acceptodds
Under review as a conference paper at ICLR 2027

FinHorizon: Persistent Financial Dynamics from Short Windows to Long Paths

Abstract

The order of daily returns determines how losses cluster and drawdowns unfold. Financial scenario generation therefore requires temporal fidelity throughout long paths, even when learning from short windows. We introduce FinHorizon, a compact neural generator that learns on 128-day windows and produces 512-day financial paths. Its key design is an explicit persistent input: stationary memory states carry latent shocks into nonlinear return dynamics, while a separate Scale Factor calibrates return magnitude after training. Across three evaluation equity indices, FinHorizon achieves the lowest mean Dependence discrepancy among nine benchmark methods at 120, 252, and 512 days, with a 23.0% reduction relative to the strongest benchmark baseline at 512 days. Equal-length segments at the beginning, middle, and end of each rollout retain this benchmark lead, showing that the advantage extends throughout the long path. A paired intervention quantifies the contribution of persistent input: retaining memory reduces 512-day Dependence discrepancy by 31.1% relative to a white-noise input control. These results show how explicit persistence supports temporal fidelity in financial scenarios well beyond the training-window length.

Primary area:
learning on time series and dynamical systems
Keywords:
Financial Time Series Generation, Long-Horizon Generation, Temporal Dependence, Persistent Memory, Volatility Clustering, Generative Adversarial Networks.

Reviews

Among:
Shape:
1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_8a6cOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

Problem. Unconditional single-asset generation of daily-return scenarios that preserve volatility clustering and leverage over paths much longer than the training window.

Method (FinHorizon, ~3.2K parameters).

  • Persistent Memory. Eight fixed exponential-decay states driven by one shared Gaussian shock. A learned, variance-normalized positive mixture yields a stationary memory signal.
  • Base Generator. A bounded 24-dim recurrent state receives the memory signal. A log-volatility head modulates a Student-t5t_5 innovation.
  • Scale Factor. Post-training multiplier equal to the ratio of validation to training median 20-day RMS volatility, applied to all paths.
  • Trained with WGAN-GP on 128-day windows, rolled out to 512 days.

Evaluation.

  • Six indices. Three exploratory (SSE, S&P 500, Nikkei 225) for design, three held out (FTSE 100, DAX, Hang Seng).
  • One chronological split. Train 2007–2013, validation 2014–2015, test 2016–2025.
  • 32 metric components in six families. Eight baselines (GJR-GARCH, two block bootstraps, SigCWGAN, QuantGAN, TimeGAN, Diffusion-TS, FTS-Diffusion).

Claims.

  • Lowest mean Dependence discrepancy at 120, 252, and 512 days and in start/middle/end 120-day segments.
  • A paired white-noise-memory intervention attributes a ~31% Dependence reduction to the persistent input.
  • GJR-GARCH and several SV controls have lower Overall discrepancy, attributed by the authors mainly to fitted drift.
Critical strengths

1. Domain-grounded design with experiments that test the actual mechanism.

  • Explicit stationary persistence as a generator input is well motivated by the stylized facts of returns.
  • The Scale Factor cleanly separates magnitude from temporal ordering.
  • The evidence targets the claim directly. Scale-invariant Dependence metrics, equal-length segments at the start, middle, and end of 512-day rollouts, and a paired white-noise-memory intervention.

2. Candid reporting.

  • Losses are reported, not hidden. Overall vs. GJR-GARCH, the Tails cost of the memory, and SV controls that beat FinHorizon on Dependence.
  • The pre-specification sequence is documented and paired intervals are used.
  • The released results/benchmark_scores.csv reproduces Table 1 exactly.

Together these make the Dependence claim credible as far as it goes.

Critical weaknesses

1. Baseline fairness is not established, including what each method sees at test time.

Appendix B.8 and the released docs/baselines.md show the baselines were not run under a common protocol.

