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Severe but Harmless: Stress-Testing Shift Severity for Frozen Time-Series Forecasters

Abstract

Zero-shot time-series foundation models (TSFMs) have become attractive alternatives to task-specific models because they handle diverse downstream tasks, including anomaly detection and forecasting, without per-series training. However, time-series data undergo distribution shifts, and the dissimilarity between two regimes is commonly scored with statistical measures such as Wasserstein-1, where a higher score is read as a more severe shift. In systematic experiments using three established severity measures on nine regime shifts from three standard traffic datasets, we show that these measures do not reliably predict degradation for instance-normalized TSFMs. The regimes rated most severe are not the regimes that degrade the models most, and degradation reaches 29% in the lowest-scoring regime. In most cases, the audit shows no positive relationship between measured severity and model degradation. We provide an equivariance-based stress-testing analysis that explains why severity readings can become decoupled from model degradation.

Introduction

Time-series foundation models (TSFMs) such as Chronos-2 [5], TimesFM [2], and Moirai [3] forecast new series from recent history without training on each series, which is called zero-shot forecasting. This makes them attractive alternatives to supervised models built for individual tasks [28], [29]. But a series encountered in use may differ from the data a model was trained on. Weekday and weekend traffic, for example, follow different patterns. Such differences are called distribution shifts [10], [16], [17]; when a shift develops over time, it is often called drift. A shift can raise forecast error even when the data come from the same source. The problem extends beyond time series to vision and tabular data [18], [31], [36]–[38]. In time-series forecasting, several methods address it by normalizing the data before prediction [19]–[21].

In traffic, these supervised models are graph forecasters [6]–[8], and on our three datasets they still have lower error than the TSFMs (§ 4-B). Although distribution shift is widely studied in the literature, including for time series, we did not find a study that audits distribution shift for TSFMs in the traffic domain, characterizing the severity of these shifts and the measures used to score it.

Wasserstein-1 is commonly used to measure how far the distributions of two datasets differ [35]. Traffic patterns can differ even within the same dataset. Morning rush and midday on the same weekday, for example, may have different distributions of readings. We call each condition used to group observations a regime, including weekdays and weekends, peak and off-peak periods, and groups of sensors. In principle, scoring regimes could help prioritize the highest-scoring shifts for investigation [10]–[14] and guide whether similar regimes should be combined or kept separate.

In the literature, various methods have normalized the data before prediction [19]–[21]. The advantage this gives is that dissimilarities are first dealt with in the data so that the models can better learn good representations from them. TSFMs already do this: they standardize every context window by its own mean and standard deviation before predicting [5]. The problem is that a distance computed on raw readings mostly measures level and scale, which is exactly what the model removes. Suppose we take a weekend that has traffic volume across a network. The distance sees a large shift and Wasserstein-1 will report this; however, after standardizing, the TSFM sees an input much like its usual one. The severity measure and the model are not looking at the same thing, and once that is true, severity can move without the model’s error moving with it.

Our goal in this work is therefore to investigate whether these marginal severity measures (Wasserstein-1, Kolmogorov–Smirnov, and mean difference) can reliably identify the distribution shifts that degrade Chronos-2 [5] and TimesFM [2]. We use the released models frozen, without any training.

We summarize our contributions below:

  • We test whether three marginal severity measures, Wasserstein-1, Kolmogorov–Smirnov, and mean difference, identify the distribution shifts that degrade Chronos-2 and TimesFM by evaluating nine dataset–shift settings across three real-world traffic datasets against five baselines.

  • We show that severity and degradation can become decoupled for instance-normalized forecasters because per-window normalization removes the level and scale changes that can dominate marginal severity. We verify

Figure 1. The nine dataset–shift settings (gray: reference, lines: shifted). The temporal failure, LargeST-SD S1 (red), has the lowest severity in its row. Bars show normalized W1W_1.

this affine-equivariance property in the released Chronos-2 and TimesFM checkpoints.

  • We show empirically that the severity measures do not identify the degrading regimes: the highest-severity shifts are largely non-degrading, while LargeST-SD weekends produce up to 29% degradation at the lowest severity reading in that dataset. We also report a pre-registered test-time adaptation experiment that fails to repair this weekend degradation.

  • We show that a validation-selected timestamp router outperforms both frozen models on LargeST-SD weekends, reaching a mean absolute error (MAE, lower is better) of 21.57 veh/15 min compared to 23.82 for TimesFM and 26.14 for Chronos-2, though trained graph models remain stronger there.

Related Work

Time-Series Foundation Models

Pretrained forecasters now transfer to unseen series without target-domain training. Chronos discretizes series into a language-modeling vocabulary [1], TimesFM trains a decoder-only forecaster on a large corpus [2], and Moirai and MOMENT extend this model class with universal multivariate and open masked-reconstruction pretraining [3, 4]. Chronos-2 standardizes each context window internally [5]. This normalization is central to the analysis in Section III-F. Deployment results differ between aggregate and regime-level evaluation. Benchmarked across ten transportation datasets, zero-shot Chronos-2 is state-of-the-art or competitive on aggregate error [29], yet zero-shot foundation forecasters fail on cloud workloads [30], and regime-stratified scoring of traffic speed finds 3 mph aggregate errors concealing transition errors near 11 mph [34]. Aggregate evaluation is further limited by contamination: standard benchmarks appear verbatim in public pretraining corpora [3, 39], so a TSFM may have seen the test data. Tools to audit this leakage are only emerging [27]. These results therefore do not establish reliability at the regime level required for deployment.

