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Under review as a conference paper at ICLR 2027

Beyond Model Ranking: Regime Diagnosis for Distributional‑Statistical Misspecification in Industrial Time-Series Forecasting

Abstract

Time-series forecasting models achieve strong benchmark performance but exhibit severe systematic bias in industrial deployments. This train–deploy gap is conventionally attributed to temporal-structural errors or distribution shifts. We characterize a complementary source that these explanations overlook: canonical losses embed fixed statistical priors, while industrial demand mixes benign and pathological regimes—zero-inflation, skewness, high variability—in which these priors are systematically violated. The induced bias persists even under perfect temporal modeling, remains in a distributional-shape component that normalization cannot remove, and creates an aggregation trade-off invisible to aggregate metrics. We turn these observations into an evaluation toolkit centered on the Regime-wise Relative Bias Vector (RBV): a metric-agnostic, regime-decomposed diagnostic that audits how pooled training allocates systematic mismatch across pathological subpopulations. A controlled attribution analysis decomposes RBV into a model-independent intrinsic floor, set by each loss's estimand, and an excess component attributable to training, tracing observed bias to the loss rather than the model. A large-scale study—13 loss objectives, 3 seeds, 60,000+ series spanning RetailShiftBench and M5, with random-split controls—shows that regime-aware diagnosis separates optimization-type from bias-type failure, and that regime-aware training resolves the pooling-induced bias that capacity scaling cannot, for mean-type losses. A formal structural observation, that risk under evaluation-distribution contamination is affine in the pathology mixture weight, grounds these findings. Our work complements model ranking with mechanism-grounded, regime-oriented evaluation.

Primary area:
datasets and benchmarks
Keywords:
time series forecasting, loss misspecification, sliced evaluation, proper scoring rules, quantile calibration, train-deploy gap

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_bEijOpenReview ↗
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Paper summary

Retail forecasters that rank well on aggregate error still show structured bias once deployed, and the paper argues the cause is a third error class, distinct from temporal-structural error and from distribution shift: the statistical functional a loss implicitly estimates (MSE the mean, MAE the median, pinball a quantile) does not match label-side distributional pathology. Each series is binned on skewness, within-series CV and zero-inflation ratio, test series are grouped into four regimes (Benign/ZIR/Skew/CV), and the proposed Regime Bias Vector is the ℓ2\ell_2 norm of the per-regime mass-ratio biases centred on the global bias. Evaluation runs on an introduced benchmark, RetailShiftBench (31,213 daily SKU series of 89 steps, built without trend breaks), plus M5, with XGBoost and TFT backbones, 13 loss objectives, and a three-stage attribution from pooled training to random-label cells to pathology-defined cells. The headline: WMAPE sits in a narrow 0.427–0.518 band while RBV spans 0.078–0.953, and regime-aware training moves XGB-MSE RBV 0.243 to 0.041 while XGB-Huber goes up 240.3%.

