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Under review as a conference paper at ICLR 2027

SAR-LCRT: RISK-GATED RESIDUAL TRANSPORT FOR FROZEN TIME-SERIES FORECASTERS UNDER DELAYED FEEDBACK

Abstract

Accurate time-series forecasts support planning in energy, transportation, and environmental systems. Yet a trained model can repeatedly overestimate or underestimate future values, and retraining it after deployment may be costly. Correcting these errors presents two challenges: error patterns vary with the input, and the usefulness of a correction can be assessed only after the predicted time interval has elapsed. We propose SAR-LCRT, a framework that improves a trained forecaster without changing its parameters. Low-Rank Conditional Residual Transport (LCRT) learns patterns in prediction errors across future steps and variables, using validation data to construct input-dependent corrections. Structure-Adaptive Risk Control (SAR) then chooses whether to use a correction or retain the original forecast, based on observed outcomes of past forecasts. The framework compares all available corrections to guide selection. It separately tracks the gains and losses of the forecasts actually used and stops correction when the accumulated evidence no longer supports it. Across eight architectures and 13 datasets, SAR-LCRT matches or improves the original models’ MSE on 86.1% of 416 forecasting tasks, based on three-seed means. On PEMS08, it reduces MSE by 11.06% on average across architectures and forecast horizons. These results demonstrate the value of combining structured error correction with delayed-feedback selection as a reusable addition to trained forecasters.

Primary area:
learning on time series and dynamical systems
Keywords:
time-series forecasting, post-training residual correction, delayed feedback, online candidate selection, risk-aware deployment

Reviews

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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_iV9UOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
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Paper summary

This paper proposes a post-hoc correction method for time-series forecasting without retraining the backbone model. It assumes that a frozen model generally underestimates or overestimates certain forecasts and therefore requires corrections (which are input-dependent and should not always be applied). The authors propose using a validation set to learn a regression model that predicts the error the base model will make based on the input context. This trained linear model (subject to low-rank constraints) is then applied during test time to estimate the base model's errors in advance and apply corrections (they evaluate two types of corrections: a pure correction and an adaptive one). Finally, at test time, they use delayed feedback to select the most suitable forecast.

Critical strengths

(i) The post-hoc corrections do not require retraining the backbone model. (ii) The proposed approach seems to yield satisfactory performance. (iii) Several ablation studies have been conducted to validate various design choices.

Critical weaknesses

(i) The method relies on a validation set, which is not always available (sometimes requiring a reduction in training set size, which hinders a fair evaluation and limits practical applicability). (ii) The method assumes the availability of delayed feedback, which is not always applicable in practice. Furthermore, the paper does not compare against existing methods that utilize delayed feedback (specifically test-time adaptation and online time-series forecasting approaches, even if those methods update the backbone). At a minimum, one would expect Pareto curves (memory vs. performance and compute vs. performance) comparing this framework to other online or test-time adaptation approaches. (iii) The low-rank constraint on the linear mapping from the input features needs to be explicitly ablated. Other algorithmic design choices also require stronger motivation. For example, why use both Pure and Adaptive corrections? Why not more variants? Why only these two, and how do they complement each other? These aspects remain unclear.

Here is a non exhaustive list of papers that will be nice to be compared to the papers at least from a performance vs. compute/memory point of view. I do not believe claiming retraining qualitatively is a reason to discard them from the baselines. We clearly need some quantitative fact (either by complexity analysis or a compute vs. performance curve for these methods and the one of the paper).

Lightweight Online Adaptation for Time Series Foundational Model Forecasts (ICML'25) Battling the non-stationarity in time series forecasting via test-time adaptation (AAAI'25) Adanodes: Test time adaptation for time series forecasting using neural odes. Shift-aware test time adaptation and benchmarking for time-series forecasting.

Also it exists several post training approaches for time series forecasting models (which uses augmented context and doesn't need retraining of the backbone which would be worthy to check)

Instance Adaptive Prompts as Context for Time series Foundational Models Adapt data to model: Adaptive transformation optimization for domain-shared time series foundation models.

