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Under review as a conference paper at ICLR 2027

When Do Heavy Tails Help? Identifiability Limits and Predictive Uncertainty in Lévy-Driven Neural SDEs for Electricity Markets

Abstract

Electricity markets shaped by renewable generation exhibit heavy-tailed price shocks that standard forecasting models neither capture nor bound. We introduce LévySDE-Net, a neural stochastic differential equation with drift and diffusion parameterized by neural networks and driven by -stable Lévy motion, paired with phase-space reconstruction and maximal Lyapunov exponent estimation to characterize a market's intrinsic predictability horizon. Evaluated on Nord Pool electricity price areas, LévySDE-Net and a Gaussian-forced counterpart both substantially outperform econometric and recurrent baselines at short horizons, but heavy-tailed forcing confers no consistent point-forecast advantage over Gaussian forcing – a result we trace, via a synthetic identifiability analysis, to a genuine confound between the Lévy stability parameter and the diffusion scale under discretely observed data. Instead, Lévy forcing's distinguishing effect is on predictive uncertainty: it systematically widens ensemble spread and interval width relative to Gaussian forcing, and in the wind-driven price area this divergence emerges at a rollout horizon consistent with the area's independently estimated Lyapunov time. Our results indicate that heavy-tailed stochastic forcing's principal value lies not in point accuracy but in producing forecast uncertainty calibrated to a market's underlying dynamical instability.

Primary area:
learning on time series and dynamical systems
Keywords:
neural stochastic differential equations, Lévy processes, heavy-tailed noise, predictive uncertainty, identifiability, Lyapunov exponents, electricity price forecasting, time series forecasting

Reviews

Among:
Shape:
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_32pyOpenReview ↗
Rating
1
Confidence
2
Informativeness
1
Presentation
2
Soundness
1
Read review
Paper summary

This paper addresses the problem of forecasting prices in electricity markets. The authors suggest modeling these via Stochastic Differential Equations (SDEs) driven by an α\alpha-stable Lévy process where the drift and diffusion coefficients are parameterized by a learned neural network and term this method LévySDE-Net. The motivation for this is that renewable energy generation induces abrupt shocks in electricity prices which cannot be appropriately modeled via a Gaussian distribution but rather require a heavy tailed distribution. A similar approach has already been chosen in a previous paper to model stock indices, however, it has been only validated on single-run experiments. The main contribution consists of (1) the authors addressing this gap in their work and evaluating the method on three different seeds as well as (2) extending the idea of using Lyapunov time to test the divergence of forcing mechanisms beyond simply comparing the model’s accuracy before and after its predicted horizon. Additionally, several experiments are conducted such as testing whether the alpha parameter can be recovered in a controlled, synthetic experiment, one-step and multi-horizon forecasting as well as predictive uncertainty. The proposed method does not outperform the existing Gaussian baseline in terms of point prediction performance and has a larger predictive spread that it.

Critical strengths

The authors identify a gap in previous work, which however only uses a single seed in their experiments and which is thus susceptible to statistical miss-evaluations.

Critical weaknesses
  • The contribution is marginal and the idea is not novel
    • The idea of using α\alpha-stable Lévy processes is already present in the literature as the authors write themselves in their paper. Simply running more seeds is not a significant extension of this work.
    • The contribution of treating the Lyapunov time as marker for faithful forecasting is thin. In line 444 the authors choose ρ∗=4.0\rho^* = 4.0 and remarks that this is "not yet justified on independent grounds". Further, in line 466 they leave testing that this relationship holds to future work which would have strengthened this contribution.
    • The results of the method are non-existing. As already mentioned the proposed method is not able to outperform the Gaussian baseline. The claimed improvement of having a wider ensemble are by itself marginal. The authors further fail to investigate this further and do not comment on why this is beneficial at all. The obvious explanation that this is only due to the heavy tails of the Lévy process is not addressed at all.
  • The presentation of the paper is not good and lacks basic principles of scientific writing
    • The citations are formatted not correctly: Each reference in the main text is indicated by a number and a link. The link does not lead to anywhere in the document. Further, the bibliography does not list the numbers of the references such that finding the corresponding work to a reference becomes a tedious counting.
    • The tables are overflowing and lack clarity, for example due to missing separation bars. Some metrics are evaluated up to 6 decimals so simply rounding them appropriately would have addressed this overflowing issue in these cases.
    • The subsection on "Limitations and positioning" is repeated in 146-158 and 159-172
Questions for authors
  • What is the significance of having a larger spread for the ensemble? Does it correlate with prediction error and is thus a useful proxy for predictive uncertainty? Or is it just an artifact of using a heavy tails process?
  • Can you elaborate on the claim of using Lyapunov-diagnostics for trajectory divergence?
3 comments
AuthorsOpenReview ↗

