acceptodds
Under review as a conference paper at ICLR 2027

TraceGate: Routing-Action History for Block Reuse in Video Diffusion

Abstract

Video diffusion transformers repeatedly evaluate costly block stacks and attention routes. Block caching skips stack evaluations; sparse attention reduces work within executed stacks. TraceGate connects these decisions: a planner reuses, repairs, or refreshes query and key clusters on executed calls, and its historical actions inform later residual reuse at the block level. The outer gate combines this delayed feedback with conditioning drift and residual magnitude history; skipped calls do not compute their own attention. A product quantization shortlist reduces planner candidate scoring. Settings focused on efficiency achieve 3.36×, 2.45×, and 3.02× overall speedups on Wan 2.1, Wan 2.2, and HunyuanVideo, respectively, with tradeoffs in task quality. On the Wan 2.1 calibration cohort of 108 videos, the setting with feedback has 0.13 dB higher mean PSNR and 0.003 higher mean SSIM than a retuned setting without feedback; both speedups round to 3.30× and LPIPS is equal at reported precision. This comparison is exploratory because the cohort also informed calibration. Substituting a stale map on 72 selected events tests propagation of inner routing error, not the outer execution versus reuse action.

Primary area:
applications to computer vision, audio, language, and other modalities
Keywords:
video generation, training-free, diffusion transformers

Reviews

Among:
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1234this paper, Top 49%
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_Tf7UOpenReview ↗
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2
Confidence
3
Informativeness
2
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3
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1
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Paper summary

TraceGate nests two known acceleration techniques for video DiTs—outer block-stack residual caching and inner sparse attention with temporal route maintenance—and claims as its contribution a feedback path by which the inner planner's action-history score η modulates later outer reuse decisions. Reported speedups reach 3.36×/2.45×/3.02× on Wan 2.1, Wan 2.2, and HunyuanVideo.

Critical strengths
  1. The observation-timing analysis (conditioning drift observable pre-decision; Q/K routing observable only post-execution) is crisply stated and correctly frames why any feedback must be delayed.

  2. The system-level speedups are substantial and training-free, and the paper is unusually candid about the limits of its own experiments.

Critical weaknesses
  1. The framework optimizes per-layer normalized gradient singular energy without establishing its link to downstream loss. Normalizing per layer discards gradient magnitudes, treating layers with vanishingly small gradients equally to task-critical ones. Furthermore, the theoretical proofs are standard fractional-knapsack/KKT derivations that only guarantee the optimality of this unproven surrogate objective, offering limited theoretical depth.

  2. Applying SVD to the averaged gradient of high-loss samples is methodologically questionable. Per-sample gradient directions can cancel out in the mean, distorting the singular spectrum, and high-loss samples often over-represent outliers. A more principled estimator of the expected gradient spectrum such as the uncentered second moment E[GG⊤]\mathbb{E}[GG^\top] is neither used nor compared against.

  3. Without a random non-uniform allocation baseline (or standard sensitivity baselines), it is unclear whether the gains stem from SEA’s specific scoring or simply from generic non-uniformity. Moreover, in the most practically relevant setting (LoRA), improvements are marginal or tied with baselines, missing standard deviations to verify significance, alongside an unexplained training-time discrepancy (Table 4) under a matched parameter budget.

Questions for authors
  1. Why use the SVD of the mean gradient rather than the second moment E[GG⊤]\mathbb{E}[GG^\top], and why normalize energy per layer instead of weighting by gradient magnitude ∥Gl∥F\|G_l\|_F? Please provide ablations comparing against both alternatives.
  2. Can you include a random non-uniform rank allocation baseline at a matched budget to prove that SEA's specific ordering drives the performance gains?
  3. Could you report standard deviations for the LoRA benchmarks to establish statistical significance, and clarify why SEA-LoRA is significantly faster per epoch than vanilla LoRA (48m vs. 1h08m in Table 4) despite having the same trainable parameter budget?
1 comment
AuthorsOpenReview ↗

Request for Clarification on Review Scope

Dear Reviewer Tf7U,

Thank you for taking the time to provide this detailed review. We have carefully compared each point with our manuscript and would be grateful for clarification regarding how the reviewed components relate to Submission 4177. Our work focuses on training-free acceleration for video diffusion, specifically stack execution versus cached-residual reuse, sparse-attention routing, and action-history feedback.