MethodWindowBudgetImplementation
FinHorizon128 d1,000 updatesauthors
Diffusion-TS512 d10,000 updatesofficial code
QuantGAN128 d10,000 updatesauthors' re-implementation
SigCWGAN128 d1,000 updatesauthors' re-implementation
TimeGAN128 d1,000 × 3 phasesauthors' PyTorch adaptation
FTS-Diffusionseparate protocol100/200/400 epochsauthors' re-implementation, stated as not an official-code reproduction

A second, more basic point must be settled. The paper states that FinHorizon receives no observed returns during rollout and that test returns enter scoring only. The paper does not state the same for every baseline. SigCWGAN is by construction conditional on a past window, and the paper does not say what history it is seeded with in this unconditional setting. If any method is seeded or re-conditioned on returns from the test period while others are not, the comparison is unfair, and the unfairness grows with the horizon. The release excludes the experimental launchers, trained weights, and data, so this cannot be checked from the code. For a paper whose headline is a 23–31% relative gain on one metric family, it must be shown that the gap is not a protocol artifact.

2. Robustness across periods is not shown.

  • One train/val/test split and one test decade (2016–2025, which includes 2020).
  • Training window fixed at 128 days.
  • No results for other training or test periods, and no measure of how much performance varies with the start date of the training data.

In finance, regimes shift and a single out-of-sample decade can be idiosyncratic. Whether FinHorizon remains effective in other periods is the central robustness question. If performance variance across start dates or training periods turns out to be large, the robustness of the method is seriously in doubt. Combined with Weakness 1, I cannot rule out that the result is specific to this exact setup. If both are resolved, I would support acceptance.

Questions for authors

Q1. What does each method observe at test time? Section 3 and Appendix B.1 state that FinHorizon's rollout uses only latent innovations and its own state, and that test returns are used for scoring only.

  • Please state this explicitly, in the main text, for every method in Tables 1–3. For each one, list what observed data, if any, enters generation at test time (seed window, conditioning history, re-estimation, burn-in source).
  • SigCWGAN is a conditional generator. What history is it conditioned on when producing the 512-day paths? If that history includes test-period returns, please explain why the comparison with unconditional methods is fair, and how the effect scales with horizon.
  • The term "Market returns" in Figure 2 and the phrase "test returns remain uncentered" in B.1 can be read as test data entering the model. Please reword so the convention that the test period never influences any model is unambiguous.

Q2. Design-stage information flow. The exploratory indices were used to design the architecture and the Scale Factor rule, and they cover the same calendar period as the evaluation indices.

  • Please confirm that no cross-index data enters training or calibration of the evaluation-index models.
  • How many Scale Factor candidate rules were tried on the exploratory group before the median 20-day RMS ratio was selected?

Q3. Conditional / macro-aware generators. The baseline set is entirely unconditional. Recent financial generators condition on macro or regime context, e.g. the conditional diffusion generator in STABLE (Soun et al., ICLR 2026) and CoFinDiff (Tanaka et al., 2025), which the paper cites but does not compare against.

  • Please include such a comparison in an unconditional or matched-conditioning mode, or justify why conditional generators are out of scope.

Q4. Does FinHorizon work in other periods, and how large is the variance? Only one split is evaluated.

  • Please report Dependence and Overall discrepancy for at least two additional splits, e.g. rolling the training start and test start by two and four years.
  • Please report the dispersion of these scores across start dates. If the variance across periods is comparable to the gap over the best baseline, the main claim does not hold in general.
  • Please also report results for training windows of 64, 128, and 256 days, and whether the memory mixture in Figure 7b changes materially.

Q5. Inference over time, not only over seeds. The paired intervals vary only the five training seeds and condition on one 2016–2025 history. The reference windows are overlapping resamples of that history.

  • The released README states that reference windows overlap and are not independent histories.
  • configs/replication_4101.yaml records only 4 non-overlapping 512-day blocks and labels longer prefixes as "descriptive stability only", yet the paper headlines 512-day results.
  • Please provide inference that accounts for temporal dependence, e.g. HAC standard errors on per-window discrepancy differences, or the moving-block bootstrap over reference windows already defined in the configuration.

Q6. Downstream consequence. The paper argues that path ordering matters for drawdowns and risk but never shows a consequence. An appendix experiment would show what the Dependence gain buys in practice, e.g.

