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Under review as a conference paper at ICLR 2027

CONSTRUCT-FIRST FLOW MATCHING FOR FEW-PASS TIME-SERIES GENERATION

Abstract

Short-window time-series generation requires reproducing both temporal depen- dence and non-Gaussian structure, some of which can be estimated directly from training data. How much learned dynamics remain necessary once these compo- nents are supplied explicitly? We investigate this question through construct-first flow matching, which combines a fitted Gaussian reference, a learned residual ve- locity, and fixed, structure-dependent output transformations. The Gaussian com- ponent is propagated analytically, and the teacher is distilled into one or two neural maps before the output transformations are applied. For the Gaussian reference flow with an isotropic source, we show that uniform-grid Euler requires Θ(√κ) steps to resolve the smallest-variance direction to fixed relative accuracy, where κis the ratio of source variance to the smallest data variance. Analytic propaga- tion eliminates this component’s discretisation error. On six short-window bench- marks, we evaluate generation using splits without timestamp overlap, memori- sation diagnostics, and re-evaluation on a separate test split. Among configura- tions not flagged by the diagnostics, our method achieves the lowest RFF-C2ST score on four datasets on both evaluation splits, using zero to two neural evalua- tions. Ablations reveal distinct contributions: learned dynamics improve ETTh1 and Stock, interact beneficially with the transformations on Energy, and are not required to attain the reported scores on Sines, MuJoCo, and fMRI. These results show where direct statistical construction can replace neural generation and where combining the two remains beneficial.

Primary area:
learning on time series and dynamical systems
Keywords:
time series generation, flow matching, few-step sampling, generative model evaluation, memorisation

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1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_Qe8rOpenReview ↗
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Paper summary

Construct-first flow matching combines a fitted Gaussian reference, a learned residual velocity, distillation into one or two neural maps, and fixed output transformations estimated from training data. The Gaussian component is propagated analytically, avoiding its numerical integration error.

The paper analyzes uniform-grid Euler complexity for the Gaussian reference problem and evaluates six short-window time-series benchmarks. Component ablations distinguish where learned dynamics help from where statistical construction alone achieves the reported scores. Evaluation includes non-overlapping splits, memorization diagnostics, and confirmation on a separate test split.

Critical strengths
  • The component ablations directly address the paper’s central question. Table 3 separates the skeleton, teacher, student, and output transformations. Learned dynamics help on ETTh1 and Stock, interact beneficially with the transformations on Energy, and are unnecessary for the reported scores on the other three datasets. This is useful evidence about when neural generation adds value beyond statistical construction.

  • The evaluation carefully examines leakage and memorization. The paper audits overlapping-window evaluation, applies the same memorization diagnostics to all methods, and excludes problematic variants of its own approach. Re-evaluation on a separate test split strengthens the evidence after development on validation data. Reporting end-to-end costs also gives a more useful efficiency comparison than neural-call counts alone.

Critical weaknesses
  • The construction procedure still depends on substantial dataset-specific choices. Detector firing does not determine whether a transformation is installed, and the skeleton family and transformation set lack a unified selection rule. Some configurations also encode dataset-specific knowledge, such as Energy’s tied-channel constraint. The experiments establish that the selected configurations work, but provide less evidence that another user could reliably construct an effective generator for a new dataset. This limits the method’s value as a reusable procedure.

  • The practical contribution of analytic propagation is not isolated from the rest of the pipeline. The theorem establishes an integration cost for a specific Gaussian reference problem with an isotropic source and uniform-grid Euler. The experiments, however, combine analytic propagation with residual learning, distillation, and output transformations. Table 3 separates statistical construction from learned dynamics, but does not establish the incremental benefit of the propagator over alternatives using the same covariance information. A covariance-matched source with comparable training and post-processing is a particularly relevant unresolved comparison.

Questions for authors
  • Which decisions in Table 6 follow a fixed selection procedure, and which require manual judgment? Please clarify how a user would choose the skeleton and installed transformations for a new dataset without reproducing the development search.

  • Do existing experiments isolate analytic propagation against a covariance-matched source or a conventional flow teacher while keeping distillation and output transformations comparable? This would help determine how much practical benefit comes specifically from the proposed integration design.

