XSci

Cap-Aware Boosting for Green Day-Ahead Electricity Price Forecasting

Shubham Pratap

Submitted by Shubham Pratap

Published November 19, 2026 · Version v1, November 19, 2026 · DOI 10.66977/xsci.2611.003a

Machine Learning

Abstract

Forecasting 15-minute Market Clearing Prices in the Indian Energy Exchange Green Day-Ahead Market (GDAM) is complicated by pronounced diurnal renewable cycles and frequent upper price-cap events (10,000 Rs/MWh10,000\text{ Rs/MWh}). We propose a leak-safe, cap-aware LightGBM architecture that blends an L1L_1 log-price regressor with an upper-price classifier alongside nine rolling-calibrated quantile heads. Across 257 delivery days (January–September 2026; 24,672 blocks), our baseline model achieves 397.9 Rs/MWh397.9\text{ Rs/MWh} MAE and 171.6 Rs/MWh171.6\text{ Rs/MWh} mean pinball loss, cutting MAE by 31.8%31.8\% relative to a zero-shot univariate Chronos-2 model (583.3 Rs/MWh583.3\text{ Rs/MWh}) and 32.5%32.5\% over persistence (589.1 Rs/MWh589.1\text{ Rs/MWh}). On a volatile October–November 2026 holdout, decoupling uncapped price regression from cap classification while adding pre-gate covariates—same-morning real-time prices, prior-day unmatched sell volumes, and capacity-weighted clear-sky solar irradiance—further reduces MAE to 716.0 Rs/MWh716.0\text{ Rs/MWh} versus 2,000.4 Rs/MWh2,000.4\text{ Rs/MWh} for Chronos-2. Domain-informed covariates within cap-aware boosting drive accuracy gains far more effectively than replacing tabular ensembles with univariate foundation models.

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Review reports

xPeerd (AI review)

November 19, 2026

AI Review (xPeerd — DAReview)

Summary

This manuscript studies 15-minute Green Day Ahead Market (GDAM) electricity price forecasting in India using a sequence of LightGBM-based systems against persistence baselines and saved Chronos-2 runs. Its main empirical claim is that Prod v1 reduces MAE by about one third relative to both a saved univariate Chronos-2 run and previous-day persistence over 257 delivery days from 1 January to 14 September 2026; Prod v2 is nearly tied with v1 on aggregate MAE, while later October–November experiments show exp5 and exp7 outperform a separate slim Chronos-2 checkpoint on a shorter, harder window. The manuscript’s strengths are unusually explicit discussion of information availability, leakage controls, paired daily comparisons, and limitations; it also documents reproduction commands and audit details better than many applied forecasting papers. However, the evidential basis for several comparative conclusions is narrower than the prose sometimes suggests: major comparisons rely on saved single runs, different Chronos-2 configurations are used in different tables, v2 feature design was informed by in-period diagnostics, and later-system conclusions come from short post hoc windows rather than a pre-registered holdout. The uncertainty analysis is careful but conditional on fixed saved forecasts rather than full retraining variability. Overall, I find the paper coherent and technically serious, but the current version reads more like a strong internal audit / engineering case study than a fully matured scientific comparison with fully controlled external validity and reproducibility guarantees.

Potential Major Revisions

  1. Clarify the exact scientific claim and narrow over-broad comparative language.

The paper is strongest when it makes restricted, operational claims, but weaker when it implies broader model-class conclusions. For example, the conclusion states: “The gain is in the inputs—morning RTM, yesterday’s unmatched sell, and the clear-sky curve—not in replacing the tree model with Chronos-2.” Page 13, Section 9, this is too strong given that the main Chronos-2 comparator is explicitly “the archived run … univariate GDAM, no covariates, no fine-tune” and that the later tables use “a saved slim checkpoint, not the univariate run in Table 3.” A fairer interpretation is that the audited LightGBM stacks beat the specific saved Chronos-2 configurations evaluated here, not that trees beat Chronos-2 as a modeling family. The paper partly acknowledges this in Related Work: “That is a real production alternative, not a claim about every Chronos-2 configuration.” Page 2, Section 2. I recommend revising the title, abstract, and conclusion to keep every superiority claim tied to the exact saved baselines and configurations.

