acceptodds
Under review as a conference paper at ICLR 2027

Data Selection for Conditional Flow Matching via State–Velocity Geometry

Abstract

Data selection for Conditional Flow Matching (CFM) asks a basic question: *when can one training sample replace another without changing the state-dependent velocity supervision used to learn the flow?* As Flow Matching scales to larger datasets, full-data training becomes increasingly expensive. However, existing data selection methods typically define sample redundancy through static representations or sample-level scores, so samples that appear redundant may still provide distinct supervision for the learned velocity field. Our key insight is that CFM redundancy should be defined by the *state–velocity geometry* of its supervision, with endpoint distance describing zero-order prescribed supervision and local velocity response capturing first-order sensitivity to state changes. Guided by this view, we introduce **State-Jac**, a lightweight one-shot selector that combines endpoint coverage with proxy-based local-response sketches while leaving final CFM training unchanged. Across balanced, long-tailed, and larger-scale paired benchmarks, State-Jac achieves consistent gains in generation quality and rollout fidelity. On CIFAR-10 and ImageNet-100 at a 20% data budget, State-Jac achieves a best-run FID reduction of **9.2%** relative to random selection. On ImageNet-100, its total GPU cost is **24.61%** of that of full-data training.

Primary area:
generative models
Keywords:
flow matching, data selection, coreset selection

Reviews

Among:
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1234this paper, Top 30%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_3R3POpenReview ↗
Rating
3(+1)
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper investigated the problem of training data selection for Conditional Flow Matching (CFM) and proposes State-Jac method. It combines target endpoint features with local velocity response features to select training samples based on coverage of the target within the joint feature space. The theoretical analysis establishes a relationship between endpoint distance and the discrepancy in prescribed state-velocity supervision under shared source noise. It further analyzes the closed-loop trajectory error between the full-data model and the subset model and characterizes differences in the state Jacobian through local perturbations and random directional probing. Experiments cover super-resolution tasks on CIFAR-10, CIFAR-100, Long-tailed CIFAR-10, and latent ImageNet-100.

Critical strengths
  1. This paper proposes a selection representation related to the CFM structure. Compared to using only static semantic features, the response of the velocity field to state perturbations provides a different type of information. I believe leveraging this for data selection is potentially a promising avenue for research

  2. The paper is generally theoretically grounded. The fundamental derivations hold under the stated assumptions. The endpoint identity in Section 3.1, the closed-loop error decomposition in Section 3.2, and the results regarding local response and random directional probing in Section 3.3 are all clearly presented. Appendix A provides further elaboration on these derivations and the practical approximations involved.

Critical weaknesses

W1: Theoretical analysis does not yet sufficiently support the claim of data interchangeability

Section 3 analyzes the distance between supervision pairs, the trajectory errors of the two models, and the Jacobian differences at various samples, yet it fails to establish a link between the coverage error in Equation (15) and the retraining model field error in Equation (5). Furthermore, the rationale behind choosing the sum of the state difference and the target velocity difference, as well as its relationship to training loss or parameter gradients, remains insufficiently explained. Additionally, uniformly sampling representative points may alter the probability mass of the original data. Equation (80) in Appendix A.8 explicitly includes a mass mismatch term that is not controlled by the coverage objective. As a result, the current theory serves better as a heuristic for representation design rather than a guarantee that learning outcomes will remain similar following sample substitution.

W2: Lack of Comparison Methods

The baselines in Table 1 mainly cover static features and scalar difficulty metrics, lacking representative methods for gradient-based subset selection or distribution matching. This setup relates to one-shot data curation, coreset selection, and certain active learning approaches. It is suggested that the authors should clarify these procedural differences and compare against strong baselines that share comparable informational assumptions. More importantly, the study lacks comparisons, under identical settings for the proxy model, compression dimensions, and selection mechanisms, between the proposed method and approaches based on standard features, speed prediction, or response representations. In Table 2, State-Jac does not outperform all simple variants on CIFAR-10, and the CIFAR-100 results omit the "Response-only" setting.

