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Paper summary
This paper proposes MURL, a reinforcement learning-based framework for visual memory management in streaming video understanding. It introduces a lightweight token selector and a history gate to preserve informative visual tokens across repeated memory compression steps. The policy is trained using caption-based rewards from a frozen vision-language backbone. Experiments with Qwen3.5-4B and Qwen3.5-9B on three video understanding benchmarks demonstrate consistent, though generally modest, improvements over adapted memory compression baselines.
Critical strengths
S1. Practical and relevant problem formulation. The paper addresses the important problem of maintaining bounded visual memory under continuous video input. Optimizing token retention across successive, irreversible memory updates is more relevant to streaming applications than one-shot video compression.
S2. Consistent experimental results and reasonable efficiency. The method is evaluated on two backbone sizes and three benchmarks, with additional ablations and efficiency measurements. MURL consistently outperforms the adapted memory baselines in aggregate performance, and Table 7 reports lower memory-maintenance latency than FluxMem and QueryStream.
Critical weaknesses
W1. Limited performance gains and insufficiently controlled baseline comparisons. Although MURL achieves the best aggregate scores within the adapted memory comparison groups, the improvements are generally marginal. For Qwen3.5-9B, the gains over the strongest competing memory baselines are only 0.56, 0.16, and 0.79 percentage points on Video-MME, StreamingBench, and OVO-Bench, respectively. No statistical variance or confidence intervals are reported. More importantly, Appendix A.4 reveals substantial modifications to the competing methods. FluxMem does not follow the same irreversible recursive compression procedure, QueryStream's original thresholding is replaced with Top-K selection, and StreamForest's full hierarchical event memory is not implemented. Matching token counts at query time does not fully establish comparable online memory constraints. Consequently, the results do not conclusively demonstrate superiority over the original methods.
W2. Insufficient isolation and validation of the core methodological contributions. The proposed reinforcement learning-based token selection builds on existing ideas, while the independent benefits of recursive compression training and the history gate are not convincingly established. In Table 3, the single-compression baseline also disables the history gate, introducing a confounding factor. Comparing the no-gate results in Tables 2 and 3 shows that repeated compression training does not consistently improve performance across benchmarks: StreamingBench decreases from 81.68 to 81.32, while OVO-Bench improves only from 58.74 to 58.80.
Furthermore, training simulates only 1–4 compression events, without directly analyzing performance degradation over substantially longer sequences of memory updates. This weakens the evidence supporting the claimed long-term recursive memory advantages.
Questions for authors
Q1. Can the authors clarify how the adaptations of FluxMem, QueryStream, and StreamForest affect their original performance? Can comparisons under consistent online memory constraints be provided? Q2. Can the authors provide a controlled ablation that independently evaluates repeated-compression training and the history gate? How do they explain the inconsistent gains of repeated compression without the gate across benchmarks? Q3. How does performance vary with the number of memory compression steps, particularly for questions requiring information from early video segments? Q4. Given the relatively small performance improvements, can the authors provide statistical uncertainty estimates and end-to-end inference efficiency measurements?
3 comments
Response to Reviewer RqCb (Part 2)
Q3:How does performance vary with the number of memory compression steps, particularly for questions requiring information from early video segments?
We thank the reviewer for the question. To examine how accuracy varies with the number of compression rounds, we grouped Video-MME questions by the number of rounds MURL performed on each video and compared MURL with the 128-frame baseline on the same questions.
| MURL compression rounds | Questions | Base-128f (%) | MURL (%) |
|---|---|---|---|
| 0 | 897 | 83.28 | 81.72 |
| 1–2 | 12 | 75.00 | 83.33 |
| 3–5 | 363 | 73.83 | 72.45 |
| 6–10 | 435 | 68.97 | 70.34 |
| 11–20 | 93 | 64.52 | 70.97 |
| >20 | 900 | 60.11 | 60.78 |
| Overall | 2,700 | 71.30 | 71.30 |
The accuracy gap showed no consistent trend as the number of rounds increased. Even after more than 20 rounds, MURL scored 60.78% versus 60.11% for Base-128f across 900 questions. The baseline’s advantage in the zero-round group likely reflects its denser sampling of these short videos. These results suggest that combining the history gate with training that simulates 1–4 compression rounds allows MURL to generalize to more compression rounds at inference time.
Current datasets do not provide exact evidence timestamps, preventing direct analysis of how evidence-to-query delay affects performance. We therefore randomly selected 700 OVO-Bench samples with at least 300 seconds of video remaining after the original query time. Since the evidence for these questions appears before the original query, postponing the query by 75, 150, 225, or 300 seconds increases the evidence-to-query delay by the corresponding amount. During this interval, MURL continued processing the video and updating its memory. We then measured accuracy at each delay to assess its impact on performance.
| Added query delay | MURL (%) |
|---|---|
| 0 s | 57.14 |
| 75 s | 57.14 |
| 150 s | 57.43 |
| 225 s | 58.00 |
| 300 s | 57.43 |
Accuracy remained between 57.14% and 58.00% across all delays. This suggests that MURL retains earlier evidence through repeated memory updates.