Critical Weakness 1. We were unable to identify a component in our manuscript that optimizes per-layer normalized gradient singular energy or analyzes such an objective through fractional-knapsack/KKT derivations. Our method instead controls runtime execution and residual reuse. We would welcome clarification if a particular section or equation was intended.

Critical Weakness 2. Our method does not use SVD of an averaged gradient of high-loss samples, estimate a gradient second moment, or select samples for spectral estimation. The controller uses runtime conditioning, residual, and routing information. We would therefore be grateful to know which component of our method the reviewer had in mind.

Critical Weakness 3. We were unable to locate SEA-specific scoring, random non-uniform rank allocation, LoRA benchmarks, or the corresponding Table 4 training-time comparison in our submission. The relevant controls in our paper concern equal tuning effort and direct execution-versus-residual-reuse decisions.

Question 1. Since our method does not use SVD of mean gradients or normalization of per-layer gradient energy, we are uncertain how the requested comparison with a second-moment estimator applies to our submission.

Question 2. A random non-uniform rank-allocation baseline concerns a rank-allocation setting that our method does not use. The closest matched-budget test in our work compares controller signals and execution decisions under comparable tuning effort and runtime.

Question 3. We were unable to identify the reported LoRA standard deviations, SEA-LoRA training times, or trainable-parameter budget referenced in this question. Consequently, we cannot provide a meaningful explanation for the 48-minute and 1-hour-8-minute values.

If these points refer to a different manuscript, we would greatly appreciate confirmation. If any point does correspond to Submission 4177, could you kindly identify the relevant section or equation so that we can provide a precise response?

Thank you again for your time and assistance.

Reviewer_TMBmOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

TraceGate combines residual reuse of an entire DiT stack with an inner sparse-attention planner. Its central proposal is to feed the planner’s historical reuse/repair/refresh actions into subsequent decisions about whether to execute the stack. The method reports acceleration across three video-generation backbones, with component ablations and feedback controls on Wan 2.1.

Critical strengths
  1. The method observes that routing information becomes available only after a stack is executed, which motivates using past routing actions to guide future block-reuse decisions.
  2. The system demonstrates useful quality (Q)–efficiency (F) tradeoffs across three backbones.
  3. The paper carefully qualifies its evidence, including calibration-set reuse, rounded speed matching, and the limited scope of the stale-route intervention.
Critical weaknesses
  1. Lack of validation. Main evidence for routing feedback is the matched-speed comparison in Tab. 3, a gain of 0.13 dB PSNR and 0.003 SSIM, w/ unchanged LPIPS at the reported precision. However, the same 108 videos were used for calibration and evaluation, and no uncertainty estimates are provided for the paired differences. This leaves the paper’s central claim without a convincing test on unseen data.
  2. The hyperparameter choices are insufficiently justified. Tab. 1 uses backbone-specific settings without testing transfer, while Tab. 3 compares a full method selected from 18 configurations over seven parameters against a control tuned over only four threshold pairs. These choices and the unequal tuning budgets remain unclear, making it difficult to separate the benefit of feedback from parameter selection.
  3. Sec. 4.5 compares current and stale routing maps while executing the stack in both cases. This shows the effect of stale routing but does not test whether feedback improves the choice between stack execution and residual reuse. A direct intervention on execution versus residual reuse is needed to support that connection.
  4. The novelty of this work is limited. All the techs are proposed by the other published works. e.g., SADA [1], Turbo4dGen [2], etc.