  • VaR or expected-shortfall backtest coverage,
  • drawdown-distribution calibration,
  • a simple allocation or risk-budgeting exercise on generated scenarios.
3 comments
AuthorsOpenReview ↗

Gentle follow-up on our response

Dear Reviewer 8a6c,

Thank you again for reviewing our work.

Should you have any further questions about our replies, we would be happy to discuss them and provide any clarification needed.

Best regards,

The Authors

Area_Chair_WQbZOpenReview ↗

Author-reviewer discussion period is ending soon

Dear Reviewer 8a6c,

If you haven't done so, please read through authors' response and let authors know if you need further clarification or have more questions. Beginning 11/19, authors are not allowed to respond any more, so this is good time to review the response and ask more.

Thank you.

-AC

Reviewer_8a6cOpenReview ↗

Response to author comment

Thank you for the detailed response and the additional experiments. I have read all four parts and the follow-ups.

What the response resolves. The method-by-method table settles Q1. Every method is seeded from training data only, and the SigCWGAN context rule is now clear. The per-market fitting statement and the four-candidate scale-rule list settle Q2. I consider the information-flow concern closed.

Why my score stays at weak reject. The new evidence strengthens the narrow Dependence claim but weakens the paper's broader claims, and none of it can be verified.

  1. Cross-period robustness of the full evaluation fails. Dependence is stable across the three splits, but Overall moves from 0.2573 to 0.1915 to 0.4345, a standard deviation of 0.1257 across splits. In the four-years-earlier split FinHorizon has the worst Overall of the six methods reported, below the white-noise control (0.3735) and GJR-GARCH (0.3335). My review stated that if period-to-period variance were comparable to the gap over the best baseline, the main claim would not hold in general. For Overall that condition is met. The response reframes this as a difference between metric families rather than as a robustness result, which I do not find persuasive.

  2. The dependence advantage over the strongest classical baseline is not established under time-block inference. The basic bootstrap interval for FinHorizon minus GJR-GARCH is [−0.0155, +0.0015] and includes zero. The paper's headline is a 23.0% reduction relative to GJR-GARCH at 512 days.

  3. The persistence mechanism degrades path-risk fidelity. The newly reported components show that persistent input worsens the terminal-log-return discrepancy (0.4618 to 0.4784) and the maximum-drawdown discrepancy (0.4785 to 0.5003) relative to the white-noise control. The introduction motivates the method by the effect of return ordering on drawdowns. The paper's own evidence now shows that the mechanism moves drawdown fidelity in the wrong direction, and no downstream experiment was provided.

  4. Conditional baselines were declined. I accept that test-time conditioning is a different setting. A matched-mode comparison with the conditioning input drawn from training history, exactly as was done for SigCWGAN, remains feasible and was not run.

  5. None of the new results can be checked. The release still excludes the experimental launchers, trained weights, and data. The additional splits, window sweeps, and time-block bootstrap exist only as tables in the response. Given that the rebuttal has produced a split in which the method is worst overall, independent verification is what would let me raise the score, and it is not possible.

What would change my assessment. Release of the launchers, weights, and data so that the three splits can be re-run. A revised set of claims that reports Overall instability and the path-risk degradation in the main text rather than treating Dependence as the sole headline. A matched-mode comparison against at least one conditional generator.

I keep my rating at 2.

Reviewer_iproOpenReview ↗
Rating
1
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper introduces FinHorizon, a small neural generator for unconditional single-asset daily return paths. It trains on 128-day windows and generates paths of up to 512 days. The model has three parts. Eight fixed exponential-decay memory states are driven by a shared Gaussian shock. The model is trained with WGAN-GP. The authors evaluate on FTSE 100, DAX, and Hang Seng, with five seeds and a 32-component discrepancy. They report the lowest dependence discrepancy at 120, 252, and 512 days, a 23.0% reduction over the best baseline at 512 days, and a 31.1% reduction from the memory input in a paired ablation.

Critical strengths
  1. The long-horizon evaluation is well designed. Most financial generation papers evaluate at the training horizon. This paper slices the same 512-day paths into start, middle, and end segments and compares each against the same 120-day reference windows. That holds the evaluation length and the reference data fixed, so a drop at the end cannot be blamed on a harder metric.

