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Under review as a conference paper at ICLR 2027

On-Policy Forcing: Autoregressive Video Generation without Bidirectional Distillation

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Abstract

Recent autoregressive (AR) video generators often rely on a separate bidirectional teacher for few-step distillation, limiting the role of AR training as a native foundation for the full generation pipeline. In this work, we show that teacher-forcing AR diffusion training can produce strong many-step video generators. We then introduce **On-Policy Forcing**, which directly distills the trained AR model into a few-step student while preserving the same causal factorization from AR training through few-step distillation. By using AR models for both real- and fake-score estimation during on-policy distillation, the method removes the need for an additional bidirectional teacher and the conditioning mismatch of asymmetric distillation, in which bidirectional score models see future context that the AR student cannot. With all methods evaluated by our VBench pipeline, our four-step student distilled with 1.3B AR score models reaches 84.08 Total, outperforming Self Forcing and Causal Forcing distilled with 1.3B bidirectional score models by 0.86 and 0.79 points, respectively. At an equal training budget, On-Policy Forcing improves Dynamic Degree on the official VBench subset by 28.33 points over distillation with bidirectional real- and fake-score models, while a conditioning mismatch in the fake-score model alone leads to severe degradation. These results validate AR training as a viable foundation for video generation and establish a fully causal training-to-distillation recipe for AR video models.

Primary area:
generative models
Keywords:
Autoregressive Video Generation, On-Policy Distillation

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
Reviewer_bWn9OpenReview ↗
Rating
3(+1)
Confidence
4
Informativeness
2
Presentation
3
Soundness
3
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Paper summary

The paper proposes OPF: On-Policy Forcing, a fully autoregressive training-to-distillation pipeline for few-step video generation. Following Causal Forcing, it first trains an AR diffusion teacher with teacher forcing and initializes a few-step student using causal ODE distillation. Its main modification is to use AR models for both real- and fake-score estimation during on-policy DMD, conditioning both on clean student-generated prefixes. Experiments on Wan2.1-T2V-1.3B compare four AR/BI score configurations and report improvements in VBench quality and motion, supported by repeated training runs and paired bootstrap intervals.

Critical strengths
  1. Conditioning the teacher on a clean generated prefix and the current noisy block is a reasonable design choice. This matches the conditional denoising problem encountered during autoregressive generation and enables the same AR teacher to support both initialization and subsequent distillation.

  2. The empirical investigation is relatively thorough within the evaluated setting. The paper includes four real/fake score configurations, a fake-score initialization control, three-seed comparisons, training trajectories, and prompt-level bootstrap intervals. These provide useful evidence that the proposed recipe can improve quality and training stability on the tested backbone.

Critical weaknesses
  1. The experiments do not sufficiently distinguish the benefits of clean-prefix conditioning from those of removing future context. Moving from BI/BI to AR/AR changes both simultaneously: the AR score models observe clean preceding blocks and cannot attend to future blocks, whereas the BI models observe the full noisy video. Consequently, the improvement may arise from more informative, inference-aligned prefix conditioning, from excluding future information, or from their combination. Since the paper attributes its gains to eliminating a conditioning mismatch, separating these effects is important to establishing its central contribution.

  2. The argument against bidirectional supervision does not adequately distinguish conditional matching from joint distribution matching. An AR teacher naturally estimates the score of the current noisy block conditioned on a clean prefix. However, a matched BI/BI pair can estimate scores of the full noised video distributions, and DMD does not generally require score estimators to share the generator's causal architecture. The collapse of AR/BI therefore demonstrates a problem with mixing differently conditioned scores, but does not by itself establish that BI/BI supervision is inappropriate for an AR generator. The paper should clarify the objective induced by its conditional scores and justify the broader interpretation of its ablations.

Questions for authors
  1. Can the authors separate the effect of clean-prefix conditioning from that of excluding future context? Controlled comparisons that vary prefix noise and future visibility independently, using score models trained for the corresponding conditioning settings, would help establish which factor accounts for the gains.

  2. What precise objective does Equation (7) optimize: full-video joint distribution matching or prefix-conditioned blockwise matching? How are gradients through generated prefixes handled? Why should the failure of mixed AR/BI scores imply a limitation of a matched BI/BI pair?

