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Under review as a conference paper at ICLR 2027

VAD-TTRL: Propose, Verify, Reinforce for Label-Free Test-Time Video Anomaly Detection and Understanding

Abstract

Multimodal Large Language Models (MLLMs) have shown strong capabilities in video understanding, yet video anomalies are often scene- and deployment-dependent, limiting the reliability of fixed pretrained models across environments. Conventional adaptation typically requires task-specific annotations and expensive post-training. Test-time reinforcement learning offers an appealing alternative by adapting models directly on unlabeled test videos using self-generated supervision. However, existing approaches commonly treat self-consensus among sampled predictions as supervision, which can reinforce systematic errors. We introduce VAD-TTRL, a label-free test-time reinforcement learning framework based on a propose–verify–reinforce paradigm. Multiple stochastic reasoning trajectories first form a structured consensus hypothesis, which is then verified using temporal and spatial consistency together with counterfactual visual evidence. Only sufficiently supported hypotheses contribute to reliability-weighted reinforcement signals, while uncertain predictions are excluded from adaptation. These rewards are optimized with Group Relative Policy Optimization (GRPO), enabling adaptation without ground-truth anomaly labels or task-specific annotations. Experiments across multiple MLLM backbones show that VAD-TTRL improves anomaly detection and temporal localization while largely preserving reasoning quality. On Qwen2.5-VL-7B, it improves accuracy from to and mIoU from to ; when applied on top of sota Vad-R1, it further improves accuracy from to and mIoU from to , demonstrating the value of evidence-verified consensus for label-free test-time video anomaly understanding.

Primary area:
reinforcement learning
Keywords:
Video Anomaly Detection, Multimodal Large Language Models, Test-Time Reinforcement Learning, Video Understanding, propose, verify, update

Reviews

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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_JoeyOpenReview ↗
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Paper summary

VAD-TTRL adapts video LLMs without anomaly labels, temporal boundaries, or annotated explanations. It forms a consensus over structured outputs covering the label, temporal interval, spatial location, and explanation. Target-drop, target-keep, and off-target interventions then assess visual support, followed by gated GRPO updates with structured rewards.

On Vad-Reasoning, Qwen2.5-VL-7B improves from 0.761 to 0.829 accuracy and from 0.567 to 0.657 mIoU. The post-trained Vad-R1 improves from 0.875 to 0.886 accuracy and from 0.713 to 0.729 mIoU. The evaluation covers six backbones, transfer to VANE-Bench, additional videos excluded from adaptation, and LLM-based explanation assessment.

Critical strengths
  1. Broad evaluation, including videos excluded from adaptation. Detection accuracy and mIoU improve on all six backbones. On additional sets of 500 and 1,000 videos not used for adaptation, accuracy rises from 0.754 and 0.766 to 0.806 and 0.819, respectively. These results support transfer beyond the adaptation set.
  2. A quantitative audit of incorrect consensus. The full configuration achieves 89.0% accepted pseudo-label accuracy at 72.7% update coverage. Among 230 proposals with unanimous 8/8 agreement, 23 are still incorrect, directly supporting the motivation that agreement does not ensure correctness. GPT-4o explanation assessment in the appendix complements token-overlap metrics.
Critical weaknesses
  1. The gate admits proposals that are insensitive to the target interval.

    Equations (4)–(7) on p. 5 average necessity and sufficiency. If the full-video, target-drop, target-keep, and off-target views all have anomaly probability 0.9, necessity is 0, while sufficiency and the control score are both 1. The resulting eA=0.45e_A=0.45 exceeds the default threshold of 0.20. A proposal satisfying the other conditions can therefore pass visual verification even when removing the target interval has no effect.

    The appendix counterbalances answer ordering and includes matched interventions and temporal-support filtering, but these do not exclude this case. Please report the frequency and accuracy of accepted proposals with near-zero necessity. Comparing raw-confidence filtering, the current verifier, and a verifier requiring positive necessity under the same consensus conditions would establish the added value of video interventions. This counterexample identifies a boundary of the gate; its practical frequency remains to be measured.

  2. The evidence weight does not necessarily control update strength.

    From Appendix E, the reward can be written as Ri=eBi+0.20fiR_i=eB_i+0.20f_i, where trajectories from the same video share ee and fif_i denotes format validity. If format rewards are identical within the group, e>0e>0, reward variance is nonzero, and ϵ\epsilon is negligible relative to the reward standard deviation, centering and standardization cancel ee. The equations therefore do not generally support the interpretation that weaker evidence produces weaker updates.

    The weight can still affect gradients when format rewards differ, ϵ\epsilon is not negligible, or an additional weight is applied outside the normalized objective. Hard gating also retains its filtering effect. Moreover, the label term aicea_i c e and visual term aiea_i e share the same indicator, so removing the visual term also changes the effective label weight. Please hold proposals and training trajectories fixed, compare normalized advantages and gradient norms, and clarify whether qq or ee is applied outside the loss.

  3. Performance is highly sensitive to training-group size, and the final configuration needs clarification.

    In Table 7, changing from N=8,G=4N=8,G=4 to N=8,G=8N=8,G=8 reduces anomaly recall from 0.745 to 0.118 and F1 from 0.802 to 0.209. With N=16,G=8N=16,G=8, recall is only 0.049. The proposed explanation, reinforcement of correlated trajectories, needs a controlled analysis of the trajectories and update budget. Please also explain how the default group size, thresholds, and weights are selected without labels.

