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Under review as a conference paper at ICLR 2027

Do TSFMs Suffer from Unreliable Contexts? Rethinking Context Usage in Forecasting with Time-Series Foundation Models

Abstract

Time-series foundation models (TSFMs) have recently improved frozen-backbone forecasting by scaling model capacity, pretraining corpora, and domain coverage. Unlike large-language-model inference, where prompt construction has become an explicit object of optimization, TSFM inference typically passes historical context directly to the forecaster and implicitly treats its observations as equally useful and trustworthy. This assumption can fail when the context contains stale regimes, local anomalies, misleading trends, noise, or irrelevant history. Scaling a forecasting backbone alone does not decide which evidence should be trusted for a particular instance. We therefore study evidence-aware forecasting: how should context become a selectable decision variable before a frozen forecaster models the future? The difficulty is that context reliability depends on both the instance and the forecaster, while the future outcome needed to assess an intervention is unavailable at inference. We introduce CARE-TSFM, a frozen-backbone inference-adaptation framework whose external controller is trained offline with counterfactual utility supervision from pre-test data. CARE represents seven evidence patterns, estimates the utility of 24 candidate interventions, and uses a risk gate to select context refinement. Across GIFT-Eval and six frozen TSFMs, CARE achieves consistent multi-metric improvements for all forecasters while revealing structured, forecaster-dependent intervention utility. These results suggest that treating context selection as a decision variable is a promising direction for evidence-aware inference.

Primary area:
learning on time series and dynamical systems
Keywords:
Time Series Foundation Models, Time Series Forecasting, Context Reasoning, Test-Time Adaptation, Evidence Reasoning

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_WawsOpenReview ↗
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Paper summary

This paper proposed a method CARE-TSFM to improve the time series forecasting by selectively modifying the historical context fed to a frozen time series foundation model. It uses features from the history, the model's initial forecast, and task metadata to predict the benefits of 24 candidate modifications. A gate decides whether to apply the selected modification or keep the initial forecast. The controller is trained offline using intervention outcomes on pre-test data. Experiments on 97 GIFT-Eval configs show improvements in average MASE and CRPS across six forecasters, with large gains for Kairos but smaller gains for the other models.

Critical strengths
  1. The paper addresses a well-motivated question and it makes a useful distinction between identifying a possible context issue, selecting a potentially helpful modification, and deciding whether the intervention is worthwhile. Ablations show that always applying the selected modification can degrade the performance.
  2. The paper evaluates six forecasting models and multiple domains.
Critical weaknesses
  1. Most of the improvements are small for 5/6 of the models and their robustness is also not clear. Specifically, except for Kairos, MASE improves from 0.21% to 1.29% and CRPS improves from 0.09% to 1.06%. It is difficult to assess whether these improves are reliable without demonstrating results across training seeds. This is my major concern that the proposed method may have limited practical value.
  2. It is not quite clear how much the seven evidence categories contribute beyond learning which preprocessing operation to apply. The evidence removal ablations retain much of the improvement. There is a lack of evidence to show the benefit of grouping them into the proposed categories.
Questions for authors
  1. What is the computational cost of generating the offline training labels and how much inference latency does the proposed method add for each model?
  2. How large are the harmful interventions when they occur?
1 comment
AuthorsOpenReview ↗

Evidence contribution, computational cost, and intervention risk

Thank you for the careful review and constructive suggestions.

W1 — Response to shared concerns

Your W1 shares the reliability concern raised in vG1K Q1 and Zann W1/Q1. Five-seed results and paired intervals are in Response to shared concerns, C1. Reviewer vG1K (Critical Strengths, first paragraph) and reviewer Zann (Critical Strengths, first item) also cite TimesFM-3 CRPS changing from +0.66% to −0.10% without gating as evidence for the execution decision, in Section 6.2, Table 3.


W2 — Contribution of the seven evidence scores. What do the scores and their grouping add beyond learning a preprocessing policy?

Using only the seven scores beats the other two single-source controls in all 12 gain-point-estimate comparisons. Each controller is refitted and its validation gate reselected. The feature controls give:

Feature controlHighest gain among the three single-group controlsGain above Full
Evidence-only12/124/12
Forecast-only0/121/12
Metadata-only0/120/12

The uniform remove-seven comparison gives:

Full versus remove-sevenResult
Higher final-gain point estimate6/12 pairs
Final-gain difference CI excludes zero0/12 pairs
Lower pre-gate regret point estimate6/6 backbones
Regret-difference CI excludes zero in favor of Full3/6 backbones

Remove-seven retains positive gains on both metrics. The results support standalone predictive value and candidate-ranking utility. See Appendix E.10, Table 16 (new experiment/analysis).