And even more which can be found in this literature review (A Survey of Post-Training in Time Series Foundation Models)

Questions for authors
  1. How can the method be applied in scenarios without a standard validation set? Should a portion of the training set be carved out for validation? Furthermore, for benchmark datasets with standardized validation sets, what if that set was already used for model selection or early stopping during backbone training? Is it still a reliable candidate for predicting residual errors?

  2. How does the framework handle applications where delayed feedback is unavailable?

  3. How does the method compare to test-time adaptation (TTA) or online adaptation approaches in terms of the performance vs. compute/memory trade-off? Could the authors provide 2D efficiency plots (e.g., performance vs. latency/memory) to illustrate the method's advantages over test-time approaches that require: (i) full retraining, (ii) fine-tuning, or (iii) neither (e.g., parameter-free methods utilizing context augmentation or output calibration) using delayed feedback (which is super additional information)?

1 comment
AuthorsOpenReview ↗

Calibration Fairness, Adaptation Costs, and Rank Ablation

Calibration fairness. Base, Pure and SAR share the training split and checkpoint; Base's training set is not reduced. Appendix D.1 uses the first 25% of validation origins for checkpoint selection, an L+H gap before calibration, and an H-origin gap between fitting and assessment. The assessment block selects both step and initial action: its LCB guides selection, not an independent post-selection certificate (Appendix E.3). If early stopping used all validation data, use fresh chronological calibration; reuse is not independent. Without a validation set, reserve history or collect later labels, disclose this cost and match comparators' data budgets. Insufficient calibration means Base fallback.

Feedback. At decision t, only losses from origins j with j+H≤t inform selection. Earlier test outcomes can inform later decisions; weights, maps and past forecasts remain unchanged. Comparators must receive the same histories and maturity schedule. Without target feedback, only pre-test static choice or Base is available, with no online-selection gain. Extra dense forecasts in the foundation-model evaluation count toward its cost.

Adaptation and costs. The candidates share one backbone prediction, without backbone backpropagation. We added Chronos-Bolt Base and Moirai-2.0-R-small comparisons with one-time/periodic fine-tuning and TAFAS-GCM/full-feedback. The accuracy pilot covers six domains with seed2025. New costs cover energy (epf_np) and cloud (bizitobs_l2c_1H): four model-task cases, five separately run methods, one repeat, 457 issued origins and 20 official scored windows per case.

Model/taskBase sSAR sOnce-FT sPeriodic-FT sSAR/periodic-FT GPU peak MiB
Chronos/energy16.06106.57113.44148.21813.5/3943.7
Chronos/cloud22.6450.7141.8361.11813.5/3943.7
Moirai/energy16.6181.16101.62118.7257.1/236.1
Moirai/cloud20.6050.6021.4925.1257.1/236.1

Totals include initialization, prediction and updates once; loading, input reads, scoring and audit I/O are excluded. Synchronization/profiling overhead remains. These are shared-GPU diagnostics, not isolated speed or minimal-RSS measurements. SAR's process-allocated GPU peaks are lower here, but it is not always faster. On Chronos/cloud, periodic FT lowers MASE by 8.51%, while SAR raises it by 0.58%.

FT uses at most 50 initial steps, pre-test checkpoint selection including zero updates, and five periodic steps every H origins. Moirai uses a declared quantile-loss reference. TAFAS-GCM omits native partial-label updates and retrospective adjustment; it cannot establish a win over native TAFAS. Of 20 measurements, 19 reproduce historical predictions within the declared tolerance. Moirai/cloud/TAFAS matches a fresh unchanged-recipe replay but not its historical artifact; the cause is unresolved and both versions are retained. Full retraining, ELF and other requested online/context baselines remain gaps. An isolated-device Pareto comparison remains outstanding; pending forecasts and audit arrays need separate memory accounting.