[1] Ting Jiang et al. SADA: Stability-guided Adaptive Diffusion Acceleration, ICML'25;
[2] Yuanbin Man et al., Turbo4DGen: Ultra-Fast Acceleration for 4D Generation, ICML'26;

Questions for authors
  1. With all settings frozen, does the matched-latency feedback gain persist on an independent evaluation cohort? Please report unrounded runtimes and paired uncertainty estimates.
  2. How does routing-action history compare with cache age, timestep, reuse streak, and historical Q/K drift under comparable tuning budgets?
  3. Does the feedback mechanism improve task-level quality at matched latency, and does its benefit extend beyond Wan 2.1?
12 comments
AuthorsOpenReview ↗

Response to W1: Independent feedback validation and uncertainty

Thank you for your attention to the adequacy of the validation of feedback gains. We further clarify the relationship between the calibration and main-result evaluation cohorts, and provide paired evaluation with confidence intervals on 76 additional TIP-Eval inputs that did not participate in calibration, using frozen configurations.

1. The 108 inputs are used for calibration and ablation, while the main results use a separate evaluation cohort.

Section 4.1 and Table 7 in Appendix A.3 explain that the 108 Wan 2.1 inputs are used for calibration, component ablations, and the feedback comparison in Table 3, separately from the main-result evaluation cohort in Table 1. The expanded I2V task-quality evaluation uses 355 input pairs. To examine whether the feedback gain in Table 3 persists beyond the calibration cohort, we added the independent frozen-configuration evaluation described in Point 2.

Table A. Relationship between calibration, main-result evaluation, and the additional independent evaluation

StageInput cohortPurposeResult location
Calibration and ablation108 Wan 2.1 inputsParameter calibration, component ablations, and feedback comparisonOriginal Table 3 and Table 7 in Appendix A.3
Main-result evaluationA cohort separate from the 108 inputs above; the expanded I2V task-quality evaluation uses 355 input pairsReport the overall performance of the selected configurationsOriginal Table 1 and task-quality results in the appendix
Additional independent evaluation76 inputs that do not overlap with the 108 calibration inputs aboveTest the feedback gain with frozen configurationsTable B in this response

2. Regarding the use of the same inputs for calibration and the feedback comparison: the feedback gain is reproduced in independent evaluation with frozen configurations.

We froze the selected full-feedback and retuned no-feedback configurations and performed a paired comparison on 76 independent inputs that do not overlap with the 108 calibration inputs above. Both groups use the same inputs, generation seeds, sampler, and dense reference. The results are reported in Table B.

Table B. Additional frozen-configuration evaluation: 76 pairs of inputs not used for calibration

MetricFull feedbackRetuned no feedbackMean paired differencePaired 95% CI
Time (s) ↓461.8462.2−0.4[−0.85, +0.05]
PSNR (dB) ↑23.44521.380+2.065[+1.930, +2.200]
SSIM ↑0.77750.6260+0.1515[+0.1448, +0.1582]
LPIPS ↓0.13650.1472−0.0107[−0.0115, −0.0099]

3. Regarding the lack of paired uncertainty estimates: the additional independent evaluation reports the means and 95% confidence intervals of per-input paired differences.

We calculate “full feedback minus retuned no feedback” for each input and use the input as the statistical unit to compute two-sided paired tt confidence intervals from all 76 paired records. As shown in Table B, the mean paired differences in PSNR, SSIM, and LPIPS are +2.065 dB, +0.1515, and −0.0107, respectively, and all three intervals support improvement. The mean runtimes of the two groups are 461.8 seconds and 462.2 seconds, respectively.

These results provide independent evidence that the feedback gain persists on inputs not used for calibration: the frozen full-feedback configuration achieves better mean fidelity at a similar mean runtime.

AuthorsOpenReview ↗

Response to Q1: Frozen-configuration feedback gains

Thank you for your question about independent validation and paired uncertainty.

Yes, with all settings frozen, the feedback gain persists on 76 independent inputs that were not used for calibration. The results are reported in Table B of our response to W1.