Distribution Shift in Spatio-Temporal Forecasting

Traffic forecasting has a mature literature on supervised graph and transformer forecasters [6, 7, 8] benchmarked at scale by LargeST [9]. Shift studies with these models retrain on the new regime and report the resulting performance gap, while out-of-distribution benchmarks document degradation without establishing a relationship between shift magnitude and harm [32].

Normalization and Affine Equivariance

Traffic is nonstationary: its mean and variance change over time. A standard architectural defense is normalization. Reversible instance normalization [19], series stationarization [20], and learned per-window statistics [21] remove each window’s level and scale before prediction, a design also used by the foundation models considered here [5]. In image denoising, networks with f(ax+b)=af(x)+bf(ax+b)=af(x)+b for a>0a>0 are called normalization-equivariant. They are built layer by layer [40], or by normalizing the input and reversing it on the output, which gives exactly this class [41]. Proposition 1 applies this property to forecasters. Those works use it to design models. We use it to explain why a raw-data distance can weigh heavily what the model removes before prediction.

Severity Metrics in Audit Practice

Deployment monitoring often begins by comparing incoming data with a reference distribution. Concept-drift research studies how to detect such changes and adapt to them [10].

Practical approaches include drift detectors, representation-based monitors, and drift benchmarks [11, 12, 13]. Optimal transport provides one way to measure the difference [14].

A detected shift does not necessarily predict a model’s error. Some shifts are harmless [16], and uncertainty estimates can become unreliable under shift [17]. Studies of shifts in the wild also find that magnitude does not consistently track loss [18]. Similar limits appear in performance estimation. Fréchet and MMD estimates have been unreliable in vision [37], shift-detection scores have been poor predictors on tabular data [31], and confidence-based estimates can outperform distance-based ones [38]. Out-of-distribution accuracy can follow in-distribution accuracy [36], but that prediction uses the model’s own performance rather than a distance between raw marginals.

For time series, one cross-dataset study reports a correlation above 0.60 between Wasserstein distance and foundation-model loss [35]. That result does not establish whether distance also ranks the effect of shifts among operating regimes within one deployment. This is the assumption we test here.

Test-Time Adaptation for Time Series

Test-time adaptation updates a deployed model using unlabeled inputs, via self-supervised objectives in vision [22] and, for forecasting, through frequency calibration, lightweight input–output modules, and feature adjustment [24, 25, 26]. Other studies document cases in which adaptation degrades performance: effectiveness is sensitive to shift type and model choice [44], continual adaptation can perform worse than the non-adapted model [42], and performance deteriorates on temporally correlated streams [43]. Adaptation under time-series dependence is therefore an empirical question rather than a guaranteed repair.

Methodology

Our approach is to audit the severity measure under the conditions of its use: fixed pools, one masking convention, and a protocol fixed before the shift evaluations. We registered the predictions in advance and report them with their outcomes in § 4-F.

Problem Setup and Notation

Each model uses the recent history of every sensor to forecast the next 12 steps. METR-LA (207 sensors) and PEMS-BAY record speed every 5 minutes, so the 3rd, 6th, and 12th forecast steps (h3h_3, h6h_6, h12h_{12}) are 15, 30, and 60 minutes ahead, following the standard traffic-forecasting convention [6]. LargeST-SD records flow every 15 minutes, making the same horizons 45, 90, and 180 minutes.

We describe all three datasets using the same notation. Let yi(t)y_i(t) denote the reading from sensor i∈{1,…,N}i \in\{1,\ldots,N\} sampled at cadence δ\delta. A window ww anchored at twt_w pairs a context Xw={yi(t)}tw−C≤t≤twX_w = \{y_i(t)\}_{t_w-C \le t \le t_w} of C=512C = 512 steps (equal for both models, a multiple of TimesFM’s 32-step patch) with targets Yw∈RN×HY_w \in\mathbb{R}^{N \times H}, H=12H = 12, and a forecaster ff maps XwX_w to Y^w\widehat{Y}_w. We score forecasts by mean absolute error (MAE; lower is better), masked and averaged over a set of windows, or pool, P\mathcal{P},

MAE⁡(f;P)=1∣V(P)∣∑(w,i,h)∈V(P)∣Y^w,i,h−Yw,i,h∣,(1)\operatorname{MAE}(f;\mathcal{P}) = \frac{1}{|V(\mathcal{P})|} \sum_{(w,i,h)\in V(\mathcal{P})} \left|\widehat{Y}_{w,i,h} - Y_{w,i,h}\right|, \tag*{(1)}

where V(P)={(w,i,h):w∈P,Yw,i,h≠0}V(\mathcal{P}) = \{(w,i,h): w \in\mathcal{P}, Y_{w,i,h} \ne0\} excludes the zero-coded missing entries identically for every model, the masking convention established by [6] and standard across the traffic literature [7], [9].