Critical strengths
  • The three-stage attribution is the right experiment, and the random-label control is the part most papers of this kind skip. Cells matched in count and size but with permuted label semantics are nearly inert on M5 (∣ΔRBV∣≤0.04|\Delta\mathrm{RBV}| \leq 0.04), which is what separates "granularity helped" from "pathology semantics helped."
  • Table 12 decodes a mean and a median from a single forward pass of one frozen Chronos-Bolt checkpoint, global bias +0.008+0.008 / RBV 0.381 versus −0.194-0.194 / RBV 0.789, so capacity, architecture and training are held exactly fixed and the gap is the estimand alone. The one place where a central claim and the data behind it line up.
Critical weaknesses
  • RBV, the metric everything rests on, is defined three incompatible ways. §4.2 uses overlapping regimes centred on BglobalB_{\text{global}} and asserts an identity that is false under overlap; Eq. (2) centres on a weighted mean; Algorithm 1 demands a mutually exclusive partition and takes an unweighted ℓ2\ell_2 norm. The implementation is the third, since the unweighted form reproduces Tables 2, 11 and 12 to ±0.001\pm 0.001, so a reader who codes RBV from the body text gets different numbers. The abstract's "intrinsic floor plus training-attributable excess" decomposition then dies on the paper's own p. 29: ql60 pooled RBV 0.11 against a floor of 0.77, an excess of −0.66-0.66.
  • The two main tables are not the same runs, and the paper never says so. Table 3's note defines its "global" column as Table 2. XGBoost matches, TFT does not: TFT-MAE WMAPE is 0.4776 in Table 2 and 0.4475 in Table 3, a gap of 0.0301, more than twice the 1.3% effects reported as findings. The giveaway is the rule heuristic, decomposition-invariant by the same note, whose RBV reads 0.033 in Table 3, precisely Table 2's rule-heuristic bias. §D.1 still claims "paired train/test splits," so the TFT half of the headline result is unverifiable.
  • The loss$\to$pathology narrative the paper is built on is denied by Table 2, repeatedly, and there is no statistical apparatus to arbitrate:
    • "MSE suffers under ZIR ... MAE performs poorly on Skew ... Huber and Tweedie degrade under CV" fails all three ways. Largest ∣bias∣|\text{bias}| is almost always CV (XGB-MAE: Skew −0.185-0.185 vs CV −0.685-0.685), and Huber, the one named CV-fragile, has its smallest bias on CV (−0.042-0.042 vs ZIR −0.110-0.110).
    • The introduction's "MSE over-predicts sparse regimes, MAE under-predicts them (Tab. 2)" is false on the whole TFT half: MSE ZIR −0.082-0.082, Tweedie −0.443-0.443, Poisson −0.532-0.532, all under-prediction. §D.1(iii) concedes the sign is preprocessing-dependent. Page 1 states it flat.
    • §B.3 claims "all cell-level biases are significant at the 1% level," but Table 5 carries only pooled BB and RBV intervals and no p-value appears anywhere. The abstract's "3 seeds" meets Table 10's "Single seed (42)," Tables 2 and 3 have no uncertainty at all, and TFT-Tweedie's +0.9%+0.9\% (absolute 0.008) is reported as a directional finding against seed std of 0.002–0.007.
Questions for authors
  1. Which definition of RBV produced the reported numbers: §4.2 (overlapping regimes, centred on BglobalB_{\text{global}}), Eq. (2) (centred on the weighted mean φˉ=∑rwrφr\bar\varphi = \sum_r w_r \varphi_r), or Algorithm 1 (single-valued regime map, unweighted ℓ2\ell_2)? Relatedly, please either prove or withdraw the §4.2 claim that ∑rαrΔBr=0\sum_r \alpha_r \Delta B_r = 0 holds exactly under arbitrary regime overlap.
  2. Table 2 and Table 3 disagree on the TFT global baseline: RBV 0.338 / 0.953 / 0.486 / 0.908 (Tab. 2) versus 0.335 / 0.914 / 0.459 / 0.873 (Tab. 3), and WMAPE 0.4934 / 0.4776 / 0.4798 / 0.4757 versus 0.4675 / 0.4475 / 0.4603 / 0.4514, despite §D.1's statement that the global and decomposed evaluations use paired splits. Which set is correct, and were the two tables produced by the same runs?
  3. In Table 3 the rule heuristic's RBV is 0.033 while Table 2 gives 0.027; 0.033 is exactly Table 2's rule-heuristic Bias(All). Was a bias value transcribed into the RBV column, and if so which other cells of Table 3 are affected?
  4. Given §E.1's own statement that "Pooled training can instead push RBV below the floor (ql60: 0.11 ≪\ll 0.77)", in what sense is RBV∗\mathrm{RBV}^* a floor, and in what sense is the abstract's decomposition into a floor plus a training-attributable excess well defined when that excess is −0.66-0.66?
1 comment
AuthorsOpenReview ↗

Response to Reviewer bEij

We thank the reviewer for the careful reading and concrete questions. Definition consistency. Algorithm 1 is the single RBV definition and produced every reported number: four overlapping marginal groups, a series counted once per flag, centered once at BglobalB_{\mathrm{global}}, unweighted ℓ2\ell_2. Per-regime training uses only the disjoint three-tier cells (27 nominal, 14 used on RSB; 22 on M5). §4.2 states this two-layer structure; the identity suggesting an alternative reading was withdrawn. RBV∗\mathrm{RBV}^* is an oracle dispersion reference, not a lower bound.

Table 2/3 and the Rule column. The submitted TFT cells mixed two epoch budgets (max_epoch 2 and 10) and an earlier date protocol (training ended 2025-07-30, evaluation began 2025-08-04), so they were not aligned with XGB's fixed-origin split. We audited every cell and regenerated all TFT cells in one batch (max_epoch=50, training labels ending before the 2025-08-03 origin, targets 2025-08-04..08-10, 3 seeds). The corrected run is canonical; old and new are never mixed. The Rule reference is 0.0220.022 (submitted 0.0330.033 was the pooled bias). These corrections preserve the regime-bias pattern, the direction of the decomposition effect for mean-type losses, and the model-class moderation. The one reading sharpened rather than reversed is the TFT feature channel: under the corrected protocol it partially reduces RBV (0.688→0.4140.688\to0.414) instead of worsening it.

