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Under review as a conference paper at ICLR 2027

Time-Series Foundation Models Anchor to Corrupted Context: A Diagnosis, a Blind Fix, and the Limits of Fixing

Abstract

Time-series foundation models forecast from a window of recent history with no training or data audit in between, transferring responsibility for data quality to the model. Operational series carry sentinel values, filled gaps and transient level artifacts, and a defect near the forecast origin forces an implicit decision about whether to trust them. We study what such defects do to zero-shot forecasts, how much of the damage a blind test-time repair removes, what produces the sensitivity, and where repair meets a limit no detector can cross. We audit ordinary defects across foundation models from several organizations and architectures, reporting aggregates on normalized errors with equal dataset weights rather than raw pooling, which one dataset dominates. We then propose a blind, training-free sanitizer pairing robust clipping with a gated level correction whose onset is estimated rather than assumed, and localize the mechanism by intervening on where the level is perturbed. Because a transient artifact and a just-started regime change are observationally identical at the origin, no context-only policy is accurate in both worlds, and an equal-weight mixture of the two readings is minimax-optimal. Fragility concentrates in level structure and grows with model scale, the sensitivity is extrapolation of the recent level rather than normalization, and the mixture alone keeps its stated uncertainty in either world. Code is available at https://anonymous.4open.science/r/tsfm-iclr27-AEB1/.

Primary area:
foundation or frontier models, including LLMs
Keywords:
Masked diffusion language models, Inference-time scaling, Token revision, Compute allocation, Difficulty-stratified evaluation

Reviews

Among:
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1234this paper, Top 49%
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_tH6DOpenReview ↗
Rating
3
Confidence
3
Informativeness
3
Presentation
3
Soundness
2
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Paper summary

The paper audits context-corruption sensitivity across eight time-series foundation models and nine benchmark targets. It proposes a training-free pipeline combining robust clipping, gated level correction, and distributional hedging. It also studies why recent level changes affect forecasts and formalizes the ambiguity between transient artifacts and persistent regime changes. The strongest contribution is the empirical diagnosis, including explicit accounting for aggregation choices and damage to clean-data forecasts.

Critical strengths
  • The audit is broad and reports consequential failure cases transparently.

    • The paper evaluates several model families, reports dataset-normalized aggregates alongside disaggregated results, and measures both corruption recovery and clean-data costs. Its poor results on drifting series are particularly informative: they show why an apparently successful sanitizer can be harmful when genuine changes resemble defects. The model-free detector comparisons also appropriately limit claims about detector novelty.
  • The artifact–regime distinction provides a useful deployment perspective.

    • Proposition 1 correctly establishes an idealized impossibility result for identical contexts with two different futures under full CRPS. The empirical evaluation then explores correction, preservation, and hedging. The paper explicitly acknowledges that its covariate-routing experiment supplies distinguishing information by construction and that independent natural-incident validation remains future work.
Critical weaknesses
  • The experiments establish behavioral recency sensitivity more convincingly than they identify its architectural cause. Section 4.3 argues that normalization by window statistics predicts approximately four times greater sensitivity to a body shift than a tail shift. This implication requires assumptions about the normalized predictor. For example, a normalized forecaster f(x)=μ(x)+σ(x) g ⁣(x−μ(x)σ(x))f(x)=\mu(x)+\sigma(x)\,g\!\left(\frac{x-\mu(x)}{\sigma(x)}\right) with �0��0� reproduces persistence: it responds to the tail and ignores the body despite using normalization. The location intervention therefore distinguishes recent-level dependence from a pure window-statistics explanation, but does not generally exclude normalization-mediated mechanisms. The direct TimeMoE intervention is informative; broader causal conclusions across families require additional interventions or narrower wording.

  • The interpretation of the scaling result is confounded by the clean-error denominator. Table 9 reports increasing degradation ratios across the Chronos size ladder, but degradation is corrupted MAE divided by clean MAE. Better clean accuracy can increase this ratio even when absolute corrupted error or sensitivity to the injected offset remains unchanged. The observed increase in relative degradation is valid. The stronger explanation that larger models are inherently more faithful extrapolators of corrupted levels requires scale-specific anchoring coefficients or added error normalized by a common dataset scale. Uncertainty estimates are also important for interpreting the small base-to-large difference.

