acceptodds
Under review as a conference paper at ICLR 2027

From Hours to Tasks: Evaluating Evidence-Grounded Decisions by Long-Video Agents

Abstract

Long-video agents must integrate observations across time, track changing objects and states, and use tools to act. Evaluation requires executable tasks with agent-accessible evidence for key choices, so missing evidence is not mistaken for limited capability. We introduce EvidBind-Bench: 3,000 tasks across 13 domains grounded in hour-scale videos, with a design–binding method that fixes goals, constraints, and required decisions before linking them to observations, objects, times, and operational conditions. The framework comprises (1) Automated task generation, which instantiates reusable decision structures, binds choices to evidence, and generates instructions and execution paths, revising unsupported choices under unchanged requirements;(2) Task review and repair, which combines automated checks and human review, reuses shared assessments, and targets affected decisions, with acceptance checking support, executability, and requirement preservation; and (3) Reference-agent evaluation, which supplies ReAct and multi-agent frameworks with common public interfaces, scoring, and diagnostic execution records. Independent human audits of 390 sampled tasks estimate collection validity. Under the evaluated conditions, the complete procedure lowers combined labor and computational cost per estimated valid task by 72.86% relative to per-task review and repair. ReAct and the multi-agent system achieve 11.23% and 17.73% success, versus 91.73% for humans, revealing persistent difficulties on tasks passing construction checks. EvidBind-Bench combines low-cost task construction and agent evaluation to study the gap between solvability and reliable execution.

Primary area:
foundation or frontier models, including LLMs
Keywords:
Long-video understanding, Multimodal agents, Evidence-grounded decision-making, Benchmark construction, Tool use

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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.
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Paper summary

This paper introduces EvidBind-Bench, a benchmark designed to evaluate video-based, tool-using agents on their ability to make "evidence-based decisions" within hour-long video scenarios. The benchmark encompasses 3,000 tasks spanning 13 domains and five decision structures. The authors propose a "design-binding" workflow and a perception-dependency repair mechanism for task construction and validation, and evaluate ReAct and multi-agent frameworks using a variety of open-weight and API-based models.

Critical strengths
  1. Addresses a genuine bottleneck in long-video agent evaluation. The paper identifies an important gap in existing long-video benchmarks: successful tool execution does not necessarily imply that an action is properly supported by video evidence. The example of a customer returning and replacing a milk carton illustrates this issue well. Observing only the checkout scene may lead to an incorrect product identification if the agent fails to track the relevant object and state transitions over time. The distinction between executability and evidence support is well motivated and conceptually valuable.
  2. Provides a clear task formulation. The paper separates the task objective, operational constraints, required decisions, and dependencies among decisions. It also introduces a principled notion of pre-action evidence support: an action should be justified by publicly accessible evidence obtained before the action is taken, rather than by information observed only later or by hidden annotations. This is a coherent formulation of an important requirement for reliable long-video agents.
  3. Introduces a sizable and structurally diverse benchmark. EvidBind-Bench contains 3,000 tasks spanning 13 domains and five representative decision structures, including sequential progression, conditional branching, multi-hop dependencies, joint constraints, and plan-execution audits. The construction effort appears substantial. The paper also reports an independent human audit of 390 sampled tasks, with an estimated overall validity rate of 96.4%, which is encouraging.
  4. Reveals a substantial gap between current agents and human performance. The experiments evaluate Qwen, DeepSeek, and LFM models. Under the reported setup, the best multi-agent configuration achieves 17.73% success, compared with 11.23% for the corresponding ReAct baseline and 91.73% for human participants. These results suggest that the benchmark is challenging and may provide useful diagnostic signal for long-context, temporally grounded agent behavior.
Critical weaknesses
  1. Important reporting and reproducibility details are missing. Several appendix sections contain unresolved placeholders, including “–” and “Appendix ??”. These missing fields concern domain boundaries, task-selection rules, concrete repair examples, dependency-propagation outcomes, and implementation details. The paper also does not disclose the models, prompts, or configurations used for task generation and repair. For a benchmark paper, these details are central to reproducibility and to assessing dataset validity.
  2. There is a mismatch between the central claim and the evaluation metric. The paper is framed around evaluating evidence-grounded decisions, but the main metric does not directly evaluate whether an agent retrieves or uses the required video evidence. As stated in Section 3.3, the external scorer accepts any trajectory satisfying the final goal and execution constraints, while success rate measures task completion rather than evidence use or failure causes. Therefore, an agent may receive full credit if it reaches the correct final state through guessing, brute-force exploration, prior knowledge, or other shortcuts without retrieving the relevant video evidence. The evidence-binding mechanism is used to validate task construction, but it is not used to determine whether an evaluated agent's execution is actually evidence-grounded. The paper should introduce trajectory-level evidence metrics or substantially narrow its claims.
  3. The reported cost reduction is confounded by scale effects. Section 4.5 and Table 4 report a 72.86% reduction in combined cost per estimated valid task. However, the baseline produces 300 tasks, whereas the proposed binding-guided procedure produces 3,000 tasks. The paper acknowledges that the original goal pools are not documented as corresponding and that the comparison is conducted at unequal output scales. At the larger scale, shared video processing, initial screening, and reusable fact verification can be amortized over many more tasks. Thus, the reported reduction may reflect scale-related amortization rather than the causal benefit of the proposed binding and dependency-aware repair mechanism. A convincing comparison should use the same pre-specified task pool, matched budgets, comparable reviewer rules, and equal-scale or scale-controlled conditions.
  4. Shortcut risk weakens the claim of long-video temporal reasoning. Among 200 pre-specified cross-temporal tasks, 19 tasks (9.5%) could be solved through a short video window or without viewing the video at all. This raises concern that some tasks may not genuinely require long-range temporal integration. Since the main metric evaluates only final task completion, agents may exploit such shortcuts while still receiving full credit. The paper should provide stronger evidence that its tasks require the intended long-video evidence, for example through temporal-window ablations, video-removal tests, time-order perturbations, and analyses of alternative solution paths.
  5. The contribution is not sufficiently differentiated from related benchmarks. The paper overlaps substantially with recent work on long-video, video-grounded, and tool-using agents, including VideoWebArena, Ego2Web, EgoBench, VideoGAIA, and TaskCraft. The proposed decision-level evidence binding may be a useful distinction, but the paper does not provide a sufficiently direct comparison or controlled ablation demonstrating that this mechanism yields benefits beyond existing task-construction and validation pipelines.
Questions for authors
  1. Missing implementation details and placeholders. Please explain why several appendix sections contain unresolved placeholders, such as “–” and “Appendix ??”, including sections related to domain boundaries, decision rules, and repair examples. Which LLMs or multimodal models were used for task generation and repair? Why are the prompt templates, model configurations, and key implementation details not provided?
  2. Trajectory-level evidence evaluation. The paper introduces a structured representation that links each required decision to supporting evidence, entity correspondence, temporal scope, and action conditions. Why is this information not used to evaluate whether an agent actually retrieves and uses the required evidence during execution? Could the authors report trajectory-level metrics, such as evidence retrieval recall, evidence precision, temporal grounding accuracy, or decision-level support accuracy, in addition to end-to-end task success rate?
  3. Controlled cost comparison. Could the authors compare the proposed binding-guided repair method with full per-task review at the same scale, for example using 300 tasks in both conditions or 1,000 tasks in both conditions? This would help separate the benefit of the proposed method from the amortization effect caused by sharing preprocessing and review costs across a much larger number of tasks.
  4. Mitigating shortcut exploitation. Given that 9.5% of tested cross-time tasks can be solved via short clips or no video at all, do the authors have a systematic filtering mechanism to purge non-temporal shortcuts from the benchmark? How do evaluated agents perform under blind/no-video control settings?
8 comments
AuthorsOpenReview ↗