    Several details affect reproducibility: Are the 439 videos reevaluated after the full adaptation pass, or is each video predicted immediately after its update? What are the intervention strength γ\gamma, normal-risk coefficient λN\lambda_N, temporal-support threshold, and fallback rules? In Table 8, τvis=1.00\tau_{\mathrm{vis}}=1.00 should reject all videos under exact softmax probabilities with finite logits, although numerical saturation to 1 could create exceptions. Since this row differs from the frozen model, accepted-sample counts, parameter changes, and prediction settings are needed. VANE transfer also lacks a direct comparison with the same frozen Qwen backbone, and end-to-end runtime should be reported.

Questions for authors
  1. How is visual evidence considered verified when identical anomaly probabilities across all intervention views can still pass the gate? What fraction of accepted proposals has near-zero necessity, and how does raw-confidence filtering perform?
  2. With identical format rewards, e>0e>0, nonzero reward variance, and negligible ϵ\epsilon, GRPO normalization cancels ee. Is qq or ee applied outside the normalized loss? Can normalized advantages and gradients be compared on fixed trajectories?
  3. What explains the recall collapse at G=8G=8 when trajectories and update budget are controlled? What independent validation information or unlabeled criterion determines the default thresholds, weights, and group size?
  4. How many videos are accepted and updated with τvis=1.00\tau_{\mathrm{vis}}=1.00 in Table 8? Are the prediction procedure and initial model identical to those of the frozen baseline?
  5. Please clarify evaluation timing, verification parameters, and end-to-end cost, and report the same frozen backbone on VANE. How much improvement comes from the additional generation and verification calls without parameter updates?
8 comments
AuthorsOpenReview ↗

Response 1/6 : (W1+Q1)

Thank you for this detailed and constructive review, and for recognising the breadth of the evaluation, the transfer beyond the adaptation set, and our quantitative analysis of incorrect consensus. Your comments helped us sharpen several parts of the paper; we respond point by point below. All changes in the revised PDF are highlighted in blue.

W1 / Q1: The gate admits proposals that are insensitive to the target interval. How often does this happen, and how does raw-confidence filtering compare?

How identical probabilities can pass the gate. We agree with your observation. Equations (4)–(7) combine necessity, sufficiency and the off-target control into one score, so a confident proposal whose removal does not lower the Abnormal probability (necessity = 0) can still pass the 0.20 threshold through sufficiency and the control term. The gate therefore does not establish that the interval is strictly necessary; it checks that the interval keeps positive visual support without relying on off-target context. This also explains why no Abnormal proposal reaches an evidence score above 0.5 (Table R2): when necessity is near zero, the averaged term (Δnec+Ssuf)/2(\Delta_{\text{nec}}+S_{\text{suf}})/2 is at most about 0.5.

How often it happens, and how accurate these proposals are. As you suggested, we measured this on the submitted run over the Vad-Reasoning test set (Huang et al., 2025), using ground truth only for this analysis. Of the 97 Abnormal proposals that pass the consensus conditions, the verifier accepts 92. Of these, 48 (52%) have necessity = 0, so the case you describe is common in practice. However, 47 of these 48 are correct: the admitted zero-necessity proposals are almost all genuine anomalies rather than false positives.

NecessityEligibleAcceptedCorrectPrecision
=0= 050484797.92%
(0,0.001](0, 0.001]333100%
(0.001,0.01](0.001, 0.01]101010100%
(0.01,0.05](0.01, 0.05]292626100%
>0.05> 0.05555100%

Comparison with a positive-necessity verifier and raw-confidence filtering, under the same consensus conditions:

Selection ruleScopeRetainedPseudo-label accuracy
Consensus onlyfull test set34084.41%
Verifier + necessity > 0full test set27187.45%
Verifier (ours)full test set31989.03%
Raw confidence pA(F)p_A(F)Abnormal, matched coverage90 / 9297.83%
Verifier (ours)Abnormal, matched coverage91 / 9298.91%

Requiring positive necessity gives a fully correct Abnormal subset, but keeps only 44 of the 97 proposals. Over the whole test set it reduces update coverage from 319 to 271 and lowers pseudo-label accuracy from 89.03% to 87.45%, because it removes 47 correct proposals along with one incorrect one. At matched coverage, the verifier is slightly more precise than raw confidence (91 vs. 90 correct).

Where the interventions add value. On Abnormal proposals the interventions add little over raw confidence, because these proposals are already highly precise after consensus. Their main contribution is on the Normal side: of the 21 proposals rejected by verification, 16 were predicted Normal (14 of them incorrect, 2 correct) and 5 predicted Abnormal (4 incorrect, 1 correct).

AuthorsOpenReview ↗

Response 2/6 : (W2+Q2)

W2 / Q2: The evidence weight does not necessarily control update strength. Is it applied outside the normalized loss, and can advantages and gradients be compared on fixed trajectories?

We thank you for this careful analysis; it is correct. In our implementation, no evidence weight (qq or ee) is applied outside the normalized GRPO objective, so the cancellation you describe holds whenever the terms that do not depend on the evidence are identical within a group and ϵ\epsilon is negligible.

How verification acts on the update. Verification mainly acts through the hard gate: for a rejected proposal, the loss is multiplied by zero, so that group contributes no GRPO or KL gradient. We also correct one phrase in the paper, that rejected proposals "produce no policy update". Because the run uses AdamW (weight decay 0.01), the optimizer step still runs, so the gate removes the GRPO/KL gradient contribution rather than every weight-decay or optimizer-state change.