The proposed recipe appears promising, but its central attribution remains unclear. If the authors convincingly disentangle clean-prefix conditioning from future-context masking and align their claims with the resulting evidence, I'm willing to raise my score.

5 comments
AuthorsOpenReview ↗

Conditioning controls: separating clean-prefix and future-mask effects (1/3)

We thank the reviewer for the focused questions about the conditioning factors and the objective optimized by our method. We have completed the additional conditioning control and clarify the score targets and implemented gradients below.

W1/Q1: clean-prefix conditioning versus future visibility. The original AR/AR–BI/BI comparison changes both factors. We introduce an intermediate causal-noisy control, which observes noisy history but masks future blocks. Both the real and fake scores in each pair use the corresponding conditioning:

Score pairPrefix observed by each scoreFuture blocks
AR/ARClean generated prefixMasked
Causal-noisy/causal-noisyNoisy prefixMasked
BI/BINoisy prefixVisible

AR/AR versus causal-noisy tests clean versus noisy history with future blocks masked. Causal-noisy versus BI/BI tests future visibility while retaining noisy history. Each score model is trained for its own conditioning, rather than changing the attention mask of a pretrained BI model at inference time.

Matched protocol and results. All three teachers use the same OpenVid data, matched effective sample exposure, optimizer and learning-rate settings, and 1,200 teacher updates. Both noisy-history configurations use a shared noise level across blocks. Each fake score starts from its corresponding real-score checkpoint, and all students share the same causal ODE initialization and downstream DMD protocol. Each setting uses one DMD training seed.

Score pair / teacherTotal @120Total @240Total @360
AR/AR, AR@120082.5683.2483.44
Causal-noisy, teacher@120082.3783.1583.26
BI/BI, BI@120082.4382.9983.12

What the controls show. With future blocks masked, clean-prefix conditioning improves Total over noisy-prefix conditioning by +0.19/+0.09/+0.18 at 120/240/360 generator updates. The positive difference appears at all three checkpoints.

With history kept noisy, future masking changes Total by −0.06/+0.16/+0.14 at the same checkpoints. Thus, masking future blocks gives higher Total at 240 and 360 updates, though not at 120. At 360 updates, the AR/AR–BI/BI gap of +0.32 separates into +0.18 for the clean-prefix contrast and +0.14 for the future-masking contrast along this three-configuration comparison.

These results provide more specific evidence than the original endpoint comparison: clean-prefix conditioning shows a positive difference throughout the evaluated trajectory, while future masking shows a positive difference at the later checkpoints. The effects are modest, and each setting uses one DMD seed.

The controls are conditional comparisons under matched training exposure, not a complete 2×2 factorial experiment. They do not estimate the interaction involving clean history with future visibility. We therefore attribute the observed differences to the tested conditioning configurations, rather than claiming that causal masking alone explains the full AR/AR advantage.

AuthorsOpenReview ↗

Conditional and joint score targets: interpretation of Equation (7) (2/3)

W2/Q2: what objective does Equation (7) represent? Our update uses clean-prefix conditional score matching, rather than the exact gradient of a full-video joint KL. A matched BI/BI pair is also a valid joint-distribution-matching design for an AR generator. The generator's causal factorization does not require its supervising scores to have the same conditioning structure.

Conditional versus joint scores. Let hi=x~0<ih_i=\tilde{x}_0^{\lt i} denote the student's generated clean history. The ideal real-score targets are

sARi=∇xtilog⁡pti(xti∣hi,c),sBIi=∇xtilog⁡ptjoint(xt1:N∣c).s_{\mathrm{AR}}^i=\nabla_{x_t^i}\log p_t^i(x_t^i\mid h_i,c),\qquad s_{\mathrm{BI}}^i=\nabla_{x_t^i}\log p_t^{\mathrm{joint}}(x_t^{1:N}\mid c).

The AR target perturbs the current block while conditioning on clean generated history. The BI target uses a jointly perturbed video, including noisy history and future blocks. The fake-score targets follow the corresponding conditioning.