W3: Actual performance-to-cost advantages and budgetary patterns have not yet been established.

There remains a significant gap between State-Jac and Full: the CIFAR-10 FID is 15.102 versus 7.555, and the ImageNet-100 FID is 15.274 versus 12.917. While this does not negate the method's value under budget constraints, Figure 4(c) lacks a comparison with Full and Random baselines at equivalent total costs. Thus, it does not yet demonstrate that data selection is more cost-effective than simply increasing the training volume. The primary experiments utilize only a 20% retention rate, with 40% results appearing solely in the long-tail setting of Table 3. Performance-versus-total-cost curves across more sample budget ratios are highly recommended to identify the practical range for compression.

Questions for authors

Q1: What is the practical value of this selection setup?

The full set of target data is available prior to selection, yet the performance of the subsets in Table 1 and Table 3 remains significantly lower than that of the "Full" set. What specific resource constraints do the authors aim to address? Does State-Jac outperform direct training on the "Full" or "Random" sets given the same total computational budget? Could the authors provide performance-vs-cost curves across various retention ratios, rather than just the results for the 20% setting used in the main benchmarks?

Q2: Why does the proposed geometry allow for determining the interchangeability of training samples?

How do the distance and Jacobian results from Section 3 relate to the training impact of sample replacement? Specifically, why does reducing the coverage error in Equation (15) improve the model field discrepancy addressed in Equation (5)? ​​Which conclusions are theoretically supported, and which serve merely as heuristic motivations for the selector? Why does the proposed geometric approach enable the assessment of training sample interchangeability?

Q3: Does the method's performance depend on the specific conditional structure of the restoration task setting? If not, could you please explain in more details. Thanks!

All experiments utilize paired super-resolution of the form (c=g(x))(c=g(x)). If the condition is not generated by a deterministic target, can the joint distance between endpoints and responses still effectively serve as a selection criterion? How should the authors qualify their conclusions regarding data selection for general CFM?

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

The paper proposes State-Jac, a one-shot data selection method for Conditional Flow Matching. Each training pair is described by (i) its endpoint and (ii) a sketch of a lightweight proxy model's local velocity response to shared random perturbations, which approximates Jacobian discrepancy. The endpoint feature is motivated by an identity showing that, under a shared source sample, Rectified-Flow state and velocity discrepancies equal (4/3)‖x_i − x_j‖². The scale-matched features are covered by K real representatives, and the final model is trained on this subset with the unchanged CFM loss. Experiments on CIFAR-10/100 8×8→32×32 super-resolution, CIFAR-10-LT, and ImageNet-100 latent restoration show FID gains over random selection at a 20% budget (e.g., 16.42 → 15.27 on ImageNet-100). The paper also includes correlation analyses and an intervention showing that reference-path agreement does not ensure closed-loop fidelity.

Critical strengths
  • Defining redundancy as interchangeable velocity supervision is a sensible, CFM-specific framing.
  • The mechanistic analyses are informative: covering distortions correlate with FID and drift (ρ=.89/.93), and the cluster-mass intervention shows that reference-path fit does not ensure closed-loop fidelity.
  • Gains over random selection are consistent across datasets and seeds, and the selector overhead is low.
Critical weaknesses
  • All experiments are paired super-resolution, where the condition already determines most of the output. It is unclear whether the method helps in class-conditional, text-conditional, or unconditional generation.
  • The gains are modest relative to the gap to full data (CIFAR-10: 16.50 → 15.10 vs. 7.56; ImageNet-100: 16.42 → 15.27 vs. 12.92). Moderate-DS and the Residual variant are close, and several baselines are single runs.
  • Existing diffusion/FM data-pruning and coreset methods are cited but not compared, and there is no compute-matched comparison with full-data training. Proposition 1 also assumes a shared source sample, which does not hold in actual CFM training.
Questions for authors
  1. Under equal total compute (~22.9 GPU-hours on ImageNet-100, including proxy training), how does State-Jac compare with training on the full dataset?
  2. How does State-Jac compare with at least one existing diffusion/FM data-pruning method?
  3. Do the gains hold in a non-restoration setting such as class-conditional CIFAR-10 or ImageNet generation?
Reviewer_j7DnOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper studies one-shot data selection for conditional flow matching (CFM). It defines two samples as interchangeable when two things hold:

