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Paper summary
This paper proposes Competitive Flow Matching, which introduces multiple competing velocity predictions during Flow Matching training, allowing the model to learn different generation modes and control the trade-off between generation quality and diversity through auxiliary conditioning.
However, applying WTA to Flow Matching offers limited methodological novelty, and its advantages over other post-training methods remain to be further investigated. According to the experimental results, the proposed method performs well in high-coverage generation settings, but does not show substantial improvements in overall performance comparisons.
Critical strengths
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The paper addresses the issue of conflicting velocity targets in Flow Matching by introducing Winner-Take-All (WTA) training, allowing different auxiliary conditions to predict different velocities and avoiding simple averaging over multiple targets. The overall method is intuitive, easy to understand, and relatively easy to apply to existing Flow Matching models.
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The paper focuses not only on generation quality but also on the coverage of the generated distribution. On ImageNet-256, Competitive FM significantly outperforms existing methods, particularly in high-recall settings.
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The paper validates the proposed method on different architectures, including SiT and RAEv2, and conducts ablation studies on the number of competing candidates , auxiliary conditioning scale, and code sampling strategy.
Critical weaknesses
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The core algorithm of this paper applies the existing Winner-Take-All (WTA) learning strategy to velocity regression in Flow Matching. However, similar multi-candidate competition mechanisms have already been extensively studied in previous WTA-based methods. This paper mainly adapts WTA to Flow Matching by introducing auxiliary conditioning. Therefore, the methodological novelty of these improvements is somewhat limited.
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The authors argue that predicting the conditional mean velocity in standard Flow Matching leads to averaging over different target velocities, thereby affecting generation quality and coverage. However, these assumptions lack sufficient theoretical justification. The optimal velocity field learned by standard Flow Matching can correctly generate the target distribution under ideal conditions. Therefore, velocity averaging itself may not be the fundamental cause of the quality–coverage trade-off.
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The paper lacks comparisons under equal computational budgets. The design involving multiple candidate velocities introduces additional computational overhead, making training FLOPs a potential concern. The authors also do not investigate whether the benefits of WTA outweigh those of allocating the same computational budget to other post-training methods.
Questions for authors
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Please provide the training FLOPs required by the multiple candidate velocity design. If possible, it would be helpful to include comparisons with other post-training methods.
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Please provide stronger theoretical justification for whether velocity averaging is indeed the cause of the quality–coverage trade-off. Clarifying this point is particularly important for my decision on whether to increase score.
4 comments
Novelty: Simply adapting WTA to Flow Matching cannot reproduce the large gain.
We thank the reviewer for raising this question, but our contribution is not simply applying WTA to velocity regression. We identify an opportunity to exploit the sample-wise target variation that standard FM does not explicitly retain, and develop competitive post-training to turn this variation into a new code-based, coverage-oriented inference-time control for FM generators. This enables different generative behaviors within a single model, complements guidance, and expands the range of accessible quality–coverage operating points.
We recognize that WTA and multiple-choice learning have been extensively studied. However, directly adapting established WTA formulations to Flow Matching does not automatically yield these improvements. We investigate two representative alternatives, with detailed methods and results provided in Revised Supplementary Sec. I, Figs. 5–6.
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Established multi-head WTA (MHP) + FM We adapt the well-established Multiple Hypothesis Prediction formulation (Rupprecht et al., ICCV 2017), which implements WTA through multiple independent prediction heads, to FM using eight velocity heads on a shared SiT trunk. Unlike our method, it learns no code-conditioned response whose strength can be scaled by λ, and therefore provides no continuous coverage control that complements guidance. The baseline trains stably, keeps all heads active, and uses approximately 14× as many additional parameters as our auxiliary branch. Nevertheless, at nearly matched Recall, MHP with AutoGuidance obtains FDᵣ,₆=15.58 at 76.12% Recall, compared with 8.31 at 76.46% Recall for our method.
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Noisy-State WTA + FM Another natural way to introduce competition into FM is to compete among different noisy realizations of the same training example, rather than competing among code-conditioned predictions at the same noisy state as in our formulation. Specifically, For each clean training example, it samples K independent noise realizations to construct K different noisy states, then updates the model only through the realization with the smallest FM regression loss. The method learns no auxiliary code-conditioned fields and provides no inference-time control. Empirically, it only modestly improves the underlying FM predictor before saturating early, while its guided results remains close to the pretrained SiT baseline and does not reproduce our quality–coverage frontier.
