WorksComputer Science
A Verifier from the Past: Test-Time Compute for Time Series Foundation Models
Abstract
Test-time compute (TTC) improves language models by spending additional inference compute to generate, verify, and select among candidate outputs, but this recipe has not transferred directly to time series forecasting. A language model can verify a proof or vote across samples, but a forecaster must be causal; it cannot use future information to score a candidate. We propose Backtest-Gated Augmentation Averaging (BGAA), a TTC algorithm for time series forecasting that builds a causal verifier from the series's own history, using rolling-origin backtests to score structured views of the context, discard those that underperform the untransformed context, and average the survivors' predictive distributions. BGAA improves every tested TSFM-benchmark combination, reducing MASE by 0.5-1.0% on GIFT-Eval, 1.3-5.0% on fev-bench, and 1.7-5.9% on BOOM, where a 313M model with TTC outperforms the 1B and 2.5B models in its family. We further show that useful views have structured, model-dependent effects consistent with a prior-transport interpretation. On the 53 cross-fittable GIFT-Eval configs, the deployed policy gains only 0.4-1.3% CRPS, versus 1.4-4.1% when choosing the best view for each dataset configuration and 17-19% when choosing the best view separately for each test window. This gap suggests that a major remaining challenge is window-level view selection.
Introduction
A time series foundation model (TSFM) is pretrained once but deployed across many diverse series. Improving performance usually requires larger models or more training. Test-time compute offers another route: keep the model frozen and spend additional inference-time compute to improve forecast accuracy. Language models do this by thinking longer [21] (Wei et al. 2022) or wider, sampling and selecting among multiple candidates (Snell et al., 2025). Thinking wider requires a verifier, a signal for which candidate is better. Language modeling has several: program synthesizers run tests [16], provers check steps, reward models score answers [7], and majority vote exploits agreement across correct chains (Wang et al., 2023).
These verifiers don’t transfer to time series. A numeric forecast has no syntax to violate, nor tests to fail. A reward model would need labeled forecasts for the deployment series, which are unavailable at inference time. Without a causal verifier, TSFMs are deployed with a single forward pass.
A forecaster has something a language model does not: the series’ own past. A language prompt provides only a single instance of the task, whereas a forecasting context contains earlier prediction problems with observed outcomes. We rebuild the deployment task from the context alone and score candidates by rolling-origin backtest, reading nothing past the last observed point.
We introduce Backtest-Gated Augmentation Averaging (BGAA), a test-time compute algorithm for time series forecasting. BGAA generates several structured views of the same context, obtains a candidate forecast from each using the same frozen model, and scores them using a rolling-origin backtest on the observed history. Candidates that outperform the untransformed input on the historical backtest are retained and aggregated. Because past performance is only a proxy for future accuracy, the verifier is a surrogate, but it is causal and available for every series at test time.
Why should structured views give different, sometimes better, forecasts from the same observations? Under a Prior Fitted Network idealization, a frozen TSFM predicts under a distribution induced by pretraining (Muller et al. [20]). For fixed pointwise, monotone transforms, forecasting a transformed context and mapping quantiles back is equivalent to prediction under a transported trajectory distribution (Proposition 1). Our deployed views are more general, so we treat this as an illustrative interpretation and test for systematic, model-dependent effects in § 6.
Test-time compute on TSFMs needs safeguards against degradation. The base forecast remains a candidate, and the backtest acts as a referee: a view is admitted only if it beats the base on held-out windows (§ 3). This makes additional inference compute selective, since views are used only when the historical backtest indicates improvement over the base.
We test Chronos-2, TiRex-2, PatchTST-FM-R1, and Toto-2-313M on GIFT-Eval, BOOM, and fev-bench. All 12 model–benchmark combinations improve with no per-model re-tuning: 0.5 to 1.0% MASE on GIFT-Eval, 1.7 to 5.9% on BOOM, 1.3 to 5.0% on fev-bench. The gain often exceeds the spacing between model sizes: on BOOM, test-time compute on Toto-2-313M beats the 1B and 2.5B models of its own family. On GIFT-Eval, the high TiRex-2 rung achieves lower MASE at more inference FLOPs than Toto-2-2.5B (§ 5). Simple view ensembling does not explain this gain: at matched compute on Chronos-2, random selection from the same pool worsens MASE by 4.8%, while BGAA improves it by 1.0%.
