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- 3
- Informativeness
- 2
- Presentation
- 2
- Soundness
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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- 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.csvreproduces 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.
| Method | Window | Budget | Implementation |
|---|---|---|---|
| FinHorizon | 128 d | 1,000 updates | authors |
| Diffusion-TS | 512 d | 10,000 updates | official code |
| QuantGAN | 128 d | 10,000 updates | authors' re-implementation |
| SigCWGAN | 128 d | 1,000 updates | authors' re-implementation |
| TimeGAN | 128 d | 1,000 × 3 phases | authors' PyTorch adaptation |
| FTS-Diffusion | separate protocol | 100/200/400 epochs | authors' 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.yamlrecords 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
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
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.
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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.
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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.
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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.
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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.
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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.
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