2 comments
AuthorsOpenReview ↗

reply (1/2)

Thank you for the precise questions. We answer in two parts. Table and section numbers refer to the submitted PDF; scores are RFF-C2ST, lower is better.

W1 (firing does not determine installation; no unified rule; evidence for a new dataset). We now let firing determine installation: every screen of Table 1 runs on the training split and whatever it detects is installed, with one precedence clause written before the runs. Against the submitted configurations (differences paired by seed):

datasetsubmitted (Table 2)one rule
ETTh1.560identical samples, 5 of 5 seeds
Energy.727identical samples, 3 of 3 seeds
Sines.503identical samples, 3 of 3 seeds
Stock.586-.001 [-.008, +.006]
MuJoCo.895+.002 [+.0004, +.0041]
fMRI.535-.006 (one sample per arm)

A new dataset. ETTh2, which no part of this work had touched: no decision by hand, no validation or test score in any setting, the remaining settings those of ETTh1; five baselines trained with their ETTh1 recipes.

ETTh2 (real vs. real .576)score
Ours, one rule, nothing chosen on ETTh2 (5 seeds).637 +- .001
FlowTS / TimeFlow / TimeBridge / Diffusion-TS.689 / .724 / .729 / .753
ImagenTime (flagged by the memorisation gate)(.657)

The skeleton with the same transforms and no network call scores .688 to .690 there. (A correction in our favour: the memorisation gate also flags ImagenTime on ETTh1, memorised fraction .44 to .45 against the threshold .10, so ours is the lowest unflagged score on five of the six datasets; the revision corrects Table 2.)

Q1 (which decisions are fixed, which manual; how a user proceeds on a new dataset).

decisionhow it is setdata it reads
which components are installedone rule (above) plus the precedence clausetraining split
split unitfixed by the data layoutdata layout
student metric; teacher step count; one or two calls; the smoothing coefficientheld-out ruleinternal subset of the training split
level-and-scale variant (exact / copula)the memorisation gategenerated sample and training split
skeleton familymanual in the submission; a rule gives the same results (below)internal subset of the training split
tied-channel pair on Energy; Sines decode settings; coefficient gridmanual-
fMRI: the construction arm is the reported onemanual, on validation; confirmed on the test splitvalidation split

The skeleton family by a rule. Generate the zero-pass sample under each of the three families and keep the one with the lowest held-out, training-internal score (no validation data, no network call). This returns the submitted family on ETTh1, Energy, MuJoCo and fMRI. On Stock and Sines it returns another, and the final score changes by +.011 ([-.036, +.058], five paired seeds; not separated) and -.001; on ETTh2 its choice changes the score by +.004 ([-.001, +.008]; not separated). The reported results do not depend on the hand choice.

A new dataset. Run the screens on the training split; install what fires; apply the clause; choose the family by this rule; take the remaining settings from the submitted dataset of the same data type; let the held-out rule pin the coefficient. ETTh2 above is that procedure, with no decision taken by hand. Each screen of Table 1 other than the tied-variates row is a fixed rule at a fixed threshold, and the submitted ETTh1 configuration retrains from scratch to the same numbers (checked on one seed).

AuthorsOpenReview ↗

reply (2/2)

W2, Q2 (analytic propagation against a covariance-matched source or a conventional flow teacher, with distillation and output transformations comparable).

Covariance-matched source. The submission has it as the negative control of Thm. 4.3; the comparison on generated samples is new. Flow matching in whitened coordinates is, after un-whitening, the matched-source flow; what does not carry over is the loss metric and the coordinates of the network, so we ran all variants. Network, budget, seeds and output transforms are shared, and every arm gets the exact propagation of its own reference (ETTh1, five paired seeds):

where the covariance entersteacher, 100 stepstwo distilled passes
in the field (the paper).611.627
in the source.736.765
in the source, whitened-coordinate loss.676.693
whitened coordinates throughout (loss, network, students), tuned in its favour.625.656

The last row is the alternative at its best: its learning rate is the best of five and its distillation the best of 66 configurations, both chosen on the validation split, while ours stayed as submitted. Its teacher is then not separated from ours (+.014, [-.002, +.030]); its two passes stay behind by +.029 ([+.015, +.043]) on validation and +.030 ([+.020, +.040]) on test (+.063 and +.018 with the output transforms), five of five seeds, unchanged at nine times our student's training. On a symmetric tuning grid the construction is ahead of the whitened-loss arm at eight of eight configurations, and on Stock that arm is behind by +.092 ([+.064, +.120]) at the teacher and +.083 ([+.055, +.110]) after the one distilled pass. With standard solvers at 2 to 10 evaluations (five solvers including DPM-Solver++(2M), the best per budget chosen in its favour) the fully whitened teacher is behind our two passes up to six evaluations (+.205 at two, +.013 at six) and not separated from seven on.