Author Response to Reviewer NpeF

Thank you for recognizing evidence-supported decisions. We address your concerns below and will revise the paper and appendices together after discussion. Attachment A provides construction prompts, frames, reference traces, and version-bound reviews; B records a separate solving episode with the same abstract goal but a different frozen instance and trajectory. We welcome feedback and would appreciate reconsideration if these responses resolve your concerns.

1. Response to Weakness 1 and Question 1

Summary

We provide the construction recipe, domain/audit criteria, and a complete supermarket record from design through binding repair, review, and reference reruns.

(1) Construction and implementation

We apologize for the unfilled entries and unresolved “Appendix ??” references. Incomplete implementation reporting and cross-reference checks made the procedures harder to verify. The two attachments provide configurations and process records. After discussion, we will complete the reporting and check cross-references in the paper and appendix. In Attachment A, Designer API_1 receives the complete Retail construction/review exemplar, public goal, five catalogue rows, and tool contracts; it freezes goals, constraints, decisions, and dependencies before source-frame decoding, without target time, pixels, or answer. Schema-specified obligations/edges constrain generation. Bindings add sources, entity correspondence, applicable time, and action conditions; repair receives old/new records and gaps without weakening requirements or scope. Source/interface/precondition/budget checks precede selection; uncertain effects require full review and fresh-state replay. Support requires a nonempty interpretation set and a choice valid throughout; conflicts/decision-changing ambiguity remain unresolved. Replay and human approval are separate.

Qwen3.8-27B uses temperature 0.1 for all construction roles, top p 1.0, and thinking off. Per-call seeds include Designer API_001 = 7315 and visual API_006 = 7320; complete parameters are recorded. All 38 requests, including earlier attempts/post-H1 revision, use 0.1: the earlier 0.2/seed-17 summary was incorrect, not version drift. Construction, Q2 solving, and Q3 cost budgets/settings are separate.

(2) Worked example and audit scope

The task identifies the bag unfolded later near checkout, orders one matching variant, and links an awaiting-arrival check to the new order while preserving existing records. Video supplies identity, instructions quantity, and execution the order ID; five catalogue rows are authored comparisons, not observed products.

The 24 coarse samples provide no observation meeting the supplied 1995s anchor’s time-applicability condition; API_4 admits no binding and no order is attempted. API_5 proposes six nearby times for fresh VLM API_6 observations. API_7 returns three bindings, deduplicated by exact object and ranked lexicographically by validation failures, declared extra accesses, and proposal index. The selected receipt binds the 1995s observation (“Yonghui Life”, dark green) to ITEM_F1514293DB09 via an explicit semantic adapter. Goal, anchor, and candidate universe stay fixed; reacquisition and revalidation address the unmet support check.

Two isolated Qwen references execute catalogue → fresh video/VLM inspection → order permission → order → read order receipt → check permission → linked check → finish. Operators receive bindings, testing reference executability rather than blind performance. The opaque purchase handle leads to the new order ID through read order receipt. None of the three references, including the later revision, calls list records; state reads are audit hooks. Runtime permissions differ from review approval.

A’s five-candidate construction_v4 uses 25 main calls/137,623 tokens and 10 post-H1 calls/29,877 tokens; its 38-request registry includes three across two failed runs. B’s four-candidate seed_511 v5 uses 19 requests/107,918 tokens/five tool calls. These are distinct frozen instances, not paired performance runs.

On 14 November 2026 at 15:09 +08:00, H1 passes facts, tools, and task/repair, requesting distractor ITEM_26857A389CAB change from unknown color to red—an authored catalogue edit, not video fact. The 10-call rebinding/fresh-observation/reference rerun passes revised DB/trajectory review at 15:39. Approval/reuse is version-bound and excludes B. H1 confirms “Yonghui Life” and green, not separately dark green; B’s audit reads are not agent actions.

Domains follow end states: buying/shelving/stock allocation; food preparation/use/storage; object assembly/restoration. Unknowns stay unknown. All five structural labels remain, but only primary multi-hop/plan-audit defines the complex subset. The separate original audit randomly samples 390/3,000 without replacement/quotas: 376/390 valid, including 145/156 complex. Independent double review, adjudication, and unresolved-case failure apply.