1. Independent evaluation with frozen configurations supports the persistence of the feedback gain.

The full-feedback and retuned no-feedback configurations were selected and frozen before independent evaluation. We then performed a paired comparison on 76 inputs that do not overlap with the 108 calibration inputs. Both groups use the same inputs, generation seeds, sampler, and dense reference, with all configurations held unchanged throughout evaluation. As shown in Table B of our response to W1, full feedback achieves better mean fidelity at a similar mean runtime.

2. Actual runtimes and timing protocol.

For the 76 independent inputs, the full-feedback and retuned no-feedback configurations have mean runtimes of 461.8 s and 462.2 s, respectively, with a mean paired difference of −0.4 s and a paired 95% CI of [−0.85, +0.05] s, as reported in W1, Table B.

Timing includes denoising and VAE decoding and excludes model loading, input preparation outside the pipeline, and MP4 encoding and disk writing. Runtime differences are calculated as “full feedback minus retuned no feedback,” and the two-sided paired tt confidence interval is computed using all 76 paired records, with the input as the statistical unit.

Selected per-input timing records are provided in Table D of our response to Reviewer e4s4, Q1, at the precision retained in the original logs. The mean runtimes here are presented at the displayed precision. These measurements support the comparison of fidelity at similar mean runtime.

3. The paired 95% confidence intervals for all three fidelity metrics support improvement.

In Table B of our response to W1, the mean paired PSNR difference is +2.065 dB, with a 95% CI of [+1.930, +2.200]; the SSIM difference is +0.1515, with an interval of [+0.1448, +0.1582]; and the LPIPS difference is −0.0107, with an interval of [−0.0115, −0.0099].

For each metric, we first calculate “full feedback minus retuned no feedback” per input, then compute two-sided paired tt confidence intervals from all 76 paired records, treating the input as the statistical unit. These results support better mean fidelity from the frozen feedback configuration on independent inputs at a similar mean runtime.

AuthorsOpenReview ↗

Response to W2: Backbone calibration and equal-budget selection

Thank you for your comments on hyperparameter selection and tuning budgets.

Our hyperparameter choices have an explicit calibration basis. We further equalized the outer search opportunities for the feedback and no-feedback groups and evaluated the feedback gain independently after freezing the configurations.

1. Table 1 uses per-backbone calibration to accommodate the operating characteristics of different backbones.

The backbones differ in model architecture, denoising schedules, and generation specifications, so we determine their operating presets separately. Section 4.1 describes the generation settings for each backbone; Tables 6–7 in Appendix A.3 report the parameter scan and TraceGate-F calibration settings for Wan 2.1, while Tables 8–9 in Appendix A.4 provide the quality-preset configurations and results for Wan 2.2 and HunyuanVideo.

All three backbones use the same control procedure with separately calibrated parameters. These results demonstrate the applicability of the method across multiple backbones; transferring the complete parameter configuration unchanged across backbones has not been tested.

2. The original configuration scan determined the system operating settings, while no-feedback threshold retuning constructed a feedback ablation at a comparable cost.

Appendix A.3 reports an 18-configuration scan involving seven parameters and separately lists the TraceGate-F configuration and results in Tables 6–7; the original Table 3 uses this full-feedback configuration. After disabling feedback, we kept the inner planner, PQ configuration, protected calls, and reuse cap unchanged and retuned only the two outer thresholds to match the reported speedup of the full-feedback group. Table 14 in Appendix C.1 records the results for four threshold pairs, from which (τr,τm)=(0.11,0.07)(\tau_r,\tau_m)=(0.11,0.07) was selected. Both groups have a reported speedup of 3.30×3.30\times.

This design preserves the same inner components while allowing the no-feedback controller to adjust its speed–fidelity trade-off. Table 15 in Appendix C.2 additionally toggles feedback at four fixed threshold pairs, showing improved fidelity together with increased runtime in all four comparisons. To address the difference in search opportunities between the two groups, we added the following equal-budget experiment.

3. The additional equal-budget search selects the original configurations again, and the feedback gain is reproduced in independent evaluation.