Beyond the performance gains, we contribution also includes a systematic study of this inference time control and the generative behaviors induced by competitive training. Our analyses cover the joint effects of auxiliary-conditioning strength and guidance on the quality--coverage frontier; different code-sampling policies; how competition strengthens the shared base field even without auxiliary conditioning; and the effects of scaling competition strength K. We further demonstrate generalizability across flow-generator families (SiT, JiT, and RAE) and stronger pretrained generators (CAFM and REPA), whose frontiers improve further after just one additional epoch of our post-training (Revised Supplementary Sec. F, Fig. 2).
Follow-up to Reviewer VYnv: Summary of Our All Responses
Thank you again for your thoughtful review! We hope our responses have been helpful. With the discussion period ending soon, we wanted to briefly recap how we addressed your main concerns.
Our Reply to All Reviewers clarifies the overall motivation and the role of the 1D toy, and provides a mechanistic analysis of our method. The new Additional Supplementary Material provides the full experimental details supporting our rebuttal. We also address your questions as follows:
1. Do we mean that averaging is wrong in Flow Matching?
No. We want to clarify our motivation. A noisy state can correspond to multiple target velocities. Under L2, these velocities are optimally averaged into their conditional mean. With ideal modeling and sufficiently fine integration, this marginal field can correctly recover the full multimodal distribution.
What we claim is: in practice, however, generation relies on approximate learned fields and finite sampling budgets. As illustrated by our toy, under these practical constraints, relying on a single mean field to cover multiple modes can leave samples off-manifold and valid modes underrepresented. In image generation, guidance can bring samples back toward high-density regions, but often at the cost of coverage.
We therefore ask: rather than relying on a single marginal field to cover all modes, can different modes be accommodated by different predictions? Competitive FM realizes this idea through code-conditioned predictions, and our experiments show that it improves both fidelity and coverage in practical generation settings.
We thank the reviewer for raising this important question and will revise the paper to make this distinction explicit and avoid any misunderstanding.
2. Is our method simply a direct adaptation of WTA to Flow Matching?
No. We implemented two representative direct adaptations—classical multi-head WTA and Noisy-State WTA. Both train successfully and provide improvements in selected settings, but neither reproduces our inference-time control or quality–coverage frontier.
Our contribution is not the WTA rule itself, but how we use it to uncover and exploit valuable learning signals in Flow Matching. Auxiliary codes allow different targets to shape specialized code-conditioned velocity fields. Fixing a code makes these responses compose coherently along a trajectory, while using and scaling different codes broadens population coverage and enables additional control over quality–coverage behavior within a single model. This control changes how the model responds to guidance, turning the usual fidelity–coverage trade-off into win-win regimes where fidelity improves without the usual loss of coverage. Together, these effects substantially expand the quality–coverage frontier beyond all the settings we evaluate.
The method also generalizes to stronger pretrained generators, further improving CAFM and REPA after only one epoch of post-training. Beyond the empirical gains, we provide a systematic study of the method, characterizing fixed-code coherence, auxiliary scaling, population-level code mixing, guidance interaction, and scaling with K.
3. Are the gains simply due to additional training compute?
No. Our entire ten-epoch post-training stage uses only 2.63% of SiT’s original pretraining FLOPs. Allocating the same or greater compute to standard FM does not reproduce the gain, and the official CAFM and MixFlow post-training schedules use substantially more compute while remaining behind our quality–coverage frontier. Our advantage therefore does not come from a larger post-training budget.
Follow-up Clarification on Conditional Averaging and the Quality–Coverage Trade-off
We sincerely thank the reviewer for emphasizing this important question and for explaining that it is particularly relevant to your assessment. In our Reply to All Reviewers, we provided three complementary discussions: how conditional averaging should be understood in our motivation, what the 1D toy is intended to illustrate, and a detailed toy-based analysis of the mechanism induced by our method. We would like to follow up here with a concise, integrated clarification, while referring to those responses and the Additional Supplementary Material for the complete analyses.
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Our intended claim is not that velocity averaging is the fundamental cause of the quality–coverage trade-off. Conditional averaging is the correct marginal solution of standard FM: with ideal modeling and sufficiently fine integration, the resulting mean field can recover all modes of the target distribution. Our motivation instead concerns practical generation, where models rely on approximate learned fields and finite sampling budgets. Under these constraints, trajectories following a single marginal field may pass through low-density regions, leaving some samples off-manifold and valid alternatives underrepresented. Although post-hoc guidance can bring samples back toward the data manifold, it often does so by concentrating generation on high-density regions, leading to mode collapse and reduced coverage. This motivates us to explore a different route: can we model modes at each intermediate timestep to cover the full modes of the distribution? Our 1D toy is used to illustrate this distinction. For standard FM, off-support mass decreases from 4.09% with 4 Euler steps to 1.95%, 1.27%, and 0.76% with 8, 16, and 32 steps, respectively, and further decreases to 0.51% with 2,000 steps. This confirms that standard FM can recover the target distribution increasingly well as integration becomes finer. In contrast, Competitive FM achieves 0.41% off-support mass with only 4 steps while covering both modes, showing that, even under such a limited sampling budget, its more mode-directed predictions can reduce off-support generation while retaining broad target-mode coverage.
