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Under review as a conference paper at ICLR 2027

Auditing Structured Forecasting Losses: Error Correction and Exact-Fit Optimality

Abstract

Structured forecasting losses combine error components and auxiliary statistics to guide learning. We audit whether these combinations pre- serve error correction after partial fit and favor exact agreement with fixed targets. In DBLoss, the trend-gradient coefficient vanishes at exact seasonal fit, leaving nonzero level biases stationary. On a fixed batch, a positive integrating factor yields a direction-equivalent scalar potential whose global minimizers still include these biased forecasts. Controlled recovery experiments on fifteen saved models test quadratic field attenu- ation near this boundary and show optimizer-dependent recovery. For the published RI-Loss helper, explicitly activated in our runner, we iden- tify how a finite-sample statistic favors residual-channel dispersion. We derive a sharp weight threshold for the full objective averaged over surro- gate noise. Zero residual is the unique global minimizer for nonnegative weights up to and including the threshold, and a saddle in residual space above it. Source checks, stochastic trajectories, and neural-parameter perturbations at constructed agreement test the local predictions. Match- ing dropout randomness largely removes the observed short-run effect of statistic replacement. Extensions to Time-o1 and PS Loss use controlled interventions to identify how equivalent encodings and batch-statistic scope alter learning signals. Five-source forecasting comparisons show heterogeneous predictive effects under the tested budgets. The resulting coefficient and weight conditions make error correction and exact-fit optimality directly testable.

Primary area:
learning on time series and dynamical systems
Keywords:
time series forecasting, loss functions, structured objectives, statistical elicitation, optimization

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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_rxPuOpenReview ↗
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Paper summary

This paper studies structured forecasting losses to test whether they preserve error correction and exact-fit optimality. For DBLoss, the authors show that exact seasonal fitting can eliminate trend-correction gradients and derive a direction-equivalent scalar potential. For RI-Loss, they find a sharp auxiliary-weight threshold. Below this, it has the unique global minimizer of the expected objective and above it, it becomes a saddle point. The theoretical findings are validated through numerical gradient checks, controlled optimization experiments, and neural-parameter perturbations. There are also analyses of Time-o1 and PS Loss testing representation invariance and batch-statistic sensitivity.

Critical strengths

The paper has some theoretical characterization of failure mechanisms in structured forecasting objectives. These results provide concrete mathematical conditions that can guide future loss design and hyperparameter selection. It has validated its theoretical results, including source-level derivative checks and controlled SGD/Adam comparisons.

Critical weaknesses

One of the limitations is that several central failure modes are shown under certain conditions rather than ordinary training trajectories. The DBLoss experiments use controlled residual interpolation and frozen-model bias adapters, while the RI-Loss curvature experiments construct exact agreement using model-generated targets. Moreover, Adam can reduce much of weak nonzero correction signals. Thus, the problems in its theoretical framework may not always translate into real optimization problems. The results also have uneven experimental depth, and the RI-Loss analysis focuses on an explicitly activated helper rather than the default training path.

Questions for authors
  1. How frequently does the DBLoss stationary-bias or near-zero correction regime occur during ordinary end-to-end forecasting training, particularly when using Adam?

  2. Can the authors demonstrate whether selecting RI-Loss auxiliary weights below the derived threshold consistently improves optimization stability or forecasting accuracy on real datasets?

  3. How representative is the explicitly activated RI-Loss helper of the configurations used to obtain the original method's reported results, and do the theoretical conclusions extend to those configurations?

  4. For Time-o1 and PS Loss, how frequently do the identified representation and batch-statistic sensitivities arise in standard implementations without deliberately constructed interventions?

1 comment
AuthorsOpenReview ↗

Response to Reviewer rxPu

Thank you for helping us examine the connection to ordinary training. We appreciate your emphasis on checking how the analysis applies to the training process. Below we summarize the additional evidence and its limits. References are to the revised manuscript.

Q1. DBLoss frequency and Adam

No exactly zero coefficient was recorded in 386,400 native updates across five runs per dataset. The marker cT=0.5S/(T+ϵ)<0.1c_T=0.5S/(T+\epsilon)<0.1 and T/τ≥0.25T/\tau\geq0.25 occurred in 45,600/45,600 Exchange updates (100%) and 21,398/340,800 Solar updates (6.28%); ϵ=10−8\epsilon=10^{-8} and τ\tau is persistence trend MAE on training windows (Table 12).