For a fixed jointly noised distribution, causal factorization gives

∇xtilog⁡ptjoint(xt1:N∣c)=∇xtilog⁡ptjoint(xti∣xt<i,c)+∑j>i∇xtilog⁡ptjoint(xtj∣xt<j,c).\nabla_{x_t^i}\log p_t^{\mathrm{joint}}(x_t^{1:N}\mid c)=\nabla_{x_t^i}\log p_t^{\mathrm{joint}}(x_t^i\mid x_t^{\lt i},c)+\sum_{j>i}\nabla_{x_t^i}\log p_t^{\mathrm{joint}}(x_t^j\mid x_t^{\lt j},c).

This establishes two differences. First, the joint score includes derivatives of later conditional factors with respect to the current block. Second, even its first term conditions on noisy history rather than OPF's clean history. Thus, removing future terms from a jointly noised score does not recover OPF's clean-prefix conditional score.

Ideal conditional objective. For a fixed prompt cc and fixed history distributions μi\mu_i, define the conditional KL for block ii as

Ki(θ,hi,t)=KL(qθ,ti,RE(⋅∣hi,c)∥pti(⋅∣hi,c)).K_i(\theta,h_i,t)=\mathrm{KL}(q_{\theta,t}^{i,\mathrm{RE}}(\cdot\mid h_i,c)\Vert p_t^i(\cdot\mid h_i,c)).

The reference objective is

Jμ(θ)=∑iEhi,t[λ(t)Ki(θ,hi,t)].J_{\mu}(\theta)=\sum_i\mathbb{E}_{h_i,t}[\lambda(t)K_i(\theta,h_i,t)].

Here hi∼μi(⋅∣c)h_i\sim\mu_i(\cdot\mid c), and tt follows the training timestep distribution. The history distribution is held fixed during differentiation. RE denotes the distribution induced by random-exit sampling and subsequent perturbation. With exact unguided conditional scores, appropriate time weights, and differentiation through the corresponding conditional sampler, the score difference admits this conditional-KL interpretation.

In practice, histories are generated by the current student but detached for the generator update. The distinction matters because the KL chain rule is an identity of objective values, not permission to ignore the parameter dependence of generated histories when differentiating a full-video KL.

Moreover, the implementation includes real-score guidance, sample-dependent normalization, and truncated generator gradients. We therefore use the conditional KL as a reference interpretation, not as a claim that the implemented update is its exact full gradient.

Relation to BI/BI. Both matched score pairs provide valid distribution-matching signals, but for different corruption and conditioning schemes. The failure of mixed real/fake conditioning does not invalidate matched BI/BI. Our contribution is an empirical comparison of these designs under controlled training protocols, together with the conditioning-factor controls reported in Part 1.

AuthorsOpenReview ↗

Implemented surrogate, random-exit training, and gradient paths (3/3)

W2/Q2: what is actually differentiated? We clarify the implemented surrogate and its gradient paths to distinguish the practical update from the ideal conditional objective in Part 2.

Random-exit training. At each iteration, an exit step KK is sampled uniformly from the four denoising steps, shared across blocks and synchronized across ranks. Each block stops at KK and supplies its clean prediction as the training sample. Thus, training uses shared-random-exit rollouts rather than always generating the final four-step output and differentiating only an intermediate pass.

Implemented surrogate. Let x~0\tilde{x}_0 concatenate the generated clean block predictions, ff denote the fake clean-sample prediction, and rr the guided real prediction. The real prediction uses negative-prompt guidance,

r=rc+w(rc−rneg),w=3,r=r_c+w(r_c-r_{\mathrm{neg}}),\qquad w=3,

while the fake prediction uses the conditional prompt without guidance.

For each video, the implementation computes

Z=mean⁡∣x~0−r∣,d=sg⁡[nantonum⁡(f−rZ)],Z=\operatorname{mean}|\tilde{x}_0-r|,\qquad d=\operatorname{sg}\left[\operatorname{nan_to_num}\left(\frac{f-r}{Z}\right)\right],

\ell_{\mathrm{sur}}=\frac{1}{2D}\left\\|\tilde{x}_0-\operatorname{sg}(\tilde{x}_0-d)\right\\|_2^2,

where DD counts latent elements and sg⁡\operatorname{sg} denotes stop-gradient. The loss is averaged across the batch.

Because the regression target is detached, the computed per-video generator gradient is

∇θautogradℓsur=1DJtrunc⊤d,\nabla_\theta^{\mathrm{autograd}}\ell_{\mathrm{sur}}=\frac{1}{D}J_{\mathrm{trunc}}^\top d,

where JtruncJ_{\mathrm{trunc}} contains only the generator paths retained during backpropagation.