The propagator itself. Isolated on the same trained field with only the integrator changed, its effect is in the few-step regime, where the theorem places it: Euler at 4 to 32 steps keeps .07 to .22 of the variance in the smallest 10% of directions, exact propagation .995 to 1.000 (App. "Proofs and Numerical Verification"). At the 100-step teacher we attribute no score gain to it; the score differences come from where the covariance enters.

Conventional flow teacher. The same network, data and training budget, isotropic source, no reference field (the network learns the whole velocity), Euler at 100 steps; then our distillation and our output stage, unchanged. Its learning rate and training length come from a grid of eight on a held-out training-side criterion. Five paired seeds:

conventional minus oursStockETTh1
teacher, 100 steps+.135 [+.117, +.152]-.025 [-.053, +.002]
with distillation and the output stage+.107 [+.084, +.130]-.035 [-.055, -.016] on validation; -.002 [-.012, +.008] on test

On Stock the reference field is what makes the learned stage work: without it the score is worse in five of five seeds, all eight settings of the conventional teacher are behind ours on the tuning seed, and 1,000 Euler steps or Heun do not help it. On ETTh1 the conventional teacher is not separated from ours at the teacher, is lower on the validation split and not separated on the test split; the samples of both variants pass the memorisation gate. So, with distillation and output transformations held equal, the reference field is decisive on Stock, and on ETTh1 the two are not separated on the test split.

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Paper summary

This paper proposes Construct-First Flow Matching for short-window time-series generation. The main idea is to explicitly construct statistical structure that can be estimated directly from training data, rather than asking a neural flow model to learn and numerically integrate everything.

The method decomposes generation into a fitted Gaussian covariance “skeleton,” a learned residual flow, distillation into one or two student passes, and several fixed dataset-dependent output transformations. The paper also derives a step-complexity result showing that uniform-grid Euler integration of the Gaussian reference can require steps in highly anisotropic directions, while the proposed Gaussian propagator integrates this component exactly.

Experiments on six short-window benchmarks use a zero-timestamp-overlap split, memorization diagnostics, and a separate confirmatory split. The reported system obtains the best unflagged RFF-C2ST score on four datasets while requiring zero to two neural evaluations.

Critical strengths
  • The zero-timestamp-overlap split and explicit memorization gate expose serious weaknesses in commonly used time-series generation evaluations. Applying the diagnostics to both baselines and the proposed method is a strong aspect of the paper.

  • The exact Gaussian propagator and the analysis of low-variance directions provide a meaningful explanation for why standard uniform-grid integration can struggle. The ablations also clearly identify when the learned residual actually helps.

Critical weaknesses
  • The skeleton family and installed transformations are selected separately for each dataset, some choices have no general selection rule, and one constraint is manually specified. Moreover, 95 configurations were evaluated on the validation scorer. The authors correctly acknowledge that re-evaluating on another split using the same scorer cannot rule out overfitting to the evaluation instrument itself. This substantially weakens the evidence that the proposed pipeline would generalize to unseen datasets without similar manual analysis and tuning. This concern is particularly important because the learned flow is only clearly beneficial on ETTh1 and Stock, with an interaction benefit on Energy; the reported Sines, MuJoCo, and fMRI results can be achieved without the learned dynamics. On Sines, the final output is entirely replaced by a fitted sinusoidal-family generator.

  • The level/scale transformation globally matches a generated batch to training-derived statistics using an (O(N^3)) assignment and can reproduce the training multiset of level/scale pairs. This makes samples batch-dependent and substantially complicates comparison with ordinary generative models. Accordingly, while neural evaluation is extremely cheap, the paper reports only a 1.6×–11× end-to-end speed advantage because this assignment dominates inference cost. The theoretical result also applies specifically to the Gaussian skeleton rather than to the complete learned flow.