Shift Construction

We construct three shifts per dataset. S1 (weekday to weekend) and S2 (peak to off-peak) are temporal: weekdays are Monday through Friday, and peak hours are 7–10 and 16–19 local time (§ 5 varies this window). For each temporal shift, πS\pi_S is a condition on the timestamp (for S1, “Saturday or Sunday”), and a test window enters the shift pool only if all HH steps it forecasts satisfy it,

PS={w:πS(tw+hδ) holds for all h=1,…,H}.(2)\mathcal{P}_S = \{w : \pi_S(t_w+h\delta) \text{ holds for all } h=1,\ldots,H\}. \tag*{(2)}

Requiring the full forecast horizon to satisfy the condition prevents windows that cross a regime boundary from entering the pool. S3 (spatial holdout) instead tests sensors in a different location. We cluster sensor coordinates with kk-means (k=5k = 5, fixed seed; § 5 tests k∈{4,6,8}k \in\{4,6,8\}) and hold out one cluster: 37 of 207 sensors on METR-LA, 36 of 325 on PEMS-BAY, and 102 of 716 on LargeST-SD. The S3 pool contains every test window restricted to the held-out sensors, with the retained sensors forming the in-distribution sensor set.

Severity Measurement

With the shift pools fixed, we measure severity as the Wasserstein-1 distance between the in-distribution and shifted marginals of the observable, that is, the distributions of raw readings (speed or flow) in each pool, ignoring time order. Following [14], for these scalar marginals the distance reduces to the closed quantile-function form

W1(μ,ν)=∫01∣Fμ−1(u)−Fν−1(u)∣ du.(3)W_1(\mu,\nu) = \int_0^1 \left|F_\mu^{-1}(u) - F_\nu^{-1}(u)\right|\,du. \tag*{(3)}

We compute this distance per sensor and report the sensor mean. For the two temporal shifts, S1 and S2, each sensor’s in-distribution and shifted target pools supply the two marginals. The spatial case differs because S3 has no shared sensor axis: each held-out sensor’s marginal is compared with the pooled marginal of the retained sensors. S3 thus compares a sensor with other sensors, not with itself, so its reading also carries location differences. With all sensors pooled on both sides instead, LargeST-SD weekends are still the lowest-severity setting (W1W_1 49.7, against 68.3 and 140.8).

For comparisons across settings, we normalize severity within each dataset by its largest reading. Alongside W1W_1, we compute two further marginal severity measures under the same conventions: the two-sample Kolmogorov–Smirnov statistic and the absolute mean difference, which isolates the level component. Section IV reports all three.

Fig. 1 shows the nine pairs of pool marginals used by these estimators; the resulting readings are reported in Table II.

DatasetS1 (Weekend)S2 (Off-peak)S3 (Spatial)
W1W_1Δ\DeltaC2Δ\DeltaTFMW1W_1Δ\DeltaC2Δ\DeltaTFMW1W_1Δ\DeltaC2Δ\DeltaTFM
METR-LA4.3−1.5−4.56.8−28.3−35.55.5+18.7+20.6
PEMS-BAY4.2−51.4−48.17.4−52.9−54.75.5−19.9−20.1
LargeST-SD55.1+28.6+8.4142.2−33.7−35.292.6−26.1−25.7

Table II. Shift severity and frozen-model degradation.

Models and Training Protocols

With the shifts and severity measures fixed, we evaluated seven models: two frozen TSFMs (Chronos-2 and TimesFM), three trained graph models (DCRNN, Graph WaveNet, and STAEformer), and two classical baselines (historical average, HA, and ARIMA). The TSFMs operate zero-shot and are never tuned. We train the graph models on the standard split of each dataset in accordance with their released configurations [6, 7, 8]. The LargeST-SD variants of DCRNN and Graph WaveNet use the benchmark authors’ released implementations [9]; STAEformer uses its upstream implementation on converted SD data, with alignment checked against the frozen arrays.

For the repair analysis of § 4-E, we use the same graph architectures but retrain DCRNN and Graph WaveNet on the corresponding in-distribution training pools. For S1, this means weekday-only target windows; for S2, peak-only target windows. We then evaluate these retrained models on the shifted pools using the same masking convention.

Evaluation Criteria

We evaluate each model under three criteria. For model ff and shift SS (S1, S2, or S3), the first measures relative MAE change,

ΔS(f)=MAE⁡(f;PS)MAE⁡(f;PID)−1.(4)\Delta_S(f) = \frac{\operatorname{MAE}(f;P_S)}{\operatorname{MAE}(f;P_{\mathrm{ID}})} - 1. \tag*{(4)}

A positive value means higher MAE under the shift. Table II reports 100ΔS(f)100\Delta_S(f) in percent. The in-distribution pool PIDP_{\mathrm{ID}} is the complementary slice of the same test period: weekday-target windows for S1, peak-target windows for S2, and retained sensors for S3. The paired pools therefore share the alignment and masking conventions.