Fixed-trajectory comparison. As you suggested, we replayed all accepted groups with the same proposals, the same selected trajectories and the same reward code, and compared the reward computed with the actual visual evidence against the same reward with the evidence set to 1:

Fixed-trajectory statisticResult
Accepted groups / fixed completions319 / 1,276
Consensus reconstruction mismatches0
Groups where the evidence-independent terms are identical202 / 319
Groups with unchanged reward ranking307 / 319 (96.24%)
Mean cosine between normalized advantages0.9899
Mean coefficient norm, actual evidence0.4298
Mean coefficient norm, evidence = 10.4310
Relative difference−0.26%

Here, the coefficient norm is the gradient with respect to the per-sequence log-probabilities, before the shared model Jacobian (not the full parameter-gradient norm). The two norms are almost equal (−0.26%), which confirms your analysis empirically: inside group normalization, the soft evidence weight does not set the magnitude of accepted updates. It can still change the relative ranking within a group when the other terms differ (117 of the 319 groups).

Shared indicator and λv=0\lambda_v = 0. We agree that the label and visual terms share the same agreement indicator, so setting λv=0\lambda_v = 0 (Table 11) also changes the effective weight on agreement, from aie(c+0.5)a_i e (c + 0.5) to aieca_i e c. We now describe that ablation as measuring their combined effect.

Revision. The revised PDF adds a paragraph to Appendix E.5 that derives this cancellation, explains how the evidence still acts (through the hard gate; through the balance between task and format rewards when format validity differs; and through cc, which re-weights the label term and does not cancel), states that no evidence weight is applied outside the normalized objective, and notes the shared indicator. Section 5.1 and Appendix E.3 now describe evidence weighting as shaping the relative contribution of the reward terms rather than the strength of the update. We have also made the notation in Appendices D and E consistent with the main text (e.g., the rationale reward RirR^r_i is now written with rir_i and did_i throughout). Thus, the hard gate controls whether a group contributes policy gradients, while the soft evidence shapes rewards within the group. This refines our interpretation of the mechanism and does not change the reported run or results.

AuthorsOpenReview ↗

Response 3/6 : (W3+Q3)

W3 / Q3: Sensitivity to the training-group size, and how the defaults were selected without labels.

We thank you for these direct questions and answer each in turn.

Final configuration. All reported results use (N,G)=(8,4)(N,G)=(8,4), τmaj=0.75\tau_{\text{maj}}=0.75, τvis=0.20\tau_{\text{vis}}=0.20, λy/λv/λt/λr/λs=1.0/0.50/0.35/0.25/0.15\lambda_y/\lambda_v/\lambda_t/\lambda_r/\lambda_s = 1.0/0.50/0.35/0.25/0.15, format weight 0.20, KL coefficient 0.04, learning rate 10−610^{-6} and one epoch, for every backbone and dataset.

What explains the recall collapse at G=8G=8 when trajectories and update budget are controlled?

We have not yet run the fully controlled comparison, so we do not claim a causal explanation. What we can state is the following:

  1. The visual gate is applied per video, before the training group is sampled, so (8,4)(8,4) and (8,8)(8,8) use the same gate criteria and the same single epoch; they differ mainly in how many trajectories enter each update.
  2. Recall drops whenever G=8G=8, for both N=8N=8 (0.118) and N=16N=16 (0.049), while all settings with G≤4G \le 4 keep much higher recall (0.500–0.745). The effect therefore follows the size of the update group rather than whether the group equals the whole proposal pool.
  3. The collapse is directional, not random. Settings that remove a core part of the design move in the same direction, with precision rising and anomaly recall falling: G=8G=8 (0.923 / 0.118), no visual gate (0.977 / 0.211), λy=0\lambda_y=0 (0.930 / 0.392) and λv=0\lambda_v=0 (0.944 / 0.417), against the default (0.869 / 0.745).
  4. This matches our analysis of the accepted proposals, in which 34 of the 35 incorrect pseudo-labels accepted by the verifier were Abnormal videos accepted as Normal: the base model's main error is a bias toward Normal.

Our working hypothesis is therefore that larger update groups admit more trajectories agreeing with a dominant Normal consensus and so amplify this bias. Training with the default group is otherwise well behaved: the KL divergence from the reference stays below 0.018 throughout adaptation (Figure 4), and (N,G)=(4,2)(N,G)=(4,2) also remains well above the frozen model. We present this explanation as a hypothesis, recommend a small update group (G≤4G \le 4 in our experiments), and list the missing controlled analysis as a limitation.

What independent validation information or unlabeled criterion determines the defaults?

No labeled validation data and no unlabeled selection criterion were used. Benchmarks that annotate labels, temporal intervals, spatial locations and reasoning together are scarce, and holding out a labeled split would contradict the label-free setting. The defaults were fixed once from what each value controls: N=8N=8 gives a diverse proposal pool at moderate cost; G=4G=4 keeps forming the consensus separate from reinforcing it; τmaj=0.75\tau_{\text{maj}}=0.75 requires a clear majority (at least six of eight) without unanimity; τvis=0.20\tau_{\text{vis}}=0.20 is a minimum support floor rather than a classification threshold; the reward weights follow task priority; and the learning rate and KL coefficient follow the standard GRPO setting of Shao et al. (2024). The sweeps in Tables 7–11 are sensitivity analyses carried out afterwards, not a selection procedure.

As evidence that this configuration is not fitted to one setting, it was reused unchanged on all six backbones in Table 2, improving accuracy and mIoU in every case, and it transfers to the 1,755 unseen videos of the Vad-Reasoning SFT split (Acc 0.765 → 0.817, mIoU 0.559 → 0.648; Appendix C.2). We agree that label-free model selection remains open. Signals available during adaptation, such as the gate acceptance rate or the fraction of Abnormal predictions, are natural candidates, and Appendix H now lists label-free hyperparameter selection as future work.