Q1–Q2 — Computational cost and intervention risk. What are the labeling cost and per-backbone online latency, and how severe are harmful interventions?

Your Q1 is also raised in vG1K Q2 and Zann Q4; your Q2 overlaps with Zann Q1 on intervention risk. Per-model labeling and online timings, harm magnitudes, and domain denominators are answered in Response to shared concerns, C2.


Reviewer_ZannOpenReview ↗
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Paper summary

CARE-TSFM studies whether modifying the historical input of a frozen time-series foundation model improves forecasting. It treats this as supervised prediction of intervention utility, with a separate decision about whether to intervene at all. A 33-dimensional state combines seven context-evidence scores with scale, raw-forecast, and metadata features. For each backbone, two ExtraTrees regressors predict the MASE and CRPS gains of 24 candidate history transformations. A validation-selected gate either executes a selected transformation and reruns the backbone or reuses the original forecast. Evaluation covers six frozen backbones and 97 GIFT-Eval configurations, with positive macro-averaged improvements for both metrics. Gains are largest for Kairos and generally small for the other models. The selector uses historical target-benchmark outcomes for supervised training, so the complete system is not zero-shot, although the forecasting backbone remains frozen.

Critical strengths
  1. A sensible formulation that explicitly allows doing nothing. Separating candidate ranking from intervention gating recognizes that detecting a suspicious pattern does not establish that changing it will improve the forecast. The identity option and reuse of the original prediction are appropriate design choices. The TimesFM-3 ablation, where removing gating changes CRPS improvement from 0.66% to a 0.10% degradation, provides concrete evidence that this distinction matters.
  2. Evaluation across several frozen models with explicit adaptation boundaries. All six backbones show positive aggregate MASE and CRPS changes, including substantial Kairos improvements of 10.05% and 9.00%. The paper examines operation preferences, gating, and transfer, and distinguishes training data from gate-selection data. It also explicitly acknowledges that evidence scores are not fault probabilities and that gating is not a formal safety guarantee; those limitations should not be misrepresented as undisclosed claims.
Critical weaknesses
  1. Most improvements are too small to assess without dependency-aware uncertainty and a clearer cost–risk analysis. Toto-2 and Chronos-2 improve CRPS by only 0.09% and 0.18%, respectively (Table 2). A fixed controller seed and point estimates do not establish the stability of these gains. The 97 configurations share physical sources, and overlapping windows cannot be treated as independent replications. Moreover, the reported same-model harmful-intervention rates of approximately 22.8%–34.2% show that positive averages coexist with meaningful downside risk; this does not contradict the absence of a formal guarantee, but it matters to practical value. The offline development budget implies about 4.5 million window-level model evaluations across six backbones and 25 candidate branches, and executed interventions require a second online forecast. These are not necessarily separate GPU calls, but without measured cost and uncertainty the deployment benefit remains difficult to judge.
  2. The experiments do not isolate the value of context-reliability modeling from ordinary supervised adaptation. The controller is fitted using approximately 23,000 target-benchmark windows and their subsequent outcomes, whereas the raw backbone receives no corresponding adaptation. Fixed, random, or single-operation policies do not answer whether equally supervised output calibration or context-length selection would achieve comparable gains. Furthermore, 26 of the 33 state dimensions are not the seven evidence scores, so the selector could primarily learn forecast-error patterns from metadata and raw predictions. Existing evidence-removal ablations are useful, but the TimesFM-3 main-table ablation removes only three scores, unlike the all-seven removal used for the other models. This prevents a clean unified assessment. The results currently establish a potentially useful conditional utility selector, rather than demonstrating that diagnosing unreliable context is the distinctive source of improvement.
Questions for authors
  1. Assessment-changing uncertainty analysis: Do the small improvements remain positive under paired resampling by physical source and temporal block, multiple controller seeds, and reasonable gate-threshold perturbations? Please include tail degradation and per-domain harmful-intervention rates alongside mean gains.
  2. Assessment-changing matched comparison: With the same labeled windows and a comparable inference budget, how do direct forecast calibration and a learned context-length selector compare with CARE? This would distinguish the proposed intervention policy from generic target-domain adaptation.
  3. Assessment-changing feature attribution: Under a consistent protocol for all six models, what are the results for evidence-only, forecast-only, metadata-only, and complete states? Do controlled corruptions with known type and severity support the interpretation of the evidence scores as indicators of harmful context?
  4. Clarification of reproducibility and value: What are the complete gate objective, search grid, and final per-model thresholds, and why do the regret values differ across Tables 3, 9, and 12? Please report offline GPU-hours and online latency so that the gains can be evaluated against their cost. For the cross-model transfer claim, can unrounded positive/neutral/negative counts substantiate “mostly negative,” rather than merely heterogeneous transfer?
1 comment
AuthorsOpenReview ↗