Response to Reviewer 32py

Thank you for the review. We have substantially revised the paper in response; numbers refer to the revised PDF.

Novelty. We agree that running more seeds alone is not a sufficient contribution, and that α\alpha-stable neural SDEs are not new; we no longer claim to introduce the model. The revised paper contributes:

  • two propositions explaining why symmetric forcing cannot improve point forecasts in this architecture, confirmed by a noise-free neural ODE ablation (Sections 3.5, 4.4);
  • a calibrated probabilistic evaluation against linear and GARCH-tt benchmarks in three markets, with five seeds, four horizons and per-seed Diebold–Mariano tests (Section 4.5);
  • a demonstration that outcome-selected tail evaluation reverses the conclusion of a proper tail score in every market, the forecaster's dilemma (Section 4.6, Figure 1).

Q1. Is the larger spread useful, or just an artifact of heavy tails? We tested this directly, and your suspicion is largely correct.

  • Spread–skill. The correlation between ensemble spread and absolute error is modest for both SDEs (Lévy 0.28–0.37, Gaussian 0.24–0.39) and no higher than for AR(8)+GARCH(1,1)-tt (0.31–0.45) (Tables 4, 11).
  • Why CRPS improves. Both SDEs are badly under-dispersed as trained: their 95% intervals cover at most 3% of outcomes. After calibration on a validation block, Lévy forcing improves CRPS because its heavier tails partly compensate for this under-dispersion. Across a sweep of α\alpha, the CRPS gain tracks interval coverage (Table 5).
  • Tails. On threshold-weighted CRPS over all hours, a proper tail score, Lévy forcing is no better than Gaussian forcing and often worse (Tables 6, 10). Its extra tail mass is placed at every hour, not when risk is high.

The paper now states this explicitly (Sections 4.5–4.6).

Q2 and the Lyapunov contribution. We agree that it was thin. We removed the rollout study, the unjustified threshold and the claim that Lyapunov time marks a forecasting horizon. The remaining phase-space diagnostics are a short exploratory appendix for DK1 only, with no forecasting claim (Appendix J). Cao's criterion indicates predominantly stochastic dynamics, so the estimated exponent is reported only as a descriptive divergence scale.

Results. The main results are now: (i) no point-forecast benefit, with a theoretical explanation; (ii) a CRPS gain from compensating under-dispersion, not from better tails; (iii) GARCH-tt outperforms both SDEs; and (iv) outcome-selected evaluation makes heavy-tailed forcing appear superior where a proper score shows it is not. We think (iv) is useful well beyond this model, since evaluating tail forecasts on observed extreme events is common practice.

Presentation.

  • Citations. Now natbib author–year with working links to an alphabetical bibliography.
  • Tables. Rounded to an appropriate precision, with horizontal rules, and fitted to the margins.
  • Repetition. The duplicated "Limitations and positioning" subsection has been removed.

Note that neural models now use five seeds throughout.

AuthorsOpenReview ↗

Follow-up (Reviewer 32py)

Dear Reviewer 32py, As the discussion period closes tomorrow, we wanted to check whether our response above and the revised PDF address your concerns. We would be glad to clarify anything before the deadline. Thank you again for your time.