Reviewer_aJPTOpenReview ↗
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Paper summary

This paper proposes VAD-TTRL, a label-free test-time reinforcement learning framework for video anomaly detection and understanding. The main idea is to let the model generate multiple predictions, check whether the agreed-upon answer is supported by visual evidence, and then use reliable predictions to improve itself through reinforcement learning.

Critical strengths

The paper addresses an interesting and practical problem. Adapting video anomaly detection models without labeled data is useful, especially when models are deployed in new environments. I particularly like the idea of checking visual evidence before trusting the majority prediction. This makes more sense than directly using self-generated predictions as training labels.

Critical weaknesses
  1. How reliable is the visual verification process? This is the most important part of the paper. However, the verification still relies on the model's own predictions. For example, removing a video segment may reduce the model's confidence, but this does not necessarily mean the original anomaly prediction was correct. I think the authors should discuss this limitation more carefully and provide more examples of cases where verification accepts incorrect predictions.
  2. The method requires multiple reasoning trajectories, several additional video evaluations, and GRPO updates. This seems quite expensive compared with regular inference.
  3. Table 7 shows that increasing the GRPO group size from 4 to 8 causes a large drop in anomaly recall. This raises concerns about training stability.
  4. The method achieves clear gains in classification and temporal localization, but the reasoning metrics show smaller and sometimes inconsistent improvements across different backbones. I would like to see more discussion of this gap.
Questions for authors

Does the model actually learn better anomaly reasoning, or does it mainly become better at predicting anomaly labels and time intervals?

5 comments
AuthorsOpenReview ↗

Response 1/3 : Weakness W1 and Weakness W2

Thank you for your review and for your positive view of the core idea: checking visual evidence before trusting the majority prediction, rather than using self-generated predictions directly as training labels. We respond to each point below. All changes in the revised PDF are highlighted in blue.

W1: How reliable is the visual verification process?

We agree that this is the most important part of the paper, and that verification still relies on the model's own predictions. Because proposal and verification use the same MLLM, a drop in confidence when a segment is removed shows how the model responds, not that the anomaly prediction is correct. We therefore see the verifier as a filter that reduces errors, not a guarantee of correctness. To measure how reliable it is in practice, we examined the full adaptation run on the Vad-Reasoning test set (Huang et al., 2025), using ground-truth labels only for this analysis and never during adaptation (Appendix F.5, Table R3).

How much does verification help? Before the visual-evidence gate, 340 proposals passed consensus, of which 287 (84.41%) were correct. The gate kept 319, of which 284 (89.03%) were correct. It removed 18 of the 53 consensus errors (34.0%) but only 3 of the 287 correct proposals (1.05%), so a wrong proposal was about 32 times more likely to be rejected than a correct one, and 18 of the 21 rejections were beneficial.

When does it accept incorrect predictions? 35 incorrect proposals still passed, and 34 of them were Abnormal videos accepted as Normal. This is the verifier's weakest case: a Normal proposal has no predicted segment to remove, so a high score only shows that "Normal" stayed stable under the perturbations. 21 of these 34 are context-dependent traffic events (wrong-way driving, jaywalking, illegal turns), where the anomaly lies in breaking a rule rather than in a clearly visible event. The highest-scoring examples are (Table R4):

VideoGround-truth classAgreementEvidence score
06_PedestrianOnRoad_007Pedestrian Jaywalking8/8 Normal0.9864
06_PedestrianOnRoad_014Pedestrian Jaywalking8/8 Normal0.9501
02_IllegalTurn_005Illegal Lane Changing8/8 Normal0.9364
05_else_002Animals Obstructing Traffic8/8 Normal0.9228

In each case, the model sees an ordinary road scene and does not recognise the rule being broken, so both stages make the same mistake with high confidence.

Revision. The revised PDF adds this analysis, the breakdown by Abnormal and Normal proposals, and these failure cases (Appendix F.5, Tables R3–R4). It describes verification as a selective error filter rather than a correctness guarantee, and Appendix H now states the shared-model limitation and lists cross-model verification and stronger tests for Normal proposals as future work.

W2: The method seems expensive compared with regular inference.

We understand the concern, and want to clarify where the extra cost occurs. Following TTRL (Zuo et al., 2025), VAD-TTRL uses test-time reinforcement learning as a one-time, label-free adaptation step, not as a search repeated at every inference. Once adapted, the model runs as a standard single-rollout Video-LLM.

No extra inference cost. Under identical settings (one RTX 3090, 24 GB, vLLM), VAD-TTRL matches the frozen Qwen2.5-VL-7B and the supervised Vad-R1 in latency (about 6.01 s vs. 6.02 s and 6.02 s per video) and peak memory (16 GB), because no extra rollouts or verification passes are needed at inference.

One-time adaptation cost. The 8 proposals, the short verification passes and the GRPO update happen only once, during adaptation: 24.02 GPU-hours in total (3.0 h on 8×A100), with no annotations. This is more than 5× cheaper than training the supervised Vad-R1 (128 GPU-hours). The adapted model also improves on unseen videos (Table 6) and on VANE-Bench without further updates, so this one-time cost is not repeated for each evaluation. The full comparison is in Appendix B.2 (Table R1).

AuthorsOpenReview ↗

Response 2/3 : Weakness W3

W3: Table 7 shows a large drop in anomaly recall when the group size increases from 4 to 8, raising concerns about training stability.

We thank the reviewer for pointing this out; it is a striking result, and we have looked into it more closely. It appears to be a consistent, directional failure tied to the size of the update group, rather than erratic or unstable training, although we do not yet have a fully controlled explanation.