  1. Strengthen the validity of the retrospective evaluation design.

The limitations section already admits that “V2’s features were chosen with July 2026 diagnostics in hand, so January–September is a retrospective check, not an untouched holdout.” Page 12, Section 8. This is an important threat to validity, not a minor caveat. If features were selected after exposure to part of the evaluation year, aggregate improvements over the same year no longer cleanly estimate forward generalization. The same concern appears for exp7, where “The quantile mix inside exp7 was fixed from earlier misses; it was not re-tuned on the 21-day table, but it is also not a pre-registered rule.” Page 12, Section 8. These are sensible engineering choices, but scientifically they reduce the force of comparative claims. The manuscript should either:

  • relabel the study explicitly as retrospective audit / production backtest rather than prospective benchmark, or
  • add a fully untouched post-design holdout with fixed pipelines and no design iteration.
  1. Address the mismatch in training histories and comparator fairness more directly.

The paper states that “the evaluation targets are matched but the training histories differ.” Page 3, Section 3. Prod v1 starts from 1 May 2022, while Prod v2 and Chronos-2 start from 1 April 2022. Appendix Table 10 quantifies this difference in usable rows and inputs. This is not fatal, but it complicates attribution: gains may partly reflect more or different history, feature richness, or retraining design rather than model class. Similarly, Chronos-2 is evaluated as a saved pretrained inference setup with “no exogenous covariates and no fine-tuning flag,” while the tree systems use many handcrafted features and repeated refits. Because the paper compares heterogeneous systems, it should include a dedicated subsection on comparator fairness that separates:

  • model family differences,
  • information-set differences,
  • feature-engineering differences,
  • historical window differences,
  • and tuning effort differences.
  1. Expand reproducibility claims and reduce ambiguity around exact reruns.

The manuscript commendably includes commands and environment details, but also concedes key reproducibility gaps. It says: “The exact immutable checkpoint revision is not present in the run log.” Page 15, Section A.3. It also notes that the inspected Python environment is not guaranteed to match the historical training environment, and that rerunning is “a new experiment.” The package “does not establish public availability or permission to redistribute the underlying IEX data or employer-owned code.” Page 16, Section A.4. As written, reproducibility is partial: readers can audit outputs and perhaps recompute tables, but not necessarily reproduce the reported forecasts exactly. The paper should distinguish clearly between:

  • computational reproducibility of tables from saved outputs,
  • repeatability of training within the same proprietary environment,
  • and external reproducibility by third parties. At minimum, the manuscript should state explicitly which results are exactly recomputable from archived predictions and which are not.
  1. Reassess the uncertainty framing and the inferential scope of the bootstrap intervals.

The uncertainty procedure is transparent, but the interpretation risks overreach if not sharply bounded. The paper notes that the intervals are “approximate uncertainty intervals conditional on the saved forecasts; they neither measure refitting variability nor resolve test-set selection effects.” Section 5/6 transition and Appendix B.2. This is appropriate. However, some readers may still infer stronger evidence than warranted from Table 4 or Table 13. In particular, the interval against v2 spanning zero is correctly described as “insufficient evidence of a stable aggregate MAE distinction … not a formal equivalence result.” Page 10, Section 7.1. I recommend moving that caution into the main results narrative more prominently and adding at least one complementary robustness analysis, such as refit-seed sensitivity for LightGBM or rolling-origin subperiod analysis, because the current setup uses no explicit LightGBM seed in the runner.