Questions for authors
  • Can the authors demonstrate a genuinely dataset-agnostic version of the method in which the skeleton family, installed transformations, and their hyperparameters are selected by a fixed rule without inspecting validation performance? Performance on a dataset not used while designing these rules would materially strengthen the paper.

  • How much of the reported advantage remains if the batch-level level/scale assignment and other dataset-specific post-processing are removed? In particular, can the authors compare the skeleton + learned residual + distillation pipeline alone against few-step flow baselines?

  • The theoretical step-complexity result concerns uniform-grid Euler on the Gaussian reference problem. Can the authors quantify how much of the empirical gain over modern baselines is actually attributable to eliminating this integration error, versus the student distillation and post-sampler transformations?

4 comments
AuthorsOpenReview ↗

reply (1/2)

Thank you for the careful reading. We answer in two parts. Table and section numbers refer to the submitted PDF; scores are RFF-C2ST, lower is better.

W1, Q1 (no general selection rule; a dataset-agnostic version; a dataset not used in design).

Transforms. One rule for all six datasets: every screen of Table 1 runs on the training split and whatever it detects is installed, with one precedence clause written before the runs. Against the submitted configurations (differences paired by seed):

datasetsubmitted (Table 2)one rule
ETTh1.560identical samples, 5 of 5 seeds
Energy.727identical samples, 3 of 3 seeds
Sines.503identical samples, 3 of 3 seeds
Stock.586-.001 [-.008, +.006]
MuJoCo.895+.002 [+.0004, +.0041]
fMRI.535-.006 (one sample per arm)

Skeleton family. It can be chosen on the training split alone: generate the zero-pass sample under each of the three families and keep the one with the lowest held-out, training-internal score (no validation data, no network call). This returns the submitted family on ETTh1, Energy, MuJoCo and fMRI; on Stock and Sines it returns another, and the final score changes by +.011 ([-.036, +.058], five paired seeds; not separated) and -.001. The reported results do not depend on the hand choice. Hyperparameters. The smoothing coefficient, the student metric and the number of passes are set by a held-out rule on an internal subset of the training split, in every run. The tied-channel pair on Energy remains manual, as the paper states.

A new dataset. ETTh2, which no part of this work had touched: no decision by hand, no validation or test score in any setting, the remaining settings those of ETTh1; five baselines trained with their ETTh1 recipes.

ETTh2 (real vs. real .576)score
Ours, one rule, nothing chosen on ETTh2 (5 seeds).637 +- .001
FlowTS / TimeFlow / TimeBridge / Diffusion-TS.689 / .724 / .729 / .753
ImagenTime (flagged by the memorisation gate)(.657)

W1 ("95 configurations ... overfitting to the evaluation instrument"). No reported configuration was selected on the test split (Table 11), and nothing at all was selected on ETTh2. The field's own discriminative and predictive scores, never our selection instrument, are in Table 12.

W1 ("the learned flow is only clearly beneficial on ETTh1 and Stock"). This dataset-dependence is what the paper sets out to measure, and Table 3 is the answer: a zero-pass construction has the lowest unflagged score on Sines and fMRI among thirteen published generators, which is a finding about what those benchmarks certify. Where the data requires dynamics the learned stage supplies them: on ETTh1 and Stock, and on ETTh2 (.688 to .690 with no network call, .637 with it).

Q2 (without post-processing). Table 3, row 3 removes every output transform: .627 (ETTh1), .585 (Stock), .934 (Energy), .969 (Sines), .993 (MuJoCo), .801 (fMRI). Two results stand with no post-processing at all: on Stock no unflagged baseline of Table 7 reaches our one-pass .585 at any step count (best .636), and on ETTh1 our two passes are at the level the flow baselines reach only with 50 to 100 steps (TimeFlow .640 / .622, FlowTS .681 / .612; .92 to .99 at two steps). On the other four datasets the constructed layers carry the result, which is the paper's finding (Table 3, Sec. 7).

Q3 (how much is due to removing integration error, to distillation, to the transforms).