Rank and design choices. All 24 fixed-rank4/full jobs are complete: SimpleTM and MDMLP-EIA on ETTh1/H336 and PEMS08/H48, with three seeds. Checkpoints, data, splits and non-rank search grids match; selected ridge, step and Adaptive structure may differ.

Model/datasetPure MSE changeSAR MSE change
SimpleTM/ETTh1+1.596%+0.0016%
SimpleTM/PEMS08+3.967%+0.3877%
MDMLP-EIA/ETTh1−0.394%+0.1615%
MDMLP-EIA/PEMS08+4.310%−0.0562%

Changes are 100×(rank4/full−1) after averaging three seed errors; negative favors rank4. Always-on Pure is the primary control: full is better in three of four combinations. We do not claim rank4 is necessary for accuracy. Small SAR differences do not establish statistical equivalence or optimal automatic rank selection.

Pure shares residual structure across steps/channels; Adaptive chooses spatial, pooled temporal or shared/channel-specific structure before testing; Base permits no correction. Separate 96-task, four-backbone, three-seed controls give mean MSE changes from Base of −4.56% for full SAR, −3.17% for Base+Pure and −3.64% without the issued-loss budget. This supports the additional candidate and accounting roles. Reserve removal and Base initialization remain competitive; we do not claim every threshold is necessary.

We will integrate verified results within the permitted revision window. As remaining experiments finish, we will complete the tables, plots, protocols, analysis and limitations, marking unfinished evidence and posting updates only within the allowed discussion period.

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

The paper proposes post-processing for frozen time-series forecasters. The mechanism includes (i) low-rank, input-dependent residual corrections on validation data, (ii) selection, online, among the original forecast and two fixed correction candidates using delayed loss feedback. The selection is based on confidence-based comparisons and involves accumulated-loss withdrawal rule.

Critical strengths
  • The topic of the paper, the post-train model adaptation, is timely and interesting

  • The selection of 8 baseline models is comprehensive. The method seems to provide consistent gains across architectures

  • limitations of the method are discussed

Critical weaknesses
  • The paper is motivated by adapting the models that are frozen in production and are expensive to train. This scenario matches most natively the foundation model application. However, the paper's experiments are focused solely on task-specific models. This does two things. First, it undermines the motivation, as task specific models are typically cheap to train. Second, since the model is operating in-domain, the adaptation gains on some datasets are small.

  • The paper's main motivation is that it is hard to retrain the model. However, a lot of the time forecasting models run in production without retraining simply because the downstream systems cannot handle frequent and abrupt changes of the forecasting model error distribution induced by model retraining/swapping, even if the aggregate model accuracy improves slightly after each swap. This is a very real operational constraint and the paper does not address it at all.

  • Missing baseline. The paper suggests that this technique replaces the retrained model. However, it never quantifies the gap that it intends to close.

  • The paper reports dataset-clustered confidence intervals, the evaluation covers a limited range of domains, and gains are concentrated on traffic datasets. Broader evaluation would help establish generality.

  • Table 1 presentation is misleading. Number is red even if two numbers are equal - this doesn't seem reasonable. In fact, it may happen in some cases that even if the rounded numbers are equal, SAR-LCRT variant will have larger (worse) full-precision value.

  • The branch-selection policy contains several asymmetric thresholds and withdrawal rules whose necessity is insufficiently justified. The part of the approach related to the branch selection based on delayed feedback has a significant flavor of heuristic that was introduced post-hoc to compensate for the imperfection of the Pure LCRT and Adaptive LCRT. This construction does not come out naturally in my mind, from the reading of the paper.

  • One of the limitations of the method is that additional validation and online adaptation samples are required to make it work. Does this imply that this method only applicable to long series? What the results will look like if this method is applied to M4 competition benchmark? Will it perform reasonably on series with relatively short history? Additionally, typical benchmarks have fixed train/validation/test splits. For example, I have monthly dataset with horizon 18, I produce all horizons at once. How does the proposed method work in this situation? The online adaptation, does it imply that values in the test are used for adaptation for branch selection?

Questions for authors
  • Why gain is so small, is it because all models operate in-domain and potential gain is small, or because proposed technique is weak?