I want to thank the reviewers for their detailed response and substantial revisions. I acknowledge that the presentation issues are partly fixed, the Lyapunov analysis has been removed, and my Q1 has received an answer.

Nevertheless, I stick with my score. The initial submission violated the ICLR formatting in several places (inconsistent citation style, overflowing margins), contained a duplicated subsection, and reported unverified results. The revision, on the other hand, changed the title, the central explanation, the theory, the baselines, and practically every reported number, after correcting errors in the original pipeline. Overall, an unfinished paper was submitted and a new one written during rebuttal, which cannot be reviewed with the necessary care at this time and is also not the purpose of a review process. Further, in my view, the contribution is not strong enough for this venue. It includes mainly a negative result for one small SDE-Net model that is uncalibrated and outperformed by the AR(1) model and its adaptation (+ GARCH(1,1)-t), as well as an interpretation of this in terms of the Forecaster's lemma, whose whole concept and theory are now central to the paper, but were added in retrospect.

I encourage the authors to rework the paper and resubmit, and to take the submission process more seriously.

Reviewer_PkLtOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
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Paper summary

The paper studies whether alpha-stable forcing improves neural-SDE forecasting of electricity price differences. It compares matched Levy-driven and Gaussian SDE-Nets on three Nord Pool price areas, with five training seeds, and reports similar point-forecast accuracy but wider stochastic ensembles under Levy forcing. Synthetic Levy-Ornstein-Uhlenbeck recovery experiments and a DK1 rollout study are used to motivate an identifiability-based explanation and a connection to an estimated Lyapunov time.

Critical strengths
  1. The paper asks a useful question and includes a matched Gaussian control. Comparing otherwise identical neural architectures over multiple seeds is a meaningful improvement over attributing an isolated forecasting gain to the heavy-tailed driver. Tables 3, 9, and 10 support the limited finding that Levy forcing has no consistent point-accuracy advantage in the reported settings.
  2. The authors report synthetic parameter recovery over 40 seeds, including uncertainty intervals, and explicitly acknowledge several unfinished checks. This makes the scope and weaknesses of the current evidence more inspectable.
Critical weaknesses
  1. The principal uncertainty and predictability claims are not established by the reported measurements. Table 5 demonstrates wider intervals, but reports neither empirical coverage nor a proper probabilistic score. Diffusion magnitude is shaped by real-versus-perturbed input classification and fixed scale constants, not by a predictive calibration objective (Section 3.3; Appendix D.2). Consequently, wider intervals alone do not establish better uncertainty representation. The claimed Lyapunov-time validation additionally relies on an independently unjustified spread-ratio threshold of 4 (Section 4.8). A crossing at approximately 67 hours before a nominal 114-hour estimate is not sufficient to establish a predictability boundary. Appendix G states that the embedding dimension came from a different transformation, while Table 8 calculates the displayed exponent from the assumed horizon. The original horizon-estimation evidence, its uncertainty, and threshold robustness are needed.
  2. The proposed explanation and its supporting evaluation contain substantive inconsistencies. Section 4.3 describes the fixed alpha gap of 0.5 as comparable to recovery errors, although Table 16 reports standard deviations of only 0.027-0.046 and the text mentions individual errors around 0.10. Correlated estimation errors do not establish an identifiability bound, and the forecasting comparison fixes alpha rather than estimating it, as Appendix L.2 itself acknowledges. The evaluation also requires reconciliation: (a) Appendices B and D.4 pair an input ending at r_t with target r_(t+T+7), implying an eight-hour rather than one-hour lead for T=1; (b) Table 15 reports MSE 2.054333 at alpha=1.5 versus 1.617658 in Table 3 despite the stated fixed-settings sensitivity protocol; and (c) all five q=1 DM statistics in Table 14 favor Gaussian, whereas the five-seed mean MSE in Table 3 favors Levy. These quantities are incompatible if computed from the same paired squared errors. Appendix D.8 also acknowledges using h=1 in all DM calls. Until the actual protocol and result provenance are established, the reported significance and mechanistic interpretation remain uncertain.
Questions for authors
  1. Clarification and verification: What are the actual input-end and target timestamps for each reported horizon? Can you supply a concrete indexed example and reconcile the alpha=1.5 results in Tables 3 and 15, and the q=1 MSE ranking with all-positive DM statistics in Table 14, using the same saved predictions?
  2. Decision-relevant validation: What empirical coverage and proper probabilistic scores do the intervals achieve, and does Levy forcing improve these relative to a Gaussian model calibrated on a separate validation set? Please specify ensemble size, interval construction, and sampling-convergence behavior.
  3. Clarification of the central explanation: What evidence establishes an identifiability limit, rather than finite-sample estimator uncertainty, and how does it explain a comparison with fixed alpha values? Please reconcile the gap of 0.5 with the recovery errors in Table 16.
  4. Decision-relevant validation: What original estimator output supports h=114 hours on the price-difference series, and how robust is it to embedding choices and stochastic-surrogate controls? Does the claimed rollout relationship survive independently selected thresholds and evaluation in terms of forecast skill or coverage?
3 comments
AuthorsOpenReview ↗