Loss–pathology narrative. We withdraw the one-to-one pairing. Under the unified protocol the largest absolute bias is the CV regime in 11 of 12 model–loss cells (the exception is the data-driven Huber threshold, whose largest bias is ZIR; 11/12 count from Tab. 2). The direction is a loss-family fingerprint: median-type and robust losses are negative in all 18 pathological cells; mean-type losses are positive in all nine raw-scale XGB cells and negative in all nine normalized TFT cells (§6.2; App. D.1(ii)). The introduction no longer states the MSE/MAE sparse-regime direction without the protocol qualifier.

Seed variance and significance. All entries follow the 3-seed protocol of the General response, including the controlled comparison, the label-normalization ablation, and both Huber protocols; non-averaged entries are labeled there; TFT feature/control arms are MSE-only. XGB gaps exceed seed dispersion by an order of magnitude: pooled-to-regime MSE 0.226±0.004→0.030±0.0020.226\pm0.004\to0.030\pm0.002, Tweedie 0.164±0.005→0.024±0.0020.164\pm0.005\to0.024\pm0.002, MAE 0.683±0.002→0.911±0.0030.683\pm0.002\to0.911\pm0.003, Huber (data-driven) 0.081±0.002→0.540±0.0030.081\pm0.002\to0.540\pm0.003 (Tab. 10); the feature arms behave the same way (0.030±0.0170.030\pm0.017, 0.029±0.0010.029\pm0.001, 0.900±0.0060.900\pm0.006, 0.243±0.0020.243\pm0.002). TFT-MSE dispersion is larger (0.688±0.160→0.292±0.1030.688\pm0.160\to0.292\pm0.103; features mean 0.4140.414, Tab. 9); every TFT contrast has ∣t∣|t| below the 5% critical value 4.30 (Tab. 11), so all TFT contrasts are reported as directional. The earlier “1% significance” claim is replaced by seed variability.

Tweedie (TFT). The TFT Tweedie/Poisson arms use a non-negative softplus-scaled target (center=False), so the deviance is defined; what remains is an estimand difference, not an implementation defect, so absolute values are not comparable to XGB's raw-scale Tweedie and only within-protocol contrasts are reported.

Huber protocol. The protocols are separated. On RSB, fixed δ=5.68\delta=5.68 gives ori 0.2060.206, features 0.0260.026, split 0.0350.035; data-driven δ\delta (holdout q75) gives 0.0810.081, 0.2430.243, 0.5400.540 (Tab. 12, θ^\hat\theta row; features in App. E). On M5 the same flip reproduces: fixed 0.364→0.0700.364\to0.070, data-driven 0.245→0.3720.245\to0.372. The mechanism is δ\delta-estimation fragility under zero-inflated data: a holdout residual quantile is pulled down by abundant easy zero/low-demand samples, pushing Huber toward a median-like estimator and blunting its response to regime information.

Normalization. On RSB-MAE softplus drives bias-RBV to 0.0850.085 while ∣E−0.5∣|E-0.5| worsens to 0.2790.279; linear z-score restores 0.7810.781 with ∣E−0.5∣=0.142|E-0.5|=0.142 (Tab. 12, TT row). Softplus rewrites the effective estimand; the residual after linear restoration is per-series reweighting, not estimand drift.

Directional signatures. The signs hold across seeds and controls but are configuration-dependent: feature conditioning, decomposition and the Huber-δ\delta protocol can reverse them. The sign pattern is the fingerprint; the magnitude is configuration-dependent.

Reviewer_A6JYOpenReview ↗
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Informativeness
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Paper summary

This paper argues that part of the deployment bias in industrial demand forecasting comes from a mismatch between the training loss and the label distribution, rather than from temporal-modeling error. Standard losses target a fixed statistic (mean, median, or quantile). When a single model is trained on a mix of regular, zero-inflated, skewed, and highly variable series, it settles on a compromise that aggregate metrics hide.

Critical strengths

The question is practically relevant. Reporting bias by regime alongside aggregate accuracy is useful for intermittent and skewed demand. The size-matched random grouping control is well designed: it shows that the gains come from grouping by regime, not simply from training on smaller groups. The oracle reference analysis and the M5 replication with bootstrap intervals add credibility.