Zero-order: their prescribed state–velocity supervision is close. For Rectified Flow with a shared source sample and time, this reduces exactly to (4/3)‖x_i − x_j‖² (Prop. 1). First-order: the full-data field responds similarly to state perturbations at their reference states. This is measured by state-Jacobian Frobenius distance and estimated through shared directional probes (Props. 2–3).

The method, State-Jac, works as follows:

Train a small proxy CFM on the full pool. Compute finite-difference responses at 4 times × 2 Rademacher directions, project them, and standardize them into a 512-d signature. Concatenate this signature with the raw target after scale matching. Select K real examples by k-medoids-style quantization. Train the final model uniformly on the selected subset.

Critical strengths

The question is well posed. Asking what makes samples interchangeable for the CFM objective, rather than borrowing generic embeddings or difficulty scores, is a sensible angle. The selector leaves final training untouched, so it composes with existing pipelines. The method is cheap: one proxy run plus forward passes. The ImageNet-100 cost accounting is complete and transparent (proxy, extraction, quantization). The appendix diagnostics are useful: proxy-vs-full response rank agreement (Table 5), measurement-state choice (Table 6), sketch sensitivity (Table 8) and selector-seed stability (Table 7). The Own/Drift diagnostics are carefully defined (App. B.1). The cluster-mass intervention is a nice controlled experiment.

Critical weaknesses
  1. The theory–method link is weaker than presented. (a) Prop. 1’s constant has no effect on the algorithm. The proposition is elementary, since the shared z cancels. Because λ_match is calibrated as C_β·E‖Δφ‖²/E‖Δρ‖², squared distances in ψ equal C_β·(‖Δφ‖² + c‖Δρ‖²) with c independent of C_β. So C_β is a global scale and the quantization argmin does not depend on it, nor on the linear-path extension in A.1. In practice, then, the zero-order block is plain pixel distance (CIFAR) or latent distance (ImageNet), i.e. k-medoids on raw targets. The shared-z coupling also does not reflect training, where source noise is drawn independently per sample, and Prop. 1 ignores the condition input entirely. (b) The first-order motivation does not follow from Sec. 3.2. In Eq. (4)–(5), the state-error propagation term involves only v_F and J_F, which do not depend on the selected subset. Selection only affects δ_B. Read literally, the Grönwall bound motivates keeping δ_B small where the full field is sensitive (large L(t)). That is sensitivity-weighted coverage, not covering a pairwise Jacobian-difference metric between samples. Pairwise Jacobian similarity as a substitutability criterion is a plausible heuristic, but the paper presents it as derived. Please either connect the covering radius in d_resp to δ_B, Own, or Drift, or reframe it as a heuristic. (c) The practical feature departs from the Frobenius geometry. It applies coordinate-wise standardization after a random projection, uses a single fixed z_i per sample, and measures at reference rather than rollout states. Props. 5–6 cover some of these approximation steps, but not the standardization.

