acceptodds
Under review as a conference paper at ICLR 2027

Triangular Resampling for Long-Horizon Motion Generation

Abstract

We introduce Triangular Resampling (TR), a post-training method for mitigating long-horizon error accumulation in motion diffusion models. TR builds on FloodDiffusion, which generates motion using a triangular denoising schedule. During training, the current model observes short, ground-truth-derived motion windows, whereas long-horizon inference repeatedly conditions on its own predictions, allowing errors to accumulate. A common remedy is to expose the model to its own rollouts during training. However, replacing only completed motion history does not capture the evolving, partially denoised states within a triangular denoising window. To address this mismatch, TR introduces a key design that extends rollout-based training to the entire active window, including partially denoised states. This exposes training to model-induced errors, but unrestricted rollout can also move the training states away from their paired ground-truth motion. We therefore introduce a denoising threshold to retain ground-truth anchoring while controlling the transition to model-generated rollouts. For each replayed training sample, TR draws a shared threshold and replays the multi-step triangular denoising trajectory without gradient tracking. After each update, states below the threshold are replaced with noise-matched ground truth, while states at or above it retain model predictions. The resulting latent window is then used in the standard forward pass, loss computation, and gradient update. This rollout construction supports both the original supervised objective (TR) and distribution matching (TR-DMD). We evaluate 120-second motion generation on HumanML3D test prompts. TR and TR-DMD achieve state-of-the-art FID AUC within their respective non-DMD and DMD comparison groups. Specifically, supervised TR reduces FID AUC by 40.9% and FID degradation slope by 55.3% relative to matched post-training without replay.

Primary area:
applications to computer vision, audio, language, and other modalities
Keywords:
long-horizon motion generation, noisy history, error accumulation, diffusion forcing

Reviews

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1234this paper, Bottom 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.25 over 4 reviews, above 49% of the others.
Reviewer_4qeEOpenReview ↗
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Paper summary

This paper proposes Triangular Resampling (TR), a post-training method for reducing error accumulation in long-horizon motion generation. It replays FloodDiffusion’s triangular denoising trajectory, including partially denoised states, and uses a shared random threshold to control the transition from noise-matched ground-truth anchoring to model-generated states.

Critical strengths
  1. The method is relatively simple, and its description is generally clear. The equations and illustrations make the replay and clamping procedures understandable.
  2. Supervised TR provides a substantial improvement over the matched TR-off baseline.
  3. The paper includes useful ablations and transparently acknowledges several limitations, including the lack of additional FID improvement from DMD over its supervised initialization.
Critical weaknesses
  1. Limited methodological novelty. Rollout-based training is already an established idea. Although TR combines rollout-based training with ground-truth anchoring, its contribution appears to be a relatively incremental adaptation to FloodDiffusion. The experiments emphasize parameter selection more than establishing broader insights.

  2. Hyperparameter sensitivity. Several settings of ss in Table 2 yield worse FID AUC than TR-off, suggesting that achieving gains with the method requires careful hyperparameter tuning.

  3. Limited evidence of generality. The method is closely tied to triangular denoising and is evaluated only on FloodDiffusion. Its effectiveness across other backbones or denoising schedules remains unverified, limiting the evidence for a broadly applicable contribution.

  4. Unconvincing overall benefit of TR-DMD. Rolling Forcing outperforms TR-DMD on five of the six metrics in Table 1. TR-DMD’s sole advantage, FID AUC, is small (1.324 versus 1.351), with overlapping confidence intervals. This raises concerns about whether TR offers a sufficiently compelling benefit when combined with DMD.

Questions for authors
  1. What motivates applying GT anchoring at high noise levels and retaining model rollouts at low noise levels? Could the authors compare this with a reversed allocation, or with randomly selecting a matched number of clamping steps within each token’s denoising trajectory? The latter differs from Random-position clamping, which matches the clamp count across positions at each Euler step.

  2. Why is the release threshold stochastic rather than deterministic? The shift sweep changes the threshold distribution but does not isolate the benefit of randomness. A fixed-threshold comparison with matched average clamping strength would clarify this choice.

  3. Although Table 2’s caption explains the convention, boldfacing an entire row can suggest that every metric in that row is optimal. Shading the selected row and reserving boldface for column-wise best values would be clearer.

3 comments

We thank Reviewer 4qeE for their careful review and helpful suggestions. Our responses are provided below.

[W1/W2]

Our contribution lies in identifying and addressing the state mismatch within the active window of triangular denoising, extending model replay to partially denoised states, and controlling their deviation through progressively released ground-truth (GT) anchoring. Table 2 shows both the effects of the parameters and the limits of the mechanism: fully self-generated rollouts substantially degrade performance, whereas moderate anchoring restores generation quality. We acknowledge the sensitivity to the threshold. At the same time, with s=0.6s=0.6 fixed, all three tested replay ratios outperform TR-off, indicating that the gains are not confined to a single ratio. Compared with the matched baseline, our main configuration reduces FID AUC and the degradation slope by 40.9% and 55.3%, respectively, demonstrating the effectiveness of our method.