  1. Resolve the tension between point-forecast success and uneven uncertainty quality.

The manuscript reports promising global uncertainty metrics for v1, including nominal-80% coverage of 81.21% with the lowest pinball loss among saved probabilistic forecasts. Yet it also acknowledges a serious failure mode: “On the 464 blocks below 1,000 Rs/MWh, v1’s nominal-80% coverage is only 64.01%, despite its 81.21% overall value.” Page 17, Appendix/Table 14. The limitations section similarly states: “The quantile residual shift has no coverage theorem; coverage on prices below 1,000 Rs/MWh is 64%.” Page 12, Section 8. This is materially important because low-price periods may be operationally salient, and the paper otherwise highlights solar-daylight structure. The uncertainty section should discuss the practical consequences of this miscalibration in more depth and test whether calibration can be improved specifically in the low-price regime.

  1. Make leakage control easier to audit in the main text.

One of the paper’s strengths is careful information-set discipline. For example, Section 6.1 states: “Anything after the gate is deleted before a single lag is computed,” and then formalizes GDAM/DAM and RTM cutoffs, with exp5/exp7 only seeing blocks 0–35 of D−1 before the 10:00 IST gate. However, because leakage concerns are central to credibility, this material should be condensed into a single explicit audit table in the main text showing for each model which variables are available at forecast issue time. That would strengthen the paper substantially and reduce ambiguity around why later experiments are “leak-safe Prod v2” or “InputFix.”

  1. Add a stronger discussion of external validity and operational meaning.

The introduction properly warns that “forecast accuracy alone does not establish financial value.” Page 1, Section 1. The limitations then reiterate: “This paper does not evaluate bids or trading P&L.” Page 12, Section 8. Given that framing, the paper should go further and discuss what level of MAE reduction would matter operationally, especially because error heterogeneity is large, tail errors remain expensive, and “near-zero mean bias does not mean cheap tails.” Page 11, Section 7.3. Without at least a stylized decision-theoretic link, the practical significance of differences such as 397.9 vs 395.5 MAE remains uncertain even when statistically described.

Potential Minor Revisions

  1. Typographic and formatting issues.

The PDF contains multiple text-encoding artifacts that should be corrected before submission. Examples include:

  • “24,672 blocks) v1 has MAE 397.9 … interval for v1 minus v2 of [−7.8, 12.6] Rs/MWh. From 25 October we compare the same question on a later, harder stretch. Exp5 adds morning real-time prices...” where line-joining and hyphenation appear uneven in the abstract.
  • “24,672 blocks) v1 has MAE 397.9 … 14-day block￾bootstrap interval” shows a visible encoding artifact in “block-bootstrap.”
  • “per￾sistence baselines,” “residual￾quantile,” “Other￾RE/DRE,” and “Conformalized quan￾tile regression” each show broken ligature or hyphen encoding.
  • The reference “Hans R. K"unsch” is incorrectly encoded and should render as “Künsch.” These are production-level issues but numerous enough to distract readers and should be cleaned systematically.
  1. Section-to-section naming consistency.

The manuscript alternates between “Prod v1,” “V1,” “Prod v2,” “V2,” “InputFix Prod v2,” “exp5 (v3_full),” “exp7 (seasonal_master),” and two distinct Chronos-2 variants. See, for example, Section 1, Table 3, and Tables 7–9. This is understandable internally but makes the narrative harder to follow. A naming table near the start would help.

  1. Some wording is too colloquial for an archival paper.

Phrases such as “Chronos-2 is not close” in Section 7.4 and “The gain is in the inputs” in the conclusion are punchy but somewhat informal and stronger than the evidence warrants. A more neutral wording would better suit a scientific manuscript.

  1. Clarify whether all equations and symbols are defined at first use.

The core notation around yd,b, yhatd,b, ed,b, solar band S, and metrics is introduced carefully in Section 3. However, the later “Eq. (13)” and “Eq. (17)–(18)” references in the experiment stack descriptions would benefit from a one-phrase reminder of what those equations represent, especially for readers jumping between sections.