  • Have you thought about reframing the paper as a post-training technique for foundation models? My bet is that such reframing would be very helpful to have this paper in a publishable form.

  • It would be very helpful to have a baseline consisting of the retrained model. Otherwise, it is unclear why post-training adaptation gain is so small. Is it because the proposed technique is weak, or because retraining in the setup authors introduced genuinely does not benefit from adaptation, even if the model is periodically retrained.

  • what are the forecast revisions caused by the adaptation and how to quantify their effects?

  • Can you present results on multiple foundation models? Task fine-tuned foundation model should give an estimate of the achievable gain.

  • Can you present results on GiftEval and fev-bench?

  • What is the motivation for Pure LCRT and Adaptive LCRT? What is the motivation (beyond improving aggregate benchmark performance) for the solution? Can you provide theoretical motivation for the selection between three specifics branches or the real life analogy behind the algorithm design?

3 comments
AuthorsOpenReview ↗

Reframing as Foundation-Model Post-Training: New Evidence and Clarifications

Yes. We will reframe SAR-LCRT as a post-training technique for frozen time-series foundation models. Residual maps are fitted after pretraining from contexts, forecasts and historical targets. At deployment, maps and backbone stay fixed; only the forecast choice changes. No backbone backpropagation or online gate training is required. We will reorganize the abstract, introduction and evaluation around this setting, with the original backbones supporting portability.

Foundation models. All 100 fev-bench tasks are complete for Chronos-Bolt Base and Moirai-2.0-R-small, with three calibration seeds. Negative percentages mean lower error.

ModelMASE (primary) [95% CI]MSEMAE
Chronos+0.04% [−1.79,+1.34]−0.75%+0.34%
Moirai+0.84% [−0.23,+2.14]−0.38%+0.54%

Changes use geometric-mean paired error ratios and source-family-clustered intervals. Seeds vary calibration, not pretraining. We retain official score windows and target-only point forecasts, adding a dense stream for delayed selection. This adds inference cost and is not strict zero-shot evaluation. MASE does not establish improvement; MAE worsens.

The 16 November GIFT-Eval snapshot covers 95/97 Chronos and 3/97 Moirai configurations, three seeds each (294/582 runs). Interim MASE/MSE/MAE changes are +1.05%/+0.02%/+1.48% and +1.08%/+0.28%/+0.60%, respectively. These different, incomplete subsets support no whole-benchmark gain or model ranking.

Original evidence and fine-tuning. Across 416 tasks/eight backbones/three training seeds, task-macro MSE changes by −3.31%, with the 13-dataset-clustered 95% CI [−5.38,−1.45]% reported in Appendix A.2. Full-precision MSE improves or ties on 358 tasks. All 128 PEMS03/04/07/08 task means improve in MSE/MAE; excluding them still gives −1.14% MSE, but +0.34% MAE. Traffic contributes strongly but is not the entire MSE result.

A completed six-domain, seed2025 pilot compares finite-budget adaptation:

MethodChronos MSE/MASEMoirai MSE/MASE
SAR−0.05%/+0.11%−0.06%/+0.09%
One-time FT−0.13%/+0.28%+0.28%/−1.13%
Periodic FT−1.88%/−0.58%+2.65%/−0.29%

These are descriptive geometric-mean changes on previously inspected tasks with H≤64. FT uses at most 50 initial steps, pre-test checkpoint selection including zero updates, then five periodic steps every H origins using available targets. Moirai uses a declared quantile-loss reference. This is not full retraining or an accuracy upper bound; small gains cannot simply be attributed to no adaptation headroom.

Forecast behavior. We compare successive forecasts for the same target time, normalized by pre-test history scale. Chronos/cloud mean revision is Base 0.09692, SAR 0.09686, periodic FT 0.06738. Moirai/hospital increases from Base 0.03860 to SAR 0.04239. Fixed weights therefore do not imply stable outputs; no downstream stability guarantee is claimed.