Gradient pathImplementation
Selected denoising pass in each blockGradient retained
Earlier denoising passesNo gradient
Generated-prefix KV-cache writesNo gradient
Score predictions, prefixes, and normalizerDetached / evaluated without gradients
Rollout used to train the fake scoreDetached from generator

Generated history remains available to later blocks during forward computation. Truncation removes backward paths through the generation and caching of that history; each block still receives its own direct gradient through the selected denoising pass.

Why truncation does not make AR/AR and BI/BI equivalent. Two distinct dependencies must be separated. The BI joint score can depend on future noisy blocks through the distribution's score function. Generator-gradient truncation instead removes particular paths through the generator Jacobian. Detaching generated histories does not remove future-dependent terms already present in a BI score.

Likewise, evaluating the real and fake scores without gradients does not discard their supervision: their numerical predictions form dd, which is applied through JtruncJ_{\mathrm{trunc}}.

The per-video normalizer ZZ also couples update magnitudes across blocks, even though each AR score observes only its permitted context. Hence our implementation should not be described as independent optimization of every block or as the exact gradient of a full-video KL.

Summary. Equation (7) is implemented as a guided, normalized, gradient-truncated score-difference surrogate on student-generated histories. The conditional-KL objective explains the intended score target under idealized assumptions; the expressions above specify the actual update. Together with the factor-separation controls, this clarifies both what distinguishes AR/AR from BI/BI and what the implementation optimizes.

Reviewer_e6uXOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This work proposes On-Policy Forcing for few-step autoregressive video generation without an additional bidirectional teacher during distillation. The method uses autoregressive models for both real and fake score estimation, with both models conditioned on the student’s generated history. This aligns causal conditioning throughout training and distillation. Experiments on VBench show improvements over Self Forcing and Causal Forcing using bidirectional score models.

Critical strengths
  • The motivation for consistent causal conditioning is clear. Reusing the autoregressive teacher for both student initialization and final distillation provides a coherent pipeline without requiring an additional bidirectional teacher.
  • The fake-score ablation is particularly informative. With the same pretrained Wan weights, causal conditioning supports successful training, while bidirectional conditioning leads to severe degradation. This provides useful evidence that the difference is not simply caused by initialization.
  • The four-step student achieves 84.08 VBench Total, outperforming the reproduced Self Forcing and Causal Forcing baselines using bidirectional score models. The additional three-seed experiments also strengthen the empirical evaluation.
Critical weaknesses
  • The fake-score control is helpful, but the autoregressive real-score model gets extra OpenVid training while the bidirectional model uses pretrained Wan weights. Could the gains partly come from this extra training? A comparison with matched data and training budgets would help.
  • The asymmetric results in Table 2 need more analysis. AR/BI collapses, while BI/AR has high Dynamic Degree but lower overall quality. The paper attributes both to conditioning mismatch, but it is unclear why the two settings fail so differently. Could the authors explain what causes this difference and how each score model affects training?
Questions for authors

Please see "Critical Weaknesses" part for reference.

4 comments
AuthorsOpenReview ↗

Matched teacher-training control and score-conditioning evidence (1/2)

We thank the reviewer for the positive assessment and the two focused questions. We have completed additional controls addressing teacher training history and the mixed-pair behavior.

W1: does the AR/AR advantage persist after matching teacher training? In the new matched-exposure comparison, AR/AR has higher Total at all three evaluated checkpoints.

We compare AR@1200 with BI@1200 using the same OpenVid data, effective sample exposure, optimizer and learning-rate settings, and 1,200 teacher updates. Input layout, history noise, and attention masks follow the respective conditioning settings. Each fake score starts from its corresponding real-score checkpoint; both students share the same causal ODE initialization. Each setting uses one DMD training seed.

Score pair / teacherTotal @120 updatesTotal @240 updatesTotal @360 updates
AR/AR, AR@120082.5683.2483.44
BI/BI, BI@120082.4382.9983.12

AR/AR exceeds BI/BI by 0.13, 0.25, and 0.32 Total points at 120, 240, and 360 generator updates. Thus, the positive Total gap persists in this run even when the BI teacher also receives the additional OpenVid training. The matched-exposure advantage is modest, and we distinguish it from the larger differences in the original experiments. Because this control compares complete score pairs at 1,200 teacher updates, it does not quantify how much of the original AR@3900 gap is attributable to teacher adaptation.