We fixed the inner planner, PQ configuration, protected calls, and reuse cap. On the same 108 calibration inputs, the feedback and no-feedback groups used the same outer-threshold grid, each evaluating 12 candidates, for 24 candidates in total.

Table C1. Additional equal-budget search: the outer-threshold grid shared by both groups

Groupτr\tau_r candidatesτm\tau_m candidatesNumber of candidatesFixed λ\lambdaFixed ηmin⁡\eta_{\min}
Full feedback0.11, 0.16, 0.20, 0.240.07, 0.10, 0.12120.200.05
Retuned no feedback0.11, 0.16, 0.20, 0.240.07, 0.10, 0.121200

The no-feedback group disables both soft feedback and the low-stability veto. Both groups search only (τr,τm)(\tau_r,\tau_m) in this experiment. They use a common runtime window of 462.0 seconds ±1% and select the configuration with the highest mean PSNR within that window. Ties are resolved first by proximity to the target runtime and then by a predetermined candidate order.

Table C2. Configurations selected by the equal-budget search

GroupSelected (τr,τm)(\tau_r,\tau_m)Correspondence to the original Table 3
Full feedback(0.20,0.12)(0.20,0.12)Matches the original full-feedback configuration
Retuned no feedback(0.11,0.07)(0.11,0.07)Matches the original retuned no-feedback configuration

The additional search selects the same two configurations as the original Table 3, with all other settings matching their respective original configurations. After selection, all settings are held fixed for paired evaluation on 76 independent inputs that do not overlap with the calibration inputs. Both groups use the same inputs, generation seeds, sampler, and dense reference. The results are reported in Table B of our response to W1.

The mean runtimes are 461.8 seconds and 462.2 seconds, respectively. The mean paired differences for full feedback in PSNR, SSIM, and LPIPS are +2.065 dB, +0.1515, and −0.0107, respectively, and all three paired 95% confidence intervals support improvement. These results show that the feedback gain persists on independent inputs under shared inner settings, equal outer-threshold search opportunities, and similar mean runtimes, further separating the effect of feedback from that of outer-parameter search opportunities.

Reviewer_e4s4OpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

TraceGate is a training-free framework that combines residual reuse across denoising calls with sparse attention within executed Transformer stacks. Its main contribution is a delayed feedback path: an inner planner maintains query/key clustering through reuse, repair, or refresh actions, and a summary of these actions informs subsequent decisions to reuse the entire stack residual. The outer controller combines this historical signal with conditioning drift and residual magnitude history. A product-quantization shortlist supports cluster selection. Experiments on Wan 2.1, Wan 2.2, and HunyuanVideo report end-to-end speedups of 3.36×, 2.45×, and 3.02× for efficiency-oriented configurations, with quality–latency tradeoffs. Additional experiments examine component contributions, feedback at matched reported speed, and the downstream effects of substituting stale routing maps.

Critical strengths
  1. The paper explicitly connects the maintenance history of an inner sparse-attention planner to subsequent outer residual-reuse decisions. It distinguishes information available before execution from current Q/K tensors and residuals that become available only after execution (Section 3 and Algorithm 1). Consequently, skipped calls do not need to compute the attention states they are intended to avoid. This is a technically coherent connection between temporal caching and sparse attention, with the potential to exploit information already produced by the planner at low additional cost.

  2. The evaluation covers both image-to-video and text-to-video generation and reports quality-oriented as well as efficiency-oriented configurations (Table 1). On the Wan 2.1 ablation cohort, adding outer residual reuse to the inner planner increases speedup from 2.04× to 3.30×, corresponding to a 38.2% reduction in normalized latency, while PSNR changes from 23.71 to 23.51 dB (Table 2). These measurements establish practical value for the integrated system. The manuscript also carefully distinguishes dense-reference fidelity from task quality and attention-pair workload from measured latency, which helps keep the empirical interpretation appropriately scoped.