The second criterion asks whether the shift changes which model is preferred. We rank the MM models available on each dataset by MAE on PIDP_{\mathrm{ID}} and again on PSP_S, and compare the two orders with Kendall’s rank correlation (τ=1\tau= 1 means the ranking does not change),

τ=nc−nd(M2),(5)\tau= \frac{n_c-n_d}{\binom{M}{2}}, \tag*{(5)}

where ncn_c and ndn_d are the numbers of concordant and discordant model pairs. We use M=7M = 7 for METR-LA and PEMS-BAY and M=6M = 6 for LargeST-SD, the model set fixed when the ranking protocol was registered. The released artifacts also include the M=7M = 7 LargeST-SD variant. We form confidence intervals by resampling sensors with replacement using 1000 resamples and a fixed seed. For S3, the two disjoint sensor sets are resampled independently. The interval endpoints are the 2.5th and 97.5th percentiles of the resulting τ\tau distribution.

The third criterion asks whether a failing shift can be repaired. We measure adaptability by whether an intervention improves upon the corresponding frozen model. The test-time adaptation protocol for this criterion is formalized in § 4-E.

Finally, to test whether severity orders the shifts by degradation (the first criterion), we compute the Spearman rank correlation between within-dataset normalized severity and ΔS\Delta_S. We report this correlation at two granularities: descriptively over all 18 model–setting evaluations, and inferentially at the setting level, where the two backbones are averaged per setting and the exact two-sided pp-value is computed over all 9! orderings. For the failing temporal setting we additionally form day-block bootstrap intervals, resampling calendar days within each pool (2000 resamples, fixed seed). We record model-specific freedoms, including context length and batching, for every run.

Theoretical Analysis: Severity–Degradation Decoupling

Chronos-2 first standardizes each context window by its own mean and standard deviation. The network therefore forecasts in normalized coordinates, after which the transformation is inverted to return to the original scale. For the argument below, let xx be one sensor’s context window and yy its target. The full context XwX_w in Section III-A stacks these series across sensors. What matters is what this normalization does to a change in level or scale. The answer is the normalization-equivariance of [40], [41], which we restate for forecasters because the consequence below rests on it.

Proposition 1 (affine equivariance). Let ff be a forecaster of the form

f(x)=s(x)g(x−m(x)s(x))+m(x),f(x) = s(x)g\left(\frac{x-m(x)}{s(x)}\right) + m(x),

where mm and ss are the context mean and standard deviation, s(x)>0s(x) > 0, and gg is any map acting in the normalized domain. Then, for every a>0a > 0 and bb, f(ax+b)=af(x)+bf(ax+b) = af(x) + b.

Proof. For a>0a > 0, m(ax+b)=a m(x)+bm(ax+b) = a\,m(x)+b and s(ax+b)=a s(x)s(ax+b) = a\,s(x). The standardized context z=(x−m(x))/s(x)z = (x-m(x))/s(x) is therefore invariant under x↦ax+bx \mapsto ax+b. Hence

f(ax+b)=s(ax+b)g(z)+m(ax+b)=a s(x) g(z)+a m(x)+b=af(x)+b.\begin{aligned} f(ax+b) = s(ax+b)g(z) + m(ax+b) \\ &= a\,s(x)\,g(z) + a\,m(x) + b = af(x) + b. \end{aligned}

Consequence. The proposition has a direct consequence for a severity audit. Suppose a regime differs only by a translation, (x+b,y+b)(x+b,y+b). The model prediction moves by the same bb, so the forecast error does not change. Yet the marginal Wasserstein-1 distance for that same shift is ∣b∣|b|, which can be made arbitrarily large. The severity score can therefore keep growing while degradation stays exactly zero. Scaling behaves similarly since absolute error scales with the data, but the relative comparison is unchanged. In this way, marginal severity and degradation become decoupled for this model class.

Chronos-2 also applies arcsinh to the standardized values, which compresses extreme values, and sinh on the way back. Both act after standardization, so they are part of gg and Proposition 1 still holds. We checked the argument against the released models rather than relying on the equation alone. For Chronos-2, scaling a real window by a=2a = 2 gives bitwise-matching transformed forecasts. With a much larger translation, b=1000b = 1000, the MAE ratio deviates from 1 by 0.78%, which we attribute to bfloat16 arithmetic. TimesFM normalizes with running per-patch mean and standard deviation statistics, which are affine-equivariant in the same way; across the same transformations its worst relative deviation is below 2×10−72 \times10^{-7}. The verification scripts are in the released repository. This result is limited to forecasters with this form of instance normalization.

Experiments

Experimental Setup

We use three real-world traffic datasets comprising 1,248 sensors and roughly 49 million observations. METR-LA and PEMS-BAY record traffic speed, while LargeST-SD records traffic flow. Every model forecasts every frozen test window, which amounts to about 60 million target values per model on LargeST-SD alone. We use LargeST’s released single-region year at full sensor count. Frozen models produce one prediction array over the full test period per dataset. We use the released Chronos-2 checkpoint and TimesFM 2.5 (200M parameters, PyTorch release). Both frozen models receive the same inputs: a context of 512 steps per sensor, batched 256 sensors per forward pass. Forecasts are invariant to the ordering of sensors within a batch for both models, so no cross-sensor information enters the frozen predictions. Shift pools are formed from the same arrays by the target-step rule, so in-distribution and shifted scores share every alignment convention. The shift-retrained variants used in § 4-E follow the protocol of Section III-D.