  2. The paper reports results that hurt its own case. Table 19 shows that the memory input has no overall benefit because tails get worse. The honesty makes the paper more useful than its headline suggests.

Critical weaknesses
  1. The model does not beat simple volatility models on the overall score, and the dependence advantage is not robust. At 120 days, GJR-GARCH has overall discrepancy 0.184 against 0.252 for FinHorizon. At 512 days the gap is 0.253 against 0.257, which is 0.004 and well inside the reported interval. Under common rescaling, FinHorizon ranks fourth among the nine methods at 120 and 252 days. I do not think that is enough to claim a better model.

  2. The memory ablation does not support the architecture. Replacing the eight decay states with one timescale gives a dependence score of 0.0348 at the start, against 0.0361 for the full model. The paired difference favors the single timescale (+0.0013, CI [0.0003, 0.0022]. The eight-state bank is therefore not needed for the main result. What matters is having some persistent input. If you replace a persistent signal with white noise, long-range dependence will fall. The paper's contribution then reduces to "feed the RNN a persistent signal", which is a design choice, not a finding.

  3. The problem about the writing. This paper does not just report results. It keeps telling the reader what the results are not. It documents when each analysis was fixed, and repeats the same denials in every table caption.

Questions for authors
  1. The dependence family uses "pooled correlations". Are these computed by concatenating all 128 paths and then taking one correlation, or by averaging per-path correlations?

  2. Why is the eight-rate bank needed if a single timescale is as good or better at the start? Was the bank size selected on the exploratory indices?

  3. Eq. 3 uses weights 4/19 for dependence and 3/76 for volatility. Why these weights?

  4. The Diffusion-TS baseline is trained on 512-day windows while FinHorizon uses 128-day windows. The other neural baselines have training budgets from 1,000 to 10,000 updates. Were any of them tuned on the validation data? A compute-matched comparison would be more convincing.

2 comments
AuthorsOpenReview ↗

Gentle follow-up on our response

Dear Reviewer ipro,

Thank you again for your time and consideration.

Please let us know if any part of our responses needs further clarification.

We would be happy to provide additional details.

Best regards,

The Authors

Area_Chair_WQbZOpenReview ↗

Author-reviewer discussion period is ending soon

Dear Reviewer ipro,

If you haven't done so, please read through authors' response and let authors know if you need further clarification or have more questions. Beginning 11/19, authors are not allowed to respond any more, so this is good time to review the response and ask more.

Thank you.

-AC

Reviewer_NvMKOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper proposes FinHorizon, a compact (3.2k-parameter) WGAN-GP-trained generator for unconditional single-asset daily returns. A shared Gaussian shock drives eight fixed exponential-decay AR(1) states (timescales ~4.5–200 days); a learned, variance-normalized positive mixture of these states (the "Persistent Memory" signal m_t) is fed into a contractive tanh RNN (‖A‖₂ ≤ 0.8) and into a bounded log-volatility head that scales a Student-t5 shock. After training, all paths are multiplied by a fixed "Scale Factor" equal to the ratio of median 20-day RMS volatility in the validation vs. training period. The model is trained on 128-day windows (2007–2013) and rolled out to 512 days; evaluation is on FTSE 100, DAX and Hang Seng (2016–2025), with three other indices used for development. The main claim is that FinHorizon has the lowest mean Dependence discrepancy (return/|r|/r² ACF and leverage at lags 1, 5, 20, 60) among nine methods at 120/252/512 days and at the start/middle/end of 512-day paths (0.0378 vs 0.0491 for GJR-GARCH at 512 days), and that replacing the memory signal with white noise raises this discrepancy by ~31%. A long appendix adds SV controls, drift-removal controls, metric-weight sensitivity, simulated processes and a pre-specification log.