We also measure the remaining headroom. On the 53 GIFT-Eval dataset configurations that support cross-fitting, BGAA improves CRPS by 0.4–1.3%. Cross-fitted selection of the best single view per configuration raises this to 1.4–4.1%, while choosing the best view separately for each forecast window using its realized outcome gives 17–19%. This gap motivates better window-level verification, while leaving open gains from better candidate views.
Our contributions are four-fold:
Test-time compute for TSFMs (§ 3). BGAA needs only a quantile-forecast API, updates no weights, reads no future labels, and improves every model we test on every benchmark.
Why augmented views help (§ 6). Under the Prior Fitted Network idealization, fixed pointwise monotone views correspond to transported trajectory distributions. This motivates three predictions about structured, model-specific view effects, which § 6 shows them for all four models.
Evidence at scale (§ 5 and § 6). Across 4 models and 3 benchmarks, we measure the accuracy–FLOPs frontier and show that the gains arise from structured, model-dependent view effects and effective backtest-based selection, rather than simply ensembling more forecasts.
4. Verification headroom (Section 7). Using cross-fitted and label-based diagnostics, we quantify the remaining gap at the window-level, showing substantial window-specific headroom.
Related work
Time series foundation models (TSFMs). TSFMs are models pretrained on large, heterogeneous corpora and deployed zero-shot. Given a context, they forecast an unseen series with no task-specific training. They differ in how series are tokenized and pretrained [2, 3, 8, 9, 14, 12] (Wen et al. 2026; Woo et al. 2024). We study a complementary question: how to improve forecasts from an already-trained TSFM by spending additional inference compute while keeping its weights fixed.
Test-time compute in language modeling. Self-consistency, best-of-n with a reward model, verifier-guided search and compute-optimal inference [7, 18] (Wang et al. 2023; Snell et al. 2025) generate candidates and use different signals to select among them. Forecasting complicates candidate selection: the future observations needed to evaluate a forecast are unavailable at prediction time, and agreement among sampled forecasts does not by itself establish accuracy.
Test-time augmentation (TTA). TTA is standard in vision, where transformed inputs are evaluated and their predictions aggregated, with the aggregation rule as important as the augmentations [5, 24, 19]. For forecasting, transformed contexts enable producing multiple candidate forecasts; the question remains which views help for a time series.
Forecast combination and label-free adaptation. Combining forecasts is a longstanding approach [4, 6] (Timmermann 2006), including the choice between averaging quantiles and probabilities [17, 11]. Our use of forecast combination builds on this literature; the question here is which forecasts from transformed inputs to include in the combination. Conformal and recalibration methods use observed data to adapt predictive distributions or restore calibration [10] (Stankeviciūtė et al. 2021), whereas our problem is candidate selection before aggregation.
Inference-time compute for frozen TSFMs. Two concurrent methods spend inference compute on a frozen forecaster. Hua et al. [13] widen a saturating sample distribution by perturbing the input, but their main aggregator takes the median over all views, so harmful views are not filtered. Their selective variant ranks views against ground truth, and thus is limited to settings with labels. Pandey et al. [22] instead edit a single context, suppressing the most disruptive patch when a meta-feature gate fires, with the gate fit by cross-validation over a subset of GIFT-Eval. BGAA instead selects among transformed-input forecasts using rolling-origin backtests on observed history, requiring neither future labels nor a separately trained cross-dataset gate (Section 3).
Method: backtest-gated augmentation averaging
Setup and notation. We consider univariate forecasting for this work. Multivariate and covariate-aware forecasting are out of scope. Let be the history observed up to the forecast origin , the last observed time step (so is also the history length); let be the forecast horizon and the unobserved target. Such a history–target pair is a forecast window. Since time steps are ordered within each series, history lengths vary across series and windows; we index windows by , writing , , and , and drop when discussing a single window. A frozen forecaster returns
a matrix with rows indexed by horizon steps and columns by quantile levels ; its entry is the predicted -quantile at step . We call the base forecast.
A view modifies how the history is presented to the forecaster or how its forecast is returned to the original forecast space. Formally, maps the frozen forecaster to a forecaster with the same interface, . Let be the fixed pool of candidate views, and the candidate forecast of view , with entries indexed as for . The identity view leaves the history and forecast unchanged, , so is the base forecast.
A configuration, or config, defines a finite set of evaluation forecast windows , all with the same horizon . BGAA selects a single set of views per config and holds it fixed across . Selection uses only the observations available before the first forecast origin in , from which we sample a finite set of historical gate windows. This pools historical evidence across gate windows and amortizes selection cost across evaluation forecasts.