[W3]

This paper focuses on the training–inference mismatch in triangular denoising, as explicitly stated in the second paragraph of the Introduction. Specifically, TR addresses model prediction errors accumulated in partially denoised states within the window. With the same backbone, initialization, and 30,000 post-training updates, TR reduces FID AUC by 40.9% relative to the baseline without TR, supporting its effectiveness in the current setting. The schedule construction also offers a natural route to extending the method to chunk-based diffusion: the generation unit can be expanded from a single latent to a chunk, with all latents within a chunk sharing the same denoising progress. When the active denoising window contains only one chunk, this schedule corresponds to an autoregressive diffusion process that completes denoising one chunk at a time. Thus, TR's trajectory replay and ground-truth clamping could potentially be extended to this setting, although their effectiveness would still require experimental validation. We have explicitly identified extensions to other backbones and denoising schedules as future work in the Conclusions, and we thank the reviewer for highlighting this important direction.

[W4]

TR-DMD is an extension introduced to enable comparisons with DMD-based methods and verify compatibility. We agree that its gap over Rolling Forcing is insufficient to establish a significant advantage, and that there are differences in initialization and chunking (please refer to our response to Reviewer 5cQG’s Q1 for details). Supervised TR still achieves the best FID AUC, reducing it by 14.7% relative to Rolling Forcing, and receives higher ratings for motion quality and text alignment in the blind evaluation. We have expanded the discussion in Section 5.2 (p. 8) to explicitly acknowledge the small FID AUC gap and overlapping confidence intervals, as well as Rolling Forcing’s stronger results on the other five reported metrics. The revised discussion distinguishes motion distribution fidelity from text alignment and temporal degradation.

[Q1]

Our design is based on the following assumption: at high noise levels, the input contains less discernible motion information, and relying on model rollouts too early may cause the generated trajectory to deviate from the paired ground truth, weakening the consistency between the training states and the supervision targets. We therefore use GT anchoring matched to the current noise level at this stage to limit excessive drift and provide a stable supervision reference for subsequent learning. As denoising progresses, the prescribed diffusion noise gradually decreases. Retaining model rollouts at this point allows the training states to incorporate prediction errors generated and accumulated by the model itself, building on the foundation provided by GT anchoring at earlier stages. The model thereby learns to continue denoising from states containing its own prediction errors, better handling the inputs actually encountered during inference and mitigating the distributional gap between training and inference. This design thus aims to balance reliable supervision with sufficient exposure to model errors: GT anchoring at high noise levels maintains the supervision reference, while model rollouts at low noise levels allow the model to learn to correct its own errors.

[Q2]

The rationale for using a random release threshold is to expose the model during training to different release timings and subsequent rollout lengths. At the same time, a single threshold is shared within each replay to maintain a continuous release boundary. To examine the role of the release structure, we have included a random-position clamping control in Table 2. This control uses the same (γ,s)=(1,0.6)(\gamma,s)=(1,0.6) and maintains exactly the same number of clamped positions as TR at every Euler step, while randomly reassigning which positions are clamped. Compared with this control, TR (the third row) reduces FID AUC from 1.857 to 1.251, supporting the advantage of a continuous release structure when the number of clamped positions is matched.

[Q3]

As stated in the Evaluation Protocol, we use FID AUC as the primary criterion for evaluating overall generation quality and selecting configurations. The other metrics provide complementary information about text alignment and performance trends over time. Therefore, bolding entire rows in Table 2 was intended to identify the configuration selected by FID AUC within each group, rather than to imply that the configuration is optimal across all metrics. We agree that bolding entire rows may cause confusion. We have revised Tables 1 and 2 (pp. 7 and 9) and their captions. Background shading identifies the row with the lowest FID AUC in each group, while boldface and underlining indicate the best and second-best means, respectively, in each metric column within that group, including ties.

Thanks for the response. My main concerns remain, so I stand by my original assessment.

  1. I still see TR as an incremental improvement to FloodDiffusion. The proposed extension to a single chunk is unconvincing. In that setup, all latents in the window share the same denoising progress. The original method uses different denoising levels within the window to decide which tokens to anchor to ground truth and which to leave to the model rollout.

  2. Q1 and Q2 still lack the requested experiments on when to apply ground-truth anchoring and whether a random release threshold helps.

  3. The authors also acknowledge that TR is sensitive to the threshold and that TR-DMD’s advantage over Rolling Forcing is inconclusive.

Reviewer_5cQGOpenReview ↗
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Paper summary

The authors propose Triangular Resampling to overcome exposure bias in long-horizon motion diffusion models. FloodDiffusion generates motion using a triangular sampling schedule but its training exposes the model to ground truth motion and noisy states instead of model's own prediction. During inference, however, the model is exposed to its own predictions and long-horizon generation is prone to error accumulation. To avoid exposure bias, their method extends rollout-based training to entire active window, including partially denoised states in addition to the models denoised states. The authors introduce a denoising threshold to keep ground truth anchoring while controlling the trasition to model-generated rollouts.