Matched supervision, evidence attribution, and gate reproducibility

Thank you for the careful review and constructive suggestions.

Q1 — Response to shared concerns

Your Q1 overlaps with the other reviewers' reliability and cost concerns. Please see Response to shared concerns, C1 for seeds, source/time dependence, and thresholds, and C2 for computation, harm magnitudes, and domain denominators. We address your other questions below.


Q2 — Equally supervised adaptation. Can forecast calibration or learned context-length selection achieve comparable gains with the same labels and a comparable inference budget?

CARE has higher gain point estimates in all 12 model–metric comparisons; both Kairos paired difference CIs exclude zero. Labels, frozen models, and validation rules are shared. For Kairos:

PolicyMASE gainCRPS gainCoverage
Learned length+5.748%+6.358%5.35%
CARE+10.045%+8.995%73.41%

Coverage and realized inference budgets differ. Length selection intervenes on Moirai-2/Kairos; four models fall back to identity after finding no eligible validation gate. Thus, 12/12 includes comparisons against raw on those four. The added control evaluates learned input selection; direct output calibration has not been evaluated. See Appendix E.11, Table 17 (new experiment/analysis).


Q3a — Contribution of the seven evidence scores. What do uniform remove-seven, evidence-only, forecast-only, and metadata-only controls establish?

The seven scores alone have higher gain point estimates than the other two single-source controls in all 12 comparisons. Each input-column control is refitted and its validation gate reselected Appendix E.10, Table 16 (new experiment/analysis):

Input-column controlBest single-source gainGain above Full
Evidence-only12/124/12
Forecast-only0/121/12
Metadata-only0/120/12

In the first paragraph of Critical Strengths, reviewer vG1K recognizes utility prediction with identity as a sensible response to heterogeneous effects. These controls test its inputs. Retaining evidence lowers regret in all six point estimates, with three pointwise paired CIs excluding zero. Removing seven still retains positive gains on both metrics. Full has higher final gains in 6/12 pairs; all gain-difference CIs cross zero. These results support the scores’ standalone predictive value and their role in candidate ranking.


Q3b — Contribution of the seven evidence scores. Do controlled corruptions of known type and severity validate the scores as indicators of harmful context?

Controlled corruptions of known type and severity have not been tested. The feature controls assess utility prediction and action selection on natural data. Scores summarize visible context, raw forecasts, and metadata, with some comparing context and forecast. See Appendix E.10, Table 16 (new experiment/analysis).


Q4a — Gate reproducibility and ranking regret. Why do Tables 3, 9, and 12 report different regrets, and how are gates selected?

The gate objective, grid, fallback rules, and final thresholds are documented in Appendix E.14, Table 22 (new experiment/analysis); test labels never select gates. Execution thresholds span 0–2.026%, requiring at least one positive metric prediction. For the discrepancy across Tables 3, 9, and 12, Tables 3 and 9 used V17/GIFT-97 ablation diagnostics with joint MASE/CRPS utility, an older feature-reconstruction path, and fixed mean-utility ranking. Table 12 retained V16/GIFT-21 diagnostics with sMAPE/MASE/WQL utility. Eligible-window filtering and oracle identity inclusion also differed, accounting for the original discrepancy. We recomputed Full CARE diagnostics using the frozen V17 main-policy state, deployed selectors, two-metric utility, and one eligibility rule. TimesFM-3 regret is now 0.1419, displayed as 0.142 in Table 3 and 0.1419 in Table 12 according to their precision, in Appendix E.5, Table 12 (updated analysis). Computation, GPU timing scope, and intervention risk are answered in Response to shared concerns, C2.