Table I reports the one-time compute. Under our released implementations, frozen-model inference accounts for most of this cost.

TaskDatasetWall time
Chronos-2 inferenceAll 3 datasets0.7 h
TimesFM inferenceAll 3 datasets192.8 h
Graph WaveNet trainingLargeST-SD2.2 h
STAEformer trainingLargeST-SD4.0 h
TTRA adapterLargeST-SD S12.8 h
Table/figure generationAll results≤33\le33 s

Table I. One-time audit compute.

Runs use an NVIDIA A100. Predictions are cached once; all tables and figures use the cached results. Both models receive identical inputs. With its released code, TimesFM 2.5 ran at about 15 series per second for any batch size from 256 to 4,096.

In-Distribution Performance

Before evaluating distribution shift, we first compare the models on the standard test split. The trained graph models achieve the lowest MAE on all three datasets, while the frozen TSFMs generally fall between the graph models and the classical baselines. On METR-LA, Chronos-2 records 4.65 MAE, compared with 4.19 for the historical average. The Std column of Table III reports the full comparison. We establish this ordering as a reference for the shift results that follow.

ModelMETR-LA (mph) StdS1S2S3PEMS-BAY (mph) StdS1S2S3LargeST-SD (veh/15 min) StdS1S2S3
HA4.193.523.444.992.631.711.942.2627.9321.5720.1622.32
ARIMA5.235.454.775.872.231.281.761.8455.4342.1645.4742.62
DCRNN3.162.732.713.731.611.021.231.3421.2017.7316.3116.10
Graph WaveNet3.042.522.643.591.581.001.221.3118.5016.2114.1914.64
STAEformer2.942.472.583.451.540.981.181.2418.4416.1713.6514.34
Chronos-24.654.614.105.341.841.051.371.5121.7026.1417.3016.67
TimesFM3.913.783.384.561.691.021.241.3822.2023.8217.3017.13

Table III. Average MAE on the standard test split and each shift pool. Std = standard test split; S1 = weekends; S2 = off-peak; S3 = held-out sensors. Bold marks the two settings where Chronos-2 and TimesFM degrade. For S3, the trained models saw all sensors during training.

Finding 1: Severity Does Not Predict Degradation

We first ask whether the shifts ranked as more severe are also the shifts that degrade the frozen models. In 7 of 9 dataset–shift settings (14 of 18 model–setting evaluations), the models maintain or improve performance under shift. PEMS-BAY improves by as much as 54.7%, and the off-peak regimes are easier on all three datasets. The two exceptions are LargeST-SD weekends (+29% for Chronos-2, +8% for TimesFM) and the METR-LA spatial holdout (+19%, +21%). Table II places these degradation values beside each setting’s severity reading, while Table III reports the corresponding MAE for all seven models.

W1W_1 is Wasserstein-1 in observable units (mph; veh/15 min for SD), so compare W1W_1 only within a row. Underline marks the lowest W1W_1 in each row. Δ\DeltaC2 and Δ\DeltaTFM report 100Δs(f)100\Delta_s(f) for Chronos-2 and TimesFM; bold marks degradation.

The severity readings do not follow this degradation pattern. LargeST-SD weekends, the strongest temporal failure, have the lowest W1W_1 in that dataset (55.1, against 92.6 and 142.2), while the METR-LA spatial failure has a mid-range reading. The highest-severity settings are instead the off-peak regimes, where both frozen models improve. Across all 18 evaluations, within-dataset normalized severity and degradation have a descriptive Spearman correlation of ρ=−0.51\rho= -0.51. Averaging the two backbones within each setting gives ρ=−0.47\rho= -0.47 with p=0.20p = 0.20. The same pattern appears with KS and mean difference (ρ=−0.24\rho= -0.24 and −0.44-0.44). Mean difference also reproduces the Wasserstein within-dataset ordering, showing that W1W_1 on these pools largely follows level change, the component removed by instance normalization. Computing W1W_1 and KS on per-window standardized data, as the models see it, does not help (ρ=−0.56\rho= -0.56 and −0.44-0.44).

One possibility is that this negative association reflects differences in regime difficulty. We therefore repeat the comparison using loss of skill relative to the historical average. The correlation disappears (ρ=+0.02\rho= +0.02, p=0.98p = 0.98), but LargeST-SD weekends still show the largest skill collapse of all nine settings (0.56 for Chronos-2 and 0.40 for TimesFM) at the lowest severity reading in that dataset. The METR-LA spatial setting no longer counts as a failure under this metric because the frozen models lose less accuracy than the historical average. With MASE the correlation stays negative (ρ=−0.51\rho= -0.51), but with sMAPE it is near zero (ρ=−0.12\rho= -0.12), because LargeST-SD off-peak, where flow is low, worsens by 63% in relative error for Chronos-2. Figure 2 shows all 18 evaluations under the three severity measures.