Problem definition. For a loss , BGAA seeks a forecaster , chosen using only the frozen black-box and , whose relative risk (its mean per-window loss divided by the base’s, so each window counts equally regardless of scale) satisfies
where contains the windows with positive base loss. Since their targets are unobserved at selection time, BGAA scores each view by the gate-window surrogate (Equation (4)).
Method overview. BGAA generates alternative forecasts from a frozen model, evaluates them on historical forecasting tasks, and combines selected alternatives with the base forecast. Each historical task holds out an already-observed segment and forecasts it using only preceding observations. These backtests select views once per config, before any evaluation window is observed. If historical evidence is insufficient or no alternative improves over the base, BGAA returns the base forecast. Figure 1 illustrates the pipeline, and Algorithm 1 summarizes the procedure. Note: is the standard gate, with a short-history exception, described in § 4.
Figure 1. BGAA system overview. (1) The observed context is the only input available at test time. (2) A fixed pool of transformed views is generated, and (3) each is forecast with the same frozen TSFM. (4) Forecasts are mapped back to the original observation space. (5) A leak-free rolling-origin backtest scores the views against the base and admits the best candidates. (6) The admitted forecasts are aggregated with the base forecast to produce (7) the final predictive fan.
Candidate generation. The candidate generator produces alternative forecasts for the same target horizon using the frozen forecaster. A view family specifies a type of modification, with different parameter settings defining individual views. For example, cropping is a family; retaining the latest 50% or 75% of the history defines two views. A view need not be an invertible input transformation: it may modify the context, post-process a forecast, or make multiple model calls, provided its output is returned to the same timestamps and units as the target. The fixed pool contains lookback crops, patch-phase offsets, differencing and seasonal differencing, decomposition and frequency-based views, distributional transforms, recursive rollout, and small perturbations. The complete catalog and pull-back rules are in Section B.
Selection using historical backtests. To evaluate a view without using any evaluation-window target, we recreate the forecasting problem inside an observed history. We index gate windows as and write for the observed history of . Each gate window provides backtests, one per rolling origin , ; at each origin, we forecast the next observations using only . For the loss , instantiated below, the empirical loss of view is
For point selection, is the mean absolute error of the median forecast. Because the MASE scale factor is common to a view and the base within a window, their relative comparison is unchanged, so we call this the MASE gate. The distributional alternative uses mean pinball loss over , a finite-quantile surrogate for CRPS, and is called the CRPS gate.
Windows with are excluded because relative improvement would be undefined. With and , each candidate view receives the score
Thus, means improves over the base on average across usable historical windows.
The deployed rule selects up to the views with the largest positive scores,
If , or no view has positive improvement, and the base forecast is returned. We also evaluate a margin rule that requires a minimum mean improvement and a minimum fraction of wins over ; its full definition is in Section A.1.
Forecast aggregation. Aggregation combines the base forecast and the candidate forecasts of , each with equal weight , into the aggregate forecast
Algorithm 1 BGAA with deployed top- selection
Require: frozen forecaster , views , horizon
Selection, once per config
for sampled historical gate windows do
evaluate for on rolling origins
end for
discard windows with
if then
else
compute and retain up to highest-scoring views with
end if
Application, per forecast window
if then
return
end if
return
Vincent averaging averages corresponding quantiles. CDF mixture converts each finite quantile fan to an interpolated CDF, averages the resulting distributions, and inverts the mixture at the nine levels in . We interpolate linearly between reported quantiles and extrapolate linearly in the tails using the slope of the nearest end segment, truncating the CDF at 0 and 1. Our deployed policy, mixtop3-mase, combines the MASE gate, top-3 admission, and CDF mixing; top3-mase uses the same selected set with Vincent averaging.
Properties of the aggregation rules. For an aggregation rule convex in the gate’s loss, Theorem 2 shows that admitted historical improvements carry over to the aggregate on the same backtest windows. Let denote the aggregate forecaster (BGAA’s ), its backtest loss, given by (3) with in place of , and
its mean backtest loss relative to the base. Under uniform weights, if is the smallest admitted relative improvement, then . This covers Vincent averaging under the MASE or CRPS gate, but not the deployed mixtop3-mase policy, because CDF-mixture quantiles are not convex combinations of member quantiles. The result bounds only; it does not bound or a benchmark’s aggregation rule.