Q4b — Cross-model transfer. Do unrounded positive, near-zero, and negative counts support the claim of mostly negative transfer?

The revised conclusion is heterogeneous, source–target-dependent transfer. The five-model figure has 12 positive and 8 negative off-diagonal gains; a ±0.1 pp band gives 6 positive, 10 near-zero, and 4 negative Appendix E.7, Figure 6.

Reviewer_vG1KOpenReview ↗
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Paper summary

The paper investigates whether modifying historical context can improve forecasting with frozen time-series foundation models. It proposes CARE-TSFM, an externally trained controller that constructs a 33-dimensional state, including seven context-failure evidence scores, predicts the utility of 24 candidate context interventions, and uses a validation-calibrated gate to either execute an intervention or retain the raw forecast.

The controller is trained using counterfactual intervention utilities from pre-test data, while both the controller and forecasting backbone remain fixed during testing. Evaluation covers six TSFMs and all 97 GIFT-Eval configurations. The paper reports positive aggregate MASE and CRPS gains for every backbone, alongside component ablations, intervention-ranking diagnostics, and cross-domain and cross-model transfer analyses. The overall system uses benchmark-specific supervision and is explicitly distinguished from a zero-shot controller.

Critical strengths

The paper formulates context modification as a selective decision rather than assuming preprocessing is uniformly beneficial. Predicting intervention utility and retaining an identity option is a sensible response to heterogeneous intervention effects. The no-gate ablations substantiate this design: for TimesFM-3, removing the gate changes CRPS RelGain from +0.66% to −0.10%, despite retaining positive MASE gain.

The evaluation provides substantial coverage and useful boundary analyses. Testing six frozen backbones across the complete GIFT-Eval configuration set strengthens the evidence beyond isolated examples. The pre-test supervision protocol, grouped out-of-fold predictions, domain holdouts, and source–target controller experiments help characterize where the method works and where transfer fails. The explicit acknowledgment that backbone freezing does not make the complete system zero-shot is also valuable.

Critical weaknesses
  1. The statistical reliability of the smaller improvements is insufficiently established. Although aggregate gains are positive for all six backbones, most improvements outside Kairos are modest. For example, Table 9 reports Toto-2 gains of 0.208% in MASE and 0.085% in CRPS, while Chronos-2 improves CRPS by 0.177%. The CARE pipeline uses one fixed controller seed, and confidence intervals for these gains are not reported.

    The large number of rolling windows does not by itself resolve uncertainty: windows overlap, and multiple horizon configurations originate from the same physical sources. Paired uncertainty estimates that account for these dependencies are needed to assess whether the small gains are robust. This is consequential to the claim that CARE consistently improves different frozen forecasters.

  2. The comparisons do not sufficiently establish the advantage over closely related learned input adaptation. The reported controls include fixed global interventions, random selection, single transformations, and a reproduced context-truncation method. These are useful for validating selective execution, but provide limited comparison against methods that also learn preprocessing from downstream forecasting feedback.

    The paper identifies EFE-Time as a close approach, yet provides a conceptual distinction without an empirical comparison. Its dataset-level policy differs from CARE’s window-level selection, but that distinction does not establish which approach offers a better accuracy–cost trade-off. A matched comparison using the same pre-test data, context limits, and frozen checkpoints would substantially strengthen the claimed methodological contribution. Reporting offline utility-label collection cost and online latency would also clarify whether the smaller gains justify the added machinery.

Questions for authors

Assessment-changing evidence: Can you provide paired confidence intervals for configuration-macro RelGain, accounting for shared physical sources and temporal dependence between rolling windows? Do the smaller Toto-2 and Chronos-2 improvements remain reliably positive?

Assessment-changing comparison: How does CARE compare with EFE-Time under matched pre-test supervision and forecasting conditions? Please also report the cost of constructing counterfactual labels and the online latency relative to raw forecasting.

Clarification: For Full CARE on TimesFM-3, Table 3 reports Ranking Regret of 0.144, whereas Table 12 reports 0.1512. Both appear to concern pre-gate ranking under joint normalized utility. Are these computed on different windows or with different aggregation rules? Please specify the distinction.

Related-work clarification: Please cite and discuss Jia et al. (2024), “GPT4MTS: Prompt-based Large Language Model for Multimodal Time-series Forecasting,” Proceedings of the AAAI Conference on Artificial Intelligence. GPT4MTS constructs forecasting inputs by combining numerical histories with corresponding textual information. Discussing this complementary approach would help position CARE’s selection and refinement of numerical context within the broader literature on forecasting input construction, while clarifying the specific novelty of reliability-conditioned intervention selection.