Severity versus degradation under Wasserstein-1, Kolmogorov–Smirnov and mean difference

Figure 2. Severity versus degradation under W1W_1, KS and mean difference. The temporal failure (SD-S1, red) has the lowest severity in its dataset under all three. Panel ρ\rho is descriptive (18 non-independent points); exact setting-level tests give ρ=−0.47\rho= -0.47, −0.25-0.25, −0.41-0.41 (p=0.20p = 0.20, 0.510.51, 0.280.28).

The LargeST-SD spatial result is split-sensitive: alternative holdout cluster counts reverse its sign and reduce the nondegrading count from 7 of 9 to 6 of 9 (§ 5). No other result in this finding depends on that spatial sign.

Finding 2: Severity Misses a Ranking Failure

Having shown that severity does not identify the degrading settings, we next ask whether those failures change model selection. Rankings remain stable under most shifts: Kendall τ\tau is at least 0.905 on METR-LA and 1.000 on PEMS-BAY. LargeST-SD weekends are the exception, where τ\tau falls to 0.333 and the historical average moves above both frozen TSFMs. A frozen model selected on weekday validation is therefore not necessarily the best choice for the weekend regime. Table IV reports the full ranking comparison, and Figure 3 shows this reordering directly.

DatasetS1 (Weekend)S2 (Off-peak)S3 (Spatial)
METR-LA0.9050.9051.000
PEMS-BAY1.0001.0001.000
LargeST-SD0.3330.8671.000

Table IV. Agreement between in-distribution and shifted model rankings (Kendall τ\tau). Bold marks LargeST-SD weekends. Its 95% confidence interval is [0.333,0.333][0.333, 0.333] by sensor (1000 resamples); the ranking never changed under sensor resampling) and [0.20,0.47][0.20, 0.47] by day (2000 resamples).

Figure 3. LargeST-SD model rankings on weekdays and weekends (τ=0.333\tau= 0.333). The historical average moves above Chronos-2 and TimesFM, while Chronos-2 falls from second to fifth.

Smaller pairwise inversions also occur on METR-LA, where the historical average passes TimesFM on weekends and Chronos-2 off-peak, but the overall ranking remains close to its in-distribution order. The LargeST-SD result also persists when calendar days are resampled: day-block bootstrap gives τ∈[0.20,0.47]\tau\in[0.20, 0.47]. For degradation, Chronos-2 has an interval of [13%,45%][13\%, 45\%], which excludes zero, while TimesFM’s [−2%,20%][-2\%, 20\%] interval does not.

Finding 3: Repairing the LargeST-SD Weekend Failure

We focus our repair analysis on LargeST-SD weekends because it is the only failing temporal setting and the only weekend regime that is harder than its weekday reference. It is a Saturday failure: Chronos-2 degrades by 67% on Saturdays and 2% on Sundays (TimesFM: 34% and −10%-10\%). This failure also becomes stronger with forecast horizon, reaching +51%+51\% for Chronos-2 at h12. For METR-LA, its spatial failure shows the same horizon-dependent pattern, while no non-degrading setting exceeds 9% at any horizon (Figure 4).

Figure 4. Degradation by forecast horizon. On LargeST-SD weekends it grows to +51% for Chronos-2 at h12; on LA-S3 it stays near +20%. Shading spans the other 14 curves.

We first test retraining. If the failure can be corrected from the reference regime alone, a model retrained on weekdays should recover on weekends. It does not. Weekday-retrained DCRNN reaches 28.96±0.72 MAE on LargeST-SD weekends, worse than frozen Chronos-2 at 26.14. Weekday-retrained Graph WaveNet reaches 24.67 ± 1.79 and does not reliably improve on frozen TimesFM at 23.82. We also notice a broader pattern across the five settings with both retrained and frozen results. The frozen models have lower MAE in four, with METR-LA weekends the only exception. The above findings leave two possibilities: either the retrained models have too little data or are missing the regime on which they are evaluated. We then separate these two possibilities at the same training budget. A random standard subset that includes weekends reaches 15.35±0.27 MAE, while weekend-only Graph WaveNet reaches 15.60 ± 0.13 and weekend-only DCRNN reaches 19.28 ± 1.55. In contrast, a weekday subset size-matched to the weekend pool reaches 29.27 ± 2.63. The failure therefore follows regime exclusion rather than training volume.

The standard-split graph models support the same explanation. Because their training data already contain weekends, Graph WaveNet reaches 16.21 MAE and DCRNN 17.73 on the identical weekend pool (Table III). These results point to regime exposure as the main difference: models trained with weekend data perform well on the weekend pool, whereas models trained only on weekdays do not.