Critical weaknesses
  1. The most relevant comparison in Table 3 reports a 0.13 dB PSNR improvement and a 0.003 SSIM improvement, with unchanged LPIPS at the reported precision, over a retuned no-feedback controller. However, this comparison uses the same 108-video cohort that informed calibration, and the speedups are matched only at the displayed precision of 3.30×. The full configuration was selected from an 18-configuration scan involving seven parameters, whereas the recorded no-feedback retuning covers four pairs of outer thresholds. Without independent evaluation and uncertainty estimates for the paired differences, it is difficult to determine whether the observed advantage is stable or sensitive to configuration selection. Moreover, the experiments do not establish whether the action-history score provides useful information beyond simpler historical signals such as cache age or recently observed Q/K drift. The 72-event stale-map intervention is informative about inner routing error, but both intervention arms execute the stack, so it does not directly validate the outer execution-versus-residual-reuse decision. The authors acknowledge these limitations; nevertheless, they leave the paper’s most distinctive contribution empirically preliminary despite the useful system-level results.

  2. Appendix A.2 explicitly identifies essential details that must still be obtained from the actual runs, including the repair weight β, the fitted polynomial coefficients, the conditioning-reference update rule, and the residual-ratio prior. Exact protected-call definitions and complete backbone execution presets are also needed. These choices directly determine the stability score, accumulated risks, and execution/reuse trajectory; they are not peripheral implementation details. For example, changing the reference-update convention while retaining the same polynomial and thresholds changes the controller. The current description therefore does not fully support independent reconstruction of the main operating points or the feedback comparison. This concern is addressable, but it materially limits the reproducibility and interpretation of the reported contribution.

Questions for authors
  1. For the comparison in Table 3, please clarify the exact configuration-selection protocol and provide the unrounded wall-clock measurements and per-video paired fidelity differences, with uncertainty estimates. Were the selected configurations evaluated without further tuning on any samples outside the 108-video calibration cohort? If such results are unavailable, a limited held-out comparison of these two frozen configurations would directly address my main concern about the stability of the reported feedback gain.

  2. What evidence indicates that η improves outer reuse decisions beyond simpler historical variables such as cache age, denoising timestep, or the most recently observed Q/K drift? An analysis of existing traces or a controlled comparison with one such substitute signal, under comparable latency and tuning effort, would help establish the specific value of planner-action feedback. A direct comparison of stack execution and cached-residual reuse from the same pre-intervention latent state would also be relevant, since the current stale-map experiment changes the route while executing the stack in both arms.

  3. Could you provide the exact β value, polynomial coefficients, conditioning-reference update rule, residual-ratio prior, protected-call definitions, and backbone presets used for the main results and feedback controls? If these are available in submitted code or supplementary files, please identify their locations. These details are necessary to determine whether the stated equations and thresholds reproduce the evaluated execution decisions.

  4. The observed ratio ρ_k = ‖r_k‖₂ / (‖r_a‖₂ + ε) is measured between executed calls whose separation k − a can vary, whereas Equation (8) applies the effective ratio once per proposed reuse call. Is the observed ratio normalized by the execution interval or the change in noise level before it enters the online estimate? Please clarify how the online estimate and timestep prior are made consistent with these variable intervals.

11 comments
AuthorsOpenReview ↗

Response to W1 (1/3): Independent evaluation and equal-budget tuning

Thank you for your detailed comments on feedback validation.

1. The 108 inputs are used for calibration and ablations; the main results use a separate evaluation cohort.

Section 4.1 and Appendix A.3, Table 7, specify that the 108 Wan 2.1 inputs are used for calibration, component ablations, and the feedback controls in Table 3, separately from the main evaluation cohort in Table 1. The expanded I2V task-quality evaluation uses 355 input pairs. To test whether the feedback gain in Table 3 persists beyond the calibration cohort, we added the frozen-configuration independent evaluation described in Point 2.

2. The additional equal-budget search selects the original configurations, and the feedback gain persists on independent inputs.