Questions for authors
  • Can the mechanism claim be supported by interventions on normalization statistics in additional model families, or narrowed to behavioral recent-level dependence?
  • Does the scaling ordering persist for corruption-induced forecast displacement and added error normalized by context scale?
  • Proposition 1 concerns an oracle mixture of two deterministic outcomes under full CRPS. What optimality or calibration claims remain for the implemented mixture of imperfect model distributions under the censored CRPS actually evaluated?
  • Please clarify whether Table 3 reports electricity-specific coefficients and how its conclusions relate to the per-dataset exceptions in Table 13.
1 comment
AuthorsOpenReview ↗

Response to Reviewer tH6D

Response to Reviewer tH6D:

Thank you for a precise review. Two of your points exposed errors in our own claims, which we corrected. The revised PDF marks new and changed text in blue, and App. O lists the changes.

Q4. Was Table 3 electricity-specific? Yes, in effect. It fitted one regression through the origin across all datasets in raw units. Electricity's offsets are two orders of magnitude larger than any other dataset's, so they set every coefficient; the printed values equal electricity's own. Table 13 and the figure now weight datasets equally. The conclusion survives, with new numbers: alpha_tail = 0.60–0.83 against alpha_body = 0.09–0.35. The tail dominates in 43 of 45 model-dataset cells, and both exceptions are on zero-inflated solar (TimesFM 0.37 vs 0.39; TimeMoE 0.36 vs 0.68). The same pooling had also set the TimeMoE intervention numbers in the text. With equal weights, alpha_tail falls from 0.60 to 0.41 and alpha_body rises from 0.35 to 0.61 under body-robust statistics, in the same direction as before.

Q1. Mechanism. We agree with your example: a normalized forecaster with g(z) = z_L behaves like persistence, so the location test cannot rule out normalization in general. We did both things you suggested.

  • Interventions inside 5 families (Chronos-t5, Chronos-Bolt, Chronos-2, Moirai, TimeMoE; App. O.7). We patched the code that computes each model's statistics, so they can be recorded on one input and imposed on another. Freezing a model's own statistics at their clean-context values, while feeding the shifted context, keeps 72–99% of the tail response. Moving only the statistics, on the clean context, moves the forecast by at most 0.10 of the offset. For body shifts, the statistics alone move the forecast and the model's reading of the normalized values cancels most of it, as in your example.
  • Narrower claim. The paper now says the fragility is recent-level dependence, which persists when the tested normalization statistics are frozen. It no longer says normalization is excluded as a mechanism or that better normalization cannot help, and the four-to-one body/tail prediction is now stated only for a forecaster that is an affine function of the window mean.

Q2. Scaling. You were right that the ratio could mislead. We re-ran the ladder on all nine datasets at 100 origins (the submission used three datasets and 40 origins), with paired bootstrap intervals (Table 27).

ChronosClean MAE / scaleDegradationDisplacement alphaAdded MAE / scale
tiny1.083.53x0.681.52
small1.024.57x0.741.68
base0.995.77x0.821.94
large1.006.09x0.821.98

"Scale" is each dataset's mean context standard deviation, which does not depend on the model. The clean error barely moves, so the rise from tiny to base is not a denominator effect: displacement and added error both grow. From base to large, displacement does not change (difference [-0.01, +0.02], 95% interval), and added error rises only a little ([+0.01, +0.09]). We withdrew "larger models are more faithful extrapolators" and the prediction that better forecasters will be more sensitive. The new claim is narrower: fragility grows from tiny to base and then levels off, so a larger model is not a more robust one.

Q3. What does Proposition 1 say about the implemented mixture? Proposition 1 is about an oracle that knows both futures, under full CRPS. For a pool of two imperfect forecasts we claim no optimality. Under full CRPS an exact identity carries over, now Proposition 2: CRPS(F1/2 + F2/2, y) = CRPS(F1, y)/2 + CRPS(F2, y)/2 - (1/4) times the integral of (F1 - F2)^2. So the exact pool scores no worse than the average of keep and de-shift, whatever the models' quality. Two things separate this from what we evaluate:

  • The score is censored. There the identity can fail, so we checked only the weaker no-worse-than-average inequality. It held in all 12,600 synthetic window-world pairs and in 97.2% of 6,300 natural windows (175 exceptions). These are observations, not a guarantee.
  • The pool is approximate. Quantile heads report only levels 0.1 to 0.9, so our pool needs a convention for unreported tail mass (App. O.6). We now report two sensitivity scenarios. Moving the tail mass from infinity to the outermost quantile changes the mixture's worst-world CRPS by +2–+9%, and it stays 19–48% below the better hard policy. Coverage is more sensitive (0.57–0.80 under the alternative), so we now flag the reported coverage as sensitive to this choice.