Response to Reviewer PkLt (1/2)

Thank you for a very detailed review. Your verification questions led us to find and correct three problems in the original submission, and every result in the revised paper has been regenerated (see the Summary of revisions). We answer each question below; numbers refer to the revised PDF.

Q1. Indexing, Tables 3 vs. 15, and Table 14.

Indexing. Thank you for catching this: the original Appendices B and D.4 misdescribed the target as rt+T+7r_{t+T+7}. We ran the original windowing code on a counting series 0,1,2,…0, 1, 2, \dots: the first window [0,…,7][0,\dots,7] has target 88 at T=1T=1 and 99 at T=2T=2, so the code always paired an input ending at rtr_t with rt+Tr_{t+T}, a lead of exactly TT hours. The error was in the description, not the forecasts. Appendix C now states the indexing with this example, and the revised code asserts it before any model is trained. Windows are built separately within the fit, validation and test segments, so none crosses a split boundary.

Tables 3 and 15. The discrepancy came from two different standardisations of the series in the scripts that produced the two tables, and 2.054/1.618 matches that rescaling. All series are now standardised with training-period statistics only. Every table is computed from the same saved predictions, and the α=1.5\alpha = 1.5 MSE is identical in the main table and the sweep (2.072 in DK1; Tables 3 and 14).

Table 14. We agree that these quantities cannot both hold if computed from the same paired squared errors. The sign convention was correct (positive statistics favour the Gaussian model), so the original DM tests and the Table 3 means were not computed from the same predictions. In the revision both are computed from the same saved predictions: per-seed DM tests use h=Th = T with the Harvey–Leybourne–Newbold correction (Appendix F.3), and their direction agrees with the seed means. For example, Lévy vs. Gaussian MSE favours Gaussian in both the means (DK1: 2.072 vs. 2.054) and the significant DM tests (Table 12).

Q2. Coverage and proper scores against a calibrated Gaussian model. We agree that wider intervals alone establish nothing. The revision evaluates this directly:

  • Calibration. For every model and seed, a single multiplier κ\kappa on the noise term is selected on a separate validation block by CRPS (grid 0.25–512; selected values 16–64, always interior). The Gaussian SDE-Net is calibrated identically (Appendix E.2).
  • Construction. N=200N = 200 forward passes per test input; intervals are empirical ensemble quantiles. At N=200N = 200, CRPS is within 0.5% and the 95% width within 2% of their values at N=1,000N = 1{,}000 (Table 13).
  • Results. Uncalibrated, both SDEs cover at most 3% of outcomes with their 95% intervals. After calibration, Lévy forcing has lower CRPS than Gaussian forcing (DK1 0.714 vs. 0.726, significant in all seeds), but coverage remains 0.33–0.68, and AR(8)+GARCH(1,1)-tt is better than both (CRPS 0.644, coverage 0.88; Tables 4, 9, 11). On threshold-weighted CRPS, a proper tail score, Lévy forcing is no better than Gaussian forcing and often worse (Tables 6, 10). So Lévy forcing does not give a better uncertainty representation; it partly compensates for under-dispersion.