Critical weaknesses

The diagnostic and the evidence do not cleanly support the claims. RBV measures bias relative to the mean, so median and quantile losses score poorly by construction. Without a stated deployment cost, the cross-loss comparisons in Tables 2 and 3 largely restate this difference, and the floor correction is applied only on M5.

Questions for authors
  • Does a pooled model given regime information as input close the gap to per-regime training?
  • On RetailShiftBench, are regime labels computed only from the training window? Please also state the data split and forecast horizon.
1 comment
AuthorsOpenReview ↗

Response to Reviewer A6JY

We thank the reviewer for raising this point. “RBV is by construction anti-median.”

We agree with the premise and restructured the answer. Bias-RBV measures the allocation of signed relative mean error; on a median-targeting loss it is large by construction because the median sits below the mean in right-skewed cells. It is not a calibration score.

Deployment cost. The stated cost is the per-regime under-forecast the allocation reports: a −0.637-0.637 relative bias in the CV cell means predictions carry 36% of that cell's demand mass, a 64% under-forecast that an inventory policy consumes directly and that a 0.42 WMAPE does not reveal (Tab. 2). We do not fit a dollar-cost model; we report the allocation any such model would consume.

Template. RBV is a template with three instantiations, not a scalar. All variants share the centering at the global functional and the unweighted ℓ2\ell_2 aggregation; they differ in the base functional ϕr\phi_r: bias-RBV (ϕr=Br\phi_r=B_r) for mean targets (MSE, Tweedie, Poisson), Quantile RBV (ϕr(τ)=Er(τ)−τ\phi_r(\tau)=E_r(\tau)-\tau) for median/quantile targets (MAE, QL), and share-normalized RBV (ϕr=(S^r−Sr)/S^r\phi_r=(\hat S_r-S_r)/\hat S_r) for predicted-volume displacement (Tab. 4). QR@τ=∣Eall−τ∣\tau=|E_{\mathrm{all}}-\tau| is the calibration companion.

The MAE pair. The pooled model has bias-RBV 0.6830.683 but Quantile RBV 0.0100.010 (cell exceedance 0.499/0.489/0.491/0.4850.499/0.489/0.491/0.485 around 0.4910.491): it is a well-calibrated median; the large bias-RBV is the mean–median gap, not miscalibration. The interventions separate the two readings (3 seeds, n=198,765n=198{,}765): softplus drives bias-RBV to 0.0850.085 but Quantile RBV to 0.1820.182 and ∣E−0.5∣|E-0.5| to 0.2790.279 (E=0.779E=0.779); linear z-score restores bias-RBV 0.7810.781 with Quantile RBV 0.1070.107 and ∣E−0.5∣=0.142|E-0.5|=0.142 (E=0.642E=0.642); regime split raises bias-RBV to 0.9110.911, keeps calibration near nominal (∣E−0.5∣=0.003|E-0.5|=0.003, E=0.503E=0.503), and raises cross-group dispersion to 0.1020.102. The QL$_{0.60}$ arm reproduces it: bias-RBV 0.505→0.112→0.6630.505\to0.112\to0.663 (split 0.8240.824), EE 0.548→0.789→0.6970.548\to0.789\to0.697. The MAE pair is tabulated in App. H, Tab. 18; QL60 values in Tab. 12, TT row. The bias variant penalizes a pooled mean built from different signed errors, not a median target.

Falsifiability. For quantile losses every RBV direction is reported with its exceedance and oracle reference, so a change that raised RBV while moving exceedance away from nominal would falsify the “exposed gap” reading. The reading follows the protocol, not convenience: the Huber flip (fixed 0.0350.035 vs. data-driven 0.5400.540) and the TFT Tweedie/Poisson increases (0.918→0.9910.918\to0.991, 0.851→0.9540.851\to0.954; Tab. 10) are reported as such.

“The floor appears only on M5.” The oracle-reference reading is computed on M5, and “lower bound” language is removed. The sub-reference case occurs on M5: ql60 pooled 0.110.11 vs. reference 0.770.77 (App. G.1), because a single compromise quantile keeps per-cell exceedances clustered and produces low dispersion of mean-relative bias even though every cell remains miscalibrated. On RSB the pooled ql60 RBV is 0.5050.505 (Tab. 2) while calibration is near nominal, so the contrast is calibration vs. allocation. When ZIR is high, low-τ\tau behavior is constrained by the atom at zero; the question is whether the loss reaches its oracle dispersion reference, not whether it beats zero.