We agree that Adam's behavior also needs to be checked directly. Separate five-seed probes fixed parameters, batch and Adam moments, floored cTc_T at 0.1, and matched native displacement lengths. Median vector differences divided by native step length were 51.70% and 17.57%; steps reducing trend MAE increased from 99/120 to 113/120 and 102/120 to 114/120, respectively (Table 13). Adam usually continued correcting error. The marker is not a failure criterion, and these separate cohorts do not yield the fraction of all updates materially affected.

Q2. Below-threshold forecasting results

Half-critical RI (λcrit/2\lambda_{\rm crit}/2) improved test MSE over RI-10 in all five paired seeds per principal setting. To address your consistency question, we report both the paired-seed result and the plain-MSE baseline. Each objective used learning rates selected on separate development seeds and 60 complete epochs without early stopping; test MSE used validation-selected checkpoints (Table 2). Model configurations and loss weights were fixed.

SettingPlain MSERI-10Half-critical RIChange vs. RI-10
Weather/PatchTST0.145200.157730.14630−7.25%
Exchange/DLinear0.091290.114850.09129−20.51%
Solar/DLinear0.222970.232400.22298−4.06%

Values are means; changes use unrounded means. Plain MSE was lowest among the four RI comparison arms before rounding. Earlier 30-epoch ETTh1 results slightly favored RI-10 (+0.06% for half-critical RI), and the weight sweep showed no clear threshold transition (Table 19). This supports the tested comparisons, not a universal weight-selection rule or numerical-stability advantage; it does not isolate the threshold condition's causal effect.

Q3. Implementation and theoretical scope

We verified the README's activation path for the weight-10 DLinear helper; five inspected default entries use MSE. We found no run records in the inspected release linking this path to the original reported scores, and did not reconstruct the original end-to-end benchmark runs. On one ETTh2 batch with shared surrogate draws, the activated code and our implementation had identical prediction gradients and a maximum parameter-gradient difference of 9.31×10−109.31\times10^{-10} (Appendix B.1).

Appendix A.4 extends the threshold to specified kernel scales and batch normalizations under the same biased-estimator and independence assumptions. Under Appendix A.5's assumptions, the standard signed, unclipped unbiased version instead preserves unique exact-fit optimality at every nonnegative weight. These conclusions do not cover unverified historical configurations.

Q4. Time-o1 and PS in ordinary pipelines

The natural-occurrence question remains partly open. We appreciate your distinction between a measured sensitivity and how often it occurs in ordinary training. Without manual sign flips, 0/384 observed Time-o1 residual batches had projected energy below 1% of scale-normalized residual energy (Table 22); this is not a sign-flip frequency estimate.

For PS, regrouping identical examples with fixed predictions, effective batch size and Adam history changed updates by more than 1% in 192/192 comparisons per dataset: median 4.01% on ETTh1 and 8.19% on ETTh2. Sharing pooled patch geometry and detached weights removed differences to numerical precision (Table 23). This measures intervention sensitivity, not natural incidence or test-error deterioration; both analyses remain in the appendix.

Reviewer_nva6OpenReview ↗
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Paper summary

This paper analyzes two common structured losses in time series forecasting, DBLoss and RI-Loss. The paper claims that for DB Loss, some edge cases ("blind spots") have zero gradients even when the forecast error is nonzero, which effectively stops learning under SGD. For RI Loss, the paper claims that a perfect forecast is a local saddlepoint for weights above a critical λCrit\lambda_{\text{Crit}}, which is an implemenation bug.

Critical strengths
  • The main propositions, particularly Proposition 4, appear correct, although they are elementary.
  • The claim about the limitations of the DBLoss with respect to the edge case (zero seasonal error gives zero error) is technically correct.
Critical weaknesses
  • The paper has serious clarity issues. The introduction uses unclear jargon, uses notation before defining it, and discusses implementation details before establishing the problem formulation. Figure 1 mixes plots and math expressions, most of which are never defined in the main body, and the caption does not clarify their meaning.
  • The impact and novelty of the contributions is unclear. The gradient is exactly zero only in edge cases. Around the edge cases it is small but nonzero, and adaptive optimizers such as Adam rescale it so learning continues (Table 3). The RI-Loss analysis is about a helper function in the original authors’ code. It uses a biased estimator, while the RI paper reportedly defines an unbiased one. The paper does not explain how its contribution goes beyond identifying this implementation issue. The empirical results on the DBLoss paper also call into question how much this is a significan problem in practice. Finally, most of the theory is just elementary propositions: eg Proposition 1 is just a chain rule identity.
Questions for authors
  1. Any loss built on batch statistics fails partition invariance. What is surprising here?
  2. The RI paper's Definition 2 uses a U-statistic, but you analyze the biased HSIC helper. Do Propositions 3 and 4 survive with an unbiased estimator? If its expectation is zero under independence, isn't the finding an implementation artifact rather than a flaw in the method?
  3. How close does S/(T+ϵ)S/(T+\epsilon) get to zero in practice during training?
1 comment
AuthorsOpenReview ↗