  1. Improve figure and table self-containment.

Several tables are interpretable only if the reader already remembers which Chronos-2 version is being referenced. Table 7 explicitly clarifies that it uses the “saved slim AutoGluon checkpoint,” which is good, but this distinction should be visually standardized across all later tables. Likewise, Table 3 and the later tables belong to different comparison regimes and should be visually separated more forcefully.

  1. AI content analysis.

Estimated AI-generated content: low to moderate, approximately 10–20%.

Rationale: the manuscript is technically specific, internally cross-referenced, numerically dense, and includes nuanced caveats that are more characteristic of human-authored technical writing than generic AI drafting. That said, some sentences have a polished, compressed, “audit-summary” cadence that could have been AI-assisted, especially in explanatory transitions such as “Coverage alone therefore gives an incomplete assessment” and “The picture changes once the window is long enough to include early November.” I do not see obvious large sections that read as fabricated or semantically hollow. The epistemic impact of possible AI assistance appears limited, because the paper’s main credibility depends on verifiable experimental design, archived outputs, and quantitative tables rather than rhetorical novelty. Still, if AI tools were used in drafting, careful proofreading is needed because the PDF shows several encoding and formatting defects inconsistent with polished journal submission quality.

  1. Fraud / paper-mill screening.

I do not see strong paper-mill traits. The work fits a recognizable scientific paradigm: applied time-series / electricity-price forecasting with tabular ML baselines, rolling evaluation, uncertainty scoring, and audit-style reproducibility appendices. The manuscript explicitly acknowledges limitations rather than hiding them, which weighs against fabrication. However, one integrity-sensitive issue deserves continued scrutiny: the study relies on proprietary code, saved runs, and incomplete public reproducibility, so readers must trust the audit chain more than they would in a fully open benchmark. This is not evidence of fraud, but it does heighten the need for exact artifact versioning and clearer release status.

Recommendations

  1. Reframe the paper as a rigorously audited applied forecasting case study unless a cleaner out-of-sample benchmark can be added. This would align the manuscript with its strongest evidence and avoid overstating generality.

  2. Tighten every comparative claim so it refers to the exact saved baselines evaluated. In particular, distinguish:

  • univariate Chronos-2 on the 257-day window,
  • slim checkpoint Chronos-2 on the October–November window,
  • and LightGBM stacks with different feature sets and issue-price rules.
  1. Add one untouched post-design holdout period with fixed pipelines, or if unavailable, explicitly mark the study as retrospective and exploratory in the abstract and conclusion.

  2. Provide a main-text audit table of information availability by model and by data source at issue time, since leakage discipline is a key contribution of the paper.

  3. Expand reproducibility documentation with immutable checkpoint identifiers, exact package locks where possible, and a precise statement of what third parties can and cannot rerun exactly.

  4. Investigate regime-specific calibration fixes for low-price blocks, because the current uncertainty story is good in aggregate but weak in that important subset.

  5. Add at least one robustness analysis addressing refit variability or seed sensitivity, especially since the LightGBM seed is “not explicitly set.”

  6. Thoroughly proofread the PDF for encoding errors, symbol rendering, and nomenclature consistency before submission. The technical content is credible enough that presentation flaws are now an avoidable weakness.

Reviewer3 (AI review)

November 19, 2026

AI Review (reviewer3.com)

Overview

Cap-Aware Hybrid Gradient Boosting Architecture

Contribution

This study introduces a gradient boosting framework that combines log-price regression with an upper-price event classifier and quantile blending to effectively model market price caps and extreme intraday price spikes.

Gate-Safe Fundamental Feature Integration

Contribution

The authors demonstrate that incorporating pre-gate morning real-time market data, unmatched auction sell volumes, and clear-sky solar irradiance curves substantially improves short-term price forecasting accuracy over standard time-series baselines.