2. Response to Weakness 2 and Question 2

Summary

We report task success and Joint-SR (success with every required decision supported before action), calibrate evidence scoring, and test content dependence through matched masking.

(1) Sampling and scoring

The 300-task diagnostic sample draws visual obligations from 3,000 tasks: 23/domain plus one by a predetermined rule, across 30 videos selected before solving without filtering on clarity, shortcuts, or scores. Full-benchmark SR remains 11.23%/17.73% for ReAct/five-role; diagnostic SR is ReAct 118/900 (13.11%), five-role 154/900 (17.11%) over three seeds. These denominators are distinct and establish no equivalence. Q2 and Q4 share backbone, caps, seeds, and Joint definition, but use separate episodes/observations; Q4 imports no Q2 trajectories. Matching seeds do not identify matching episodes.

Rules verify source versions, delivery, action order, and receipts. Two reviewers independent of construction/annotation judge relevance, completeness, and parameter support, with third-rater adjudication, blind to model/condition, final state, and SR. Unlisted evidence receives the same source/entity/time/sufficiency checks before uniform rescoring. Role summaries need sufficient facts and traceable receipts acquired/delivered before action; unsupported conclusions or undelivered links fail.

Calibration uses 20 videos, ten held out, with balanced SR-pass/fail strata hidden from reviewers. Per-condition samples are 150 relevance frames (75/stratum), 180 complete-evidence visual decisions (90/stratum), and 240 parameter-support decisions (120/stratum). Pooled agreement across four conditions is, respectively, 586/600 = 97.67% (κ = 0.945), 698/720 = 96.94% (κ = 0.935), and 934/960 = 97.29% (κ = 0.932). The 960 include 720 visual/240 nonvisual decisions; overlaps are not independent. Of the 26 parameter-support disagreements, 14 involve alternative evidence (8), provenance (4), or time boundaries (2). Revised held-out agreement is 470/480 = 97.92% (four false accepts/six rejects), with 90 visual/30 nonvisual decisions per condition.

The further 120 held-out trajectories include 30/condition, half SR-passing. Blinded support adjudication AND frozen SR forms Joint; 60 SR failures are automatic negatives. Among 60 SR successes, supported cases yield 39 accepts/one reject (40); unsupported cases two accepts/18 rejects (20); totals are 41/19. Agreement is 57/60 = 95.00%, versus 117/120 = 97.50% including automatic negatives. False acceptance is 2/20 = 10.00% (Wilson 95% interval 2.79–30.10%); false rejection 1/40 = 2.50%; unsupported among accepted is 2/41 = 4.88%. All results use one final version untuned on held-out checks; this pooled sample cannot establish condition-specific errors.

(2) Evidence coverage and experimental settings

Confirmed relevant positions cover 2.15% of the video grid, not exhaustive density; unannotated positions stay unknown. All accessed frames undergo relevance/boundary/alternative-evidence review, reusable only for the same task/version/location. The 128,342 within-run-deduplicated accesses are not independent judgments.

QWEN3.8-VL 27B uses seeds 17/29/43: 300 × three = 900 runs/condition; decision/vision-ranking temperatures 0.2/0.1, top_p 1.0, thinking off. Each run’s roles jointly share 180,000 input/output tokens, 48 model requests, 64 tool calls, 96 visual-frame processing events, and 900 seconds, including auxiliary calls/retries. Private-binding position hints are oracle assistance; charging them does not remove their information advantage.

Visual/total obligation denominators are fixed at 3,108/4,908 per condition, retaining unvisited/unfinished/exhausted cases. Retrieval needs a complete legal pre-action evidence combination; support also checks chosen parameters. Localization scores model-submitted pre-action intervals, not request windows: one-to-one matching to every interval of one legal combination at IoU ≥ 0.5; one broad interval cannot match separated events, and missing predictions fail. Single frames count only for registered static facts within valid intervals, with half-step boundary tolerance and correct entity mapping, never event intervals. Table 1. Trajectory evidence metrics in percent

ConditionComplete retrievalFrame precisionLocalizationVisual supportAll-obligation support
ReAct45.7922.0737.8442.4157.60
Five-role53.8028.9746.9149.2063.81
ReAct + oracle64.9636.9058.7859.6571.09
Five-role + oracle72.2344.1267.6068.7378.14

For sensitivity, let S and J denote SR and scored Joint success counts. Assuming common sensitivity a = 39/40 and false acceptance b = 2/20, supported successes are (J − bS)/(a − b):

Table 2. Task success, pre-action support, and scoring sensitivity

ConditionSRJoint-SRJoint-SR 95% CI (%)Joint under shared errors (%)
ReAct118/900, 13.11%68/900, 7.56%[4.00, 11.89]7.14%
Five-role154/900, 17.11%99/900, 11.00%[6.11, 16.78]10.62%
ReAct + oracle183/900, 20.33%128/900, 14.22%[8.78, 20.44]13.93%
Five-role + oracle254/900, 28.22%183/900, 20.33%[15.00, 26.56]20.01%

Intervals use 2,000 video-cluster bootstrap draws preserving task/seed dependence, excluding scoring uncertainty. Of 154 five-role successes, 99 score supported and 55 unsupported. The five-role–ReAct gap is 3.44 pp as scored, 3.48 under shared errors; this neither replaces counts nor proves robustness to condition-specific error. SR masking results (154→31 versus 152) independently test content dependence, conditional on SR-checker validity, not internal reasoning.

(3) Regenerating actions after frame removal

Each arm removes 6,976 frames across 900 unassisted five-role runs, matched per run, with fixed acquisition/no replacement. Controls are confirmed irrelevant outside all sufficient combinations. From before the first affected observation, regenerate judgments, role messages, memory, parameters, actions, and tool returns; reuse no removed evidence, summaries, IDs, or receipts.