1 comment
AuthorsOpenReview ↗

EFE-Time comparison, ranking regret, and related work

Thank you for the careful review and constructive suggestions.


Q1 — Response to shared concerns

Your Q1 shares the reliability concern raised in Zann W1/Q1 and Waws W1. We answer the seed, source/time, and threshold analyses in Response to shared concerns, C1. We address your other questions below.


Q2 — EFE-Time comparison and computational cost. How does CARE compare under matched forecasting conditions, and what labeling and online costs does it add?

CARE has higher mean gains than EFE-Time on both metrics in the eight selected configurations. Forecasting inputs and frozen checkpoints are matched; EFE-Time uses five search proposals per configuration:

MethodMASE RelGainCRPS RelGain
EFE-Time−0.630%−0.353%
CARE+0.098%+0.099%

Full results are in Appendix E.12, Table 18 (new experiment/analysis). On the same pre-test windows, local construction takes 176.1 → 187.8 s for EFE-Time → CARE; paired median online latency is 20.47 → 124.42 ms Appendix E.12 (new experiment/analysis). Per-model overhead relative to raw is answered in Response to shared concerns, C2. Local construction timings exclude API waits and controller fitting. CARE reuses its GIFT-97 controller; EFE-Time searches per configuration, with training scopes stated in the appendix. CARE achieves higher mean forecasting gains; EFE-Time is faster online.


Q3 — Ranking regret and gate reproducibility. Why do Tables 3 and 12 report different pre-gate regrets for Full CARE?

The unified TimesFM-3 ranking regret is 0.1419. Table 3 used V17/GIFT-97 two-metric ablation diagnostics, whereas Table 12 used V16/GIFT-21 three-metric diagnostics, with different eligible windows and oracle candidate sets. We recomputed the Full CARE references under the frozen main policy, two-metric utility, and one eligibility rule in Appendix E.5, Table 12 (updated analysis). The main forecasting results are unchanged.


Q4 — GPT4MTS positioning. How does reliability-conditioned numerical-context selection relate to multimodal forecasting input construction?

Thank you for highlighting the valuable GPT4MTS work. Combining textual information with numerical histories broadens forecasting-input design and provides useful context for our study. We added the citation and discussion of Jia et al. (2024) Section 2.2. CARE complements this direction by predicting window-specific utility for numerical-context interventions and retaining the original input when predicted benefit is insufficient. The revision clarifies this distinction within forecasting input construction.

Comments on the paper

2 comments
AuthorsOpenReview ↗

Response to shared concerns

We thank the reviewers for their constructive feedback, and the reviewers and Area Chair for their time and effort. All three reviewers raise two overlapping concerns: reliability of small gains (vG1K Q1; Zann W1/Q1; Waws W1) and computational cost (vG1K Q2; Zann W1/Q4; Waws Q1). We consolidate the answers here to provide a common reference and facilitate discussion among reviewers. C2 also answers the intervention-risk questions from Zann W1/Q1 and Waws Q2. The revised PDF contains the supporting experiments and clarifications, with added or replaced text marked blue. Individual replies address the remaining questions.


C1 — Reliability of small gains. Are modest improvements repeatable under controller randomness, source dependence, and threshold changes?

Although several gains are modest, their positive direction repeats across all five controller seeds and, separately, all five local gate-threshold settings on fixed GIFT-97. Supervision, frozen checkpoints, and official test windows are fixed. All 30 model–seed runs have positive configuration-macro MASE and CRPS gains. For two modest-gain models, five-seed mean ± sample SD is shown below (pp denotes percentage points):

BackboneMASE gainCRPS gain
Chronos-2+0.701% ± 0.082 pp+0.214% ± 0.079 pp
Toto-2+0.405% ± 0.139 pp+0.307% ± 0.131 pp

This supports repeatable aggregate benefits under the tested training randomness. Separately, paired bootstrap for the original frozen controllers retains related frequencies, horizons, and rolling windows within 28 base-source clusters. Seven of 12 pointwise 95% CIs exclude zero; five cross zero, including Chronos-2 CRPS and both Toto-2 metrics. Source/relative-time-segment sensitivity gives six positive lower bounds. Segments follow relative origin order, without calendar alignment. Means, intervals, and local-threshold checks are in Appendix E.9, Tables 14, 15 (new experiment/analysis).