Critical strengths

The paper addresses a real problem: FloodDiffusion is trained on "ground-truth-derived" windows but conditions on its own predictions at inference, and errors accumulate over long-horizon rollouts. The authors note that this mismatch also affects the partially denoised tokens in the active window, not just the finished windows. Their fix, exposing the model to its own rollouts during post-training with a ground-truth threshold to limit drift, is simple, easy to add on top of an existing model, and works with both supervised and DMD training.

The supplementary videos show better stable long-horizon motion than FloodDiffusion and Rolling Forcing.

Critical weaknesses

The paper argues that replaying the partially denoised window matters beyond replaying completed history. Eq. 6 is Resampling Forcing’s threshold distribution (same shift, s = 0.6), and Rolling Forcing as published already trains on its own re-noised window states. The new part is therefore ground-truth-clamped replay in a triangular window. That is reasonable, but Table 2 has no clean history-only baseline. The nearest rows (s ≥ 100) score worse than TR-off, so it is unclear what they test.

TR and TR-off start from the official FloodDiffusion checkpoint. The other baselines are adapted and trained from scratch with small budgets, so Table 1 mostly shows that the backbone matters. The informative comparisons are TR vs TR-off and vs Gaussian noise. In the DMD group, TR-DMD vs Rolling Forcing is within the confidence intervals (1.324 ±\pm 0.051 vs 1.351 ±\pm 0.061). Rolling Forcing is better on slope, Matching Distance and R-precision, and the two also differ in initialization and chunking. The “state-of-the-art” claim rests on one metric.

The main configuration was chosen using the reported evaluations (Appendix A), with a single training seed. The ablations are non-monotonic: FID AUC by shift is 2.04, 1.25, 1.92, 1.35, 1.98 for s = 0.3, 0.6, 1, 3, 10, and by ratio 1.15, 1.50, 1.25 for γ\gamma = 0.25, 0.5, 1. This may reflect run-to-run variance.

The 270 judgments are 90 pairs viewed three times, so they are not independent. No annotator count is given, the prompts were hand-picked, and there is no tie option. FloodDiffusion’s own study used 100 participants.

Questions for authors
  • Does your Rolling Forcing adaptation roll through its own re-noised window states, as the published algorithm does? If so, what separates TR-DMD from it beyond the clamp and the initialization?

  • Can you add a history-only replay run on the FloodDiffusion backbone, using Resampling Forcing’s noise-level distribution? Do the s ≥\ge 100 rows already amount to this, and why do they score worse than TR-off (2.78 vs 1.95)? A clear gain would raise my assessment.

  • Were the prompts used to choose the main configuration the same ones used for the final numbers? Can you report more than one training seed for TR-off and TR? I can’t tell whether the 40.9% gain is robust without this.

  • How many annotators took part in the human study, and did the same ones judge all three rounds?

  • Does FID on 10-second windows capture the global trajectory drift shown in Figure 1? If not, can you report a trajectory-level metric?

  • Does TR change FloodDiffusion’s standard HumanML3D results, and how does it behave when the prompt changes mid-stream? A regression would lower my assessment, while no regression would remove a concern.

4 comments

We thank Reviewer 5cQG for their careful review and helpful suggestions. Our responses are provided below.

[W1/Q2]

We have added an experiment with history-only replay. Specifically, after completing replay, we reset the denoising window to the standard FloodDiffusion training configuration while retaining the replayed history. The results are shown below. We have incorporated the history-only replay results into the “Replay scope” group of Table 2 and added the corresponding analysis to Section 5.3 (p. 9). At matched settings, full TR improves FID AUC and all three degradation slopes over history-only replay, while history-only replay has slightly better Matching Distance and R-precision AUCs. Results demonstrate the benefit of incorporating the model's own prediction errors into the denoising window through TR.

MethodFID AUC ↓FID slope ↓Matching Distance AUC ↓Matching Distance slope ↓R-precision AUC ↑R-precision slope ↑
TR-off (Table 1 in the paper)1.951 ± 0.0680.526 ± 0.0703.864 ± 0.0260.399 ± 0.0280.648 ± 0.007−6.837 ± 0.574
History-only replay (γ=1, s=0.6)1.574 ± 0.0850.435 ± 0.1833.777 ± 0.0150.338 ± 0.0550.649 ± 0.011−6.487 ± 1.060
TR (γ=1, s=0.6)1.251 ± 0.0240.376 ± 0.0393.780 ± 0.0140.259 ± 0.0210.646 ± 0.005−4.391 ± 0.492

Relationship between s≥100 and TR-off: Even when s is very large, the history still contains model errors. The clamping condition in the code is α < r. At s=100, the median threshold r is approximately 0.9901: most intermediate states are pulled back to noisy ground truth, but when a token reaches α=1, this condition no longer holds, and the model's final-step prediction is retained. Thus, a large s approximately produces a history that is guided by ground truth throughout the preceding steps and completed by the model at the final step, whereas the history in TR-off comes directly from ground truth. The two are not equivalent. A large s reduces exposure to errors accumulated over the full generation process while retaining a history containing model errors. These changes may make the benefits insufficient to offset the costs, resulting in worse FID than TR-off. We have also clarified in Section 5.3 (p. 8) why strongly GT-anchored replay at large shift values is not equivalent to TR-off.