Table 3. Fixed-schedule content intervention

ConditionSRJoint-SRSR change, pp [95% CI]
Full observations154/900, 17.11%99/900, 11.00%—
Selected key evidence masked31/900, 3.44%2/900, 0.22%−13.67 [−18.56, −9.55]
Matched irrelevant frames masked152/900, 16.89%97/900, 10.78%−0.22 [−0.89, 0.44]

Key masking yields 128 success→failure/five failure→success, with 26 stable successes/741 failures. Irrelevant masking yields five success→failure and three failure→success transitions, leaving 152 successes. These exhaust runs; intervals cluster by video. SR tests fixed-schedule content dependence; Joint additionally enforces support. Neither establishes individual internal reliance.

Reviewer_ybPmOpenReview ↗
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Paper summary

EvidBind-Bench is a benchmark for longvideo agents where agents have to watch hour scale videos and then use tools to act on what happened, for e.g. buying the milk that was actually purchased in the video and not the first carton that was picked up. Its core contribution is a construction method that fixes the task goal, constraints and required decisions first, and then links each decision to evidence in the video that the agent can find before it acts, so tasks don’t end up failing because the evidence was never there to begin with. Review and repair reuse shared fact checks and only recheck the decisions affected by a change, which the authors report cuts cost per valid task by about 73%. The benchmark has 3,000 tasks across 13 domains and 5 task structures, and independent audits estimate 96.4% of tasks are valid. Even the best agent only reaches 17.7% compared to 91.7% for humans, with multi-hop and plan audit tasks being the hardest, and this benchmark can be used to study the gap between tasks being solvable and agents actually executing them reliably.

Critical strengths
  1. Decision-first, evidence-before-action design: Fixing the decisions before searching for evidence, and not letting tasks get easier when evidence is hard to find, is a really nice way to make sure failures come from the agent and not from a broken task. The milk example makes this concrete, since an early clear label can point to the wrong carton if the swap is missed.
  2. Checks on the benchmark itself: The validity audit, scorer calibration and especially the restricted-access search are thoughtful additions. Trying to solve cross-time tasks with short clips or no video, and reporting that 9.5% have shortcuts, is an honest test that most benchmarks skip.
Critical weaknesses

1.Reliability and reproducibility of results: Results are reported without intervals and it’s not stated how many runs they come from, while some domain results swing a lot, for eg 27B Cooking goes from 3.35% with ReAct to 46.84% with the multi-agent setup. The paper also points to supplementary material for hyperparameters, but none was submitted, so key settings like budget limits, decoding settings, prompts and the fine-tuning setup are missing.. 2. The appendix has several fields left as “–” (domain rubrics and subset selection details in A.2, reviewer agreement stats in C.1, propagation counts in C.2, repair examples in C.3) and a broken reference (“Appendix ??” in C.2). This makes it hard to trust the smaller gaps or compare new agents under the same budgets. 3. Limited failure and evidence-use analysis: The paper defines failure types (evidence acquisition, entity or temporal mismatch, execution or recovery) but doesn’t report how often each happens, and apart from budget exhaustion rates in Table 9 the analysis is qualitative. Success rate also doesn’t show whether agents actually used the evidence, which is the main idea behind the benchmark. Since every task already has decision-level bindings with evidence times, it seems possible to show which decisions agents get wrong, whether successes relied on the bound evidence, and whether difficulty grows with how far apart the evidence is. It’s also unclear why the multi-agent setup helps in some domains and hurts in others, since there are no role ablations.

Questions for authors

A. Clarifications

  1. How many runs are the agent results based on? Could you report variance or intervals, ideally clustered by source video since each video contributes about 25 tasks?
  2. Do all five multi-agent roles use the same backbone, including the VideoSeek scheduler, and how does DeepSeek-V4.1 handle video?
  3. Could you share the agent budget limits (tokens, tool calls, time), decoding settings, prompts and fine-tuning setup including the teacher model? Will the code and tasks be released?
  4. Section 4.2 mentions results on tasks with verified budget-feasible reference paths, and says Section 4.3 covers evidence assistance. Where can these be found?
  5. Who were the human participants, how many were there, and what instructions and time limits did they have? The ethics statement says no human subjects were recruited, so it would help to clarify how the human baseline was collected.
  6. Several appendix fields are left as “–” and C.2 has a broken reference. Could you fill these in, especially whether the complex audit subset uses primary labels or all tags, the selection rule for the 200 cross-time tasks, and the reviewer agreement statistics?

B. Additional analysis (can be done on existing runs or bindings) 7. Could you report how often each failure type occurs per model and framework? Using the bindings, which decisions do agents most often get wrong? 8. How many successful runs never viewed the supporting evidence for their decisions? It would be interesting to see a success rate that also requires looking at the bound evidence before acting, since the paper notes success rate alone doesn’t capture evidence use. 9. Does success drop with video length, or with how far apart the required evidence moments are? This would help show the difficulty really comes from long-range integration. 10. On the 19 tasks found to have shortcuts, do agents score higher than on the rest? 11. Did you try ablating roles like Reflection or VideoSeek to see what drives the multi-agent gains and losses compared to ReAct? 12. The cost comparison uses 300 baseline tasks versus 3,000 with undocumented starting pools. Could you estimate how much of the 72.86% saving comes from amortizing shared checks alone?

9 comments
AuthorsOpenReview ↗

EvidBind-Bench Author Response to Reviewer ybPm

EvidBind-Bench Author Response to Reviewer ybPm

Thank you for your careful review. We agree that missing details and inaccurate references made the submission harder to assess. Below, we provide additional analyses and clarify their scope. We will revise the main text and appendices together after the discussion and welcome further feedback. If this evidence addresses your concerns, we would be grateful for your reconsideration.

1. Response to Weakness 1 and Questions 1–3

Summary

(1) Reliability (Tables R1–R2). We add video-clustered confidence intervals and a separate three-seed stability check.