Critical strengths
  • Careful and unusually transparent evaluation protocol. Chronological train/val/test splits, a separate exploratory vs. evaluation group of markets, paired replications with shared random streams, equal-length start/middle/end segments that keep the reference data fixed, and an explicit log of which analyses were fixed before vs. after seeing results. Negative findings are reported rather than hidden (e.g., Table 23, Table 36, Table 25). This makes the paper's claims checkable, and it is the main reason I trust the numbers I criticise below.
  • A clean, cheap demonstration that an explicit persistent input matters for a small neural generator. With the recurrent core, data, seeds and selection held fixed, swapping m_t for variance-matched white noise raises Dependence discrepancy from 0.036 to 0.053 and Volatility discrepancy from 0.35 to 0.47 (Table 4), and the effect holds in the terminal segment (Table 13, Figure 3). This is a useful, well-controlled ablation.
Critical weaknesses
  • It is not clear that the learned neural component adds value beyond a classical model with the same priors. Several stylized facts are specified in the design rather than learned: fixed decay rates, Student-t5 innovations, a bounded log scale, a contractive recurrent core (‖A‖₂ ≤ 0.8), signed and absolute shocks as inputs, and critic input channels |r| and log(1+r²). The Scale Factor was selected among candidate rules on the exploratory indices (Appendix I.3) and accounts for a 31.6% Overall reduction (Table 4A). I could not find clear evidence that the reported gains come from the learned dynamics rather than from these specified components. Observations from the paper:

    • A one-factor Student-t5 leverage SV model has lower mean Dependence than FinHorizon at 512 days (0.0341/0.0343 vs 0.0378, Table 46) and at the start, middle and end segments (Tables 36, 44). This model is not part of the nine-method comparison in Tables 1–3 or the abstract.
    • A single learned AR(1) memory state gives similar Dependence to the eight-state bank (0.0348 vs 0.0361 at 120 days; Tables 24–25).
    • Student-t GJR-GARCH has lower Overall discrepancy at the primary 120-day horizon (0.184 vs 0.252, Table 10).
    • Appendix G.1 removes only the cumulative-return critic channel; the |r| and log(1+r²) channels are not ablated.

    Given these observations, does the claim that FinHorizon achieves "the lowest mean Dependence discrepancy among nine benchmark methods" reflect an advantage of the proposed neural design? Would this conclusion still hold if the leverage SV model were included in the comparison and the critic's |r| and log(1+r²) channels were removed?

  • It is not clear that the evidence supports temporal fidelity beyond the training window. Observations from the paper:

    • The Dependence family uses lags 1, 5, 20 and 60, all shorter than the 128-day training window.
    • At lags 128 and 192 (Table 23), the paired intervals of FinHorizon against GJR-GARCH, both bootstraps, SigCWGAN, QuantGAN, TimeGAN and the white-noise control all include zero.
    • Figure 5(c) reports a 61.3% maximum relative error when the main decay bank fits a power-law kernel through lag 512.
    • The white-noise control keeps the same ‖A‖₂ ≤ 0.8 constraint on the recurrent core.

    Given these observations, do the results show that FinHorizon carries temporal dependence beyond the 128-day training window, or mainly that short-lag statistics (lags ≤ 60) remain stable as the stationary model is rolled out? And does the 31.1% reduction over the white-noise control reflect the value of the persistent input, or the constraint on the recurrent core?

Questions for authors
  • The one-factor Student-t5 leverage SV model has lower mean Dependence than FinHorizon at every horizon and segment position reported (Tables 36, 44, 46). What evidence shows an advantage of FinHorizon over this model? Could it be included in the main comparison?
  • How does the white-noise control perform when the recurrent core is not constrained (e.g., a GRU/LSTM, or the norm bound relaxed to ~0.99)? Does the explicit persistent input still reduce Dependence discrepancy in that setting?
  • With the generator unchanged, how much of the Dependence improvement remains when the critic receives raw returns only, without the |r| and log(1+r²) channels?
2 comments
AuthorsOpenReview ↗

Gentle follow-up on our response

Dear Reviewer NvMK,

We appreciate your time in considering our responses.

If any questions remain, please feel free to let us know.

We would be glad to clarify them.

Best regards,

Area_Chair_WQbZOpenReview ↗

Author-reviewer discussion period is ending soon

Dear Reviewer NvMK,

If you haven't done so, please read through authors' response and let authors know if you need further clarification or have more questions. Beginning 11/19, authors are not allowed to respond any more, so this is good time to review the response and ask more.

Thank you.

-AC

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

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