Complementary control: conditioning versus fake initialization. Appendix B.3 addresses a different question. It fixes the AR real score, student initialization, and initial Wan weights of the fake score, while changing fake-score conditioning. Causal conditioning reaches 83.19 Total and 65.56 Dynamic Degree at 360 generator updates, whereas bidirectional conditioning severely degrades despite starting from the same fake weights.

These controls separate two explanations that the original comparison alone could not distinguish: the new experiment tests unequal teacher-training exposure, while B.3 tests fake-score conditioning at fixed initial weights. The former retains a small AR/AR Total advantage under matched exposure; the latter shows that successful causal distillation does not require AR-teacher initialization of the fake score.

AuthorsOpenReview ↗

Explaining the mixed-pair asymmetry and testing additional fake updates (2/2)

W2: why do AR/BI and BI/AR behave differently? The two mixed pairs change different parts of the distillation signal: AR/BI retains the AR target but changes the estimate of the student's distribution; BI/AR retains the AR student-distribution estimate but changes the target. They are therefore not equivalent interventions with opposite signs.

Let A/B denote AR/BI conditioning, and let sps_p and sqs_q denote the real and fake score estimates. On a fixed rollout and noise realization, with the real-score guidance convention held fixed, define ΔAA=spA−sqA\Delta_{AA}=s_p^A-s_q^A. Then

\Delta_{BA}=\Delta_{AA}+(s_p^B-s_p^A).$$ The added terms concern different distributions, so one is not generally the negative of the other. This explains why symmetric behavior is not required. The specific low- versus high-activity outcomes are empirical observations, rather than predictions of these identities; normalization and the truncated generator Jacobian also affect the actual parameter update. **Interpreting the observed asymmetry.** In Table 8, AR/BI already has Total **64.34** and Dynamic Degree **2.50** at 120 generator updates. BI/AR has Dynamic Degree **100.00–89.17** over 120–360 updates, but lower quality than AR/AR. The asymmetry is therefore between two degradation patterns: loss of activity in AR/BI and high activity with reduced quality in BI/AR. Dynamic Degree measures activity, not whether that activity is coherent. **Does more fake-score training rescue AR/BI?** We tested this directly with fresh 5:1 and 10:1 fake-to-generator update runs, using the same initialization and training seed and a prespecified endpoint of 120 generator updates. These are new runs, separate from Table 8. | Generator updates | Total, 5:1 | Total, 10:1 | Dynamic Degree, 5:1 | Dynamic Degree, 10:1 | |---|---:|---:|---:|---:| | 30 | 73.70 | 75.09 | 12.22 | 10.00 | | 60 | 71.70 | 70.77 | 11.94 | 8.06 | | 120 | 63.88 | 67.26 | 1.94 | 0.83 | Doubling fake updates improves endpoint Total by **3.38** points, but does not recover activity: Dynamic Degree is **0.83**, versus **1.94** with 5:1 updates. Both Total trajectories decline across the evaluated checkpoints. Thus, the extra updates partially improve endpoint Total but do not stabilize the tested AR/BI run. Importantly, increasing update frequency leaves the AR/BI conditioning unchanged. It further trains the BI-conditioned fake score on student samples while the real score remains AR-conditioned; it does not align their conditioning. The experiment therefore tests whether more fake-score training alone is sufficient under this unchanged pairing. Each arm uses one training seed. The 10:1 arm has twice the fake-score updates and associated prompt exposure, not equal compute. Extra updates also consume random draws, so later generator batches, noise, and exit steps are not paired across arms. The conclusion is specific to this tested increase in update frequency. In summary, the two mixed pairs alter different score terms and exhibit different forms of degradation, which must be assessed using both activity and quality. Additional fake updates improve AR/BI's endpoint Total but do not resolve its low-activity failure.

Thanks for the authors' response. After carefully reviewing the response, I think the matched teacher-training control and the analysis of the mixed-pair asymmetry address my main concerns. Thus, I will keep my score of 3.