[W2]

We thank the reviewer for raising this point. First, retraining on motion data does not imply using only a small training budget. We adapted each method according to its publicly available implementation and training procedure, and report the full settings in Appendix B/Table B1. For example, DART's VAE and denoiser were trained for 200k and 300k steps, respectively; MotionStreamer's generator was trained for 100k steps; and Resampling Forcing completed its full 31.5k-step training curriculum. The DMD methods adapted from video generation also include teacher training and ODE/AR initialization stages.

Our core evidence also comes from controlled comparisons: with the same backbone, initialization, and number of post-training updates, TR reduces FID AUC by 40.9% and 18.2% relative to TR-off and Gaussian noise, respectively. This indicates that the gains cannot be attributed solely to the backbone.

TR-DMD is an extension introduced to enable comparisons with DMD-based methods and verify compatibility. We agree that its gap over Rolling Forcing is insufficient to establish a significant advantage, and that there are differences in initialization and chunking (please refer to our response to Q1 for details). Supervised TR still achieves the best FID AUC, reducing it by 14.7% relative to Rolling Forcing, and receives higher ratings for motion quality and text alignment in the human evaluation. We have expanded the discussion in Section 5.2 (p. 8) to explicitly acknowledge the small FID AUC gap and overlapping confidence intervals, as well as Rolling Forcing’s stronger results on the other five reported metrics. The revised discussion distinguishes motion distribution fidelity from text alignment and temporal degradation.

[W3/Q3]

We evaluated the checkpoints used in the paper on 64 additional prompts from the official HumanML3D validation set, distinct from those in the paper's evaluation set. The results are shown below, with 95% confidence intervals reported in the same format as in the paper. The Spearman correlation between the FID AUC rankings here and those in Table 2 is 0.983, indicating almost identical overall trends: when γ=1, s=0.6 performs best, while full replay and large shifts perform worse; with s fixed at 0.6, γ=0.25 outperforms γ=1, which in turn outperforms γ=0.5. These results leave the paper's conclusions unchanged. For each candidate configuration, we evaluate its final checkpoint on the validation set and select the main checkpoint by validation FID AUC for test-set evaluation. We have clarified this selection protocol in Section 5.1 (p. 7) and Appendix A (p. 13), and updated the corresponding description at the beginning of Section 5.2 (p. 7).

GroupSettingFID AUC ↓
Shift s (γ=1)0 (fully self-generated replay)20.694 ± 0.072
0.33.844 ± 0.037
0.62.614 ± 0.030
13.696 ± 0.029
33.179 ± 0.055
103.763 ± 0.007
1004.890 ± 0.187
10005.466 ± 0.018
100005.466 ± 0.018
Random-position clamping3.513 ± 0.060
Curriculum shift (3→0.6)3.180 ± 0.384
Replay probability γ (s=0.6)0.252.315 ± 0.048
0.53.166 ± 0.005
12.614 ± 0.030
Additional baselineTR-off (triangular resampling disabled)3.574 ± 0.083

We also repeated the TR and TR-off experiments in Table 1 with three additional training seeds for each method, retraining and evaluating them under the same settings. As shown below, the variation relative to the results reported in the paper is small and does not affect our conclusions. We have added these results to Appendix A.1, Table A1 (p. 13).

GroupSettingFID AUC ↓
Original results in Table 1TR (γ=0.25, s=0.6)1.153 ± 0.030
TR-off (triangular resampling disabled)1.951 ± 0.068
Additional run 1TR (γ=0.25, s=0.6)1.165 ± 0.054
TR-off (triangular resampling disabled)1.956 ± 0.118
Additional run 2TR (γ=0.25, s=0.6)1.136 ± 0.054
TR-off (triangular resampling disabled)1.975 ± 0.126
Additional run 3TR (γ=0.25, s=0.6)1.158 ± 0.043
TR-off (triangular resampling disabled)1.922 ± 0.105

[W4/Q4]

We used 30 prompts and three models, with three evaluations for each pairwise model comparison on each prompt. We ensured that each video pair was evaluated by three different participants. There were 30 participants in total, each evaluating nine video pairs corresponding to different prompts. The prompts were randomly selected from prompt types suitable for long-duration generation, with balanced motion categories. Regarding the absence of a tie option, we used a preference-only setup to remain consistent with prior work (DART and FloodDiffusion).