CDF mixing has a separate exact-CRPS property: for member CDFs with weights , , and an outcome , is at most the weighted average of the members’ CRPS values (Theorem 3). This does not imply the mixture beats the base or the best member, and the identity applies to the full CDF before conversion back to nine quantiles. Full assumptions and proofs are in Section A.
Computational cost. BGAA separates selection from application. Selection evaluates the view pool on historical backtests once per config; the resulting is reused across its forecast windows. Application must still recompute the base and admitted candidate forecasts for each new context–horizon pair. Individual views can require zero additional calls when they post-process a cached base forecast, one call for a transformed context, or multiple sequential or seeded calls for recursive or stochastic views. A cached base forecast is reusable only for the same input, not across forecast windows. The four thinking modes vary the number of candidate views, gate windows and rolling origins, and admitted views. Across the four models they span roughly 2.3–9.5× the cost of a single pass on GIFT-Eval (Table 5); exact forward-pass accounting is in Section C.1.
Experimental setup
Models. We evaluate four public frozen TSFMs spanning different architectures and pretraining corpora: Chronos-2 ([3]), TiRex-2 ([23]), PatchTST-FM-R1 ((Wen et al., 2026)), and Toto-2-313M ([15]), all evaluated in their univariate settings. Toto-2-313M is the 313M family member used in our model-scaling comparisons.
Benchmarks. GIFT-Eval [1] contains 97 configs. BOOM [8] contains 7413 dataset×term observability tasks, of which the official leaderboard evaluates a 6750-task scaled subset. fev-bench [25] contains 100 forecasting tasks.
Metrics and statistics. We report MASE for point accuracy and CRPS on GIFT-Eval and BOOM, with SQL on fev-bench. GIFT-Eval uses the geometric mean of metric-to-seasonal-naive ratios, BOOM uses shifted geometric mean normalized by DataDog’s seasonal-naive run, and fev-bench uses raw metric means and skill against its published seasonal-naive baseline. We report relative changes, paired win/loss counts, and paired Wilcoxon tests over matched benchmark configs/tasks.
Evaluated method. All main results use mixtop3−mase, with and . The candidate pool and global design choices were chosen once using CHRONOS-2 on a labelled 15-config subset of the GIFT-Eval validation split and then frozen. No test, BOOM, or fev-bench data were used for this choice, and nothing is retuned by model or configuration. This global design choice is distinct from BGAA’s inference-time selection, which selects views from each configuration’s observed history. For GIFT-Eval and BOOM, we use a light gate of one rolling origin per gate window for configurations with , which account for a third of BOOM tasks. For 16 of the 100 fev-bench tasks, the history before the first evaluation window is too short for a single backtest fold. For these tasks, we forecast the first 23 evaluation windows with the base model and score them as base forecasts in all reported results. Once their targets are observed, the remaining windows are forecast with BGAA, whose gate backtests only on these initial windows, is run once. These initial windows receive no benefit from BGAA.
Baselines. The primary baseline is each model’s unchanged-input forecast. We also compare against alternative BGAA selection and aggregation policies, compute-matched random, noise, and identity controls, and published larger-model results used only for the model-scaling comparisons.
Main results
BGAA improves all evaluated model–benchmark combinations. Table 1 shows that BGAA improves both point and probabilistic forecasting across all 12 model×benchmark combinations without per-model or per-benchmark retuning. MASE improves by 0.5–1.0% on GIFT-Eval, 1.7–5.9% on BOOM, and 1.3–5.0% on fev-bench. These are benchmark-level aggregate improvements; individual configurations can regress, as analyzed below.
Table 1: BGAA improves performance across all 12 model×benchmark combinations. Frozen base versus the deployed mixtop3−mase policy, with no per-model or per-benchmark retuning. Boldface marks the lower score within each matched base−BGAA comparison; it does not indicate a ranking across models. reports relative change in MASE and the probabilistic metric, respectively; negative values indicate improvement.