  2. The gains are modest, and the evidence that the combination matters is thin.

  • CIFAR-10 FID: State-Jac 15.10±.14, Residual 15.08±.24, Response-only 15.37±.19, Endpoint 15.53 (single run).
  • Residual has the best FID and Response-only has the best Own/Drift. Most differences are within 1–2 std, and Endpoint has no error bars. “State-Jac balances both” is weak support for complementarity.
  • Missing ablations: the CIFAR-100 ablation omits Response-only. ImageNet-100 compares only Random20 against State-Jac20, with no Endpoint-only or other selector. At the scale that matters most, we cannot tell whether response features help over latent-space k-medoids.
  • CIFAR-10-LT: results are single runs with small differences (Own 33.7 vs 33.3; Drift 8.25 vs 8.13), so “improves every reported metric” is not established.
  • No weighting sweep: there is no sweep of the endpoint/response weighting. Such a sweep would interpolate between Endpoint and Response-only and test complementarity directly.
  • Missing control: proxy features that are not Jacobian-based, such as proxy velocity outputs v_p(q_i(t_k)) or hidden activations under the same projection and standardization. This would show whether the finite-difference response specifically matters, or whether any proxy-derived feature helps.
  1. Baselines and the compute comparison. Data-pruning baselines for generative models that are cited in Sec. 2 are not compared:
  • clustering-based diffusion pruning (Briq et al., 2024)
  • pruning-then-reweighting (Li et al., 2025)
  • ELFS (Zheng et al., 2025)
  • gradient coresets (CRAIG, GradMatch) computed on the proxy

A compute-matched full-data baseline is needed. On ImageNet-100, train on the full data for roughly 22.9 GPU-h, State-Jac’s total budget. The relevant question is whether selection beats simply training on everything for fewer steps. On CIFAR, the paper states that all primary methods use 33,548 steps. Does Full use the same number? If so, there is no compute saving on CIFAR. The gap to full data remains large: CIFAR-10 FID 15.1 vs 7.6, ImageNet-100 15.3 vs 12.9. A budget sweep (e.g. 10–50%) would show where selection matters. It would also show how these results relate to Briq et al. (2026b), whose finding that Flow Matching is robust to pruning the paper cites.

  1. Statistical reporting. State-Jac reuses one fixed manifest across seeds, while Random resamples its subset. State-Jac’s ± therefore excludes selection variance. Table 7 shows Jaccard ≈0.6 across selector seeds, so please report FID for several selector seeds. The abstract headlines a “best-run FID reduction of 9.2%”. The mean reductions implied by the tables are about 8.4% (CIFAR-10) and 7.0% (ImageNet-100). Means, not best runs, should be reported. Several Table 1 baselines are single runs.

  2. Evaluation scope. Only paired super-resolution is evaluated, where c = g(x) is deterministic. The title and abstract frame the method as general CFM data selection, but unconditional, class-conditional and text-conditional generation are untested. For super-resolution, FID-10K alone is unusual. Consider adding input-consistency (downsample the output and compare to c), PSNR/LPIPS, and a diversity measure. Own/Drift measure agreement with the full-data model. That is a reasonable diagnostic, but it is not a quality measure. It is also partly circular, since the response features come from a proxy trained on that same full data.

  3. The Q3 “counterexample” has a simpler explanation. Cluster-mass sampling concentrates training on a few large-cluster representatives. This reduces the effective number of distinct examples, which could degrade rollout behaviour and FID regardless of the closed-loop argument. Please report the effective sample size (e.g. 1/Σp_b²) and a memorization check. Note also that this result is a single run. That reference-state agreement does not imply rollout fidelity is also closely related to the well-known exposure-bias phenomenon. Its framing as a contribution should be softened.

Questions for authors
  • Does Full use the same step count as the subset runs on CIFAR? What does full-data training achieve at matched total compute?
  • What is State-Jac’s FID across ≥3 selector seeds (probe, solver and z_i seeds)?
  • What do Endpoint-only and Response-only give on ImageNet-100?
  • How sensitive are results to the endpoint/response weighting?
  • What are the proxy architecture and training budget for the ImageNet-100 latent setting?
  • How were the 30 manifests in Table 11 generated? Do the correlations hold within method families, rather than being driven by between-method clusters?

Minor

  • Eq. (2) sums state and velocity discrepancies with equal weights despite different units. Worth a remark, though it is moot given the C_β cancellation.
  • Fig. 1(a) shows a single illustrative sample. Please use several random samples or drop it.
  • Bring the definition of “Worst” (maximum class-mean Own) into the main text.

Comments on the paper

2 comments
Area_Chair_XdkSOpenReview ↗

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Thanks for the reply. I believe the explanations and extra results have addresses most of my concerns and I will raise my score to 3.

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