What happens. In Table 7, recall drops sharply whenever G=8G=8, for both N=8N=8 (0.118) and N=16N=16 (0.049), while all settings with G≤4G \le 4 keep much higher recall (0.500–0.745). The drop is not random: precision rises at the same time, the same direction we see when the visual gate is removed.

ConfigurationPrecRec
Default (N,G)=(8,4)(N,G)=(8,4)0.8690.745
(N,G)=(8,8)(N,G)=(8,8) (Table 7)0.9230.118
(N,G)=(16,8)(N,G)=(16,8) (Table 7)0.9330.049
No visual gate, τvis=0\tau_{\text{vis}}=0 (Table 8)0.9770.211

Likely cause. Our analysis of the accepted proposals shows that the base model's main error is a bias toward Normal: 34 of the 35 incorrect pseudo-labels that passed verification were Abnormal videos accepted as Normal. With a larger update group, more trajectories that agree with a dominant Normal consensus enter each update, which can reinforce this bias and suppress Abnormal predictions. This is consistent with the pattern above, but we have not run a controlled experiment that fixes the trajectories and the number of updates, so we present it as a likely explanation rather than a proven one. Using a smaller subset for the update is also in line with TTRL (Zuo et al., 2025), which votes on a large pool of responses and trains on a smaller subsample.

Training is otherwise stable. With the default update group, the KL divergence from the reference model stays below 0.018 throughout adaptation (Figure 4). The same configuration improves accuracy and mIoU on all six backbones in Table 2 without re-tuning, carries over to unseen videos of the Vad-Reasoning SFT split (Acc 0.765 → 0.817, mIoU 0.559 → 0.648), and changes by at most 2.7 points when the order of the test videos is shuffled. A smaller setting, (N,G)=(4,2)(N,G)=(4,2), also stays well above the frozen model (0.804 Acc / 0.608 mIoU vs. 0.761 / 0.567).

Revision. Appendix F.1 now includes this explanation, clearly marked as a hypothesis, together with the practical recommendation to keep the update group small (G≤4G \le 4 in our experiments), and Appendix H states the sensitivity to the group size.

AuthorsOpenReview ↗

Response 3/3 : (W4 + Q)

W4: Reasoning metrics show smaller and sometimes inconsistent improvements across backbones.

We agree, and thank the reviewer for asking for this discussion. The gains on token-overlap reasoning metrics are smaller than those on detection and localization, and on a few backbones they are slightly negative. Relative change of the reasoning metrics after adaptation (from Table 2):

BackboneBLEU-2METEORROUGE-2
Qwen2.5-VL-7B↑ 15.9%↑ 6.1%↑ 34.5%
Qwen3-VL-8B↑ 0.6%↓ 5.1%↑ 8.8%
Qwen3.5-4B↑ 43.6%↑ 9.7%↑ 92.0%
Vad-R1↓ 0.4%↓ 0.2%↑ 10.8%
InternVL2.5-8B↑ 9.4%↑ 9.2%↑ 8.7%
InternVL3.5-8B↑ 3.1%↑ 3.2%=

Most changes are positive, ROUGE-2 never decreases, and the three decreases are small (at most 5.1%). One reason the gains are limited is how the method learns: the rationale reward only encourages agreement with the model's own consensus explanation, so it can make explanations more consistent but cannot teach the model reasoning it does not already have. Appendix H states this gap.

Q: Does the model learn better anomaly reasoning, or mainly better labels and time intervals?

Mainly better labels and time intervals. These gains are the largest and most uniform; reasoning gains are real but appear in specific aspects rather than across all metrics. For Qwen2.5-VL-7B, VAD-TTRL closes 55–74% of the gap to the supervised Vad-R1 on detection and localization, but only 11–15% on BLEU-2/METEOR:

MetricQwen2.5-VL+ VAD-TTRLVad-R1 (supervised)Gap closed
Acc / F10.761 / 0.7300.829 ↑ / 0.802 ↑0.875 / 0.86260% / 55%
mIoU / [email protected]0.567 / 0.6100.657 ↑ / 0.729 ↑0.713 / 0.77062% / 74%
BLEU-2 / METEOR0.113 / 0.2640.131 ↑ / 0.280 ↑0.233 / 0.40615% / 11%
ROUGE-20.1160.156 ↑0.19451%
LLM Reasonability0.6380.766 ↑0.734>100%
LLM Detail0.5550.605 ↑0.65948%
LLM Consistency0.5420.566 ↑0.66220%

Why token-overlap metrics understate reasoning changes. Metrics such as BLEU and METEOR are known to correlate weakly with human judgments of generated text (Novikova et al., 2017); they mainly reward matching the annotators' wording. Vad-R1 is fine-tuned on annotations written in the same style as the test references, whereas VAD-TTRL never sees reference text. Its explanations are also shorter (228.6 vs. 254.7 tokens on average), which recall-oriented METEOR penalises. LLM judges agree much more closely with human assessments (Liu et al., 2023; Zheng et al., 2023) and are widely used to evaluate video-language outputs (Maaz et al., 2024) and anomaly explanations (Tang et al., 2024; Huang et al., 2025).