Comments (11)

1. Figure 3 misstates equation range for exp7 mix — Editorial

exp7 mix Eq. (17)–(13)

In Figure 3 (page 8), the bottom-right box labeled "exp7 mix" cites "Eq. (17)–(13)". However, Equation (13) is the cap-blend formula for exp5, while the exp7 quantile clock mix is defined in Equations (14)–(18) (or as cited in Table 1, "Eq. (17)–(18)"). Writing "Eq. (17)–(13)" is a typo that references the wrong equation range in reverse order.

2. Block count vs. duration of the pre-peak window — Editorial

The hour before the evening cap is the line we care about. On blocks 62–68 (15:30–17:00),

In Section 6.4 (page 9), the text refers to the pre-peak window as "The hour before the evening cap" and states it is "On blocks 62–68 (15:30–17:00)", followed by "After 17:15 the cap classifier returns". Under 15-minute resolution where block 0 is 00:00–00:15 (as established in Section 3 where blocks 24..73 correspond to 06:00 inclusive to 18:30 exclusive, and Section 6.1 where blocks 0–35 are 00:00–08:45), blocks 62 through 68 inclusive comprise 7 blocks (1 hour and 45 minutes), spanning block-start times 15:30 to 17:00 (and ending at 17:15). Referring to this 7-block, 105-minute interval as "The hour before sunset" (page 8) and "The hour before the evening cap" (page 9) conflicts with the 7-block range 62–68 (15:30–17:15).

3. Step 6 is skipped in Table 1 and Figure 2 — Editorial

  1. exp5. Steps 1–4, issued price still Eq. (13) 7. exp7. Wind and other-RE, raw-price loss, quantile clock

In Section 6, both Figure 2 (page 6) and Table 1 (page 7) enumerate the progressive experimental stack by step number, but jump directly from Step 5 ("exp5") to Step 7 ("exp7"), omitting Step 6 without explanation.

4. Unisolated effect of the cap-aware classifier blend — Major

Prod v1 blends a log-price LightGBM regressor with a cap-event classifier. Quantiles are fit

Although the paper highlights cap-aware boosting as a core contribution, Prod v1 is never compared against an uncapped LightGBM regressor (or a direct raw-price L1 tree) using the same 49 features. Without an ablation isolating Eq. (3) from the multi-market lag features, it is unclear how much of the 31.8% MAE reduction over Chronos-2 is driven by the cap-classifier blend versus the lagged DAM and RTM predictors.

5. No statistical uncertainty reported for probabilistic forecast differences — Major

V1 has the lowest mean pinball loss among the three saved probabilistic forecasts. Its nominal- 80% interval covers 81.21% of observations with a mean width of 1,394.6 Rs/MWh. V2 attains

Unlike the point-forecast evaluation in Table 4, the pinball loss and coverage comparisons in Table 6 are presented as single point estimates without block-bootstrap confidence intervals or paired significance tests. Providing paired uncertainty intervals for mean pinball loss differences would establish whether Prod v1's probabilistic advantage over Prod v2 and Chronos-2 is statistically stable across the 257 delivery days.

6. Confounded intermediate steps and hyperparameters between InputFix and exp5 — Major

Table 1 is the list. Figure 2 draws the same list. Exp5 is steps 1 through 4 trained together, and it still publishes the cap blend. Exp7 adds wind and other-renewable sell, changes the loss, and

Although Table 1 and Figure 2 present steps 1 through 4 (hurdle setup with 45-day half-life and price weights, morning RTM, auction shape, and clear-sky GHI) as a sequential stack, only the combined system (exp5) is scored in Tables 7-9. Because exp5 changes the training objective, sample weights, recency half-life, and three distinct feature groups simultaneously without intermediate ablation scores, the error reduction over InputFix cannot be attributed specifically to the domain inputs rather than the hurdle objective or 45-day weighting.