We have clarified the evaluation protocol, participant allocation, and vote-agreement statistics in Section 5.4 (p. 9) and Appendix C (pp. 15–16). Section 5.4 now explicitly states that our preference-only evaluation adapts the protocols of FloodDiffusion and DART.

[Q1]

Our adaptation of Rolling Forcing follows the original algorithm: the model's own predictions are re-noised and used as inputs to subsequent rolling windows, so it also rolls out partially denoised states. Apart from ground-truth clamping and initialization, there are two main differences. First, TR-DMD uses per-latent triangular Euler updates, whereas Rolling Forcing denoises and re-noises chunks, with the five motion latents within each chunk sharing the same noise level. Second, the two methods construct outputs for DMD training differently: TR-DMD randomly samples a shared denoising stage within each sample and recomputes the clean prediction with gradients enabled when each latent reaches that stage; Rolling Forcing extracts predictions from non-overlapping windows and mixes the Rolling Forcing and Self Forcing training paths with equal probability.

[Q5]

We agree that although FID computed over 10-second windows captures root motion information within each window, it cannot adequately measure global trajectory drift over an entire long sequence. The qualitative comparisons in our supplementary materials show that our method (TR) better preserves the intended trajectory shape and mitigates drift accumulated over time compared with TR-off and Rolling Forcing. This provides visual evidence of improved global trajectory consistency. Signature MMD (Sig-MMD) offers a promising metric for global trajectory consistency: it compares trajectory distributions in path space while accounting for temporal dependencies. However, such an evaluation requires representative real long trajectories as references. In the available motion data we use, real sequences lasting continuously for 120 seconds or longer are very limited, and samples covering the corresponding text conditions are even scarcer. It is therefore currently difficult to reliably estimate and compare distributions of complete long-duration trajectories. We have added Footnote 1 to the Evaluation Protocol in Section 5.1 (p. 6), clarifying the limitations of window-wise metrics for evaluating global trajectory drift and the scarcity of suitable long-duration reference trajectories. The footnote also makes clear that our global-trajectory observations are qualitative and supported by examples in the supplementary materials.

Andrew Alden, Blanka Horvath, and Zacharia Issa. “Signature Maximum Mean Discrepancy Two-Sample Statistical Tests.” arXiv preprint arXiv:2506.01718, 2025.

[Q6]

The TR results below use the paper's main configuration, γ=0.25 and s=0.6.

The short-clip evaluation results on HumanML3D are as follows:

MethodFID ↓Matching Distance ↓R@3 ↑
TR-off0.093 ± 0.0042.923 ± 0.0080.806 ± 0.002
TR0.181 ± 0.0082.980 ± 0.0100.796 ± 0.003

TR does exhibit a slight degradation in short-clip metrics. However, prior work has noted that models may overfit the HumanML3D evaluator's feature space, improving alignment scores without corresponding improvements in motion fidelity [1]; the evaluator is also overly sensitive to redundant motion features [2]. Other experiments have reported worse FID despite human evaluators preferring the generated results [3]. We therefore assess visual quality together with the qualitative videos in the supplementary materials, where TR is clearly better than TR-off.

For text switching during generation, we used the same models to evaluate 256 sequences of 120 seconds each, based on the BABEL validation set, changing the text every 20 seconds:

MetricTR-offTR
FID AUC ↓5.454 ± 0.1274.161 ± 0.099
FID slope, per minute ↓1.679 ± 0.2100.506 ± 0.149
Matching Distance AUC ↓5.139 ± 0.0255.021 ± 0.033
R@3 AUC ↑0.390 ± 0.0040.413 ± 0.005
Boundary Peak Jerk ↓0.1242 ± 0.00280.1202 ± 0.0020

Compared with the matched TR-off baseline, TR reduces FID AUC under changing text conditions by 23.7%, increases R@3 AUC, and reduces boundary jerk, demonstrating its improvements in long-duration generation with changing text conditions. We have added the changing-text evaluation protocol and results to Appendix A.2, Table A2 (p. 13), with a pointer in Section 5.2 (p. 8).

References

[1] Zhu et al. MotionGPT3: Human Motion as a Second Modality, Appendix C.1.

[2] Meng et al. Rethinking Diffusion for Text-Driven Human Motion Generation: Redundant Representations, Evaluation, and Masked Autoregression, CVPR 2025, §2.3.

[3] Sheng et al. Exploring Text-to-Motion Generation with Human Preference, CVPR Workshops 2024, Table 1, Figure 3, and §5.

We sincerely appreciate the time and effort you have dedicated to reviewing our manuscript. We have tried our best to provide responses to all of your questions and we hope our responses would address your concerns.

As the discussion period nears its conclusion, we would be grateful for any final feedback you may have. Please don't hesitate to let us know if further clarifications would be helpful - we remain ready to provide additional details as needed.

Thank you again for your valuable insights and constructive feedback throughout this process.