Under the LLM-judge protocol used by Vad-R1 (Huang et al., 2025) and HAWK (Tang et al., 2024), VAD-TTRL exceeds the supervised Vad-R1 in Reasonability (0.766 vs. 0.734) without any labels. Applied on top of Vad-R1, it leaves BLEU-2 and METEOR essentially unchanged (0.233 → 0.232 ↓, 0.406 → 0.405 ↓) while improving all three judge scores (Reasonability 0.734 → 0.859 ↑, Detail 0.659 → 0.721 ↑, Consistency 0.662 → 0.667 ↑; Table 5), changes that n-gram overlap does not capture. Detail and Consistency still trail the supervised model, so we describe reasoning as largely preserved with selective gains, not as the main benefit of the method.

We hope these clarifications and new results address your concerns, and we would be grateful if you would take them into account in your assessment. We are happy to provide any further details.

Reviewer_Ljv8OpenReview ↗
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Paper summary

This paper studies label-free test-time video anomaly detection and understanding, aiming to directly adapt pretrained multimodal large language models using unlabeled test videos. To address the issue that existing Test-Time RL methods directly use consistency across multiple rollouts as pseudo-supervision, which may reinforce model errors, the authors propose VAD-TTRL based on a Propose - Verify - Reinforce paradigm. Specifically, the method first generates structured anomaly hypotheses through multiple stochastic rollouts, then verifies these hypotheses using spatiotemporal consistency and counterfactual visual interventions, and finally performs reliability-weighted GRPO updates only on the results supported by visual evidence. The authors conduct experiments on 439 test videos from Vad-Reasoning and on VANE-Bench, using multiple MLLM backbones. For Qwen2.5-VL-7B, VAD-TTRL improves Accuracy from 0.761 to 0.829 and mIoU from 0.567 to 0.657. When further applied to Vad-R1, Accuracy and mIoU improve from 0.875 and 0.713 to 0.886 and 0.729, respectively.

Critical strengths
  1. The method provides a targeted solution to the issue that self-consistency in existing Test-Time RL methods may reinforce erroneous predictions. By treating the results from multiple rollouts as candidate hypotheses rather than directly using them as pseudo-labels, and further verifying them with spatiotemporal consistency and counterfactual visual evidence, the method can reduce the risk of directly using erroneous consensus for model updates.
  2. The Propose-Verify-Reinforce mechanism enables selective model updates based on the reliability of visual evidence. Predictions without sufficient supporting evidence can be excluded from the reinforcement learning signal, thereby reducing the interference of unreliable samples during online adaptation. This reliability-aware updating strategy is well suited to the label-free test-time learning setting.
Critical weaknesses
  1. The visual verification mechanism is not independent of the model being adapted. Both the Proposal and Verification stages rely on the same MLLM, and the visual evidence score is also derived from changes in the model’s own abnormal/normal probabilities under synthetic temporal perturbations. Therefore, a high evidence score may reflect the model’s sensitivity to the intervention rather than the correctness of the proposed anomaly hypothesis itself. This means that systematic visual or temporal errors of the model may still affect both the proposal and verification stages.
  2. The performance of VAD-TTRL is sensitive to several manually selected hyperparameters. The experiments in the appendix show that different rollout configurations, consensus thresholds, visual-evidence thresholds, and reward weights can lead to substantial performance variations. However, the paper does not sufficiently explain how these hyperparameters are determined in the label-free test-time setting, which raises concerns about the stability and practical applicability of the method across different datasets and models.
Questions for authors
  1. Both the Proposal and Verification stages rely on the same MLLM being adapted. When the model has a systematic misinterpretation of a certain type of anomaly, could this error propagate through both stages and consequently result in a high visual evidence score? In such cases, how does the visual evidence distinguish the model’s sensitivity to the intervention from genuine evidence of an anomaly?
  2. Several thresholds and reward-related hyperparameters in the paper affect the final test-time adaptation results. In the fully label-free test-time setting, what is the basis for selecting these parameters? Do different datasets or backbones require different parameter settings?
  3. During online test-time adaptation, the model continuously updates its parameters as test videos are processed. Do updates induced by earlier test videos affect the prediction results of subsequent videos? If the order of test videos is changed, does the final performance vary substantially?
  4. Compared with directly using a Video-LLM for inference and existing Test-Time RL methods, VAD-TTRL requires multiple rollouts, video perturbation-based verification, and GRPO updates. How large is the additional computational and inference overhead introduced by the entire test-time adaptation process?
4 comments
AuthorsOpenReview ↗

Response 1/4

Thank you for your careful review, and for recognising that treating rollout agreement as a candidate hypothesis rather than a pseudo-label, and updating only on visually supported cases, suits the label-free test-time setting. We respond to each point below. All changes in the revised PDF are highlighted in blue.

W1: The visual verification is not independent of the model being adapted.

We agree with this observation. Both stages use the same MLLM, and the evidence score is computed from the model's own Abnormal/Normal probabilities under temporal perturbations, so a high score reflects how the model responds rather than whether the hypothesis is correct. We see the verifier as a filter that reduces, but cannot remove, the model's own systematic errors. Our answer to Q1 below explains why we accept this trade-off and measures how often such errors still get through.

Q1: Answer

Yes, a systematic misinterpretation can propagate through both stages.

Why a single model. Our goal is test-time adaptation: improving a model beyond its own frozen behaviour on unlabeled videos from an unseen environment, as in TTRL (Zuo et al., 2025), TTRV (Singh et al., 2025) and TTA-Vid (Jahagirdar et al., 2026). This differs from distillation, which needs a stronger judge that already understands anomalies better than the adapted model; such a judge would itself need anomaly-specific training and would add cost at test time. We therefore use the model's own responses, accepting that this allows shared systematic errors.