The equal weight is minimax only in the idealized case. For real models the best weight on keep, on a 0.1 grid chosen on the evaluated windows, is 0.6–0.7 (App. O.4), because de-shift fails harder in its bad world. That is an in-sample choice, not an estimated minimax weight. Neither result is a calibration claim; coverage is measured, not implied (Sec. 4.4).

Reviewer_YpXrOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
3
Read review
Paper summary

The paper investigates how artifacts in time-series context windows can degrade TSFMs at inference time. It focuses specifically on artifacts occurring immediately before the forecast window, quantifies their impact across different datasets and model families, and evaluates how detection and correction strategies can mitigate the resulting performance degradation.

Critical strengths
  • The paper tackles a practical and important problem that can significantly affect time-series forecasting models in real-world deployments.
  • The evaluation framework is diverse, covering datasets with different dynamics, multiple types of injected corruption, and several TSFM families.
  • Good reproducibility, with code and artifacts made available to reproduce the experiments.
Critical weaknesses
  • Most experiments rely on artificially injected corruptions. While useful for controlled analysis, they do not establish that the proposed methods generalize to real-world scenarios with potentially different artifact distributions and regime-change patterns.
  • The paper does not sufficiently validate whether artifacts can be reliably distinguished from genuine regime changes in real-world settings, where both may produce similar patterns in the observed context.
  • The covariate-corroboration approach is evaluated under controlled assumptions about how artifacts affect the target series relative to its covariates. It remains unclear how well these assumptions hold in practice, where artifacts may affect multiple variables or genuine regime changes may not be reflected consistently across covariates.
Questions for authors

The injected faults are motivated by real-world problems, but do naturally occurring time-series datasets contain similar patterns of level shifts and other artifacts that can be confidently identified as faulty measurements? More specifically, how representative are the injected corruptions of real-world artifact distributions? I am trying to understand whether the injected faults are sufficiently obvious or severe that they trivially degrade forecasting performance, or whether their characteristics and magnitudes are representative of what TSFMs encounter in practice.

1 comment
AuthorsOpenReview ↗

Response to Reviewer YpXr

Response to Reviewer YpXr:

Thank you for the careful review and the clear question. We answer it first, then the three weaknesses. The revised PDF marks new and changed text in blue, and App. O lists the changes. We also rewrote the paper in shorter, plainer sentences, and added a guide at the start of the appendix: a contents table and a map from every table and figure to the research question and section it supports.

Q. Do natural datasets contain such faults, and are the injected ones representative or trivially severe?

  1. Natural faults of this kind exist and hurt. New RQ5 (Sec. 4.5, Table 4) uses the Intel Berkeley Lab deployment. As batteries ran down, temperature readings drifted upward for hours while the other sensors did not move. The data carry no fault labels, so we treat these as suspected battery faults. Their onset is inferred from the target's divergence from a peer reference (the median of the other sensors, fitted on the sensor's healthy days; held-out error 0.80 C). The drift reaches 0.9, 1.7, 3.0 and 4.4 sigma of the context at 2, 4, 6 and 8 hours after onset, so our 3-sigma step lies within the range of these faults. Kept as is, a faulty context costs 3.0x the clean-context error, over 8 models; that is less than our injected step, because these drifts are young.

  2. The damage does not need an obvious defect (App. O.2). With the boundary known, on four models, a 1-sigma step, which our gate catches about half the time, already raises MAE 1.8–2.2x; a 2-sigma step 3.2–4.0x. On the benchmarks, 5% of clean contexts carry a natural tail move as large as the median injected 3-sigma step (13% on exchange and solar, 0% on electricity and traffic). These checks support the plausibility of the injected amplitudes. They do not show that our injected faults match the distribution, shape or duration of real artifacts, and the paper now says so.

  3. Other realistic faults (Table 2). A gradual drift to 3 sigma costs 5.6x, a 20% gain error 3.4x, a dropout to zero 17.2x, and a stuck sensor 2.2x. Gain errors and dropouts are largely repaired (72% and 91%). Slow drifts are not (11%), because inside the context a drift looks like a trend.