Reviewer_bofiOpenReview ↗
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Paper summary

The paper introduces Triangular Resampling (TR), a post-training strategy for improving long-horizon motion generation with diffusion models. By replaying the triangular denoising trajectory during training and using a shared threshold to control the transition between ground-truth states and model-generated predictions, TR aims to reduce the train–inference mismatch and accumulated errors. The method supports both supervised training and distribution matching (TR-DMD). Experiments on HumanML3D demonstrate improvements in long-horizon motion quality, with additional ablation studies and human preference evaluations supporting its effectiveness.

Critical strengths
  1. The paper identifies an important problem in long-horizon motion generation, namely the mismatch between training-time ground-truth states and inference-time model-generated states. The proposed triangular resampling strategy is intuitive and well motivated.
  2. The experimental results demonstrate substantial improvements over the matched TR-off baseline, particularly in FID AUC and long-term degradation. The ablation studies further support the effectiveness of the proposed ground-truth anchoring mechanism.
  3. The evaluation includes long-horizon generation, multiple quantitative metrics, and pairwise human preference comparisons, providing complementary evidence for the proposed method.
Critical weaknesses
  1. The experiments are mainly conducted on the FloodDiffusion backbone and HumanML3D evaluation prompts. It would be beneficial to investigate whether TR generalizes to other motion generation architectures or different denoising schedules.
  2. The main hyperparameters are selected based on FID AUC on the reported evaluation set. Using a separate validation set for hyperparameter selection would provide stronger evidence of the robustness and generalization of the reported improvements.
  3. Although TR-DMD achieves competitive FID AUC, its performance is not consistently better across all evaluation metrics, particularly Matching Distance and R-precision. A more detailed discussion of these trade-offs would strengthen the experimental analysis.
Questions for authors
  1. Have the authors considered evaluating TR on other motion generation backbones or alternative denoising schedules?
  2. Could the authors clarify whether hyperparameter selection on a separate validation set leads to similar improvements?
  3. Could the authors provide additional details about the number of annotators and the variability of the human preference evaluation?
3 comments

We thank Reviewer bofi for their careful review and helpful suggestions. Our responses are provided below.

[W1/Q1]

We thank the reviewer for recognizing our motivation and for the suggestion regarding generalizability. This paper focuses on the training–inference mismatch in triangular denoising, as explicitly stated in the second paragraph of the Introduction. Specifically, TR addresses model prediction errors accumulated in partially denoised states within the window. With the same backbone, initialization, and 30,000 post-training updates, TR reduces FID AUC by 40.9% relative to the baseline without TR, supporting its effectiveness in the current setting. The schedule construction also offers a natural route to extending the method to chunk-based diffusion: the generation unit can be expanded from a single latent to a chunk, with all latents within a chunk sharing the same denoising progress. When the active denoising window contains only one chunk, this schedule corresponds to an autoregressive diffusion process that completes denoising one chunk at a time. Thus, TR's trajectory replay and ground-truth clamping could potentially be extended to this setting, although their effectiveness would still require experimental validation. We have explicitly identified extensions to other backbones and denoising schedules as future work in the Conclusions, and we thank the reviewer for highlighting this important direction.

[W2/Q2]

We evaluated the checkpoints used in the paper on 64 additional prompts from the official HumanML3D validation set, distinct from those in the paper's evaluation set. The results are shown below, with 95% confidence intervals reported in the same format as in the paper. The Spearman correlation between the FID AUC rankings here and those in Table 2 is 0.983, indicating almost identical overall trends: when γ=1, s=0.6 performs best, while full replay and large shifts perform worse; with s fixed at 0.6, γ=0.25 outperforms γ=1, which in turn outperforms γ=0.5. These results leave the paper's conclusions unchanged. For each candidate configuration, we evaluate its final checkpoint on the validation set and select the main checkpoint by validation FID AUC for test-set evaluation. We have clarified this selection protocol in Section 5.1 (p. 7) and Appendix A (p. 13), and updated the corresponding description at the beginning of Section 5.2 (p. 7).

GroupSettingFID AUC ↓
Shift s (γ=1)0 (fully self-generated replay)20.694 ± 0.072
0.33.844 ± 0.037
0.62.614 ± 0.030
13.696 ± 0.029
33.179 ± 0.055
103.763 ± 0.007
1004.890 ± 0.187
10005.466 ± 0.018
100005.466 ± 0.018
Random-position clamping3.513 ± 0.060
Curriculum shift (3→0.6)3.180 ± 0.384
Replay probability γ (s=0.6)0.252.315 ± 0.048
0.53.166 ± 0.005
12.614 ± 0.030
Additional baselineTR-off (triangular resampling disabled)3.574 ± 0.083

[W3]

We thank the reviewer for this suggestion. We agree that TR-DMD's competitiveness in FID AUC should be discussed together with its text alignment performance. FID measures the distributional discrepancy between generated and real motions in feature space, whereas Matching Distance and R-precision measure the semantic consistency between motions and their corresponding text descriptions. Therefore, a generated motion distribution that is closer to real data does not necessarily imply better adherence to each individual text instruction.