Retraining shows that exposure to the weekend regime matters. We therefore ask whether the frozen model can recover from the test context alone, without weekend targets. We use TTRA, a pre-registered adapter that adds fast weights [23] to the frozen backbone and updates them by one self-supervised gradient step on each context window, with no future target entering the update. Its initialization is meta-learned on weekday windows using the backbone’s pinball loss [15],

ρτ(y,q^)=2∣(y−q^)(1{y≤q^}−τ)∣,(6)\rho_\tau(y,\hat{q}) = 2\left|(y-\hat{q})\left(\mathbf{1}\{y \le\hat{q}\}-\tau\right)\right|, \tag*{(6)}

averaged over the forecast horizon and the backbone’s 21 quantile levels. On weekday validation, the adapter reduces pinball loss by 13.1%. On weekends, however, the same procedure increases pinball loss by 8.3% and MAE from 26.14 to 27.80. The adapted model has higher MAE at every forecast horizon (Figure 5). TTRA therefore improves its weekday objective without transferring that improvement to the failing regime. A shorter context does not repair the failure either (Table V). With 48 hours of context instead of 128, weekend MAE changes by about 3% and stays above the historical average; with 24 hours it rises, and weekday MAE more than doubles for both models.

ModelInterventionAvg MAE
Chronos-2None26.14
TimesFMNone23.82
Chronos-2TTRA adaptation27.80
Chronos-248-hour context26.80
Chronos-224-hour context29.76
TimesFM48-hour context23.11
TimesFM24-hour context33.15
Graph WaveNetWeekday-only retraining24.67 ± 1.79
Graph WaveNetWeekend-only training15.60 ± 0.13
Graph WaveNetStandard subset, size-matched15.35 ± 0.27
Graph WaveNetWeekday subset, size-matched29.27 ± 2.63
Graph WaveNetPer-window normalization27.85 ± 0.61
DCRNNWeekday-only retraining28.96 ± 0.72
DCRNNWeekend-only training19.28 ± 1.55
Regime routerTimestamp routing21.57

Table V. Model performance on LargeST-SD weekends. Retrained models report mean ± std over three seeds. Bold marks the best frozen model and the router.

Figure 5. Test-time adaptation on LargeST-SD weekends. (a) The adapted model has higher MAE at every horizon. (b) The adapter reduces weekday validation pinball loss by 13.1% but increases weekend pinball loss by 8.3%.

The TTRA result leaves a second model-level possibility. Our mechanism analysis shows that per-window normalization removes level and scale changes before forecasting, so we test whether giving Graph WaveNet the same normalization makes the weekend shift easier to absorb. The matched variant replaces its training-set normalization constants with each window’s own per-sensor statistics, placing the estimator in the form of Proposition 1 while leaving everything else unchanged. The relative weekday-to-weekend gap does narrow, from 43% to 26% at the pinned seed, but the model reaches 27.85 ± 0.61 MAE. The normalization changes the relative degradation without recovering the lost accuracy.

None of these interventions recovered the weekend failure. Our weekday retraining never sees the failing regime, our TTRA adapter improves its weekday objective while worsening weekend performance, and our matched-normalization variant narrows the relative gap without recovering the lost accuracy. Each of them tries to make a single model handle both regimes. We instead use a fact these model-level repairs do not exploit: whether a window falls on a weekday or weekend is known from its timestamp before forecasting. This lets us select a model for the regime rather than require one model to handle both. We therefore route by timestamp, choosing among the historical average, Chronos-2, and TimesFM by validation MAE within each regime, which requires labeled validation data from each regime. The rule selects Chronos-2 for weekdays and the historical average for weekends. On the frozen test period it reaches 21.57 MAE on weekends and 20.46 over the full period, improving on both frozen TSFMs and on DCRNN’s 21.20, though standard-trained Graph WaveNet remains better at 18.50 (Table III). We select entirely on validation data and never touch the test set. Our repair experiments therefore mark a boundary. Models trained with weekend data handle the regime, while weekday-only retraining, test-time adaptation, and matched normalization do not recover the failure. For the frozen deployment, routing works by using the known regime to select the model that performed best on validation.

Pre-Registered Predictions vs. Outcomes

Table VI reports each pre-registered prediction against its outcome, including the two falsifications. We registered the predictions on 2026-06-08 and amended P4 to P4′ on 2026-07-04, before any adapter was trained. P4 originally predicted that the adapter on frozen Chronos-2 would cut shift-induced degradation by at least 10% on two of the three shifts. The frozen-degradation grid falsified its premise before any adapter existed, since Chronos-2 does not degrade on most settings, and P4′ retargets the one cell where degradation is observed on both backbones. The only substantial ranking reordering occurs on LargeST-SD, where STAEformer was not part of the registered ranking set.

IDPredictionOutcomeVerdict
P1Ranking τ lower under S1 than S2Held on LargeST-SD (0.333 < 0.867); ties elsewherePartially held
P2Graph models degrade more than per-sensor models under S3Needs S3-retrained graph baselines; scoped out by protocolNot testable
P3STAEformer top-2 under S2, drops ≥ 2 ranks under S1Rank 1 under both shifts on every dataset evaluatedFalsified
P4′TTRA cuts frozen SD-S1 degradation by ≥ 10%Adapted MAE 27.80 > frozen 26.14 at every horizonFalsified
P5Inner-loop steps > 0 beat static registersNot run; gated on the failed adaptation gate (Sec. IV-E)Not evaluated

Table VI. Pre-registered predictions and their outcomes.