W1. Beyond injected corruptions. On the suspected natural faults, with thresholds fixed in advance:

PolicyFaulty, MAE / oracleHealthy windows, cost
Keep the context3.0x0%
Sanitizer as submitted2.3x+9.0%
Same gate, replace correction1.8x+8.5%
Gate + mixture (7 probabilistic models)2.7x-0.8%
Differential test vs. other sensors1.5x+4.7%

Repair helps faulty windows, but the healthy-window cost matters because faults are rare (the drifting phase fills about 2.8% of a record). At that rate the single-series sanitizer would not pay off (median break-even 15.2%), and the mixture has the lowest average healthy-window cost, though it still raised that cost on 3 of 7 models (up to +5.7%). We report this in Sec. 4.5.

W2. Can artifacts be told from real changes in real data? From the target series alone, not always. That is Proposition 1, and the data agree: healthy windows contain real level moves, and the gate fires on 24% of them. In this deployment, neighbouring sensors improve the separation. A differential test, the target minus the median of other sensors (as in climate-station homogenization, Menne & Williams, 2009), cancels movement they share. It fires on 74% of faulty and 13% of healthy windows. Two caveats, both now in the paper: the fault labels are inferred, not independently annotated, and the test shares peer sensors with the reference.

W3. The covariate assumptions. We now test them directly (Table 23).

  • Faults shared by covariates: when half share the fault, the hard router's error rises from 1.5x to 4.2x the oracle; when all do, to 5.6x, the naive level.
  • Regimes the covariates do not show: the router de-shifts and reaches 6.7x.
  • In real data, the sensor's own humidity, light and voltage channels do not corroborate usefully (2.6x), because they follow the daily cycle in healthy and faulty windows alike.

We added soft routing (Sec. 3.3): corroboration tilts the pool weight instead of switching, by a trust setting rather than a calibrated probability. Over the tested scenarios its worst case is 4.7x, against 6.7x for the hard router. The paper states that corroboration is only as good as the independence of its channels.

Limits we now state. One deployment, one suspected fault mechanism, and a peer-derived reference instead of annotated labels.

Reviewer_XN6vOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
2
Soundness
3
Read review
Paper summary

This paper investigates how zero-shot Time-Series Foundation Models (TSFMs) handle context window defects like sentinel values and level shifts. It evaluates eight different model architectures, covering many popular models in the time series community (Chronos, TimesFM, Moirai, TS-ICL, etc.).

The authors demonstrate that models are highly sensitive to level shifts near the forecast origin, as they cannot physically distinguish between a transient artifact and a persistent regime change. To address this, they propose a “blind sanitizer” using changepoint statistics to infer data shift in the channel shifts. The work then implements a corroboration gate checking covariate channels to decide whether to de-shift the data or keep it, and outputs a linear mixture “hedging” of the two predictions when the gate is inconclusive.

Critical strengths
  1. Real-World Relevance. I think this is a valuable line of research for actually using zero-shot models in the real world. Standard benchmarks assume the context window is perfectly clean, which obviously isn't true for many tasks. I appreciate the authors looking at how these models silently swallow data defects when there's no human analyst in the loop to catch them.
  2. Architectural Breadth. Evaluating across a large number of different models proves the fragility to level shifts isn't just an artifact of a single architecture or model class.
  3. Mechanism Isolation. The ablation comparing tail versus body shifts effectively isolates that models are extrapolating the recent level, proving the sensitivity isn't just a basic normalization bug.
Critical weaknesses
  1. A weakness of this paper is the reliance on a single type of simplistic synthetic corruption. The core evaluation rests on a simple additive step function onto the end of the target channel. Real-world sensor data rarely degrades this cleanly. The paper does not test on a variety of real world corruptions. Such as gradual sensor drift, multiplicative calibration errors, multi-channel degradations, etc. While the authors show a a fix works on a perfect 3 sigma + synthetic jump, titanium would be great to have evidence that it will have a net positive effect on real world data.

  2. Lack of covariate complications. The corroboration gate functions on the assumption that if multiple channels jump, it must be a broad regime move, and if only the target jumps, it’s an isolated artifact. In reality, physical data generating processes don't always behave this way. A localized hardware failure can simultaneously drop multiple sensors, shifts in weather can shift multiple sensors, etc. Under the paper's logic, the method could treat a multi-channel hardware failure as a valid regime change.

  3. Missing Real-World Evaluation: The downstream evaluation relies on synthetic injections rather than natural, real-world incidents. While there is a brief mention of weather data, the paper does not evaluate the sanitizer on datasets with documented, naturally occurring sensor faults where the ground truth (artifact vs. regime) is definitively known from outside the series.