7. Exp7 confounds new renewable sell features with the quantile clock mix — Minor

unmatched-sell shape, and a clear-sky solar curve on top of leak-safe Prod v2. Exp7 keeps those inputs, adds lagged wind and other renewable sell, and issues a block-dependent mix of quantiles instead of the cap blend. On 25–28 October, exp7 has the lowest MAE (789 Rs/MWh), ahead

Exp7 simultaneously adds new predictors (lagged wind sell, other-renewable sell, and a thin-shelf flag) and replaces the cap-blend output rule with the block-dependent quantile clock mix. Because both the feature set and the output rule change together, it is not possible to conclude that the extra quantile rules alone caused the performance reversal between the 4-day October window and the 21-day window.

8. No paired uncertainty or day-level win counts for October-November — Major

InputFix block files are not stored for every one of those 21 days. On the 10 November days where they are (6–12 and 14–16 November; Table 9), the order is the same: exp5 607, exp7 697, InputFix 708, Chronos-2 1,418.

The October-November comparisons in Tables 7-9 rely solely on aggregate MAE and MAPE over small sample sizes (4, 10, and 21 days) without paired daily loss differences, win counts, or bootstrap intervals. Given the high day-to-day volatility in electricity prices, reporting day-level paired statistics is necessary to verify that exp5's advantage over InputFix (e.g., 606.7 vs 708.1 Rs/MWh over 10 days in Table 9) is not driven by one or two extreme outlier days.

9. Incomplete InputFix baseline coverage and stitched Chronos-2 files — Major

InputFix block files are not stored for every one of those 21 days. On the 10 November days where they are (6–12 and 14–16 November; Table 9), the order is the same: exp5 607, exp7 697, InputFix 708, Chronos-2 1,418.

In the 21-day extended window (Table 8), the InputFix baseline is omitted entirely because block-level predictions were only saved for 4 October days and 10 November days, and the Chronos-2 baseline is stitched together from two different file sources across 25-29 October and 30 October-16 November (Appendix C). Re-running or reconstructing InputFix and a single consistent Chronos-2 pipeline across all 21 days would ensure a uniform comparison across the full holdout.

10. Univariate Chronos-2 baseline lacks covariates given to LightGBM — Critical

]. Chronos-2 is a pretrained time-series model that can take covariates [ 1 ]. The run we compare against does not: it is the released checkpoint, univariate GDAM, prediction length 96. That is a

Chronos-2 is evaluated strictly in univariate mode without exogenous covariates, whereas the LightGBM models receive up to 97 multi-market, auction, and solar features. Because Chronos-2 natively supports covariates, comparing a covariate-rich tree model against a univariate neural baseline confounds model architecture with feature availability, leaving untested whether Chronos-2 would perform competitively given the same domain inputs.

11. Potential gate-cutoff leakage in the 257-day Prod v1/v2 runs — Critical

They start from InputFix, which is Prod v2 with one extra rule: the feature row for delivery day D may use only what a desk can know at the 10:00 IST gate.

In Section 6, you introduce InputFix for the October-November stretch by adding the rule that features for delivery day D may only use information available at the 10:00 IST gate, implying that Prod v1 and Prod v2 in the 257-day evaluation did not enforce this strict cutoff. If the 257-day LightGBM runs used unmasked D-1 or D-2 blocks that had not yet cleared by the 10:00 IST gate, their reported accuracy advantage over Chronos-2 and persistence baselines on the main evaluation window may be inflated by look-ahead leakage.

XSci (AI review)

November 19, 2026

Summary

The manuscript reports a production forecasting system for 15-minute clearing prices on the Indian Energy Exchange Green Day-Ahead Market. Prod v1 combines a LightGBM L1 regressor on log price, a classifier for upper-price (cap) events, and nine quantile heads with a rolling residual shift, built on 49 lagged price and calendar features and refit every 14 days. On 257 delivery days (24,672 blocks, 1 January–14 September 2026), v1 reaches MAE 397.9 Rs/MWh against 583.3 for a saved univariate Chronos-2 run and 589.1 for previous-day persistence, while a feature-richer Prod v2 is statistically indistinguishable (paired daily interval [-7.8, 12.6] Rs/MWh). A second study on 25 October–16 November adds two later variants built on a leak-safe reconstruction of v2; exp5 reaches MAE 716 over 21 matched days against 824 for exp7 and about 2,000 for a slim Chronos-2 checkpoint.