Sensitivity Analysis

We rerun the audit under three alternative peak-window definitions, narrowing, widening, or shifting the registered Section III-B window by one hour, and under holdout cluster counts k∈{4,5,6,8}k \in\{4,5,6,8\}. The off-peak improvement holds in all eleven window–dataset pairs that admit a valid pool, and ranking stability remains at τ≥0.81\tau\ge0.81 across the peak variants and τ≥0.905\tau\ge0.905 across the cluster counts (Figure 6). The exception is the LargeST-SD spatial result, whose degradation sign changes with the holdout definition. This changes the non-degrading count from 7 of 9 to 6 of 9 but does not affect the temporal failure or the severity-ranking result.

Figure 6. Ranking stability under other split choices: S2 peak windows (left) and S3 cluster counts kk (right). Dashed line: τ=0.905\tau= 0.905.

Discussion

a) Regime-Level Monitoring: These findings suggest that monitoring a single severity score may not be enough for frozen TSFMs, because the degrading regime can appear first as a change in model ranking rather than as a large distribution shift. On LargeST-SD weekends, this change reduces Kendall τ\tau to 0.333 and moves the historical average above both TSFMs (Table IV, Figure 3). Yet the same weekend setting receives the lowest severity reading in its dataset (Table II). This mismatch is consistent with earlier traffic studies showing that aggregate evaluation can conceal errors at finer levels: corridor-level validation conceals per-lane errors [33], while aggregate MAE conceals transition-regime error [34]. Our results show the same problem at the shift level, where a single severity reading does not identify the regime carrying the degradation (Table II). This suggests that monitoring should also compare model performance across known operating regimes. In the weekend regime, the timestamp itself provides useful regime information, allowing a historical average to outperform both TSFMs. The router in § 4-E uses this information to select the better of the available frozen candidates in that regime.

b) Boundary of Distance-Based Severity: Our findings do not imply that Wasserstein distance is generally uninformative. Chen et al. report correlations above 0.60 between Wasserstein distance and foundation-model loss across datasets [35]. That comparison is made across separate datasets, where we expect level and scale differences to contribute strongly to the distance. Our setting is different. Within one deployment domain, Proposition 1 shows that an instance-normalizing forecaster removes the affine component that can dominate marginal W1W_1. This removal can break the expected relationship between the severity reading and model degradation (Figure 2). The accuracy-on-the-line result similarly reports strong correlations across architectures, hyperparameters, and training scale, while also identifying cases where that relationship weakens [36]. Regime shifts under instance normalization provide another such case, as our experiments show. These results suggest that a useful severity measure should depend on the forecasting task, because a distance on raw observable marginals can be dominated by information that the model removes before prediction. Vision reports a similar pattern, where behavior-based estimators predict degradation in settings where distributional distances fail [37], [38]. Quantile-spread and reference-residual monitors are possible time-series alternatives, although this audit does not evaluate them.

c) Normalization and Model-Class Differences: The different behavior of the two model classes is consistent with their normalization schemes. The graph baselines normalize with training-split statistics, while the frozen TSFMs restandardize every context window (Section III-F). As a result, a regime whose level differs from the training statistics reaches the graph models without per-window normalization, while the frozen TSFMs remove that level difference before prediction. This difference helps explain why the same shift can affect the two model classes differently. Section III-C traces these normalization designs and their connection to severity-based auditing.

d) Contamination and Within-Dataset Auditing: These findings must also be interpreted in light of possible training-data contamination, since the backbones may have seen these datasets in pretraining. PEMS-BAY and LargeST appear verbatim in at least one public TSFM pretraining corpus, the one released with Moirai [3]. The pretraining corpora of the two backbones we evaluate are not public, so their exposure cannot be checked directly. A recent audit finds only a small fraction of benchmark datasets absent from every pretraining corpus [39], and methods for auditing this contamination are emerging [27]. Our within-dataset comparison reduces this concern because the reference and shifted regimes come from the same dataset. Any memorization can therefore affect performance on both regimes rather than only one side of the comparison. The weekend failure remains present under this comparison, regardless of the backbones’ possible exposure to the dataset.

Limitations

All evidence here comes from traffic data and two backbones, so it does not show that severity fails for every instance-normalized forecaster or in other domains. Nor do we show that every notion of severity fails. A severity measure tied to the forecasting task remains open.

Conclusion

In this work, we conducted a systematic audit that shows that the tested measures used to rank distribution shifts by severity do not predict degradation for instance-normalized TSFMs in these settings. Our results show that the regime carrying its dataset’s lowest severity score causes the largest degradation, and this degradation reorders the audited models’ ranking, with a plain historical average model passing both Chronos-2 and TimesFM. We show that the equivariance property of these models provides a mechanism by which severity measures can fail to track degradation. Experiments across three datasets (METR-LA, PEMS-BAY, and LargeST-SD) on nine shifts show that severity measurement does not predict failure for instance-normalized TSFMs, because none of the severity measures we tested identifies the regimes in which these models fail. When these models fail, they fail without warning, and the failing regime has the lowest severity reading in its dataset with degradation of up to 29% for these models. Lastly, test-time adaptation did not repair the failure, while models trained with weekend data did.

Acknowledgment

Claude was used to assist with related-work synthesis and as a secondary check of the proof of Proposition 1. Claude also assisted with the coding. All results and claims are the true work of the authors.

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