Candidates and rules. Pure fits joint horizon/channel residual structure; Adaptive selects spatial, shared-temporal or channel-blended structure before testing. Both freeze; Base allows no correction. Candidate comparisons ask what to issue; the loss account tracks issued losses against Base. On 96 tasks with three seeds, MSE changes are −4.56% for full SAR, −3.64% without its loss budget and −3.17% for Base+Pure. Delayed FTL gives −4.36%; simpler initialization/reserve variants remain competitive. These controls support the main roles, not optimal thresholds or future-loss guarantees.

History and feedback. Test-period outcomes inform only later choices, once j+H≤t; weights/maps and prior outputs never change. A single 18-month forecast uses only pre-forecast choice. The GIFT-Eval Chronos runs cover all six M4 frequency groups: monthly H=18 changes MSE/MAE/MASE by +0.087%/+0.080%/+0.159%, with 62.59% unable to fit correction. Its single window tests pre-forecast calibration, not online selection. fev's fit fallback is 59.64%; fallback cases remain in totals and do not establish short-history improvement.

Table 1. Its caption already distinguishes lower displayed errors (red bold) from ties (underlined red bold), at three decimals. A tie is not a strict win or statistical equivalence; full-precision counts and MSE estimates are separate. We will make this distinction and signed changes easier to inspect.

Within the revision window, we will integrate verified results and the new framing. As remaining experiments finish, we will complete the tables, protocols, analysis and limitations, explicitly marking unfinished evidence. The PDF has not yet been revised.

Thank you very much for the detailed, candid response and for the substantial amount of additional experiments. However, in my view the new evidence reinforces, rather than resolves, my concerns.

  • The authors agree that frozen foundation models are the natural setting for the method. However, in this setting the method does not help. On fev-bench, MASE changes by +0.04% (Chronos-Bolt) and +0.84% (Moirai-2.0), with confidence intervals covering zero. MAE worsens for both models. The interim GIFT-Eval numbers are worse on all three metrics for both models. It looks like the the paper reframed around foundation-model post-training would therefore have its central claim unsupported.

  • Comparison to fine-tuning. The pilot answers the question I asked, but the answer is not favourable to the method.

  • Forecast stability. SAR does not reduce revisions.

  • Short histories and fixed splits. Thank you for clarifying that test targets inform choices only after they mature. The M4 monthly result (+0.16% MASE, with 62.6% of series unable to fit a correction; 59.6% fallback on fev-bench) confirms that the method is largely inapplicable to short series.

  • Table 1. I understand the caption convention. My point is that marking ties with the same colour as wins visually inflates the result.

Overall, the original gains are concentrated on the PEMS traffic datasets, and the new results show essentially no gain on foundation models, no advantage over lightweight fine-tuning, and no stability benefit on extended benchmarks. Therefore, I prefer to keep my original score.

AuthorsOpenReview ↗

Clarifying the scope of the supported results

Thank you for explaining why the additional results have not changed your assessment. We agree that they do not establish an overall foundation-model gain, an accuracy advantage over fine-tuning, or improved forecast stability.

Our reframing commitment needs to reflect this evidence. We will retain foundation-model post-training as a central evaluation, but explicitly state that the tested pipeline has not established improvement in its primary metric. The original task-specific results cannot serve as proof of foundation-model effectiveness.

There are two narrower findings that we believe remain worth assessing. First, the original matched-checkpoint evaluation supports output correction without changing the backbone. We agree that traffic contributes strongly: outside the four PEMS datasets, MSE changes by −1.14%, while MAE changes by +0.34%. This is a limited MSE benefit, not broad improvement across metrics.

Second, the same-candidate controls directly test the deployment policy. Relative to budgeted window FTL, SAR's mean MSE change is lower by 0.171 percentage points, with a six-dataset-clustered 95% interval [−0.334, −0.049], and mean switches are 4.08 versus 19.79. Budgeted window FTL has slightly better MAE and the same worst observed degradation. This supports a specific accuracy/switching trade-off, not general superiority over simpler selectors or fine-tuning.