(continued in the next comment)

AuthorsOpenReview ↗

Response to Reviewer PkLt (2/2)

(continued)

Q3. Identifiability vs. finite-sample estimator uncertainty. We agree that correlated estimation errors do not establish an identifiability bound, and that the original text misstated the comparison with recovery errors. We tested the distinction directly by repeating the recovery at n∈{300,1,200,4,800,19,200}n \in \{300, 1{,}200, 4{,}800, 19{,}200\}. sd(α^\hat\alpha) falls at the n−1/2n^{-1/2} rate of a consistent estimator (log–log slopes −0.49-0.49 to −0.54-0.54), to 0.009 at n=19,200n = 19{,}200, comparable to our training lengths, while the error correlation persists (Table 18, Appendix I). The coupling is therefore ordinary estimator variance, and the fixed gap Δα=0.5\Delta\alpha = 0.5 is roughly fifty standard deviations, not comparable to estimation error.

As you note, the forecasting comparison fixes α\alpha, so estimation uncertainty cannot explain it anyway. The revised paper explains the null result instead with two propositions (Section 3.5, proofs in Appendix A). Under affine drift, symmetric zero-mean forcing leaves the expected forecast exactly equal to the neural-ODE forecast. Under Lipschitz drift, it can move it by at most eℓK1−1/ακσg c mαe^{\ell}K^{1-1/\alpha}\kappa\sigma g\,c\,m_\alpha. Empirically, a noise-free neural ODE matches the Gaussian SDE-Net to four decimal places in all three markets, and LévySDE-Net within seed variation (Section 4.4).

Q4. Provenance of h=114h = 114, embedding robustness, surrogates and the rollout threshold. We agree that this evidence did not support a predictability claim, and we have removed the claim.

  • Rollout and threshold. The rollout study and the ρ⋆=4\rho^\star = 4 threshold are removed entirely. The paper no longer claims a predictability boundary or a relationship between ensemble spread and Lyapunov time.
  • Circularity. The original table derived λmax⁡\lambda_{\max} from the assumed horizon. Table 20 now reports the direct output of the Wolf estimator on the price-difference series (λmax⁡=0.00874\lambda_{\max} = 0.00874, h=114.5h = 114.5).
  • Embedding. We recomputed Cao's E1/E2E_1/E_2 on the price differences (Table 19). The automated rule selects m=6m = 6, but E1E_1 rises slowly and E2≈1E_2 \approx 1 throughout, which indicates predominantly stochastic dynamics. We therefore treat m=8m = 8 as a design choice shared by all models. We also recomputed the AMI on the price differences: it would select τ=3\tau = 3, so τ=1\tau = 1 is likewise stated as a design choice.
  • Surrogates. No surrogate test was performed, and the paper says so. Because Wolf-type estimators can return positive exponents for stochastic series, λmax⁡\lambda_{\max} is reported only as a descriptive divergence scale, for DK1 only, in an exploratory appendix (Appendix J). No forecasting result depends on it.

We are grateful for the specificity of your questions, which materially improved the paper.

AuthorsOpenReview ↗

Follow-up (Reviewer PkLt)

Dear Reviewer PkLt, As the discussion period closes tomorrow, we wanted to check whether our responses above and the revised PDF address your questions. We would be glad to clarify anything before the deadline. Thank you again for your time.

Reviewer_bM7sOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2(+1)
Presentation
2
Soundness
3(+2)
Read review
Paper summary

The authors propose to apply the heavy-tailed Levy-SDE to electricity market prediction. They motivate it by the known fact, that electricity markets often have heavier tails, due to market shocks, often caused by renewable energy sources. In the empirical study, they establish that:

  1. The used datasets indeed have heavy tails (Experiment 1).
  2. On synthetic data, the Levy (alpha not 2.0) vs Gaussian (alpha=2.0) generated data is often non-identifiable, and the differences in alpha may be compensated by sigma (Experiment 2).
  3. On real, heavy-tailed electricity data, the methods match in the pointwise forecasting quality, which is argued to be due to sigma-compensation from point 2, contradicting the prior LDE-Net work's findings (Yang et al., 2023), that Levy makes some real gains on pointwise forecasts (Experiments 3 through 5).
  4. However, as expected, the Levy SDE does indeed make the ensembles wider, as demonstrated in experiments 6 and 7.
Critical strengths

You have an intersting negative finding -- that the LDE-Net findings do not carry over to electricity, and the Levy-SDE does not improve point forecasts after all, in a reasonable heavy-tailed setup. That is well-tested in your paper, and you give a plausible explanation: the identifiability constraint, that sigma may compensate for alpha's behaviour.

Critical weaknesses

At the moment, I believe that your main novelty is the negative finding I outlined above -- not the first contribution, which explicitly says that you "introduce LevySDE-Net", already taken by LDE-Net in 2023. The negative finding, framed as contributions 2 and 3, is real: the authors conjecture, sigma may adapt to alpha. Unfortunately, I find that the mechanism is only weakly established in the paper: the recovery experiment shows the alpha error to be 0.03-0.1, and the Gaussian-vs-Levy comparison uses a delta of 0.5 (alpha = 2.0 for Gaussian, and 1.5 for Levy). I would like to see some theoretical explanation, or a more rigorous practical effect here. Then, the negative finding could be a good contribution, but in my opinion is not enough, I would like some positive conclusion to follow here.

Another thing that concerns me is Experiment 7: I don't see how it is motivated, and the setup is not clean enough to make any definite conclusions. Yes, the Levy SDE indeed produces more uncertainty and longer horizons, and may possess wider ensembles. But that is the reason people already use it: LDE-Net used that motivation, completing it with a full mechanism description of how it works, and why it should be better. The interesting thing here could be your comparison of this rho-threshold time to the Lyapunov exponent time, but it is again, unmotivated (as you admit yourself, that the rho* threshold is "not yet justified on independent grounds"). It is unclear, why these two values are comparable, and, more importantly, what conclusion do we want to make here, other than "Levy produces heavier tails" (which is by design, and not necessarily a good thing). There are established calibration methods, which you could use to establish that Levy's uncertainty is better in some way -- but then, your novelty compared to LDE-Net is still unclear.

Questions for authors
  1. Why are the rho-threshold time and the Lyapunov exponent time comparable, and what conclusion (other than that Levy tails are heavier) can we make from this?
  2. How can you explain the fact that your findings differ from that of the LDE-Net paper (that Levy doesn't improve pointwise forecasts); how specifically is the protocol different, and what is the mechanism which makes the finding work in the older paper, but fails in your setup?
  3. Can the effect that Levy and Gaussian-based SDEs have matching point forecasts, be established in theory?

Suggestions for the authors. I would recommend framing this paper concisely around the fact that the Levy SDE/LDE-Net, an established way to model heavy tailed-data, is not really better than using a Gaussian SDE: focus on contributions 2-3, remove contribution 1, since it's not yours, as you say yourself. The title does this framing well, but the content misses it. Then, I also recommend you do a more definitive test for whether the uncertainty of the Levy model matches the uncertainty of the data: this can be given by any of the various diverse calibration methods, or at least a simple probabilistic forecasting score, like CRPS. Finally, I would like to see some positive result.

Update: the authors succesfully addressed most of my concerns, clarified their positioning and strengthened their findings. They used the framing I recommened, strengthened their empirical results, and formulated a specific takeaway useful for future research. I will raise my mark.

3 comments
AuthorsOpenReview ↗

Response to Reviewer bM7s

Thank you for the thoughtful review and the concrete suggestions; we followed all of them. Numbers refer to the revised PDF.

Framing and contribution 1. We removed the contribution "we introduce LévySDE-Net" and now frame the paper, as you suggested, around whether Lévy forcing helps relative to an otherwise identical Gaussian SDE. Section 2 states that our model follows LDE-Net's design and that the separate name only distinguishes our implementation.