In this additional experiment, we fix the inner planner, PQ configuration, protected calls, and reuse cap. The feedback and no-feedback groups share the following grid, with 12 candidates per group and 24 candidates in total:

\tau_m\in\{0.07,0.10,0.12\}.$$ The feedback group fixes $\lambda=0.20$ and $\eta_{\min}=0.05$; the no-feedback group sets both to zero. All candidates are evaluated on the same 108 calibration inputs. We select the configuration with the highest mean PSNR within a runtime window of 462.0 seconds ±1%. Ties are resolved first by proximity to the target runtime and then by a predetermined candidate order. The search selects the same two configurations as the original Table 3: $(\tau_r,\tau_m)=(0.20,0.12)$ with feedback and $(0.11,0.07)$ without feedback, with the remaining settings unchanged. We then freeze both configurations and conduct a paired evaluation on 76 TIP-Eval inputs that do not overlap with the calibration inputs, without further parameter search. Table A shows higher mean fidelity across all three metrics at similar mean runtimes, with paired 95% confidence intervals supporting improvement. Both groups use identical inputs, generation seeds, samplers, and dense references. Timing includes denoising and VAE decoding, but excludes model loading, input preparation outside the pipeline, and MP4 encoding and disk writing. **Table A. Frozen-configuration evaluation after equal-budget selection: 76 pairs of inputs not used for calibration.** | Metric | Full feedback | Retuned no feedback | Mean paired difference | Paired 95% CI | | --- | --- | --- | --- | --- | | Time (s) ↓ | 461.817 | 462.219 | −0.402 | [−0.85, +0.05] | | PSNR (dB) ↑ | 23.445 | 21.380 | +2.065 | [+1.930, +2.200] | | SSIM ↑ | 0.7775 | 0.6260 | +0.1515 | [+0.1448, +0.1582] | | LPIPS ↓ | 0.1365 | 0.1472 | −0.0107 | [−0.0115, −0.0099] | Paired differences are computed per input as “full feedback minus retuned no feedback.” The 95% confidence intervals use a two-sided paired $t$ procedure.
AuthorsOpenReview ↗

Response to W1 (2/3): Historical-signal comparisons

3. Action history outperforms simpler historical signals under equal tuning budgets and similar runtimes.

We compare action history η\eta, cache age/reuse streak, the denoising-position lookup, and historical Q/K drift. All four signals use the same outer-threshold grid on the same 108 calibration inputs, with 12 combinations per signal and 48 candidates in total:

τr∈{0.11,0.16,0.20,0.24},τm∈{0.07,0.10,0.12}.\tau_r\in\{0.11,0.16,0.20,0.24\},\qquad \tau_m\in\{0.07,0.10,0.12\}.

The four groups use the same gating structure, with all other control parameters, the inner planner, PQ configuration, protected calls, and reuse cap held constant. Each group follows the same selection rule: select the configuration with the highest mean PSNR within a calibration runtime window of 462.0 seconds ±1%. Ties are resolved first by proximity to the target runtime and then by a predetermined candidate order.

The selected (τr,τm)(\tau_r,\tau_m) values are (0.20,0.12)(0.20,0.12) for action history, (0.16,0.12)(0.16,0.12) for historical Q/K drift, (0.20,0.07)(0.20,0.07) for the denoising-position lookup, and (0.16,0.12)(0.16,0.12) for cache age/reuse streak.

After selecting a configuration for each signal, we freeze all settings and conduct paired evaluation on the same 76 inputs from a different dataset, TIP-Eval. All four groups use identical inputs, generation seeds, sampler, and dense reference.

Signal mapping. The three substitute signals are mapped to stability scores, with larger values favoring reuse. Cache age uses

zkage=1−min⁡(Ak/K,1),z_k^{\mathrm{age}}=1-\min(A_k/K,1),

where AkA_k counts consecutive reuse calls within the same CFG branch and resets after stack execution; the proposed reuse length is Ak+1A_k+1. Cache age and reuse streak therefore coincide under this counting convention and are reported together.

Historical Q/K drift uses

zkQK=1−clip⁡(da/dscale,0,1),z_k^{\mathrm{QK}}=1-\operatorname{clip}(d_a/d_{\mathrm{scale}},0,1),

where dad_a is the aggregated drift saved at the most recent stack execution, and dscale>0d_{\mathrm{scale}}>0 is the 95th percentile of calibration drift values.