(2) Reproducibility (Table R3). We clarify role backbones, video access, budgets, fine-tuning, and the staged release plan. Thank you for identifying these missing details.

Detailed Response

(1) Video-clustered confidence intervals

Each backbone–framework configuration was evaluated once on 3,000 tasks from 120 source videos (approximately 25 tasks/video). We use 20,000 source-video bootstrap resamples, preserving within-video tasks and framework pairings. Each resample computes Micro SR (total successes/total tasks) and paired framework differences; Table R1 reports percentile 95% confidence intervals. These measure video-sampling uncertainty, not run-to-run variance. The 3B paired interval includes zero and does not establish consistent five-role improvement.

Table R1. Full-evaluation success rates and paired differences with source-video-clustered 95% confidence intervals

BackboneReAct SR, % [95% CI]Five-role SR, % [95% CI]Paired difference, percentage points [95% CI]
27B11.23 [8.17, 14.62]17.73 [13.87, 21.78]+6.50 [3.05, 10.16]
9B5.50 [3.63, 7.65]7.80 [5.62, 10.32]+2.30 [1.21, 3.39]
3B2.60 [1.51, 3.90]2.20 [1.20, 3.42]−0.40 [−1.14, 0.33]
DeepSeek11.10 [8.13, 14.39]14.90 [11.54, 18.54]+3.80 [2.04, 5.62]

(2) Three-seed stability check

Based on existing positive, negative, and smaller differences, we select Cooking, Fitness Training, and Travel Packing. With sampling seed 20261112, we select four videos per domain containing at least 25 tasks each, then sample 25 tasks/video without replacement. This pool is frozen before additional runs. Eight configurations each use the same 300 tasks with seeds 17, 29, and 43: 7,200 task runs. Table R2 gives success counts/300 and mean SR (%) ± sample SD (percentage points, denominator n−1n-1).

Table R2. Three-seed stability check on the fixed 300-task pool

ConfigurationSeed 17Seed 29Seed 43Mean SR ± SD
27B ReAct46/30032/30043/30013.44 ± 2.46
27B five-role84/30081/30086/30027.89 ± 0.84
9B ReAct35/30019/30019/3008.11 ± 3.08
9B five-role35/30037/30032/30011.56 ± 0.84
3B ReAct10/30015/30019/3004.89 ± 1.50
3B five-role14/30019/30020/3005.89 ± 1.07
DeepSeek ReAct30/30038/30025/30010.33 ± 2.19
DeepSeek five-role64/30054/30065/30020.33 ± 2.03

These results cover only three domains and 12 videos, cannot replace the full 13-domain evaluation, and are reported separately from other 300-task diagnostic panels.

(3) Role backbones and video access

Master, Vision, Tool, Code, and Reflection all use their configuration’s tested backbone. The same backbone runs VideoSeek’s overview/skim/focus scheduler within Vision. Fine-tuned 3B/9B roles share adapters within each backbone, never across backbones.

DeepSeek-V4.1-Flash natively supports vision: sampled frames and task text enter its multimodal interface for direct visual understanding, observation scheduling, and reasoning. Video access starts with 24 uniformly spaced midpoint overview frames, followed, as needed, by at most two windows totaling 60 seconds at 1 fps. Per-request frame and image-size limits appear in Table R3. ReAct uses identical sampling and preprocessing.

We will list actual model identifiers and versions and, for API configurations, call dates, system_fingerprint, and seed support, marking unverified fields.

(4) Evaluation budgets and decoding

The main set spans 13 domains and five decision structures: eight configurations give 24,000 task runs, with repeated checks counted separately. All use identical tasks, public information, and tool interfaces, starting each task from an isolated state without private bindings, reference trajectories, or target answers.

Table R3. Shared budgets and decoding settings for the main evaluation and repeated-run check

ItemSetting
Decodingtemperature = 0.2; top_p = 1.0; thinking disabled; at most 2,048 output tokens per request
Cumulative tokensAt most 180,000 per task, counting input and output tokens across all model requests
Model requestsAt most 48 per task
Tool attemptsAt most 64 per task, including failures and retries
Visual processingAt most 96 frame-processing instances per task; at most 16 frames per visual request; longer image edge at most 768 pixels
Total timeAt most 900 seconds per task
Per-request timeoutAt most min(300 seconds, remaining time)

All roles and visual/auxiliary calls share these limits, counting tokens, frame processing, failures, retries, repeated access, and elapsed time; reaching any limit stops execution. Submission Table 9 reports actual average consumption, distinct from these caps.

(5) Fine-tuning and teacher

Corrective supervised fine-tuning covers 3B/9B ReAct and five-role configurations, including the deployed VideoSeek scheduler. The auxiliary set has 1,200 tasks from 60 videos, separated from the main test set by source video; train/validation/auxiliary-test splits contain 48/6/6 videos.

LoRA uses rank = 16, alpha = 32, dropout = 0.05 on language-layer q/k/v/o/gate/up/down_proj, with the vision tower frozen. Adapters are shared only within a backbone. The API teacher, gpt-6-astra, receives only public tasks, observations, and tool returns then available to the student, without private bindings, reference trajectories, or target answers. Loss covers assistant continuations and EOS only; validation loss selects the adapter.

(6) Attachments and release

Attachment A contains construction-example model identities, per-call decoding, complete prompts, tool contracts, reference trajectories, and review records; B contains role assignments, prompts, and execution records for an independent interaction. Their example-specific configurations do not replace main-evaluation settings; complete main prompts and fine-tuning configurations will be released.

We will release construction/evaluation code, tools/scorers, complete prompts/configurations, tasks/splits, de-identified trajectories, and license-permitted adapters in stages. Competition arrangements defer the complete multi-agent code; timing will be determined after the competition. Remaining materials will receive an anonymous read-only repository and checksummed archive within 14 days after discussion ends, then a public repository and long-term archive within 30 days after acceptance. Restricted videos receive source IDs, access instructions, and temporal indices only; weights follow upstream licenses.