  • Integration error. At the 100-step teacher, none of the score gain. What analytic propagation removes is the reference's discretisation error and its step cost, and its effect is in the few-step regime: with only the integrator changed, Euler at 4 to 32 steps keeps .07 to .22 of the variance in the smallest 10% of directions, exact propagation .995 to 1.000.
  • Distillation. The student is behind its teacher by .016 on ETTh1 (.611 to .627) and .015 on Stock (.570 to .585).
  • Output transforms. .627 to .560 on ETTh1, .934 to .727 on Energy, none on Stock.
  • Where the covariance enters. +.03 to +.14 at two passes on ETTh1 and +.08 on Stock (part 2/2).
AuthorsOpenReview ↗

reply (2/2)

W2 (level/scale assignment: batch-dependent, cubic cost, reproduces the training pairs). The cost is stated in Sec. 8 and included in the end-to-end timings, which is why the paper reports 1.6x to 11x. New: the reported scores do not depend on matching a whole batch. We re-ran the output stage with only the assignment replaced (change against the reported arm, paired by seed):

level/scale assignmentETTh1 (.560)Energy (.727)MuJoCo (.895)fMRI (.535)time
inside sub-batches of 256 windows+.002 [-.001, +.005]-.008 [-.068, +.051]+.003 [-.000, +.007].0001/40 to 1/110
cross-fitted (no window's pair depends on the windows generated with it)+.004 [-.004, +.011]-.011 [-.044, +.021]+.002 [-.007, +.011]+.0031/2.5 to 1/4
per window: the nearest training pair+.007 [-.016, +.029]-.013 [-.069, +.043]-.016 [-.019, -.014]-.0091/7 to 1/80
per window: an independent draw+.013 [+.006, +.020]-.003 [-.109, +.104]+.018 [+.010, +.026]+.004negligible

Sub-batches and the cross-fitted map are not separated from the reported arm on any dataset. Even with the fully independent per-window draw, which involves no batch at all, ours remains the lowest unflagged score: .573 against .619 on ETTh1, .724 against .871 on Energy, .540 against .759 on fMRI (on ETTh1 ImagenTime is flagged by the memorisation gate, memorised fraction .45; the revision corrects Table 2, which makes ours the lowest unflagged score on five of the six datasets). The cross-fitted and per-window variants do not reproduce the training multiset (they use 26 to 64% of the distinct training pairs). Drawing the pairs from a Gaussian copula, so that no training pair is reused at all, changes the score by +.001 on ETTh1 ([-.007, +.009]) and +.026 on Energy ([-.004, +.055]), against leads of .144 on Energy and .224 on fMRI. Windows are not copies: on ETTh1 the memorised fraction is .000 and 4096 of 4096 windows are unique.

W2 ("the theoretical result applies to the Gaussian skeleton rather than to the complete learned flow"). By design: the reference flow is where the step cost sits and the part that can be analysed exactly (Sec. 1; Thm. 4.3). For the complete flow we measured the design choice the theorem motivates, against using the same covariance in the source or by whitening. Network, budget, seeds and output transforms are shared, and every arm gets the exact propagation of its own reference (ETTh1, five paired seeds):

where the covariance entersteacher, 100 stepstwo distilled passes
in the field (the paper).611.627
in the source.736.765
in the source, whitened-coordinate loss.676.693
whitened coordinates throughout (loss, network, students), tuned in its favour.625.656

The last row is the alternative at its best: its learning rate is the best of five and its distillation the best of 66 configurations, both chosen on the validation split, while ours stayed as submitted. Its teacher is then not separated from ours (+.014, [-.002, +.030]); its two passes stay behind by +.029 ([+.015, +.043]) on validation and +.030 ([+.020, +.040]) on test, five of five seeds, unchanged at nine times our student's training. On a symmetric tuning grid the construction is ahead of the whitened-loss arm at eight of eight configurations, and on Stock that arm is behind by +.092 ([+.064, +.120]) at the teacher and +.083 ([+.055, +.110]) after the one distilled pass.

Thank you for the detailed rebuttal and additional experiments. The dataset-agnostic configuration results on ETTh2, alternative level/scale assignment strategies, and covariance-placement ablations substantially address my original concerns.