Response to Reviewer nva6

Thank you for the careful assessment. Your questions helped us clarify the estimator assumptions and the practical scope. References are to the revised manuscript.

Q1. Partition invariance

We agree that batch dependence itself is familiar, and appreciate your request to clarify what the audit adds. Our narrower point is that using batch statistics does not by itself imply partition dependence: population variance plus squared mean equals mean squared residual, preserving the loss under sample-count-weighted regrouping at fixed predictions.

For PS, sharing pooled detached weights removed gradient and Adam-update differences on ETTh1; ETTh2 required sharing both weights and patch geometry (Table 23). This identifies implementation-specific requirements; it does not estimate their prevalence in unmodified pipelines or effects on test error.

Q2. Biased versus unbiased RI

Thank you for drawing attention to the estimator distinction. We agree that it changes the answer, and address the unbiased case explicitly below. The dispersion expression and finite threshold in Propositions 3–4 do not carry over to the standard signed, unclipped unbiased estimator. With at least four channels, zero-diagonal Gaussian Gram matrices and iid surrogate rows independent of fixed residuals, its statistic has zero conditional expectation and vanishes at exact fit on every draw. Jensen's inequality gives

Ru(r)−Ru(0)≥∥r∥F2BDH,λ≥0.R_u(r)-R_u(0)\geq\frac{\lVert r\rVert_F^2}{BDH},\qquad\lambda\geq0.

Exact fit therefore uniquely minimizes the expected objective at every nonnegative weight (Appendix A.5). The exponential auxiliary requires this additional argument: zero statistic expectation does not make its expected value constant.

For the biased helper, exact fit uniquely minimizes the expected objective at nonnegative weights up to and including the critical value, and becomes a residual-space saddle above it. The contribution is this estimator-dependent characterization, not a claim that every RI formulation or the unverified configurations behind the original benchmarks are flawed.

Q3. How small is the DB ratio in training?

To answer your question quantitatively, we recorded the ratio in five native runs per dataset. The following summarizes the observed values (Table 12):

S/(T+ϵ)S/(T+\epsilon)ExchangeSolar
Minimum0.008250.06354
Range of per-run medians0.02220–0.022250.12991–0.12998

The coefficient is half this ratio (β=0.5\beta=0.5, ϵ=10−8\epsilon=10^{-8}). No exact zero was recorded in 386,400 updates across both datasets.

In a separate cohort, native Adam reduced trend MAE in 99/120 Exchange and 102/120 Solar probes. With parameters, batch and Adam moments fixed, a coefficient floor of 0.1 at matched displacement length changed update vectors by medians of 51.70% and 17.57% (distance divided by native step length; Table 13). Adam usually continued correcting error. The separate cohorts do not estimate the fraction of all updates materially affected, and the floor did not lower mean test MSE in full training (Tables 18 and 21).

Reviewer_bwSKOpenReview ↗
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Paper summary

The paper audits whether several structured forecasting losses continue to correct remaining error and whether exact prediction is locally or globally optimal. It derives a stationary level-bias boundary for DBLoss, a sharp auxiliary-weight threshold for an RI-Loss helper, and additional tests for Time-o1, PS Loss, and other objectives. Source-level checks, curvature probes, matched-randomness controls, and forecasting experiments are used to connect the derivations to implemented updates.