Thank you for carefully considering our response. We appreciate your feedback, which helped us clarify the teacher-training comparison and the interpretation of the mixed-pair results. These experiments and clarifications are now included in the revised manuscript.

Reviewer_WVj4OpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper replaces the bidirectional real/fake score models in self-forcing DMD with a teacher-forcing-trained AR teacher (frozen, real) and an online AR model (fake), so that TF training, causal ODE initialization, and DMD all share the student’s causal factorization. On Wan2.1-1.3B/VBench the 4-step student reaches 84.08 (single run), above its teacher (82.90) and Self Forcing/Causal Forcing retrained with 1.3B BI real scores (83.22/83.29). A 2×2 study of real/fake conditioning shows AR/BI collapses, BI/AR degrades, and BI/BI loses motion over training, all attributed to “conditioning mismatch”.

Critical strengths
  1. The 2×2 study from a shared initialization, plus the B.3 control separating the fake model’s attention mask from its weights, cleanly establishes that mismatched real/fake conditioning breaks DMD, a new and reproducible result.
  2. Three seeds trajectories to 480 updates, paired bootstrap CIs, and a candid limitations section are above the norm for this area.
  3. Replacing the 14B bidirectional teacher with a 1.3B causal one would be practically attractive if the gains hold and the much heavier Stage1 is accounted for.
  4. The paper is clearly written.
Critical weaknesses
  1. The AR-teacher → causal ODE init → self-forcing DMD with AR real/fake models recipe already appears in CausalCine (arXiv 2605.12496); the contribution is a controlled analysis, not a new method, and “without bidirectional distillation” still relies on a bidirectional pretrained backbone.
  2. The name misplaces the increment: Self Forcing is already on-policy and Stage3 is standard DMD; what changes is the score models’ causal conditioning.
  3. Core argument. “Mismatch” is defined relative to the student, but DMD only requires real and fake scores to share a distribution family. That explains AR/BI and BI/AR, but BI/BI satisfies it, both scores estimate the joint, as in Self Forcing, so the paper shows “real/fake must match”, not “AR beats BI”; the latter has no tested mechanism are unexplained.
  4. VBench only, no human study, and no long-horizon test although that is the stated motivation for AR generation.
Questions for authors
  1. Training details of Self Forcing/Causal Forcing (steps, seeds, schedule, checkpoint selection), the Stage3 prompt source, and which denoising steps the DMD gradient passes through?
  2. Why is BI/BI a mismatch if both scores estimate the joint, and why do AR/BI and BI/AR fail in opposite directions?
  3. How does OPF differ from CausalCine’s AR/AR self-forcing DMD?
  4. Is Stage2 still needed with an AR real score? Please report AR/AR initialized directly from the AR teacher.

I will raise my score if my concerns are addressed, in particular if the bidirectional real-score model is fine-tuned on OpenVid so that the difference in training data is removed as a confound from the claim that AR distillation outperforms BI distillation.

5 comments
AuthorsOpenReview ↗

Comment 1/3 — Positioning and controlled score-pair experiments

We thank the reviewer for the detailed feedback and for recognizing the controlled score-pair study and the Appendix B.3 control.

Relation to CausalCine (W1, Q3). Both OPF and CausalCine use a causal teacher, causal ODE initialization, and self-forced DMD. Our contribution beyond these shared components is a controlled study of real/fake score conditioning: a 2×2 comparison with shared student initialization and a common DMD protocol, a fake-score weight/conditioning control, and repeated training trajectories. These experiments reveal distinct degradation patterns and late-training behavior. The matched-training and prefix-noise controls further examine explanations for these differences.

Title and on-policy terminology (W1, W2). “Without an additional bidirectional teacher” refers to distillation: the adapted AR teacher provides ODE initialization and DMD supervision, although the backbone was pretrained bidirectionally. We use “on-policy” in the sense of Self Forcing: training samples come from the current student's rollout. OPF conditions both scores on the same clean generated prefix. Sample source and score conditioning are separate design choices.