Sensitivity vs. evidence. The score is not designed to reward sensitivity to arbitrary perturbations. For an Abnormal proposal, it combines the model's confidence on the full video with how its belief changes when the proposed interval is removed (necessity) or kept alone (sufficiency), and multiplies this by an off-target check: masking a different interval of the same length should not cause the same change. A model that reacts to any masking is penalised by this last term. Necessity and sufficiency are averaged, so a proposal can pass with little necessity; we report how often this happens in our reply to Reviewer Joey. For a Normal proposal, the score rewards stability across perturbations and penalises the strongest Abnormal response. All of these remain responses of the same model, so they cannot certify correctness.

How often does it happen? We audited the full adaptation run, using ground truth only for this analysis and never during adaptation (Appendix F.5, Table R3):

AcceptedCorrectPrecision
Consensus only340/43928784.41%
+ Visual verification319/43928489.03%

Verification rejected 21 proposals, 18 of them wrong. It removed 34.0% of the errors that passed consensus but only 1.05% of the correct proposals, so a wrong proposal was about 32 times more likely to be rejected. This supports our core premise: agreement alone admits systematic errors, and treating it as a hypothesis to verify gives more reliable pseudo-labels.

Failure cases. 35 wrong proposals still passed, and 34 of them were Abnormal videos accepted as Normal. This is the verifier's weakest case: a Normal proposal has no interval to test, so a high score only means that "Normal" stayed stable. 21 of these 34 are context-dependent traffic events (wrong-way driving, jaywalking, illegal turns). The highest-scoring errors (two jaywalking clips, 02_IllegalTurn_005.mp4 and 05_else_002.mp4; Table R4) had unanimous 8/8 Normal agreement and scores of 0.92–0.99, so fine-grained errors about scene norms do pass through both stages.

Revision. Our submitted Limitations (Appendix H) already noted that verification can be affected by "incorrect but highly consistent model predictions, particularly when the underlying model lacks sufficient visual or temporal understanding." The revised PDF adds the audit, the Abnormal/Normal breakdown, and the failure cases (Appendix F.5, Tables R3–R4), expands Appendix H, and lists cross-model verification as future work.

AuthorsOpenReview ↗

Response 2/4

W2: Performance is sensitive to manually selected hyperparameters, and the paper does not explain how they were chosen.

We thank the reviewer for raising this, and agree that the submission should have explained the choice. The sweeps in the appendix were meant to show sensitivity, not to select values, and we did not make this clear. Below we explain how each value was set, show that the default lies in a stable range, and show that the same configuration carries over unchanged to other backbones and to unseen videos.

Q2: Answer.

No labeled data was used to choose them, and one configuration was reused unchanged for all backbones and datasets.

How the values were set. Benchmarks that annotate anomaly labels, temporal intervals, spatial locations and reasoning together are rare. The Vad-Reasoning test set (Huang et al., 2025) is one of the very few, and holding out a labeled part of it for tuning would contradict the label-free setting. We therefore fixed each value once, from what it controls:

ParameterValueRationale
Proposals NN / update group GG8 / 4diverse proposal pool at moderate cost; half of it is used for the update
Majority threshold τmaj\tau_{\text{maj}}0.75a clear majority (6 of 8), without requiring unanimity
Visual threshold τvis\tau_{\text{vis}}0.20a low bar that only rejects weakly supported proposals
λy/λv/λt/λr/λs\lambda_y / \lambda_v / \lambda_t / \lambda_r / \lambda_s1.0 / 0.50 / 0.35 / 0.25 / 0.15task priority
Format weight0.20keeps outputs parseable without dominating the reward
KL / learning rate0.04 / 10−610^{-6}the standard GRPO setting of Shao et al. (2024); one epoch

Using four of the eight proposals for the update keeps forming the consensus separate from reinforcing it, and lets both agreeing and disagreeing trajectories take part in the comparison. The reward weights follow task priority: the label decision first, then visual verification, temporal localization, reasoning and spatial grounding. The thresholds act as quality checks on the proposal rather than as decision thresholds for anomaly classification. The sweeps in Tables 7–11 were run afterwards as sensitivity analyses.

Stability around the default. Moderate changes to these values still improve over the frozen Qwen2.5-VL-7B (Acc 0.761, mIoU 0.567) in both accuracy and mIoU: τmaj=0.50\tau_{\text{maj}}=0.50 (0.822 / 0.619), τmaj=1.00\tau_{\text{maj}}=1.00 (0.768 / 0.596), τvis=0.40\tau_{\text{vis}}=0.40 (0.795 / 0.603) and (N,G)=(4,2)(N,G)=(4,2) (0.804 / 0.608).

The large drops come only from settings that remove a core part of the design, the visual gate, the use of a subset for the update (G<NG<N), or a core reward term, and they all fail in the same way: precision rises while anomaly recall collapses.

ConfigurationPrecRec
Default (N,G)=(8,4)(N,G)=(8,4)0.8690.745
G=8G=8 (Table 7)0.9230.118
No visual gate, τvis=0\tau_{\text{vis}}=0 (Table 8)0.9770.211
No label reward, λy=0\lambda_y=0 (Table 11)0.9300.392
No verification reward, λv=0\lambda_v=0 (Table 11)0.9440.417

This matches our analysis of the accepted proposals, where 34 of the 35 errors were Abnormal videos accepted as Normal: the base model's main error is a bias toward Normal. With G=N=8G=N=8, every trajectory, including all those agreeing with a dominant Normal consensus, enters the update, which strengthens this bias. Over-weighting the secondary terms (e.g. all four weights at 0.50, Table 10) fails in the opposite direction, raising recall at the cost of precision and mIoU. In other words, the components that the default keeps are exactly the ones whose removal causes failure.