Critical strengths
  1. The paper moves beyond comparing final benchmark numbers and derives concrete, testable conditions on the actual update field. The DBLoss coefficient analysis and the RI exact-fit threshold are technically substantive and clearly separated from claims about optimizer behavior.
  2. The implementation-level controls are strong. In particular, matching dropout randomness, restoring whole-batch statistics, checking neural parameter directions, and distinguishing seed variation from source-level uncertainty make the causal interpretations more credible.
Critical weaknesses
  1. The practical relevance of the two sharp failure states remains unclear. The DBLoss experiments use label-based interpolation toward exact seasonal fit, and the RI experiments construct exact agreement targets; the paper does not measure how often training trajectories approach these regions closely enough to affect ordinary forecasting. This matters because Adam can overcome small but nonzero DBLoss attenuation, while the RI helper analyzed here is explicitly activated in a controlled runner rather than being the pinned default training entry.
Questions for authors
  1. How frequently do ordinary DBLoss and RI training trajectories enter neighborhoods where the derived attenuation or negative curvature changes the optimizer step materially?
  2. Was the analyzed RI helper and weight used in any reported experiment of the original method, or is it only exposed in the released code while the default entry trains with MSE?
  3. Do the coefficient-floor and below-threshold controls improve or stabilize forecasting under fully tuned, longer-budget training rather than only the constructed local probes?
1 comment
AuthorsOpenReview ↗

Response to Reviewer bwSK

Thank you for helping us distinguish practical frequency, implementation scope, and forecasting outcomes. We appreciate your emphasis on whether the mathematical cases affect the optimizer and the resulting forecasts. References below refer to the revised manuscript.

Q1. Frequency and actual Adam updates

We observed attenuation and directional effects, but have not estimated the fraction of all updates materially affected. We agree that occurrence counts and controlled interventions answer different parts of your question, so we report them separately.

Across five native DBLoss runs per dataset, none of 386,400 updates had a zero trend coefficient. The marker requires cT=0.5S/(T+10−8)<0.1c_T=0.5S/(T+10^{-8})<0.1 and T/τ≥0.25T/\tau\geq0.25, where τ\tau is persistence trend MAE on training windows (Tables 12–13).

MeasurementExchangeSolar
Trace: attenuation with remaining error45,600/45,600 (100%)21,398/340,800 (6.28%)
Separate probes: median update-vector difference51.70%17.57%
Separate probes: trend-MAE reductions, native → floor99/120 → 113/120102/120 → 114/120

The separate five-seed probe cohort fixes parameters, batch and Adam moments, floors cTc_T at 0.1, and matches actual displacement length. Differences are vector distance divided by native step length. Adam usually continued correcting error. The marker describes attenuation, not failure; these cohorts cannot yield the all-update incidence of material effects.

For RI, at the same 20 scheduled checkpoint–batch pairs using observed targets, searched directions passed the negative-curvature screen in 20/20 cases and native Adam directions in 0/20, with all Adam curvature estimates positive (Table 15). These checks establish available negative directions, not their all-update prevalence or use by Adam.

Q2. Which RI implementation was verified?

We inspected the released code and README and verified the documented activation path, but found no run records in that release linking it to the original reported scores. We did not reconstruct the original end-to-end benchmark runs. The README documents activation of the DLinear helper with training weight 10; five inspected default entries use MSE. On one ETTh2 batch with shared surrogate draws, the activated code and our runner had identical prediction gradients and a maximum parameter-gradient difference of 9.31×10−109.31\times10^{-10} (Appendix B.1). This verifies the documented loss call, not historical benchmark configurations.

Q3. Longer training and forecasting

Half-critical RI (λ=λcrit/2\lambda=\lambda_{\rm crit}/2) improved over RI-10; the DB floor did not lower mean test MSE. To examine the broader training setting you asked about, we added the following comparisons. Each fixed objective independently selected learning rates on development seeds, then trained five reporting seeds for 60 complete epochs without early stopping. Test errors use validation-MSE-selected checkpoints.

SettingComparisonRelative mean test-MSE change
Weather/PatchTSTHalf-critical RI vs. RI-10−7.25%
Exchange/DLinearHalf-critical RI vs. RI-10−20.51%
Solar/DLinearHalf-critical RI vs. RI-10−4.06%
Exchange/DLinearFloor vs. DBLoss+0.305%
Solar/DLinearFloor vs. DBLoss+0.141%

Changes use unrounded means (Tables 2 and 18). Half-critical RI improved in all five paired seeds per setting, but plain MSE had the lowest means among the four RI comparison arms before rounding. DB MSE block-resampling intervals spanned zero (Table 21). Earlier ETTh1 results slightly favored RI-10, and the weight sweep showed no clear threshold transition (Table 19). These results do not establish numerical-stability gains; learning-rate selection was not full hyperparameter tuning.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Summary of revisions and main findings

Thank you for the careful assessment. The reviewers’ questions guided additional checks and a clearer statement of the contribution and its limits. References below are to the revised manuscript.