Contribution and Significance

The contribution is an audited engineering case study: a cap-aware boosting pipeline for one market, evaluated with more care than industrial forecasting reports usually receive. The evaluation protocol is the real asset — an exact 257×96 grid with matched actuals to 1e-8 (Appendix A.1), two persistence baselines, paired daily losses, and 10,000-replicate circular block-bootstrap intervals with a block-length sensitivity check (Table 13) — and the authors use it to report a negative result about their own system: v2, built second, does not beat v1.

What is new relative to the closest prior work is small. The model components are stock LightGBM objectives with stock settings (Table 11); the market-specific pieces — the clear-sky GHI blend of Equation (10), the unmatched-sell features, and the block-dependent quantile clock of Equations (14)–(18) — are hand-chosen constants fitted by inspection rather than a learned or principled construction. Relative to Lago et al. [10], the paper adopts the stated best practices but implements neither the benchmark models that paper supplies (LEAR and the DNN in epftoolbox) nor its recommended significance tests. Relative to Grinsztajn et al. [4], the finding that trees beat a neural alternative on tabular inputs is a further instance rather than a new result. Appendix A.4 states that neither the IEX data nor the employer-owned code can be released, so the artifact is not reusable either.

Strengths

  • The self-limitation is specific and correctly located: Section 4.1 states that Equation (3) is a heuristic upward adjustment and not an identified mixture mean; Section 4.2 states that the residual shift carries no conformal guarantee; Appendix A.3 notes that v2's own price check was bypassed and is reinstated here.
  • The outcome-conditioned diagnostics in Table 14 are the most informative part of the results: 64.01% coverage of the nominal-80% interval on the 464 blocks below 1,000 Rs/MWh against 81.21% overall, and bias of -374.4 Rs/MWh on the 6,398 cap blocks.
  • Table 6 makes the right comparison for probabilistic forecasts, reporting coverage against sharpness: v2's 83.22% coverage comes with a mean width of 3,565.6 Rs/MWh against v1's 81.21% at 1,394.6.
  • The leak-safety construction for the later stack is written as checkable rules (Equations (7)–(9)): the 10:00 IST gate, and RTM blocks 36–95 of D-1 masked to missing rather than imputed.

Recommendation

Reject for the International Conference on Learning Representations. The 257-day analysis is sound, but for this venue the advance is too small: there is no new learning method, representation, theory, or releasable benchmark, and the components that are new are hand-set constants for a single proprietary market. The one comparison that would interest an ICLR audience — boosting against a pretrained time-series model — is run against that model's weakest documented configuration, and Section 9 nonetheless draws a conclusion about model families from it. An applied energy-forecasting venue would value the careful protocol and the failure-mode diagnostics far more.

Major Concerns

  1. The neural comparison is configured against the baseline's documented strength, yet a model-family conclusion is drawn from it (Sections 2, 5 and 9; Tables 3, 7–9). The Chronos-2 run is "the released checkpoint, univariate GDAM, prediction length 96" with "no covariates" and no fine-tuning, while v1 receives 49 engineered features including DAM and RTM history and is refit every 14 days. Chronos-2 [1] is presented by its authors precisely as a covariate-informed and multivariate model, with its largest reported gains on covariate tasks relative to univariate inference, so the chosen configuration is the one expected to do worst here. Section 2 hedges this correctly, but Section 9 then states that "the gain is in the inputs ... not in replacing the tree model with Chronos-2" — a claim about the model family that the experiment cannot support, since the covariate-enabled configuration that would test it was never run. The headline 31.8% MAE reduction, repeated in the abstract, inherits the same limitation. Resolving this needs one further run: Chronos-2 given the same covariates v1 sees under the same leak-safe cutoffs, ideally alongside a fine-tuned variant and the LEAR and DNN benchmarks of [10].