Q1 — Does a pooled model with regime information close the gap? On RSB yes: XGB features reach split parity (0.0300.030 vs. 0.0300.030; Tab. 9). On M5 features stop above split (0.0600.060 vs. 0.0410.041); on TFT they recover part of the gain (0.688→0.4140.688\to0.414) rather than reaching decomposition (0.2920.292).

Q2 — Split, horizon, label window. RSB series are 89 steps. Origin 2025-08-03; targets 2025-08-04..08-10 (h1–7). For horizon ii, fitting uses rows with dt<2025-08-03−idt < \text{2025-08-03} - i, so neither origin nor targets enter fitting. Regime labels are computed from pre-origin observations only and frozen at the origin; the target window starts after it. The Rule heuristic and all features use pre-origin information only.

Reviewer_fHobOpenReview ↗
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Paper summary

This paper investigates distributional-statistical misspecification in industrial time-series forecasting, arguing that conventional aggregate evaluation metrics may conceal systematic forecasting biases across heterogeneous demand regimes.

The authors introduce a pathology taxonomy based on zero-inflation rate (ZIR), skewness, and coefficient of variation (CV), together with a Regime-wise Relative Bias Vector (RBV) to characterize cross-regime bias heterogeneity and a Pathological Coverage Score (PCS) for dataset auditing.

The paper further distinguishes loss–estimand mismatch from pooling-induced aggregation bias and investigates their effects through experiments involving multiple forecasting objectives and architectures. The empirical study includes RetailShiftBench and M5, with random-partition controls and regime-aware training comparisons.

Critical strengths
  1. The proposed regime-based evaluation is relatively easy to understand and interpret. Considering zero-inflation, skewness, and variability provides a useful perspective for analyzing forecasting failures.

  2. The authors conduct a reasonably comprehensive experimental study, including different loss functions, forecasting models, and regime-aware training strategies. I also appreciate the random-partition controls and the additional experiments on M5.

Critical weaknesses
  1. The motivation for introducing RBV is not entirely convincing. The main idea is to evaluate systematic bias separately across different regimes, which is reasonable. However, I am not sure whether the proposed RBV provides substantially more information than simply reporting the bias or forecasting error for each regime. The authors should better explain what specific evaluation problem RBV solves that existing subgroup evaluation metrics cannot.

  2. Some conclusions about loss-function misspecification seem too strong. For example, the paper argues that MSE is problematic for zero-inflated or skewed distributions. However, MSE still provides an optimal conditional-mean estimate under such distributions, assuming the relevant moments exist. I think the authors should distinguish between a loss function being statistically inappropriate and its implied prediction target being unsuitable for a particular application.

  3. The experiments do not fully support the conclusion that pooling-induced bias cannot be addressed by increasing model capacity. The authors show that regime-aware training improves RBV compared with global training, which is interesting. However, I wonder whether a single model with explicit regime information could achieve similar results. Without such comparisons, it is difficult to determine whether the improvements come from separating models or simply providing more information about the data distribution.

Questions for authors
  1. Why is RBV necessary? Could the authors compare RBV with simpler alternatives, such as the standard deviation of regime-wise biases or worst-regime bias? I would like to understand whether RBV reveals any additional information that these metrics cannot capture.

  2. Can the authors clarify the definition of loss-function misspecification? In particular, why should MSE be considered misspecified for zero-inflated data if the forecasting objective is to estimate the conditional mean?

  3. Have the authors tried adding regime information as input features to a globally trained model? It would be interesting to see whether such a model can achieve improvements comparable to regime-aware training. This experiment could help clarify whether the observed bias mainly comes from pooled optimization or insufficient regime information.

  4. How sensitive are the results to the selected regime dimensions? The paper focuses on ZIR, skewness, and CV. Could the authors explain why these three dimensions are sufficient? In addition, since these statistics may be correlated, how does their overlap affect the interpretation of RBV?

1 comment
AuthorsOpenReview ↗

Response to Reviewer fHob

We thank the reviewer for the careful reading and constructive comments. Your assessment tells us the contribution was not communicated clearly enough. The paper starts from a deployment phenomenon: despite strong benchmark performance, deep and foundation models exhibit severe systematic bias. Mean-type losses (MSE, Tweedie, Poisson) target a conditional mean, but pooled training delivers a compromise functional whose regime bias is protocol-set, not loss-set. Quantile losses name a level τ\tau, but the delivered empirical quantile need not equal τ\tau. The new information is not the RBV instrument but three falsifiable boundaries of configuration-induced effective-estimand drift—the regime-specific gap between the deployment target ϕr\phi_r and the delivered functional ψr\psi_r; RBV/QR make the drift visible without causing it.