BI/BI and the empirical claim (W3, Q2). A matched BI/BI pair is a valid joint-distribution-matching design for an AR generator. “Mismatch” describes the different real/fake score conditioning in mixed pairs, not a defect of BI/BI. Whether AR/AR outperforms BI/BI is an empirical question. In Table 7, three-seed Total at 120 generator updates is 83.75 ± 0.28 for AR/AR and 83.33 ± 0.36 for BI/BI (mean ± sample SD). Over the evaluated 120–360 updates, BI/BI mean Dynamic Degree declines to 56.48, while AR/AR stays within 68.24–69.63. The abstract's +28.33 is from a separate fixed-checkpoint AR/AR–BI/BI comparison at 360 updates, with the prompt-paired bootstrap interval in Appendix B.2; it is not the difference between those three-seed means.

Conditioning versus fake initialization. Appendix B.3 fixes the AR real score and student initialization, while initializing the fake score from pretrained Wan weights. With identical fake-score initialization, causal conditioning reaches 83.19 Total and 65.56 Dynamic Degree at 360 updates, whereas AR/BI severely degrades. Thus fake-score conditioning matters even with fixed initial weights; successful distillation does not require initializing the fake score from the AR teacher.

Matched teacher training (W3). To examine whether additional OpenVid training explains the AR/AR–BI/BI difference, we compare AR@1200 with BI@1200, matching OpenVid data, effective sample exposure, optimizer and learning-rate settings, and 1,200 teacher updates. Input layout, history noise, and attention masks follow each conditioning setting. Each fake score starts from its corresponding real-score checkpoint, all students share causal ODE initialization, and each setting uses one DMD seed.

Score pair / teacherTotal @120Total @240Total @360
AR/AR, AR@120082.5683.2483.44
BI/BI, BI@120082.4382.9983.12

AR/AR exceeds BI/BI by 0.13/0.25/0.32 Total points at 120/240/360 generator updates. The advantage persists with matched teacher-training exposure, so additional OpenVid updates are not the sole explanation for these particular results. These differences are modest and come from one DMD seed per setting; we do not claim statistical significance.

AuthorsOpenReview ↗

Comment 2/3 — Baseline training and checkpoint comparison

Baseline training details (Q1). SF† and CF† are our reproduced baselines with 1.3B BI real-score models; published 14B-teacher results appear in separate rows. SF†, CF†, and OPF share effective batch size 32, generator/fake learning rates 2e-6/4e-7, and a 5:1 fake-to-generator update ratio. SF†/CF† use ODE initialization from Wan2.1 1.3B; OPF uses causal ODE initialization from its 1.3B AR teacher.

DetailSF†CF†OPF
LR scheduleConstantConstantConstant
Optimizer / betas / weight decayOfficial SF repository settingsOfficial CF repository settingsAdamW / (0, 0.999) / 0.01
Original main-table selection ruleHighest VBench Total over evaluated updatesHighest VBench Total over evaluated updatesHighest VBench Total over evaluated updates
ODE initialization sourceWan2.1 1.3BWan2.1 1.3B1.3B AR teacher

Fixed-checkpoint baseline comparison (Q1). The supplementary evaluation uses non-EMA generator weights, four denoising steps, generation seed 0, and inference shifts 5/5/8 for SF†/CF†/OPF, preserving each method's inference recipe. Before examining the new scores, we fixed three candidates per method against OPF's 120/240/360-update targets: the nearest saved checkpoint, with ties resolved toward the earlier one. All nine checkpoints, including actual generator-update counts, are reported below.

MethodGenerator updatesTotalDynamic Degree
SF†12083.1383.61
SF†24082.7269.17
SF†36082.1235.28
CF†10083.3485.28
CF†25083.3270.56
CF†35083.0459.72
OPF (AR@3900)12083.8164.67
OPF (AR@3900)24084.0870.83
OPF (AR@3900)36083.9871.67

Late-training behavior. Across the reported checkpoints, SF† Dynamic Degree falls from 83.61 to 35.28 and CF† from 85.28 to 59.72, whereas OPF increases from 64.67 to 71.67. Between 240 and 360 updates, OPF Total changes from 84.08 to 83.98 and Dynamic Degree from 70.83 to 71.67. At the final checkpoints, OPF Total is 83.98 versus 82.12 for SF† and 83.04 for CF†. These single-seed trajectories show less late-training degradation for OPF at approximately matched endpoint budgets (360/350/360 updates for SF†/CF†/OPF).