  2. No experiment isolates any of the gains the paper attributes to specific inputs (Section 6, Table 1, Table 2, Section 7.4, Section 9). Table 1 and Figure 2 present the later work as an incremental stack in which each step adds exactly one change, but only InputFix, exp5 and exp7 are ever scored. Between InputFix and exp5 at least six things move together: the point tree is retrained only below the cap, a floor classifier at 1,005 is added, the half-life drops from 180 to 45 days, a (1000/y)^0.35 weight is introduced, and three feature groups (morning RTM, auction shape, clear-sky GHI) are added. The conclusion that "the gain is in the inputs — morning RTM, yesterday's unmatched sell, and the clear-sky curve" therefore has no supporting measurement; it could as easily come from the hurdle reformulation or the shorter half-life. Appendix C refers to "the Oct ablation files for 25–28 Oct", so the per-step scores may already exist; reporting steps 1 to 4 individually on a common window would settle the attribution.

  3. The later-window evidence is too thin to carry the claims made from it (Tables 7, 8, 9 and Section 7.4). The three later tables rest on 4, 21 and 10 delivery days, and none carries an interval, a paired test, or any uncertainty statement — in sharp contrast to the care taken over the 257-day table. The instability is visible within the paper: exp7 leads on 25–28 October (789.2 against 827.7) and trails over 21 days (823.8 against 716.0), which implies exp5 beats exp7 by roughly 140 Rs/MWh on the remaining 17 days. Since exp7's quantile-clock coefficients were hand-set on earlier misses (Sections 6.4 and 8), and reporting exp5 and exp7 out of a numbered experiment sequence is itself a selection on nearby data, the 21-day ranking should be read as provisional. Applying the paired daily block bootstrap of Section 5 to these windows, and extending them towards the length of the main study, is the minimum needed to support Section 9.

Minor Comments

  1. Section 6.4 describes Equation (17) as a "ramp" from the low pair toward the median and upper quantile, but sunset_pull is 0 on blocks 62–65 and 1 from block 66, which is a step, not a ramp.
  2. The training configuration of exp7's nine quantile heads is never stated, yet the scored exp7 forecast is a mix of exactly those heads; Table 2's exp7 point-target and weight rows describe the two L1 models Section 6.4 says are not scored.
  3. Neither the Diebold-Mariano test nor the LEAR and DNN reference models supplied with Lago et al. [10] appears, though Section 2 cites that paper for "statistically grounded comparisons"; adding at least LEAR and the test is inexpensive.
  4. Section 4.3 and Table 11 record that no LightGBM seed is set for v1 and v2, so every reported gap — including the 108 Rs/MWh between exp5 and exp7 — lacks a refit-noise scale to be judged against.
  5. The Sunday-evening and Monday mixes mentioned at the end of Section 6.4 are never specified, so that part of exp7 cannot be reproduced.
  6. Section 4.1 notes that training prices reach 20,000 while the classifier threshold is fixed at 9,990; please report how many training rows carry a label that does not match the contemporaneous cap.
  7. Given the 64.01% low-price coverage in Table 14, attempting conformalized quantile regression [11] or adaptive conformal inference [3], both already cited, would strengthen the probabilistic claim.
  8. Section 6 is written in a markedly different register from Sections 3–5 ("Midday wants the low quantiles"); unify it with the rest of the paper.
  9. Table 8, the headline later comparison, omits InputFix on 11 of its 21 days, so the production baseline is absent from the window used to rank exp5 above exp7.
  10. The wall-clock figures in Section 8 (v1 17.2 min, v2 38.0, Chronos-2 11.2) are disclaimed as not a benchmark; a proper cost comparison would support the practical case for the pipeline.
  11. The shelf-snap flag that Section 6.3 says is "present in the code and is not used" should be removed from the description or evaluated.