The revision substantially reorganizes the paper around the original questions about DBLoss correction and exact-fit optimality for the biased RI helper. The DBLoss bias and potential analysis and the biased RI threshold were already in the submission. In response to the reviews, we extend the theory to standard signed, unclipped unbiased HSIC (Appendix A.5), add measurements during ordinary training and Adam controls with matched step lengths (Tables 12–16), and report 60-epoch comparisons with separately selected learning rates (Table 2). Time-o1 and PS remain in the appendix. We also narrow the practical interpretation: these results do not establish a general forecasting advantage or identify these mechanisms as the sole cause of forecast differences.

Core contribution

For adaptive DBLoss, exact seasonal fit can eliminate the correction signal despite a remaining level bias; these forecasts also globally minimize the constructed fixed-batch potential (Section 3).

For the released biased RI helper, exact fit uniquely minimizes the expected objective for 0≤λ≤λcrit0\leq\lambda\leq\lambda_{\rm crit} and becomes a residual-space saddle above that boundary. The standard signed, unclipped unbiased estimator instead preserves unique exact-fit optimality at every nonnegative weight, assuming at least four channels, zero-diagonal Gaussian Gram matrices and iid surrogate rows independent of fixed residuals (Appendix A.5). The guarantee therefore depends on the estimator.

Ordinary training and actual updates

Five native DBLoss runs per dataset recorded 386,400 updates in total (Tables 12–13).

MeasurementExchangeSolar
Exactly zero trend coefficient0/45,6000/340,800
Attenuation marker45,600/45,600 (100%)21,398/340,800 (6.28%)
Separate probes: median update difference51.70%17.57%
Probes reducing trend MAE, native → floor99/120 → 113/120102/120 → 114/120

The marker requires cT=0.5S/(T+ϵ)<0.1c_T=0.5S/(T+\epsilon)<0.1 and T/τ≥0.25T/\tau\geq0.25, with ϵ=10−8\epsilon=10^{-8} and τ\tau the persistence trend MAE on training windows. In a separate five-seed cohort, paired probes fix parameters, batch and Adam moments, floor cTc_T at 0.1, and match displacement length. Difference is vector distance divided by native step length. Native Adam usually continued correcting error; these separate cohorts do not estimate the fraction of updates materially affected.

For RI, searched directions passed the negative-curvature screen at 20/20 scheduled state–batch pairs using observed targets, while native Adam directions at those same pairs passed at 0/20, with all Adam curvature estimates positive (Table 15). These checks do not establish how often Adam encounters or follows negative curvature.

From those origins, 256-step MSE continuations at RI-10’s step lengths reduced validation MSE relative to native RI-10 by mean paired percentages of 0.88–0.98% on ETTh2 and 4.48–5.00% on Weather across the two starting epochs. This does not isolate curvature’s causal contribution (Table 16).

Forecasting and remaining limits

The principal comparisons use 60 full epochs, independently selected learning rates, five reporting seeds, and validation-selected checkpoints. Mean test MSE is shown below; changes use unrounded means and half-critical RI uses λcrit/2\lambda_{\rm crit}/2 (Table 2).

SettingPlain MSERI-10Half-critical RIChange vs. RI-10
Weather/PatchTST0.145200.157730.14630−7.25%
Exchange/DLinear0.091290.114850.09129−20.51%
Solar/DLinear0.222970.232400.22298−4.06%

All five paired seeds improved over RI-10 in each setting; plain MSE remained lowest among the four RI comparison arms before rounding. The DB floor increased mean test MSE by 0.305%/0.141% on Exchange/Solar, although MAE decreased by 0.625%/1.119%. MSE block-resampling ranges included zero (Tables 18, 21). The earlier ETTh1 comparison favored RI-10 slightly, and the weight sweep showed no clear predictive breakpoint at the threshold. We have not established a general forecasting or numerical-stability benefit.

We verified the README-documented RI loss call against our implementation on one batch. We found no run records in the inspected release linking it to the original reported scores, and did not reconstruct the original end-to-end benchmark runs (Appendix B.1). Our conclusions concern specified implementations and assumptions. Time-o1 and PS remain supplementary checks whose prevalence across training pipelines remains unmeasured.

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