2. Response to Weakness 2 and Question 6

Summary

(1) Appendix completeness. We acknowledge the missing fields and broken reference and clarify domain boundaries and subset selection below.

(2) Audit and propagation (Tables R4–R5). We provide reviewer agreement and omission statistics. After discussion, we will revise the main text and appendices together, distinguish reported, uncomputed, and inapplicable items, and add repair examples.

Detailed Response

(1) Domains and the complex-task subset

We did not complete appendix and cross-reference checks before submission, impairing verification. Domains follow the public objective’s required final state: Personal Shopping concerns personal purchases; Shelf Management, shelf states; Stock Distribution, inventory allocation. Cooking concerns dishes for current consumption; Meal Preparation, preparation, portioning, and storage for later use. PC Assembly concerns component assembly; Equipment Repair, restored function. Appendix A.2 will add full criteria and boundary examples.

Primary structural labels follow this fixed pre-evaluation priority, retaining all applicable secondary labels:

plan–execution audit > joint constraints > conditional > multi-hop > sequential.

Only primary multi-hop or plan–execution audit labels define the complex subset; passing runtime IDs alone does not constitute multi-hop. The original 390 tasks were sampled uniformly without replacement from 3,000 frozen tasks, without domain/complexity quotas. The 156 complex tasks emerged within that sample.

(2) The 200 cross-time tasks

Eligibility follows public requirements to connect distinct event intervals or compare states across events. The pool was frozen before shortcut tests and additional runs; fixed-seed sampling selected 200 tasks without replacement, recording source videos and primary labels independently of outcomes.

All 200 tasks remain after shortcut discovery, without replacement: 17 have short-window solutions, three no-video solutions, with one overlap—19/200 (9.5%) distinct tasks. Finding none for 181 within budget does not prove temporal necessity. The supplementary 40-task diagnostic leaves the denominator unchanged. The revised appendix will list the seed, candidate pool, and tasks.

(3) Reviewer agreement

Table R4 gives independent judgments by two reviewers uninvolved in construction, before adjudication.

Table R4. Reviewer agreement before adjudication in the original 390-task audit

Reviewer 1 / Reviewer 2ValidInvalidTotal
Valid3628370
Invalid81220
Total37020390

Agreement is 374/390 = 95.90%; Cohen’s κ = 0.5784. High valid-class prevalence raises chance agreement, so we give both measures and the matrix. Adjudication resolves 16 disagreements as 14 valid and two invalid. Validity is 376/390 (96.41%) overall, 145/156 (92.95%) for complex tasks, and 231/234 (98.72%) for others, distinct from pre-adjudication agreement.

(4) Propagation, omissions, and repairs

Per revision, independent full review identifies required rechecks, compared with the algorithm’s union of recheck sets under old/new dependencies. Counts across revisions: TP = correct selections, FP = extra rechecks, FN = required decisions omitted.

Table R5. Propagation checks and omitted decisions

Change typeRevisionsDecisions requiring recheckAlgorithm-selected decisionsTPFPFN
Source facts844454321
Entity mappings857605730
Temporal applicability842434121
Total2414314814172

Omissions: 2/143 = 1.40% of decisions; 2/24 = 8.33% of revisions. Both triggered full review. After adding dependencies, we rechecked pre-action evidence support and fully replayed from an isolated state. Both remain in records and denominators after repair.

C.2 will add these methods/statistics and replace the broken reference with Table R5. C.3 will add Attachment A’s examples of changes invalidating review conclusions and triggering rebinding/reference execution, with version scope preserved.

3. Response to Question 4

Summary

(1) Correcting the references. We will correct Sections 4.2–4.3: Attachments A–B record individual executions; Table R6 is a new diagnostic, separate from the full evaluation.

Detailed Response

(1) Reference execution records

Attachment A records construction, repair, and reference replay. The main process, including two reference executions, used 25 model calls, 137,623 tokens, 32 frame deliveries, and 459.83 seconds, within its limits of 48 calls, 180,000 tokens, 48 frame deliveries, and 900 seconds. After a human-requested candidate-database change, rebinding and replay used 10 calls, 29,877 tokens, one frame delivery, and 34.21 seconds, within the revision's limits. All three executions passed final-state and associated-record checks.

These checks validate individual executions with private bindings, not unaided-agent budget feasibility. Attachment B records a separate interaction with 19 online calls, 107,918 tokens, and 91.586 seconds; prebuilt-index costs are separate, and its budget differs from the main evaluation. We will remove Section 4.2's inaccurate claim of reported results on a budget-feasible subset.

(2) Evidence-assistance diagnostic

Section 4.3's reference to existing evidence-assistance results was inaccurate. Table R6 is newly added: 27B, 300 tasks, 30 videos, 13 domains, and seeds 17, 29, and 43 (900 runs per condition).

Table R6. Additional diagnostic with oracle evidence-location hints

ConditionSRJoint-SR
ReAct118/900, 13.11%68/900, 7.56%
Five-role154/900, 17.11%99/900, 11.00%
ReAct + oracle location hints183/900, 20.33%128/900, 14.22%
Five-role + oracle location hints254/900, 28.22%183/900, 20.33%

Joint-SR requires success and evidence support before action for every required decision. Oracle hints reveal private-binding evidence locations. Assistance calls and retries count toward the shared budget, which does not remove the oracle advantage. We will add the settings and correct the reference. This diagnostic is separate from the main 3,000-task evaluation, whose ReAct/five-role SR remains 11.23%/17.73%.

Reviewer_LCHSOpenReview ↗
Rating
2
Confidence
2
Informativeness
1
Presentation
1
Soundness
1
Read review
Paper summary

This paper proposes a semi-automatic framework to generate tasks to test VLMs that process long-horizon videos for evidence and answering questions via tool-calling over collected evidence. With a human-in-the-loop they check if generated task goal is supported by evidence shown in the video. Human feedback is used to invalidate tasks or iterate on task design. Resultant benchmark has low success rate for LLMs while a ~91% for humans showing solvability and validity. It reports a 72.86% lower cost per valid task than a repair-based control.