However, I would like clarification on one important discrepancy. The submitted paper reports that ImagenTime on ETTh1 has a memorized fraction of 0.000 and is unflagged, whereas the rebuttal reports 0.45 and excludes it. Could the authors explain what caused this change and confirm whether the other baselines were evaluated consistently under the corrected protocol?

AuthorsOpenReview ↗

Response to the follow-up on ImagenTime (ETTh1)

Thank you. Both questions have a direct answer.

What caused the change. Nothing in the protocol: the rule (duplicate-window rate above 1% or memorised fraction above .10), its thresholds and its script are those of the submission, and no score changed. The difference is confined to the two diagnostic values quoted for this one entry in the appendix. We traced them: they match those of ImagenTime's Stock sample, on which the method is not flagged (it is the best unflagged baseline on Stock in Table 2), not those of its ETTh1 sample. On the ETTh1 sample the gate gives a memorised fraction of .45 against the threshold .10.

Why the ETTh1 value is reliable. It holds on the stored sample behind Table 2 and on two newly trained seeds (.45, .45, .44): 73 to 75% of the windows lie nearer to a training window than the first percentile of real-vs-real distances, and the authenticity is .006 to .008 (ours: .92). The paper's script, a second implementation and independent code reading the raw sample files agree, and in the same run the controls behave as they should (real validation and test windows .000; the training windows submitted as a sample 1.000). It also agrees with what the submission already reports for this entry: in the test-split appendix its ETTh1 score rises by .094 from validation to test, together with the gated methods (.089 to .091), described there as the arms "that reproduce the training windows most closely"; its validation lead is gone on the test split (.630 for both methods); and its validation score (.535) lies below the real-vs-real reference of Table 2 (.566).

Were the other baselines evaluated consistently? Yes, and we verified it for all of them rather than for this entry alone. With the same script and thresholds we recomputed the gate for all thirteen baselines on all six datasets (78 cells): 76 reproduce the flags of Table 2; besides this entry, the only change is TimeVAE on fMRI, a collapsed sample that is now flagged and alters no comparison. For the scores: the stored sample of every baseline on every dataset re-scores to the value logged for the submission within .005, our own six entries within .001, and a full retraining of our submitted configurations reproduces Table 2 within .008.

What depends on it. None of the submission's claims: the paper claims the lowest unflagged score on four datasets and does not claim ETTh1 on the validation split. With the entry flagged, ours (.560) is the lowest unflagged score on ETTh1 on validation (next: TimeFlow, .619) and on test (.630; next: TimeFlow, .662). The revision updates Table 2 and the text accordingly.

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Paper summary

The method fits a Gaussian skeleton to the training windows, integrates its flow-matching velocity exactly, learns a residual on top, and distills the result into a student that needs one or two passes. Per-dataset output transforms are applied afterwards. Thm 4.3 shows that with an isotropic source, Euler integration on a uniform grid needs Theta(sqrt(kappa/eps)) steps.

Critical strengths

The evaluation protocol includes an audit of train/test overlap in 11 codebases, block splits, a memorization gate applied to all methods, and a re-scoring on a third split. The ablations are informative and useful.

Critical weaknesses

I feel the methodological contribution of the paper is fairly modest and the application area (time series generation) somewhat limited for a conference of the caliber of ICLR. More precisely:

  1. The gains rest largely on hand-tuned, per-dataset post-processing. 95 configurations were tuned on validation data and chosen "without a rule", and the Sines output is a sinusoid draw. It is unclear what general method is being evaluated.
  2. The theory is modest. The closed-form Gaussian propagator is known. A geometric time grid reduces the cost to O(log kappa), and whitening the data removes it entirely.
  3. Several baselines are missing: flow matching on whitened data or with Gaussian-process / data-dependent priors (PriorGrad, TSFlow), reflow, and consistency, shortcut and MeanFlow students. The method is straightforward on the flow learning side, maybe the data is too simple to require more effort?
  4. The evidence is narrow. There is one primary metric, the baselines are single runs, scores on Energy and MuJoCo remain far from the null value, and ETTh1 degrades on the test split. The level/scale OT step reproduces the training (m, log s) values, which is a form of partial copying.
Questions for authors
  • How does flow matching in whitened coordinates with DPM-Solver at 2 to more steps (e.g. 10 steps) compare?
  • What are the results with one fixed transform configuration for all datasets?
  • What happens if the same transforms are applied to all baselines?
2 comments
AuthorsOpenReview ↗

Reply (1/2)

Thank you for the detailed review. We answer in two parts. Table and section numbers refer to the submitted PDF; scores are RFF-C2ST, lower is better.