We also accept your point about Table 1's visual emphasis. We will give displayed ties neutral formatting and reserve highlighting for strictly lower displayed errors, with full-precision changes reported separately. We will not describe M4 fallback as successful short-history adaptation or closeness to Base as improved stability.

We will make these limits explicit in the revised abstract, main results and conclusions. We hope you will reconsider the contribution of the matched-checkpoint and same-candidate findings on this stated scope, while retaining your concerns about transfer to foundation models.

Reviewer_rXHMOpenReview ↗
Rating
2
Confidence
2
Informativeness
1
Presentation
2
Soundness
2
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Paper summary

The paper proposes SAR-LCRT, a framework combining validation-fitted low-rank residual corrections with online selection for frozen time-series forecasters. Under delayed feedback, the controller uses historical candidate losses and cumulative realized gains to select corrections or revert to the original forecast. Experiments cover eight forecasting architectures and thirteen datasets.

Critical strengths
  • Ease of deployment. The rule-based controller can operate on pre-fitted residual predictors without training an additional gating network or updating model parameters online.
  • Extensive evaluation. Experiments across eight architectures, thirteen datasets, multiple forecasting horizons, and three random seeds provide broad empirical support for the overall framework’s effectiveness.
Critical weaknesses
  • Largely limited methodological novelty. The framework largely combines established residual correction, low-rank modeling, and online selection techniques. Its historical-loss-based switching and fallback rules appear to be a straightforward extension, and the paper does not convincingly establish their added value over simpler selection strategies using the same candidates.
Questions for authors

no oustanding questions, i would like to see other reviewers' oppinion.

2 comments
AuthorsOpenReview ↗

what the controller adds with the candidates held fixed

The contribution we ask you to assess is the deployment policy that separates comparison of fixed residual proposals from accounting for the forecasts actually issued. Residual regression and low-rank modeling are ingredients; the technical question is how their fixed outputs should be used when feedback is delayed and the backbone cannot be updated.

The original Table 3 shows −3.31% MSE relative to Base and −1.25% relative to always-on Pure across 416 tasks. The latter comparison includes the additional Adaptive candidate, so it should not be read as isolating the controller alone. We isolate selection using the same cached Base/Pure/Adaptive candidates on 96 tasks: four backbones, six datasets, four horizons and three seeds, with the same complete-target feedback schedule.

SelectorMean MSE changeMean MAE changeWorst observed task MSE changeMean switches
Validation-static−3.54%+0.41%+35.18%0.00
Delayed FTL−4.36%−0.62%+15.00%1.65
Window FTL−4.23%−0.88%+15.00%12.38
Window FTL + budget−4.39%−1.20%+6.28%19.79
SAR-LCRT−4.56%−1.17%+6.28%4.08

These are arithmetic task-macro error changes from Base; negative values are better. SAR's paired MSE-change difference from budgeted window FTL is −0.171 percentage points, with a six-dataset-clustered 95% interval [−0.334, −0.049]. It therefore achieves a small mean-MSE advantage with substantially fewer switches in this slice. Against delayed FTL, the difference is −0.199 points [−0.915, +0.274], so that mean-MSE comparison remains uncertain. Budgeted window FTL's MAE is slightly better and its worst observed degradation is identical; delayed FTL makes fewer switches than SAR. The evidence is a specific trade-off, not dominance on every criterion.

A component control further gives −3.64% MSE/−0.22% MAE without the issued-loss budget, versus −4.56%/−1.17% with it. This supplies evidence for the loss-accounting component beyond a verbal explanation. Reserve removal and Base initialization show that some details can be simplified without erasing the value of correction plus deployment selection. The completed rank ablation tests a separate question: the effect of a fixed rank constraint. It does not replace these same-candidate controls, which hold the proposals fixed and test how they are used. We will base the controller contribution on these direct comparisons, without claiming optimal thresholds or future-loss guarantees.

Thanks for your reply. After carefully reading other reviewers' opinions. I tend to keep my original rating.

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

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