Q4: Given the relatively small performance improvements, can the authors provide statistical uncertainty estimates and end-to-end inference efficiency measurements?
We thank the reviewer for this suggestion. The MURL accuracies reported in Table 1 of the paper are the means of three independent training runs with different random seeds. All runs used the same training configuration and checkpoint-selection rule, and all evaluations used greedy decoding. Below, we report each run’s accuracy alongside the mean and sample standard deviation to show how performance varied across training seeds on each benchmark.
| Training run | Video-MME (%) | StreamingBench (%) | OVO-Bench (%) |
|---|---|---|---|
| Run 1 | 71.19 | 81.90 | 60.03 |
| Run 2 | 71.41 | 81.82 | 60.07 |
| Run 3 | 71.30 | 81.92 | 59.99 |
| Mean ± SD | 71.30 ± 0.11 | 81.88 ± 0.05 | 60.03 ± 0.04 |
We also measured inference efficiency on 200 Video-MME videos using Qwen3.5-9B in BF16 on one NVIDIA H200 GPU, with one warm-up and three timed repetitions per video. All methods compressed memory from 11,520 to 5,760 visual tokens at each update and averaged 21.08 updates per video.
| Method | Visual encoding (s) | Memory updates (s) | Prefill (s) | Query TTFT (s) | Answer generation (s) | End-to-end replay (s) | Throughput (frames/s) |
|---|---|---|---|---|---|---|---|
| MURL | 11.695 | 41.153 | 0.516 | 2.876 | 0.835 | 126.224 | 25.94 |
| FluxMem (adapted) | 11.570 | 80.447 | 0.590 | 2.774 | 0.882 | 164.785 | 15.21 |
| QueryStream (adapted) | 11.261 | 69.062 | 0.474 | 2.499 | 0.735 | 152.817 | 17.40 |
MURL had the lowest cumulative memory-update time (41.153 s), the shortest end-to-end replay time (126.224 s), and the highest streaming throughput (25.94 frames/s). TTFT runs from query-input assembly to the first generated token, with memory already prepared. Answer generation includes prefill, and end-to-end replay covers video decoding through answer generation. Throughput covers visual encoding, position construction, and memory maintenance. We will include both tables and these timing definitions in the revision.
Kind Follow-up on Our Rebuttal
Dear Reviewer RqCb,
Thank you again for your thoughtful feedback. We have provided detailed responses and additional experimental results to address your concerns, and incorporated the key updates into the revised manuscript. With the discussion period drawing to a close, we would be grateful if you could revisit our rebuttal when convenient and let us know whether any points need further clarification. We would welcome the opportunity to address any remaining concerns.
We sincerely appreciate your time and consideration.
Best regards,
The Authors
Response to Reviewer RqCb
We thank the reviewer for recognizing the strengths of our work and for their constructive feedback. Below, we respond to the comments in Weaknesses (W) and Questions (Q).
W1&Q1: Impact of Baseline Adaptations on Performance
We thank the reviewer for raising this concern. Table 1 compares all methods using the same Qwen3.5 backbone, sampled frames, evaluation examples, QA prompts, and decoding settings. We match the visual token count exactly at each query while preserving each baseline’s selection or compression strategy.
QueryStream retains its question-aware importance scores. Top-K selects the highest-scoring tokens under the shared budget, preserving the ranking used by its original threshold rule. The evaluation protocol fixes the answer time, so RTAR’s response scheduling is unnecessary. By “FluxMem does not follow the same irreversible recursive compression procedure,” we mean that, when adapting FluxMem, we followed its original compression strategy more closely instead of applying the repeated, irreversible compression used in MURL. FluxMem retains broader access to past information.
Since it was difficult to preserve StreamForest’s original hierarchical memory updates while matching the visual token budget exactly for every example, we omitted this mechanism from the original comparison. We also evaluated an adaptation that restores hierarchical event memory.
Table 1 thus provides a fair comparison of compression strategies under a shared backbone and query input budget, while preserving QueryStream’s access to the question and FluxMem’s access to the full history.
W2&Q2: Insufficient isolation and validation of the core methodological contributions. We thank the reviewer for pointing this out. We agree that reporting the ablations in two separate tables made the relationship between repeated-compression training and the history gate difficult to see. With the gate disabled, switching from single- to repeated-compression training yielded inconsistent gains across benchmarks. StreamingBench accuracy fell from 81.68% to 81.32%, while OVO-Bench accuracy rose only slightly, from 58.74% to 58.80%. The best results came when we paired repeated-compression training with the history gate. The gate lets each compression step use information about which tokens were important in earlier rounds, and repeated training teaches the model to use that information across successive updates. In the revision, we will present the three settings side by side so readers can see both the effect of switching to repeated training with the gate disabled and the further improvement from enabling the gate.