Questions for authors
  1. Could the authors evaluate the sanitizer on datasets containing documented, naturally occurring sensor faults?
  2. How does your CUSUM changepoint detector and de-shifting logic adapt to more complex corruptions, such as gradual sensor drift or multiplicative calibration errors?
  3. How might the corroboration gate safely account for a single point of hardware failure that simultaneously knocks out multiple covariate channels?
1 comment
AuthorsOpenReview ↗

Response to Reviewer XN6v

Response to Reviewer XN6v:

Thank you for a clear and practical review. Each weakness led to a new experiment. The revised PDF marks new and changed text in blue, and Appendix O lists the changes. We also rewrote the paper in shorter, plainer sentences, and added a guide at the start of the appendix: a contents table and a map from every table and figure to the research question and section it supports.

W3 / Q1. Natural faults. We added RQ5 (Sec. 4.5, Table 4) on the Intel Berkeley Lab deployment: 54 sensors reporting temperature, humidity, light and battery voltage. As batteries ran down, temperature readings drifted upward for hours while the other sensors did not move. We treat these as suspected battery faults (median voltage at onset 2.32 V). We must be clear about one limit. The data carry no fault or regime annotations. We infer each onset from the target's divergence from a peer reference: the median of the other sensors, fitted to the target on its own healthy days (held-out error 0.80 C). Faulty windows are scored against this reference. So this is natural-data evidence, not the independently documented incident labels you asked for, and the paper now says so. We score 168 faulty windows (2 to 8 hours after onset) and 459 healthy windows (against their measured future). Thresholds were fixed in advance.

PolicyFaulty windows, MAE / oracleHealthy windows, cost
Keep the context3.0x0%
Sanitizer as submitted2.3x+9.0%
Same gate, replace correction1.8x+8.5%
Gate + mixture (7 probabilistic models)2.7x-0.8%
Differential test vs. other sensors1.5x+4.7%

Rows are means over 8 models unless marked. On your question of net effect, the honest answer is mixed. Natural faults here are rare: the drifting phase fills about 2.8% of a sensor's record. The median per-model break-even fault share is 15.2% for the submitted sanitizer (range 4.7–24.6%), 6.7% with the replace correction and 3.6% for the differential test (1.0–8.1%). So in this deployment the single-series sanitizer would not pay off, the differential test is near break-even, and the mixture has the lowest average healthy-window cost (-0.8%), although it still raised that cost on 3 of 7 models (up to +5.7%). These figures assume the evaluated mix of windows and are not deployment guarantees. The paper now says this, and recommends hedging as the default.

W1 / Q2. Drift, gain errors and other realistic corruptions. We added four sensor-fault families (Table 2), each reaching the forecast origin. Thresholds are set on clean windows only.

  • Gain error (x1.2): 3.4x damage; 72% recovered. At the origin a gain error acts on the forecast like a level shift.
  • Dropout to zero: 17.2x; 91% recovered.
  • Gradual drift to 3 sigma: 5.6x. The single-series sanitizer recovers only 11%. A drift that builds up inside the context looks like a trend, so the backcast follows it. This is our identifiability limit again, and the paper says so. On the natural drift, the differential test against other sensors did better.
  • Stuck sensor: 2.2x. A level gate cannot see it; a flatline rule recovers 64% with no measurable clean cost.

W2 / Q3. One hardware fault that moves several channels. You are right: the hard router reads such a fault as a regime. We now test this (Table 23, 7 models, normalized CRPS). When half the covariates share the target's fault, its error rises from 1.5x to 4.2x the oracle, and to 5.6x (the naive level) when all do. A regime that reaches no covariate is wrongly de-shifted (6.7x). Two remedies:

  1. Soft routing (Sec. 3.3). Corroboration tilts the pool weight instead of switching: weight 1 - eps on keep when corroborated, eps when not. eps is a trust setting for how far channel independence is doubted, not a calibrated probability. With eps = 0.3 the worst case over our tested scenarios falls from 6.7x to 4.7x; the plain mixture gives 3.7x. These are observed results, not bounds.
  2. Corroborate with independent hardware. In the Intel data the sensor's own humidity, light and voltage channels add little (2.6x). A differential test against the other sensors, as in climate-station homogenization (Menne & Williams, 2009), fires on 74% of faulty and 13% of healthy windows. It shares peer sensors with the reference, which the paper discloses.

Limits we now state. One deployment and one suspected fault mechanism, a peer-derived reference instead of annotated labels, and slow drifts that escape single-series repair.

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

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