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The toy also mirrors the behaviors observed in image generation. Different auxiliary codes support distinct generative behaviors, while scaling the auxiliary conditioning provides a smooth additional control over population coverage. Our image-generation results further show that this different route can improve quality at broad coverage and expand the accessible quality–coverage frontier. In particular, after our post-training, traditional guidance no longer improves quality in the direction of sacrificing coverage, instead, it can improve quality while largely preserving coverage. We consistently observe these benefits across different pretrained generators, model families, and guidance mechanisms.
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We further provide a detailed mechanism analysis in our general response and Additional Supplementary Material. At ambiguous noisy states, competition causes different code-conditioned predictions to specialize toward different valid target directions. Holding a code fixed allows these local responses to compose consistently over time, whereas disrupting code identity weakens trajectory coherence and increases off-support generation. Across a population, using different codes covers different target modes, while the auxiliary-conditioning scale smoothly controls the amount of expressed variation. Together, these results provide a mechanistic picture of how sample-wise target variation—although not required for the correctness of ideal marginal FM—can serve as a valuable additional learning signal under practical generation conditions.
We have incorporated this clarification into the revised abstract and introduction and added the finite-step comparison as a footnote to Figure 2, with all changes highlighted in blue. We hope these revisions clarify our intended motivation. As the discussion period draws to a close, we would greatly appreciate any further feedback and would be happy to clarify any remaining questions. We hope this clarification will be helpful as you finalize your assessment.
Computational cost analysis: our gains do not rely on a larger training budget
We thank the reviewer for raising this important concern. We provide detailed analytical FLOP accounting, measured runtime, cross-method cost comparisons in Revised Supplementary Sec. J (Tables 8–9).
Computational cost vs. standard FM. Our method is a post-training procedure that does not require training from scratch. We evaluate K candidate velocities without gradients and backpropagate only through the winner. Under standard analytical FLOP accounting, K=8 requires 3.674× the model-core training FLOPs per update of standard FM. Over ten epochs, this totals 33.49 EFLOPs. In practice, our optimized implementation has a lower measured runtime overhead of 2.441× (0.500 vs. 0.205 s/update). The full post-training stage takes approximately ~6.95 hours on a single 8×H200 node (55.57 H200 GPU-hours) of projected active training, corresponding to just 2.63% of SiT's original pretraining FLOPs.
Allocating the same or greater compute to standard FM does not reproduce the gain. The runtime budget of our ten-epoch post-training would allow approximately 24.4 additional epochs of standard FM. However, even 50 additional epochs of FM continuation leave FID essentially unchanged (14.41 → 14.31; Main Paper Appendix B.2). Increasing the training batch size also yields no consistent improvement. In contrast, our post-training achieves substantial gains within ten epochs.
Alternative post-training methods use more compute yet do not match our quality–coverage frontier. While many recent methods require training from scratch, we focus on two representative post-training methods, CAFM and MixFlow. We measure the per-update runtimes of their released implementations under the same eight-H200 protocol and combine them with the official training schedules used to obtain their reported final checkpoints. CAFM's schedule includes discriminator updates and Jacobian-vector products and corresponds to 121.60 H200 GPU-hours (2.19× ours). MixFlow's final checkpoint is trained for 200 epochs, corresponding to 454.05 H200 GPU-hours (8.17× ours) (Revised Supplementary Sec. J, Table 8). Thus, the official schedules used to produce these methods' reported final checkpoints already require much more post-training compute than ours, yet their quality–coverage frontiers remain behind ours. Our advantage therefore does not come from a larger post-training budget.
One epoch of efficient post-training further advances stronger generators. Just one additional epoch of our post-training further expands the quality–coverage frontiers of already stronger CAFM and REPA generators (Revised Supplementary Sec. F, Fig. 2). For reference, one epoch at our profiled SiT training rate corresponds to approximately 5.56 H200 GPU-hours (~42 minutes on one 8×H200 node).