"The methodological contribution is fairly modest and the application area somewhat limited." We disagree, on three counts.

  1. The paper shows what these benchmarks actually require. On Sines and fMRI a construction with zero network passes has the lowest unflagged score among thirteen published generators whose diffusion and flow samplers run 100 to 1000 steps; with one or two passes the same holds on Stock, Energy and ETTh1. Whether "the data is too simple to require more effort" is what Table 3 measures, per dataset.
  2. The evaluation this line of work relies on leaks training data into its test set. All eleven official codebases we audited split window rows at random (Table 5); under a split without overlap and one memorisation gate, three published methods are flagged on every dataset.
  3. Two passes give what whitening and the published flow baselines need many evaluations for (part 2/2).

The baselines are ICLR 2024 and NeurIPS 2024 papers: the topic is active at this venue.

W1, Q2 (hand-tuned post-processing; one fixed configuration). We fixed one rule for all six datasets: every screen of Table 1 runs on the training split and whatever it detects is installed, with one precedence clause written before the runs. Against the submitted configurations (differences paired by seed):

datasetsubmitted (Table 2)one rule
ETTh1.560identical samples, 5 of 5 seeds
Energy.727identical samples, 3 of 3 seeds
Sines.503identical samples, 3 of 3 seeds
Stock.586-.001 [-.008, +.006]
MuJoCo.895+.002 [+.0004, +.0041]
fMRI.535-.006 (one sample per arm)

Applied blind to ETTh2, never used in design and with nothing chosen on it: ours .637 (five seeds; real vs. real .576) against FlowTS .689, TimeFlow .724, TimeBridge .729 and Diffusion-TS .753; the skeleton with the same transforms and no network call scores .688 to .690, so the transforms do not carry this alone. Without any transform (Table 3, row 3) our two passes on ETTh1 (.627) are at the level the flow baselines reach only at 50 to 100 steps (TimeFlow .640 / .622, FlowTS .681 / .612; .92 to .99 at two steps), and our one pass on Stock (.585) at a level they do not reach (best .636). "95 configurations were tuned on validation data": the test-split re-score (Table 11) uses windows on which no reported configuration was selected, and on ETTh2 nothing was selected at all. "The Sines output is a sinusoid draw": the paper states this and presents Sines as a positive control for the detector (App. "Per-Dataset Diagnoses"), not as evidence about the learned flow.

Q3 (same transforms for all baselines). We passed the stored full-schedule samples of all thirteen baselines through our output stage (configured as for our own arm, coefficient re-selected per baseline by the same held-out rule) and re-scored them; values with +- are three training seeds.

datasetourslowest unflagged baselines: as is -> with our transforms
ETTh1.560TimeBridge .671 -> .593 +- .018; TimeFlow .619 -> .603 +- .008
Stock.586KoVAE .717 -> .693 +- .007; ImagenTime .715 -> .713 +- .008
fMRI.535TimeFlow .763 -> .550 +- .004; TimeBridge .756 -> .616 +- .042
Energy.727ImagenTime .998 -> .666; TimeFlow 1.000 -> .684 +- .001; PaCoDi .949 -> .705; WaveletDiff .983 -> .706

Ours remains the lowest unflagged score on ETTh1, Stock and fMRI (ours minus the best transformed baseline: -.034 on ETTh1, [-.070, +.003], not separated; -.107 on Stock, [-.133, -.081]; -.014 on fMRI, [-.024, -.005]). On Energy four transformed baselines score below ours; Table 3 attributes the Energy result to the transforms combined with the learned stage (.934 without them, .787 with them and no network, .727 with both). The transformed baselines still run tens to hundreds of network evaluations; ours uses one or two.