Prompt source and gradient paths (Q1). Stage 3 uses 248,221 filtered and extended VidProM prompts. One exit step is sampled uniformly from the four denoising steps, shared across blocks and synchronized across ranks. Each block stops at that step and provides its clean prediction as the training sample. Only the selected denoising pass receives gradients; earlier passes and clean-prefix KV-cache writes run without gradients, and score prefixes are detached. Forward dependence on generated history is retained. This is random-exit training, not differentiating one intermediate pass while continuing to the fourth-step output.

AuthorsOpenReview ↗

Comment 3/3 — Stage 2 ablation and evaluation scope

Role of Stage 2 (Q4). With AR@3900, we compare causal ODE initialization against direct AR initialization, followed by the same AR/AR DMD protocol. The single-seed fixed-checkpoint Total trajectories are:

Generator updatesWith Stage 2: TotalDirect AR initialization: Total
081.7265.52
12083.8182.80
24084.0883.15
36083.9882.94

Stage 2 increases initial four-step Total by 16.20 points (81.72 versus 65.52) and retains advantages of 1.01, 0.93, and 1.04 at 120, 240, and 360 generator updates. In this run, causal ODE initialization provides a stronger few-step starting point and higher Total at every evaluated checkpoint. Direct AR initialization also improves substantially under DMD, so Stage 2 is beneficial, not a prerequisite for successful distillation.

Mixed-pair asymmetry (Q2). Changing the fake score perturbs the student-distribution estimate; changing the real score perturbs the target estimate. These affect different terms of the score difference and need not behave symmetrically. Empirically, AR/BI has low activity, while BI/AR has high activity with reduced quality. Increasing the AR/BI fake-to-generator update ratio from 5:1 to 10:1 does not prevent degradation: endpoint Total is 67.26 and Dynamic Degree 0.83. The reply to reviewer e6uX provides the algebra and complete trajectory.

Evaluation and uncertainty (W4). Appendix B.6 evaluates a separate 100-prompt rich-motion set with VBench Dynamic Degree. For independent three-seed runs extended to 480 generator updates, AR/AR scores 79.00 ± 5.57 versus 50.33 ± 3.21 for BI/BI on that set; standard VBench Total is 83.84 ± 0.18 versus 81.97 ± 0.87 (Appendix B.5).

Appendix B.2 separately reports prompt-paired bootstrap differences at 360 updates: AR/AR minus BI/BI is +1.20 [0.54, 1.86] in Total and +28.33 [19.17, 37.78] in Dynamic Degree (95% intervals, 10,000 resamples). The three-seed experiments characterize run-to-run variation, whereas the bootstrap characterizes prompt variation at fixed checkpoints. We report them separately rather than treating the bootstrap intervals as training-seed uncertainty.

Evaluation scope. The fixed-checkpoint baseline comparison and Stage 2 ablation each use one training seed. The three-seed results are separate controlled AR/AR–BI/BI experiments. Extending those runs to 480 updates still generates 81-frame videos, not longer-horizon outputs. Longer-horizon generation and human evaluation remain future work. Dynamic Degree measures motion activity, so it must be interpreted alongside quality and consistency metrics.

Comments on the paper

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General Response to All Reviewers

We thank the Area Chair and all reviewers for their constructive feedback. We have revised the manuscript to incorporate the additional experiments and clarifications discussed in our responses. New or substantially revised text is marked in blue.

  • Sections 1–2: Clarified our contribution as a controlled study of real and fake score conditioning, and its relation to CausalCine.
  • Section 3.5 and Appendix F: Clarified on-policy sampling, conditional versus joint score targets, and why BI/BI can supervise an AR generator. We also describe the DMD loss, random-exit sampling, and gradient truncation used in training.
  • Section 4.3, Table 3: Added the OpenVid comparison of AR/AR, causal-noisy, and BI/BI after the same number of teacher updates and sample exposure, to examine clean-prefix conditioning and future masking. We also discuss why changing the real or fake score can produce different training behavior.
  • Section 4.3 and Appendix B.7, Table 13: Added the Stage 2 ablation comparing causal ODE initialization with direct AR-teacher initialization.
  • Section 4.1 and Appendix A, Table 5: Added baseline training settings, checkpoint selection, ODE initialization sources, and the Stage 3 prompt source.

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