Table 1 illustrates this trade-off. Compared with Rolling Forcing, TR-DMD has a slightly lower mean FID AUC (1.324 vs. 1.351), but a higher Matching Distance AUC (3.785 vs. 3.574) and a lower R-precision AUC (0.633 vs. 0.694), indicating that its text alignment remains limited. Moreover, the FID gap is small and the reported 95% confidence intervals overlap, so this advantage should not be overstated. In terms of temporal trends, TR-DMD's R-precision slope is −4.750 percentage points per minute, compared with +0.270 for Rolling Forcing, indicating more pronounced degradation in semantic alignment during sustained generation. This also shows that a better overall FID AUC does not imply greater stability across all performance metrics.

Regarding the optimization objective, TR-DMD's distribution-matching objective does not directly optimize the evaluator's text–motion distance or retrieval accuracy, and therefore does not guarantee simultaneous improvements in these metrics. We thus interpret the TR-DMD results primarily as evidence of the compatibility of triangular resampling with distribution-matching training, rather than as a comprehensive improvement over supervised TR. We have expanded the discussion in Section 5.2 (p. 8) to explicitly acknowledge the small FID AUC gap and overlapping confidence intervals, as well as Rolling Forcing’s stronger results on the other five reported metrics. The revised discussion distinguishes motion distribution fidelity from text alignment and temporal degradation.

[Q3]

We used 30 prompts and three models, with three evaluations for each pairwise model comparison on each prompt. We ensured that each video pair was evaluated by three different participants. There were 30 participants in total, each evaluating nine video pairs corresponding to different prompts. For both motion quality and text alignment, 78 of the 90 video pairs received unanimous votes (3:0, 86.7%), while the remaining 12 received split votes (2:1, 13.3%). These results indicate consistent judgments across participants.

We have clarified the evaluation protocol, participant allocation, and vote-agreement statistics in Section 5.4 (p. 9) and Appendix C (pp. 15–16). Section 5.4 now explicitly states that our preference-only evaluation adapts the protocols of FloodDiffusion and DART.

Thank you to the authors for the detailed and thoughtful responses. I appreciate the additional validation results and clarifications, which help address my concerns. While some limitations remain, I believe the paper makes a meaningful contribution to long-horizon motion generation. I will maintain my original rating of 3 (Weak Accept).

Reviewer_5uobOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
3
Soundness
3
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Paper summary

This paper improves the triangular denoising method used in FloodDiffusion for long-horizon motion generation. It exposes the model during training to some of its own rollout states to reduce the mismatch between training and inference input-state distributions. This issue can also arise in standard diffusion models. A denoising threshold retains ground-truth (GT) anchoring to limit drift away from the paired GT. The method achieves substantial improvements over the baseline on metrics such as FID AUC.

Critical strengths
  1. The paper addresses an important issue: the mismatch between diffusion models' training and inference input-state distributions. This mismatch can affect generation quality. The paper provides an interesting solution within the triangular denoising framework, and the experiments support its effectiveness.
  2. Key design choices, such as GT anchoring, are well motivated. The ablation studies are reasonably thorough.
Critical weaknesses
  1. The paper does not prove that its changes to the training input states and target velocities preserve the guarantee that inference samples follow the data distribution. Standard diffusion models, flow matching, and FloodDiffusion have such guarantees under ideal conditions. I would increase my score if the authors could provide this proof.
Questions for authors
  1. Can the authors prove that the modified training input states and target velocities preserve the guarantee that inference samples follow the data distribution under ideal conditions?
5 comments

We thank Reviewer 5uob for their careful review and helpful suggestions.

We prove that, under the stated stability and fitting assumptions, supervised TR's current-window distribution remains within Wasserstein-1 distance η+ε\eta+\varepsilon of an ideal FloodDiffusion reference, independently of generation length. Under the stated assumptions and η+ε≤Cδ\eta+\varepsilon\le C\delta, the TR upper bound is CδC\delta, while the AR upper bound is nδn\delta after nn output tokens. We have added the full theoretical analysis, including the assumptions, proof, and comparison with autoregressive generation, to Appendix D (pp. 17–18). A brief summary and reference to the proof have also been added to Section 4.2 (p. 6).