C2 — Computational cost and intervention risk. What are the offline and online costs, and how large are harmful interventions?

The added median latency stays at approximately 82–149 ms per request across the six backbones, with full CARE median latency below 230 ms in the measured setting. Here, Raw denotes direct forecasting by the frozen TSFM on the original context, as in the manuscript; CARE denotes the full pipeline including feature computation, gating, and a second forecast when an intervention is executed. On an RTX 5070 Ti, batch=1, we time 168 paired independent requests per backbone. Label computation separately uses 160 shared pre-test windows and identity plus 24 interventions:

BackboneFrozen TSFM (Raw) → full CARE median latency (ms)Labeling (s)
Chronos-213.35 → 104.0816.21
Moirai-29.14 → 100.7824.53
Toto-211.27 → 98.8914.52
TimesFM-3125.78 → 229.77310.66
Kairos65.96 → 214.3148.82
FlowState18.83 → 109.5941.87

Median paired online increments are 82.09–148.61 ms. Label timings exclude loading, I/O, and controller fitting. Sampling 75 forecast branches per backbone yields 63.25–1611.69 ms of GPU activity. Timing scope and sampled GPU measurements are in Appendix E.13, Table 19 (new experiment/analysis).

Among harmed windows, median relative degradation spans 1.75–7.01% for MASE and 2.28–5.06% for CRPS across backbones; median absolute increases span 0.004–0.050 and 0.004–0.012. These conditional window summaries differ from configuration-level aggregate gains. Domain harm rates include eligible counts: Toto-2's 100% Transport rate comes from one eligible intervention. Magnitudes and domain rates are in Appendix E.13, Tables 20, 21 (new experiment/analysis).

AuthorsOpenReview ↗

Summary of new experiments and the revised PDF

We thank the reviewers for their constructive feedback, and the reviewers and Area Chair for their time and effort. The PDF has been updated with supplementary experiments and clarifications. Added or replaced text is marked blue. The responses below address each reviewer question.

We answer the reliability of small gains and computational cost, raised by all three reviewers, in Response to shared concerns, together with intervention risk. The remaining questions are answered individually. The table summarizes the main findings of the added experiments and their locations in the revised PDF.

New experiment / revisionReviewer concerns addressedMain conclusion and evidenceLocation
Reliability of small gainsvG1K Q1; Zann Q1; Waws W1 — Are small gains repeatable under training randomness and evaluation dependence?Both gains positive in all 30 model–seed runs and at five local thresholds; source CIs support 7/12 pairsAppendix E.9, Tables 14, 15
Computational cost and intervention riskvG1K Q2; Zann Q4; Waws Q1–Q2 — What do labeling, online inference, and harmful interventions cost?Per-model timing, sampled GPU activity, degradation magnitudes, and domain denominatorsAppendix E.13, Tables 19–21
Contribution of the seven evidence scoresZann Q3; Waws W2 — Do scores add selection information beyond forecasts and metadata?Evidence-only leads the three single-group controls in 12/12 gain point estimates; Full lowers remove-seven regret in all six modelsAppendix E.10, Table 16
Ranking regret and gate reproducibilityvG1K Q3; Zann Q4 — Why do regrets differ, and how are gates selected?Unified TimesFM-3 regret 0.1419; documented validation objective, grid, fallback, and frozen thresholdsAppendix E.5, Table 12; Appendix E.14, Table 22
Equally supervised adaptationZann Q2 — Can other policies exploit the same labeled windows?CARE exceeds learned length in 12/12 gain point estimates; both Kairos paired difference CIs are positive, with different coverageAppendix E.11, Table 17
EFE-Time comparisonvG1K Q2 — How do learned input-adaptation methods compare under matched forecasting conditions?On eight configurations with five EFE search iterations, CARE has higher mean gains and EFE lower online latency; training scopes differAppendix E.12, Table 18
Cross-model transferZann Q4b — Are cross-model gains mostly negative?20 off-diagonal transfers have 12 positive/8 negative joint gains; interpretation corrected to heterogeneous transferAppendix E.7, Figure 6
GPT4MTS positioningvG1K Q4 — How does CARE relate to broader forecasting input construction?Added multimodal-input discussion and its relationship to numerical-context selectionSection 2.2

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