| benchmark | model | base (MASE / CRPS†) | BGAA (MASE / CRPS†) | (MASE / CRPS†) | (MASE / CRPS†) | win/loss |
| GIFT-Eval | CHRONOS-2 | 0.7043 / 0.4830 | 0.6975 / 0.4778 | 0.004 / 0.004 | −0.97 / −1.07 | 55/38 |
| TIREX-2 | 0.6972 / 0.4791 | 0.6940 / 0.4776 | 0.021 / 0.028 | −0.45 / −0.32 | 54/38 | |
| PATCHTST-FM-R1 | 0.7052 / 0.4820 | 0.7018 / 0.4811 | <0.001 / <0.001 | −0.49 / −0.19 | 64/28 | |
| TOTO-2-313M | 0.7032 / 0.4838 | 0.6984 / 0.4806 | 0.023 / 0.042 | −0.69 / −0.66 | 60/32 | |
| BOOM | CHRONOS-2 | 0.6547 / 0.3935 | 0.6259 / 0.3803 | <0.001 / <0.001 | −4.39 / −3.38 | 4165/1691 |
| TIREX-2 | 0.6418 / 0.3855 | 0.6191 / 0.3763 | <0.001 / <0.001 | −3.54 / −2.39 | 3917/1941 | |
| PATCHTST-FM-R1 | 0.6812 / 0.4071 | 0.6410 / 0.3885 | <0.001 / <0.001 | −5.91 / −4.58 | 4283/1580 | |
| TOTO-2-313M | 0.5853 / 0.3532 | 0.5755 / 0.3501 | <0.001 / 0.008 | −1.67 / −0.89 | 3456/2299 | |
| fev-bench (MASE / SQL†) | CHRONOS-2 | 1.6332 / 1.3416 | 1.5513 / 1.2836 | <0.001 / 0.002 | −5.02 / −4.32 | 56/38 |
| TIREX-2 | 1.6192 / 1.3653 | 1.5989 / 1.3436 | 0.005 / 0.009 | −1.26 / −1.59 | 54/39 | |
| PATCHTST-FM-R1 | 1.5852 / 1.3150 | 1.5461 / 1.2845 | <0.001 / <0.001 | −2.46 / −2.32 | 65/27 | |
| TOTO-2-313M | 1.6652 / 1.3881 | 1.6444 / 1.3622 | 0.003 / 0.005 | −1.25 / −1.87 | 56/37 |
Table 1.
Test-time compute can dominate a larger model under the same compute–accuracy comparison. On GIFT-Eval, the high TIREX-2 + BGAA configuration achieves lower MASE than TOTO-2-2.5B with approximately 26% less estimated inference compute: 0.6945 versus 0.6956 MASE at approximately 89 versus 121 PFLOPs (Figure 2). This is a pairwise dominance result under our estimated inference-FLOPs accounting. Separately, on BOOM, BGAA on TOTO-2-313M achieves lower MASE than the published 1B and 2.5B members of the same family (Table 2).
Figure 2 compares the four thinking modes, which vary test-time compute while keeping the BGAA procedure fixed (Table 5). Returns diminish with budget: high captures 61–96% of the high MASE gain while using 54–78% of its compute. The CRPS ladders improve over their corresponding bases but do not establish the same dominance result. Cross-learning-on CHRONOS-2 also improves over its univariate counterpart at similar base compute, illustrating that test-time compute is not the only useful scaling direction. The FLOPs axis ignores batching and should be interpreted as estimated inference-compute accounting rather than latency. Full accounting is given in Section C.1. Complementary H100 measurements show that CHRONOS-2+BGAA requires 7.02–14.3 seconds to produce 10,000 forecasts across thinking budgets, compared with 28.5 seconds for Toto-2-2.5B, while using substantially less GPU memory (0.48 versus 10.30 GiB). Although the larger model retains better absolute accuracy, these results show that historical verification can be more efficient than deploying a much larger model for high-throughput forecasting (Table 7 and Table 8).
Figure 2. Test-time compute improves MASE under estimated inference-FLOPs scaling. On GIFT-Eval (97 configurations), lines connect four test-time compute budgets for each frozen model; stars denote published models at 1× compute. Each rung uses the model’s measured benchmark PFLOPs scaled by its measured forward-pass ratio (base + gate + apply)/base. The CRPS ladders also improve over their corresponding bases.
