. Even success conditioned on earlier tasks being solved remains affected by task difficulty and case composition; a controlled decomposition would compare the same downstream tasks under model history and controlled correct history.

8. Placement of the supplementary Kimi evaluation

Kimi K2.6 and Kimi K3 were evaluated as supplementary models during the final stage of manuscript preparation, separately from the original eight-model evaluation. Their results were therefore reported separately in the appendix. Both cover the same 344 cases and 1,080 tasks and use the same sequential-history rule and GPT-5.2 judging protocol. We will clarify the supplementary evaluation arrangement in the main text and direct readers to the full comparison in the appendix.

9. Relationship to MMCL-Bench

MMCL-Bench and our work both evaluate acquiring local knowledge from multimodal context. We will cite it and clarify the difference in evaluation structure. MMCL-Bench primarily organizes transfer tasks around a teaching context and a new test instance. Our benchmark instead uses multiple ordered tasks within a shared case, carrying the same model's actual earlier responses into subsequent history to evaluate whether local knowledge and intermediate states can be maintained and reused throughout continued interaction.

Whereas MMCL-Bench emphasizes transferring knowledge from a teaching context to new test instances, we emphasize continued application across tasks within a shared case: later tasks retain the model's actual earlier responses, testing whether local rules and intermediate states can be maintained and reused.

Case-local rules, organization by learning form, and strict rubric scoring are shared settings. Our distinction lies in the multi-task case and sequential-history evaluation structure, together with its capability coverage and construction resources, rather than task count alone. This comparison does not imply that MMCL-Bench lacks multi-step state reasoning.

Reference: MMCL-Bench.

AuthorsOpenReview ↗

Request for feedback

Dear Reviewer un37,

Thank you again for your thoughtful and constructive feedback, which we have carefully addressed in our author response. As the discussion deadline is approaching, we would greatly appreciate any further feedback you may have. If our responses have resolved your main concerns, we would also be grateful if you could update your assessment accordingly.

Sincerely,

The Authors

Reviewer_3B8mOpenReview ↗
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2
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Paper summary

In this draft, the authors introduced Multimodal-CL-Bench to evaluate whether MLLMs can learn new rules and procedures from multimodal context and apply them to later tasks. The benchmark has 344 contexts, 1,080 tasks and 7,309 rubrics, scored by GPT-5.2 as the judge. Experiments on eight frontier models showed that the best model only reached 12.8%.

Critical strengths
  1. The problem is timely, and organizing the benchmark by the type of learning instead of domain is a nice idea.
  2. The benchmark is large and diverse and leaves a lot of room for improvement.
Critical weaknesses
  1. The main numbers seem inconsistent. Table 2 appears to be computed per context instead of per task, and the task-level numbers in the appendix change the ranking and the "Thinking does not help" finding.
  2. The GPT-5.2 judge is not validated against humans, it is also one of the evaluated models, and it does not see the context when checking the rubrics.
  3. 70% of the tasks are synthetic without reported human checks, and there is no human baseline, so it is unclear whether the tasks are solvable.
  4. Many Typos such as L1132 "shortcuts.Instead" (missing spaces), L1520 "formulating the The response", and L1527 "2.mp43.mp44.mp4".
Questions for authors

Please refer to the Critical Weaknesses section for details.

3 comments

Thank you for recognizing the organization by learning form. We have added reproducible task-level results, a judge-review account, and a complete reference derivation to address your questions about the results and evaluation validity.

1. Aggregation and the Thinking comparison

Thank you for identifying this aggregation issue. The original Overall column in Table 2 corresponds to the first tasks of 344 cases, rather than all 1,080 tasks. We have recomputed task-level micro-averages as successful tasks divided by 1,080 and will update the main table, rankings, and associated statements consistently.

Among the original eight models, Sonnet Thinking now leads with 141/1,080 (13.06%). Thinking improves Opus and Sonnet by 1.94 and 0.09 percentage points, respectively. We therefore revise the conclusion to configuration-dependent Thinking gains. Task-level scores and reproduction code are provided in Task-level scores and reproduction materials.

2. The judge's basis and calibration

We used three judges: GPT-5.2, Claude-Opus-4.6 Thinking, and Gemini-3.1-Pro-Preview (High). Main results consistently use GPT-5.2 to maintain a common scoring scale across inference models and tasks. The other two judges support cross-checking and disagreement analysis, rather than directly replacing the primary judge through majority voting.

We have added matched judgments from all three judges on identical responses and rubrics, together with representative examples. A fixed primary judge also supports efficient scaling: each additional inference model requires 1,080 task-level judgments under one judge, compared with 3,240 under all three, excluding retries. The protocol and cross-judge records are available in the three-judge materials.

Judges receive the response and rubrics rather than rereading the full multimodal context. This design relies on the rubrics specifying the reference conclusions and constraints needed for verification, and measures satisfaction of those requirements. Rubric checking does not replace independent visual verification of facts that require the original media. Because GPT-5.2 is also an evaluated model, the matched three-judge records make disagreements inspectable; they do not establish the absence of self-preference.

3. Synthetic-task answerability and a human baseline

Synthetic tasks are constructed through a controlled framework grounded in real multimodal evidence. Source materials come from SlideVQA (Tanaka et al., 2023) and MMLongBench-Doc (Ma et al., 2024). The framework connects source evidence, case-local rules, reference derivations, and task-level rubrics, making task requirements and the basis for answers individually inspectable.

Specifically, Self-Construct organizes evidence, local rules, and dependent task chains. Self-Evolve introduces exceptions, distractors, and counterfactual updates while preserving source facts and requiring affected reference answers and rubrics to be updated together. Self-Improve performs targeted repairs for insufficient evidence, answer ambiguity, conflicts between rules and answers, and missing grading requirements. The prompts, structured schemas, validators, and reference implementation are included in the anonymous supplement so these construction constraints can be examined.

We also provide 60 complete cases spanning all 20 subcategories, together with an inspectable reference derivation. For example, MCL-0083 Turn 3 asks which conclusions remain supported when one evidence image is hypothetically removed. The supplement directly connects the original images, local rules, derivation, and six grading requirements, showing how the answer follows from the supplied materials. Our argument for the synthetic tasks therefore rests on inspectable evidence–rule relationships rather than treating low model success as proof of validity.

Material index: Synthetic-framework evidence index.

4. Text and filename issues

Thank you for the specific locations. We will correct spaces, duplicated words, and concatenated video names, distinguishing display formatting from actual input references. Changes affecting grading semantics will be logged separately so that textual corrections and score changes are not conflated.

AuthorsOpenReview ↗

Request for feedback

Dear Reviewer 3B8m,

Thank you again for your thoughtful and constructive feedback, which we have carefully addressed in our author response. As the discussion deadline is approaching, we would greatly appreciate any further feedback you may have. If our responses have resolved your main concerns, we would also be grateful if you could update your assessment accordingly.

Sincerely,

The Authors

Dear Reviewer 3B8m,

As the discussion deadline approaches, we would appreciate your consideration of our updated responses and supplementary materials. Reviewer un37 raised related concerns, which we have also addressed through further clarification and supporting evidence. If these responses resolve your concerns, we would be grateful if you could reconsider your assessment and score. Thank you for your time and constructive feedback.

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

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