F1 — backbone boundary. XGB features reduce RBV 0.226→0.0300.226\to0.030, matching removal of pooling (0.0300.030); on TFT the same features give 0.688→0.4140.688\to0.414 while decomposition reaches 0.2920.292. The feature–decomposition difference is not resolved (3-seed mean 0.1220.122, t=1.08t=1.08; Tab. 9; App. E), so TFT features are a partial channel. XGB/TFT changes normalization and architecture jointly, hence a backbone boundary, not a single-factor model-class effect.

F2 — normalization boundary (TT). Softplus makes a quantile loss look better under bias-RBV (0.1120.112) while exceedance is 0.7890.789; linear z-score unmasks the bias (0.6630.663) and improves calibration (0.6970.697), but neither returns to raw (0.505/0.5480.505/0.548; Tab. 12, TT row). Bias and estimand identity can point in opposite directions.

F3 — loss-configuration boundary (θ^\hat\theta). With Huber fixed, the δ\delta protocol changes RSB split RBV from fixed-δ\delta 0.0350.035 to data-driven 0.5400.540, consistent with M5 0.3720.372 (Tab. 12, θ^\hat\theta row; App. F).

Figure 2 summarizes only the pooling axis (three anchors are measured configurations, the rest positional schematics; horizontal positions encode breadth; vertical placement and the curve are schematic). Capacity is measured in App. D.3 (Figs. 9–10): pooled RBV saturates at 0.0950.095, and the error- and RBV-minimizing configurations differ, so capacity acts on fitting, not on the pooling compromise.

Q1 — Why RBV rather than std, worst-cell, or accuracy? RBV is an allocation measure: it separates average fit from where the error is concentrated. Scalar summaries of the bias vector (max⁡∣ΔB∣\max|\Delta B|, SD, range) rank Table 2 almost identically (Spearman 0.990.99), so the contribution is the coupled protocol—signed vector, calibration companions, and interventions—not the scalar. Tables 2 and 3 are the concrete instance: TFT-MSE has the better WMAPE (0.42130.4213 vs. 0.45910.4591) and pooled MSE (9.5489.548 vs. 11.27111.271) but the worse RBV (0.6880.688 vs. 0.2260.226), with CV/ZIR biases −0.637/−0.324-0.637/-0.324 vs. +0.247/+0.112+0.247/+0.112. The aggregate and regime-allocation rankings point in opposite directions.

Q2 — Is the criticism of MSE overstated? We agree and softened it. MSE is legitimate when the target is the conditional mean. Our claim is narrower: the pooled estimand can diverge from the deployment functional in specific regimes, and aggregate accuracy does not reveal it. The issue is not “MSE is wrong” but “a single pooled target reallocates error across ZIR/SKEW/CV.”

Q3 — Why not give regime information as input instead of decomposing? We tested it. XGB addfeature matches split on RSB-MSE RBV (0.0300.030 vs. 0.0300.030); on M5, 0.0600.060 vs. 0.0410.041. For TFT-MSE the ordering is as in F1 (features 0.4140.414, control 0.6060.606, split 0.2920.292), with the same unresolved gap (0.1220.122, t=1.08t=1.08; App. E; M5 in App. E). The revised claim: when the class cannot express a regime-conditional solution, information without a structural intervention leaves a residual allocation gap. On RSB the control also improves accuracy, so only the RBV reduction is regime-specific; on M5 it is inert.

Q4 — Are the three dimensions orthogonal? They are distinct but correlated, and the groups overlap. RSB (N=28,395N=28{,}395): ZIR 22,456, Skew 20,042, CV 14,458; overlap lower bounds 14,103/8,519/6,10514{,}103/8{,}519/6{,}105 (Jaccard 0.49/0.30/0.210.49/0.30/0.21). M5 (N=27,787N=27{,}787): 23,218/21,671/11,168; bounds 17,102/6,599/5,05217{,}102/6{,}599/5{,}052 (Jaccard and cell sizes in App. H, Tab. 17). RBV uses the four overlapping marginal groups; per-regime training uses the disjoint three-tier cells (27 nominal, 14 used on RSB; 22 on M5). The vector is an allocation profile, not a decomposition into independent factors. On sufficiency: the three dimensions violate the losses' shape assumptions directly—mass at zero, asymmetry, scale; kurtosis or multimodality overlap them or enter as temporal confounds. We do not claim the set exhausts the space.

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

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