Setup. Let S=(z1,…,zw)S=(z_1,\ldots,z_w) be the rolling window and YY the paired clean GT token. Denoising levels and text conditioning are implicit. For an active token with level α<1\alpha < 1, Eqs. (8)–(9), with the numerical floor inactive, give

v_{\mathrm{tar}}&=\frac{Y-z}{1-\alpha},\qquad m_R(S):=\mathbb E_{\mathrm{TR}}[Y\mid S],\\\\ v_R(S)&=\mathbb E_{\mathrm{TR}}[v_{\mathrm{tar}}\mid S] =\frac{m_R(S)-z}{1-\alpha}. \end{aligned}$$ Here, $m_R(S)$ is the conditional mean of the paired clean token under the TR training joint distribution of replayed inputs and GT labels; $v_R$ is the corresponding ideal TR velocity. For comparison, let $X$ be an ordinary GT-noised window, with active token $X_j=\alpha Y+(1-\alpha)\xi$, $\xi\sim\mathcal N(0,I)$. Define $$m^*(s):=\mathbb E_{\mathrm{GT}}[Y\mid X=s],\qquad u^*(s):=\mathbb E_{\mathrm{GT}}[Y-\xi\mid X=s].$$ Thus, $m^*$ is the clean-token conditional mean under ordinary GT training, and $u^*$ is its optimal flow-matching velocity. These means use different input–GT joint distributions. At a reference window $S^*$ with active token $z^*$, $m^*(S^*)=z^*+(1-\alpha)u^*(S^*)$. The reference sampler uses $u^*$ with the same Euler steps and window schedule as TR. Let $S_k$ and $S_k^*$ denote the TR and reference windows after Euler step $k$ and any scheduled window shift. Define $Q_k:=\operatorname{Law}(S_k)$ and $P_k:=\operatorname{Law}(S_k^*)$, their respective probability distributions. **Proposition.** Write $d_\infty(S,S^*)=\max_j\\|z_j-z_j^*\\|_2$. Assume, uniformly over time, active tokens, and states within distance $r_0$ of a reachable reference window, - **A (conditional-target stability):** $\\|m_R(S)-m^*(S^*)\\|_2\le\eta$. - **B (regression accuracy):** $\\|v_\theta(S)-v_R(S)\\|_2\le\varepsilon$. where $R:=\eta+\varepsilon\le r_0$, and the constants do not depend on generation length. Starting from identical initial states, $$D_k^{\mathrm{TR}}:=W_{1,d_\infty}(Q_k,P_k)\le R\qquad\text{for every }k,$$ where $W_{1,d_\infty}$ is the Wasserstein-1 distance with ground metric $d_\infty$, assuming finite first moments. **Proof.** Couple both samplers using identical incoming Gaussian noise. Define $F_\theta(S)=z+(1-\alpha)v_\theta(S)$. Assumptions A–B imply $$\\|F_\theta(S)-m^*(S^*)\\|_2 \le\eta+(1-\alpha)\varepsilon\le R.$$ For an Euler increment $0 < h\le1-\alpha$, put $\lambda=h/(1-\alpha)\in(0,1]$. The updates are $$\begin{aligned} z^+&=(1-\lambda)z+\lambda F_\theta(S),\\\\ z^{*+}&=(1-\lambda)z^*+\lambda m^*(S^*). \end{aligned}$$ Consequently, $$\\|z^+-z^{*+}\\|_2 \le(1-\lambda)\\|z-z^*\\|_2+\lambda R.$$ An error at most $R$ therefore remains at most $R$. Retaining or dropping tokens cannot increase the maximum error, and identical incoming noise contributes zero error. Induction gives $d_\infty(S_k,S_k^*)\le R\le r_0$, keeping the assumptions valid. This coupling yields $W_{1,d_\infty}(Q_k,P_k)\le\mathbb E[d_\infty(S_k,S_k^*)]\le R$. $\square$

Comparison with AR. Let DnARD_n^{\mathrm{AR}} be the W1,d∞W_{1,d_\infty} distance between actual and ideal autoregressive window distributions after nn output tokens. Assume the ideal AR transition does not increase this distance and, at each common input window, the actual and ideal next-window distributions differ by at most δ\delta. The triangle inequality gives

\qquad D_0^{\mathrm{AR}}=0 \quad\Longrightarrow\quad D_n^{\mathrm{AR}}\le n\delta.$$ Let $k(n)$ be the Euler step at which TR commits token $n$. If $R\le C\delta$ for a constant $C$ independent of $n$, then $$D_n^{\mathrm{AR}}\le n\delta,\qquad D_{k(n)}^{\mathrm{TR}}\le C\delta.$$ Intuitively, the AR bound allows existing error to persist while each new token adds up to $\delta$, so the worst-case allowance grows with sequence length. Under A–B, each TR update instead bounds the new token error by a weighted average of its previous error and the fixed threshold $R$. Starting below $R$, the error therefore stays below it, yielding a uniform ceiling independent of sequence length. These bounds do not imply that AR error must grow linearly or that TR error converges to the ceiling.

I do not think the proof in the authors’ response resolves my concern. I consider the training–inference mismatch an important issue in diffusion models, and a proof addressing it would be a very elegant contribution.

The central question is how to preserve the target data distribution after exposing the model to its own rollout states and altering the original input–ground-truth pairing. Assumption A assumes that the modified conditional targets remain close to the original ones, which is precisely the property I am asking the authors to justify. Deriving an error bound under this assumption is therefore insufficient to answer my original question.

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

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