The denoising-position lookup uses

zkstep=Lb(j),Lb(j)=mean⁡i∈Cb,jηhist(i,b)(j).z_k^{\mathrm{step}}=L_b(j),\qquad L_b(j)=\operatorname{mean}_{i\in\mathcal C_{b,j}} \eta_{\mathrm{hist}}^{(i,b)}(j).

For each CFG branch bb and denoising position jj, the table stores the mean valid historical action score across calibration trajectories. Evaluation reads the fixed entry for the current branch and position. The mapping scale and lookup table are fixed before independent evaluation. Each substitute score replaces the historical score in Equations (7) and (11) of the main text.

Table B1. Outer-signal comparison after equal-budget tuning: frozen-configuration evaluation on 76 TIP-Eval inputs

Outer gating signalMean time (s) ↓PSNR (dB) ↑SSIM ↑LPIPS ↓
Cache age / reuse streak462.021.2550.64370.1484
Denoising-position lookup462.221.2150.65290.1488
Historical Q/K drift462.021.3850.65450.1460
Planner-action history η\eta461.823.4450.77750.1365

Paired comparison with historical Q/K. Historical Q/K drift has the best mean fidelity on all three metrics among the simpler baselines above. Table B2 reports per-input differences calculated as “η\eta minus historical Q/K,” with 95% confidence intervals computed using the two-sided paired tt method.

Table B2. Mean paired differences and uncertainty for η\eta relative to historical Q/K

MetricMean paired differencePaired 95% CI
Time (s)−0.20[−0.75, +0.35]
PSNR (dB)+2.060[+1.923, +2.197]
SSIM+0.1230[+0.11614, +0.12986]
LPIPS−0.0095[−0.01064, −0.00836]

Tables B1 and B2 show that η\eta improves all three fidelity metrics over historical Q/K drift at similar mean runtime, with paired confidence intervals supporting each improvement.

Equation (4) in Section 3.2 defines the planner’s Q/K drift, while Equation (5) aggregates its actual reuse, repair, and refresh actions into η\eta. Equations (7) and (11) in Section 3.3 use this history for subsequent outer gating. The comparison supports the value of this maintenance history for outer reuse decisions.

AuthorsOpenReview ↗

Response to W1 (3/3): Direct execution-versus-reuse interventions

4. The additional action intervention directly compares stack execution with cached-residual reuse.

Across the 76 independent inputs, we select calls where the planner-action-history η\eta and historical Q/K controllers disagree along trajectories generated by the frozen full-feedback policy. Eligible calls have valid caches and historical information for the current branch, lie outside the protected-call set, and have a proposed consecutive reuse length no greater than KK. Both controllers use their respective calibrated and frozen configurations to make decisions from the same pre-gating state.

Events are selected before the intervention rollouts. For each event, we duplicate the same hidden state, caches, planner history, and random-number-generator state, then force stack execution in one branch and cached-residual reuse in the other. Both branches continue to the final video under the same frozen full-feedback policy used for the η\eta group in Table B1, making subsequent decisions according to their respective states. Final-video PSNR is measured against the same dense reference. This experiment therefore measures the total downstream effect of changing the current outer action.

Table C. Outer-action intervention from identical states.

Decision disagreementEvents / distinct videosStack execution PSNR (dB) ↑Residual reuse PSNR (dB) ↑Mean execution gain
η\eta selects execution; historical Q/K selects reuse32 / 2423.6022.60+1.00 dB
η\eta selects reuse; historical Q/K selects execution27 / 2123.5423.50+0.04 dB

As shown in Table C, among the tested disagreement events, execution improves mean PSNR over reuse by 1.00 dB when η\eta selects execution, compared with 0.04 dB when η\eta selects reuse. These results support the ability of action history to distinguish calls with different execution benefits and prioritize stack execution where the benefit is greater.

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