AuthorsOpenReview ↗

Response 3/4

Q2 (continued): Answer: Reuse across backbones and transfer to unseen data

Reuse across backbones. The same configuration was applied unchanged to all six backbones in Table 2 (two model families and a task-specific model), and it improved accuracy and mIoU in every case:

BackboneAccmIoU
Qwen2.5-VL-7B0.761 → 0.8290.567 → 0.657
Qwen3-VL-8B0.770 → 0.8360.524 → 0.621
Qwen3.5-4B0.726 → 0.7900.526 → 0.551
Vad-R10.875 → 0.8860.713 → 0.729
InternVL2.5-8B0.703 → 0.7430.417 → 0.482
InternVL3.5-8B0.749 → 0.7630.600 → 0.623

Transfer to unseen data. We adapt once on the unlabeled Vad-Reasoning test set and evaluate the resulting checkpoint, with no further updates or re-tuning, on the entire Vad-Reasoning SFT split (Huang et al., 2025), whose 1,755 videos are never seen during adaptation (Appendix C.2, Table 6). Models trained on this split, such as Vad-R1, are excluded to avoid training-set exposure.

Vad-Reasoning SFT splitAccPrecRecF1mIoU[email protected][email protected][email protected]
Qwen2.5-VL-7B0.7650.7230.8010.7590.5590.6220.5660.515
+ VAD-TTRL0.8170.8480.7380.7880.6480.7210.6620.608

The gains on unseen videos (+5.2 Acc, +8.9 mIoU) closely match those on the adaptation set (+6.8 Acc, +9.0 mIoU), indicating that the configuration does not overfit the videos it was adapted on. The F1 gain comes mainly from precision, with a modest drop in recall, consistent with the Normal bias discussed above. TTRL, TTRV and TTA-Vid similarly report that gains from test-time adaptation carry over to benchmarks not used for adaptation.

Scope. These results support a single reusable default across the backbones and data we evaluated, rather than a universally optimal setting. The revised PDF adds the transfer results on the full SFT split (Appendix C.2), and Appendix H now discusses this sensitivity and lists label-free hyperparameter selection as future work.

AuthorsOpenReview ↗

Response 4/4 (Q3 + Q4)

Q3: Do updates from earlier test videos affect predictions on later videos, and does changing the order change the final performance?

We first clarify our protocol, which follows TTRL (Zuo et al., 2025). Adaptation and evaluation are two separate passes. In the adaptation pass, the model processes the unlabeled Vad-Reasoning test set (Huang et al., 2025) once, so updates from earlier videos do shape the updates that follow. We then freeze the final checkpoint and run inference on the whole test set again from the start. All reported metrics come from this second pass, so no prediction is taken in the middle of adaptation: every video is evaluated by the same final model, regardless of where it appeared in the order.

To test whether the order changes the final result, we repeated the full adaptation pass with a randomly shuffled video order:

OrderAccPrecRecF1mIoU[email protected][email protected][email protected]
Default0.8290.8690.7450.8020.6570.7290.6560.615
Shuffled0.8130.8470.7300.7840.6360.7060.6380.588
Δ\Delta−0.016−0.022−0.015−0.018−0.021−0.023−0.018−0.027

All metrics change by at most 2.7 points, and the shuffled run keeps most of the gain over the frozen Qwen2.5-VL-7B (Acc 0.761 → 0.813, mIoU 0.567 → 0.636). We ran one shuffled order, so we cannot fully separate the effect of order from ordinary run-to-run variation, but the final performance does not vary substantially.

Q4: How large is the additional computational and inference overhead?

Following TTRL, we use test-time reinforcement learning as a one-time, label-free adaptation step, not as a search performed at every inference. Once adapted, VAD-TTRL runs as a standard single-rollout Video-LLM, with no extra modules, multiple rollouts or verification calls at inference time.

One-time adaptation cost. All additional computation is confined to a single pass over the Vad-Reasoning test set: 24.02 GPU-hours in total (24.62 s wall-clock per video on 8×A100 GPUs, about 197 GPU-seconds per video). For each video, this pass generates 8 proposals, runs up to 12 short verification passes (each view is scored under two answer orders), and computes log-probabilities for the 4 sampled trajectories before the GRPO update. By comparison, the supervised Vad-R1 requires 128 GPU-hours (4×A100, 32 h) on annotated data, whereas VAD-TTRL starts from the frozen Qwen2.5-VL-7B and uses no labels.

Zero inference-time overhead. On identical hardware (one RTX 3090, 24 GB) and vLLM settings, VAD-TTRL has practically the same latency as the frozen baseline and Vad-R1, with the same peak memory:

Qwen2.5-VL-7B (frozen)Vad-R1VAD-TTRL
Labels requirednoneSFT + RL annotationsnone
Training / adaptation (GPU-h)0128 (4×A100, 32 h)24.02 (8×A100, 3.0 h)
Inference (s/video), mean / median6.02 / 5.34~6.02 / 5.30~6.01 / 5.32
Peak inference memory (GB)161616

This comparison has been added to Appendix B.2 (Table R1).

We hope these clarifications and new results address your concerns, and we would be grateful if you would take them into account in your assessment. We are happy to provide any further details.

Comments on the paper

2 comments

Dear Reviewer,

Thank you for your review. We have addressed your concerns in our rebuttal and revised manuscript. We would appreciate it if you could reconsider your assessment and revise your overall rating in light of our response.

With the rebuttal discussion closing in about an hour, we would greatly appreciate the opportunity to have at least one interaction with you before the deadline, as we have not yet received any feedback on our responses. We hope to hear your thoughts and address any remaining concerns.

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

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