Critical strengths
  • The validity auditing (Sec 4.4) is a strength. Two independent auditors, not involved in construction spot-checked 390 tasks, and found 96% to be valid. The automatic grader that judges AI performance has 98% human agreement.
Critical weaknesses
  • The paper is hard to evaluate mainly due to a lack of clarity. The paper introduces multiple terms without ever explaining on grounding them , e.g. "public acquisition path”, “private records”, “decision support”, “acceptance”, “screened proposals”, “packaging”. I could not confidently reconstruct the actual algorithm from the text.
  • The headline claim of lower cost per valid task is undermined by an unfair experiment between 300 tasks from one method and 3k from another, which entangles amortization into the claim.
Questions for authors
  • Please define the terms “public acquisition path”, “private records”, “decision support”, “acceptance” and “packaging”. Please also ground these in a specific example: template, bindings, detected gap, repair, final accepted task.
  • Concretely, how does this pipeline differ from the construction pipelines of Ego2Web, VideoGAIA or VideoWebArena? What does this pipeline add or produce that is novel in positioning. Is that difference in task type, in validity guarantees, or only in cost?
  • Can you redo the cost comparison s.t. overall work and output tasks are comparable so the effect of binding can be separated from amortization?
7 comments
AuthorsOpenReview ↗

Author Response to Reviewer LCHS

Author Response to Reviewer LCHS

Thank you for your careful review and for asking us to explain the task construction and repair process, clarify our contribution relative to existing benchmarks, and make the cost comparison more transparent. We agree that the submission should have explained these points more clearly. We will revise the main text and appendices together after the discussion ends, incorporating the clarifications, findings, and further feedback from this exchange. We address your concerns below and welcome further discussion. If the evidence resolves your concerns, we would be grateful if you would reconsider your assessment.

1. Response to Weakness 1 and Question 1

Summary

  1. Design origin and terminology. We provide the actual Designer input, output and freeze record, followed by six operational definitions.

  2. A worked construction example. The supermarket case traces a rejected binding, new visual acquisition, candidate screening and model-operated reference execution, followed by an H1-requested DB revision and affected rerun.

  3. Two supplementary records. Attachment A supplies the construction prompts, full run registry, source frames, reference traces and version-bound H1 reviews. Attachment B records a separate solving episode with a different frozen instance.

Detailed Response

(1) Design origin and overall process

We agree that the design source needed a concrete explanation. In Attachment A, Designer API_1 received the complete Retail construction/review exemplar, a public goal, five catalogue rows and tool contracts. It generated a design specifying the goal, constraints, required decisions and dependencies, and the output was frozen before this run’s first source-frame decode. Its request contained no target time, target pixels or selected answer. The schema supplied information-obligation types and dependency edges, so this is constrained prospective design generation.

Construction validates a supported reference path and retains its evidence and review records. During evaluation, the tested agent receives the public task and permitted interfaces and chooses its own observations and actions. Attachment A records construction; Attachment B supplies a separate solving episode.

(2) Operational definitions

TermMeaning in task construction and review
Public acquisition pathPermitted observation/tool calls selectable from public instructions and already acquired information, without presupposing private answers.
Private recordsEvidence bindings, review findings, reference answers, and reference trajectories retained for construction and checking, outside agent-facing tool returns.
Decision supportBefore the corresponding reference action, the acquired public information supports the choice across all compatible in-scope interpretations. This set must be nonempty; conflict or decision-changing uncertainty cannot pass.
Screened proposalsConstruction candidates for observations, bindings, or reference actions, checked for source validity, interfaces, preconditions, and budget before selection.
PackagingPreparing public instructions, a private reference trajectory, and a goal/constraint checking specification from the design, bindings, and executed reference path. Other valid solutions remain admissible.
AcceptanceSupported reference decisions, reviewed scope, successful isolated replay, unchanged requirements, and prescribed review approvals. Replay alone does not establish evidence support.

(3) Worked example: bag identification, ordering, and record checking

Design. The task is to identify the bag unfolded later near checkout, order one matching catalogue variant, and create an awaiting_arrival receiving check while preserving existing records. Identity comes from video, quantity from the instruction, and the new order ID from runtime: identity + quantity → place_order → read_order_receipt → create_receiving_check.

Binding. Each required decision receives a record of its supporting evidence, entity correspondence, applicable time and action condition. For identity, the selected binding uses API_6’s observation receipt, maps the bag to ITEM_F1514293DB09, uses point evidence at 1995s and supports place_order with quantity 1. The VLM reports "yong hui sheng huo" and dark green; an explicit semantic adapter links these attributes to the catalogue. The five rows are benchmark-authored comparison entities, not five observed products.

Applicability check and repair. The walkthrough uses a supplied 1995s anchor and a target-time applicability check. The 24 coarse samples provided no observation meeting this time condition, so the candidates generated by API_4 failed the screening program’s binding-admission checks, and no order was attempted. Collector API_5 then proposed six nearby times; new frames were decoded and processed by VLM API_6. API_7 returned three binding proposals, deduplicated and ranked by validation failures, declared extra accesses and proposal index. The selected tuple passed the binding checks. The goal, anchor and five-item universe stayed fixed. This sequence illustrates reacquisition and revalidation after an unsatisfied support check.

Reference executions. Two Qwen-operated references followed, each from isolated state: list_catalog → inspect_video → request_permission(order) → place_order → read_order_receipt → request_permission(check) → create_receiving_check → finish. Each video inspection used a fresh decode and VLM call. These operators received the binding; they check reference executability rather than blind agent performance.