The mechanism was weakly established. We agree, and on testing it further we found that identifiability is not the mechanism. A new sample-size study shows sd(α^\hat\alpha) falling at the n−1/2n^{-1/2} rate, to 0.009 at n=19,200n = 19{,}200 (Table 18). At our sample sizes, α\alpha is well determined, and the gap Δα=0.5\Delta\alpha = 0.5 is about fifty standard deviations. The α\alpha–σ\sigma coupling is ordinary estimator variance. Since the forecasting comparison fixes α\alpha, it cannot explain the null result in any case.

Q3. Can the matching point forecasts be established in theory? Yes; this is now the paper's explanation (Section 3.5, proofs in Appendix A). Proposition 1: with affine drift, symmetric zero-mean forcing leaves the expected forecast exactly equal to the noise-free (neural-ODE) forecast, for any α\alpha, noise scale or diffusion network. Proposition 2: with Lipschitz drift, the deviation is at most eℓK1−1/ακσg c mαe^{\ell}K^{1-1/\alpha}\kappa\sigma g\,c\,m_\alpha, first order in the noise scale. The bound grows as α→1\alpha \to 1, consistent with the MSE degradation we observe at α=1.2\alpha = 1.2 (Table 14). Empirically, a neural ODE trained without noise matches the Gaussian SDE-Net to four decimal places in all three markets (e.g. DK1 2.0535 vs. 2.0536), and LévySDE-Net within seed variation (Table 3).

Q2. Why do the findings differ from LDE-Net? The protocols differ in three ways:

  • LDE-Net compares single training runs without significance tests.
  • We use five seeds, per-seed Diebold–Mariano tests and linear baselines.
  • We study electricity price differences rather than stock indices.

Our propositions apply to LDE-Net's design whenever the forcing is symmetric and the diffusion is evaluated at the initial state, so we would not expect a systematic point-forecast gain there either. In our runs, the seed-to-seed standard deviation (e.g. 0.030 in DK1) is the same order as the Lévy–Gaussian difference, so a single-run comparison can show a gain in either direction. We cannot verify the cause in their setup without their code, and we do not claim their result is wrong for their data. We also find that a direct AR(8) matches or beats both SDEs on point accuracy (Section 4.4).

Q1 and Experiment 7. We agree that the ρ\rho-threshold time and the Lyapunov time were not shown to be comparable, and that the experiment showed little beyond Lévy tails being heavier. We removed the rollout experiment and the threshold entirely. The phase-space diagnostics are now a short exploratory appendix with no forecasting claim (Appendix J).

Calibration test. We did this as you recommended: the noise level of every SDE is calibrated on a separate validation block, and the predictive distributions are evaluated with CRPS, threshold-weighted CRPS, coverage and spread–skill correlation (Section 4.5; Appendices E.2, G). After identical calibration, Lévy forcing has lower CRPS than Gaussian forcing, but both SDEs remain under-dispersed, and AR(8)+GARCH(1,1)-tt beats both.

A positive result. The revision has one we think is useful beyond this model. Evaluating forecasts only on hours with large price moves, a common practice, makes Lévy forcing look better in every market, whereas the proper threshold-weighted CRPS over all hours shows it is worse (Section 4.6, Figure 1, Table 6). This is a concrete instance of the forecaster's dilemma in heavy-tailed neural forecasting, with a clear recommendation: tail claims should rest on proper weighted scores computed over all observations. We also show that a well-specified volatility model (GARCH-tt) gives better tail forecasts than either SDE, which points to state-dependent forcing as the more promising direction (Section 5).

Thank you for this revision. All my serious concerns have been honestly addressed, and I'm inclined to raise my mark.

AuthorsOpenReview ↗

Thank you to Reviewer bM7s

Thank you for reading the revision and for your reply. We are glad the changes address your concerns. Your suggestions, especially framing the paper around the matched comparison and testing the predictive distributions with proper scores, substantially improved the paper. If any remaining points would be useful to clarify before the discussion closes on 18 November, we would be happy to address them.

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

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