AuthorsOpenReview ↗

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W2, Q1 (theory; whitening; DPM-Solver at 2 to 10 steps). The propagator is not claimed as new (Sec. 2), and the geometric grid is the paper's Obs. 4.4 (34 to 74 steps at our kappa). The theorem gives the rate: for the Gaussian part alone, uniform-grid Euler needs 682 to 784,008 steps at the kappa of five of the six datasets; in the field it costs none. Its content is the few-step regime: Euler at 4 to 32 steps keeps .07 to .22 of the variance in the smallest tenth of directions, exact propagation .995 to 1.000.

We measured whitening. Flow matching in whitened coordinates is, after un-whitening, the covariance-matched-source flow; what does not carry over is the loss metric and the coordinates of the network, so we ran all variants. Network, budget, seeds and output transforms are shared, and every arm gets the exact propagation of its own reference (ETTh1, five paired seeds):

where the covariance entersteacher, 100 stepstwo distilled passes
in the field (the paper).611.627
in the source.736.765
in the source, whitened-coordinate loss.676.693
whitened coordinates throughout (loss, network, students), tuned in its favour.625.656

The last row is the alternative at its best: its learning rate is the best of five and its distillation the best of 66 configurations, both chosen on the validation split, while ours stayed as submitted. Its teacher is then not separated from ours (+.014, [-.002, +.030]); its two passes stay behind by +.029 ([+.015, +.043]) on validation and +.030 ([+.020, +.040]) on test (+.063 and +.018 with the output transforms), five of five seeds, unchanged at nine times our student's training. On Stock the whitened-loss arm is behind by +.083 ([+.055, +.110]).

With standard solvers (Euler, midpoint, Heun, RK4, DPM-Solver++(2M) on four grids; the best per budget, chosen on the scoring split in the alternative's favour; our two passes score .627):

function evaluations2345678910
covariance in the source.845.774.751.740.735.741.734.742.736
+ whitened-coordinate loss.807.735.699.686.692.683.675.677.679
+ network in whitened coordinates, best learning rate.832.730.671.642.640.630.625.623.624

The first two stay above our two passes at every budget. The third is behind at 2 to 6 evaluations (five of five seeds) and not separated from 7 on: whitened-coordinate flow matching needs seven evaluations for what the construction gives in two.

W3 (missing baselines). Flow matching on whitened data and a data-dependent Gaussian prior (the PriorGrad idea; on ETTh1 a stationary covariance with the empirical kernel, i.e. a fitted Gaussian-process prior) are the arms above; TSFlow's released unconditional configuration is univariate, whereas this protocol scores joint windows of 5 to 50 channels. Our students are plain regression students, and Table 3 bounds what a better one (reflow, consistency, shortcut, MeanFlow) could add: .016 on ETTh1, .015 on Stock. FlowTS (rectified flow) and TimeFlow score .92 to .99 at two steps (Table 7). New: SpectralMeanFlow sampled with its own sampler at 2 / 4 / 6 / 10 evaluations scores .793 / .697 / .669 / .641 on ETTh1 and .974 / .893 / .815 / .759 on Stock, above ours at every budget on all six datasets.

W4 (narrow evidence).

  • Single runs. We trained two further seeds of the two best unflagged baselines of every dataset. On Stock, Energy, Sines and fMRI ours is below every individual seed (smallest gaps .100, .135, .261, .202).
  • A correction in our favour. Those seeds showed that the memorisation gate flags ImagenTime on ETTh1 (memorised fraction .44 to .45 against the threshold .10; the values printed for that entry are wrong). Ours (.560) is then the lowest unflagged score on ETTh1 as well: five of six datasets.
  • One metric. Table 12 gives the field's own discriminative and predictive scores under the same protocol; Table 11 re-scores every arm on the test split.
  • Energy and MuJoCo far from the null. The claims there are relative to the baselines; on MuJoCo the scorer is near saturation (noise of 1e-3 of the value range added to real windows already gives .984 to .997; App. "Evaluation Protocol"), and the paper claims no lead there.
  • ETTh1 on the test split. Reported in Tables 10 and 11; ours remains the lowest unflagged score there (.630; next TimeFlow, .662).
  • Partial copying. Drawing the (level, scale) pairs from a Gaussian copula, so that no training pair is reused, changes the score by +.001 on ETTh1 and +.026 on Energy, against leads of .144 and .224. Windows are not copies (ETTh1: memorised fraction .000, 4096 of 4096 unique).

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