Execution checks. place_order returns an opaque purchase handle; read_order_receipt then exposes the new order ID used by the linked check. Each run creates one order and one awaiting_arrival check and preserves existing rows. Business permission responses come from the isolated environment; they are distinct from H1’s review approvals. None of the three reference executions calls list_records.

Table V1 separates A’s construction/reference runs from B’s solving episode; they are not one trajectory or a performance comparison. Main construction uses 25 model calls and 137,623 tokens; the post-H1 revision uses 10 calls and 29,877 tokens. The full registry retains 38 physical requests, including three across two earlier failed runs. Full prompts, frame inputs, budgets and raw outcomes are supplied.

Table V1. Construction and separate solving records

RecordAttachment A: constructionAttachment B: solving
Instance / versionconstruction_v4; post_H1 catalogue revisionsupermarket_seed_511 / seed_511 (v5)
Model requests / tokens (all roles)Main: 25 / 137,623; post-H1: 10 / 29,87719 / 107,918
Catalogue / selected item5; ITEM_F1514293DB094; ITEM_ACD0DDA52438
Active list_recordsNo; new order_id is read via read_order_receipt; initial state is captured by the environment auditNo; state reads are audit hooks

Human review and revision. On 14 November 2026 at 15:09 +08:00, H1 passed facts, tools and task/repair, while requesting that distractor ITEM_26857A389CAB change from unknown color to red. This is an authored DB revision, not a new video fact. A new binder call and actual reference execution followed (10 model calls, 29,877 tokens), including fresh video decoding and VLM observation. At 15:39, H1 passed the revised DB and affected trajectory. The package preserves the original passes’ version scopes and records which were reused. H1 transcribed "Yonghui life" and green; the finer dark-green label was not separately human-confirmed.

2. Response to Question 2

Summary

Our primary contribution is an auditable task-validity assurance protocol, with lower construction cost as a practical benefit.

  1. Construction protocol. Fix requirements before evidence binding; check each required decision’s support before acceptance.

  2. Rechecking protocol. Invalidate dependent findings after changes; recheck affected decisions without relaxing requirements, and retain full replay.

  3. Quantified benefit. In the common-pool comparison, binding-guided review reduces construction labor by 73.58% and cost per qualified task by 66.92%, including binding overhead.

Detailed Response

(1) Fixing requirements before binding evidence

Ego2Web (§3.2) generates instructions from video profiles; VideoGAIA (§3.1) derives candidate tasks from video anchors and target attributes. EvidBind fixes requirements and decision dependencies before binding target-specific answers or evidence. Missing support leaves an explicit construction gap; requirements cannot be weakened to accommodate it.

(2) Checking each required decision

VideoWebArena (§§3.6–3.7) separately evaluates intermediate video questions and final completion. EvidBind records each decision’s public evidence, entity correspondence, applicable time, and consuming reference action. Before acceptance, we check whether the preceding public history supports that action parameter across compatible in-scope interpretations. Acceptance requires both this evidence support and successful replay.

(3) Rechecking after a change

Source, entity-mapping, or applicability changes invalidate dependent findings. Rechecking follows old and new dependencies under unchanged requirements and scope. Uncertain effects trigger full review; complete replay remains required. The resulting record identifies both the unsupported decision and the findings requiring repair.

Attachment A illustrates reacquisition and rebinding when coarse observations fail the time-applicability criterion for the supplied 1995s anchor. The later catalogue-colour revision triggers another version-bound recheck and model-operated reference execution.

Protocol contribution and benefit. This protocol makes support gaps and the required repair and review scope explicit. In the single-reviewer comparison on 1,000 frozen targets (Q3, Tables S1–R2), binding-guided repair reduces labor from 70.40 to 18.60 person-hours (73.58%) and cost per qualified task by 66.92%, including binding overhead. Independent assessment qualifies 957 targets with per-task review and 963 with binding-guided repair.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Summary of Reviewers’ Feedback and Authors’ Response

We sincerely thank all three reviewers for their constructive feedback, which has helped us strengthen the clarity, reproducibility, and diagnostic value of our work. We recognize that several important details were not sufficiently explained in the original submission. During the rebuttal period, we devoted substantial GPU time and manual review effort to addressing these gaps. Below, R1 (LCHS), R2 (ybPm), and R3 (NpeF) denote the three reviewers.

Strengths. The reviews recognize the value of our construction principles and benchmark checks. We appreciate R1’s recognition of the independent validity audit and grader agreement, R2’s support for decision-first construction and shortcut checks, and R3’s recognition of the distinction between executability and evidence support, together with the benchmark’s structural diversity.

Our supplementary materials make construction and repair more concrete and easier to reproduce (R1, R3). We provide operational definitions, prompt templates, implementation settings, and a worked supermarket example. Two attachments separately document construction and agent interaction. We clarify the protocol’s contribution: fixing requirements before evidence binding, checking decision-level support, and rechecking affected findings after changes without weakening requirements.

The additional diagnostics assess evidence support and result stability more directly (R2, R3). We report video-clustered intervals, separate repeated-run checks, budgets, failure distributions, and role ablations. Joint-SR complements task success by requiring every necessary decision to be supported before action. Matched content removal, no-video and short-window controls, event-order interventions, and shortcut-stratified results provide complementary diagnostics while admitting legitimate alternatives. Human-baseline participation, viewing conditions, and consent and ethics reporting are also clarified.

The common-target comparison provides a fairer assessment of construction efficiency (R1, R2, R3). Both procedures attempt the same 1,000 prespecified targets, with paired initial candidates and common budget caps, retaining failed and unfinished attempts. Including binding overhead, construction cost per independently qualified task decreases by 66.92%, with 957 versus 963 qualified targets. This supplementary comparison uses single-reviewer construction staffing; independent assessment costs and sensitivity analyses are reported separately.

Together, these additions provide a clearer basis for assessing the benchmark’s contribution and practical trade-offs. We hope they help address the reviewers’ main concerns. We will incorporate them into a consolidated revision after discussion and would be grateful for any remaining questions or corrections.

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

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