| System | Mode | MASE | WQL | PFLOPs | ms/fc | GPU (GiB) | ||||
| toto_2.0_2.5b | — | 0.6956 | 0.4759 | 121.0 | 0.133 | 0.319 | 2.86 | 28.5 | 2.85 | 10.30 |
| TiRex-2 | base | 0.6972 | 0.4791 | 15.6 | 0.0562 | 0.212 | 1.77 | 17.7 | 1.77 | 5.96 |
| TiRex-2+BGAA | high | 0.6940 | 0.4776 | 148.8 | 40.4 | 41.1 | 47.7 | 114 | 7.40 | 5.96 |
| CHRONOS-2 | base | 0.7043 | 0.4830 | 22.1 | 0.0143 | 0.0203 | 0.173 | 1.71 | 0.17 | 0.48 |
| CHRONOS-2+BGAA | low | 0.7012 | 0.4805 | 53.0 | 0.125 | 0.160 | 0.780 | 7.02 | 0.69 | 0.48 |
| CHRONOS-2+BGAA | medium | 0.7009 | 0.4797 | 66.8 | 0.280 | 0.358 | 1.11 | 8.59 | 0.83 | 0.48 |
| CHRONOS-2+BGAA | high | 0.7001 | 0.4802 | 111.9 | 0.993 | 1.09 | 1.99 | 11.0 | 1.00 | 0.48 |
| CHRONOS-2+BGAA | xhigh | 0.6975 | 0.4778 | 208.7 | 4.49 | 4.58 | 5.47 | 14.3 | 0.99 | 0.48 |
Table 7. Accuracy, compute, latency, and memory across thinking modes. MASE, WQL, and PFLOPs are from the full GIFT-Eval sweep (97 configurations); Toto-2-2.5B accuracy is published. Latency and peak GPU memory are measured on an H100 using synthetic contexts representative of the median GIFT-Eval configuration. BGAA times include historical selection, view transformations, and aggregation. ms/fc is the per-forecast application cost after selection at ; GPU is peak allocated memory at , including model weights. CHRONOS-2+BGAA is faster and more memory-efficient than Toto-2-2.5B at high forecast volumes, although the larger model retains better absolute accuracy.
| Model | Time (s): Base | Time (s): BGAA cold | Relative to frozen base (): Cold batched | Relative to frozen base (): Cold unbatched | Relative to frozen base (): Passes | Relative to frozen base (): Warm batched | GPU (GiB): Base | GPU (GiB): BGAA | |
| CHRONOS-2 | 1 | 0.0143 | 4.49 | 313 | 22,594 | 22,276 | 1.12 | 0.26 | 0.46 |
| 10 | 0.0158 | 4.49 | 285 | 2,260 | 2,231 | 1.30 | 0.27 | 0.46 | |
| 100 | 0.0203 | 4.58 | 226 | 230 | 227 | 5.55 | 0.42 | 0.47 | |
| 500 | 0.0864 | 4.97 | 57.5 | 49.2 | 48.5 | 5.77 | 0.47 | 0.47 | |
| 1,000 | 0.173 | 5.47 | 31.7 | 26.6 | 26.3 | 5.78 | 0.47 | 0.48 | |
| 2,000 | 0.345 | 6.45 | 18.7 | 15.4 | 15.1 | 5.74 | 0.48 | 0.48 | |
| 10,000 | 1.71 | 14.3 | 8.38 | 6.32 | 6.23 | 5.77 | 0.48 | 0.48 | |
| TIREX-2 | 1 | 0.0562 | 40.4 | 718 | 22,131 | 22,276 | 1.04 | 0.35 | 5.96 |
| 10 | 0.0659 | 40.4 | 613 | 2,222 | 2,231 | 1.70 | 0.45 | 5.96 | |
| 100 | 0.212 | 41.1 | 194 | 226 | 227 | 3.53 | 1.44 | 5.96 | |
| 500 | 0.884 | 44.0 | 49.8 | 48.3 | 48.5 | 4.19 | 5.83 | 5.96 | |
| 1,000 | 1.77 | 47.7 | 27.0 | 26.1 | 26.3 | 4.19 | 5.96 | 5.96 | |
| 2,000 | 3.54 | 55.1 | 15.6 | 15.1 | 15.1 | 4.19 | 5.96 | 5.96 | |
| 10,000 | 17.7 | 114 | 6.46 | 6.20 | 6.23 | 4.18 | 5.96 | 5.96 | |
| toto_2.0_2.5b base | Time (s) | GPU (GiB) | |||||||
| 1 | 0.133 | 9.47 | |||||||
| 10 | 0.133 | 9.50 | |||||||
| 100 | 0.319 | 9.79 | |||||||
| 500 | 1.44 | 10.28 | |||||||
| 1,000 | 2.86 | 10.29 | |||||||
| 2,000 | 5.70 | 10.30 | |||||||
| 10,000 | 28.5 | 10.30 |
Table 8. Detailed inference latency and memory across forecast volumes. Measurements use one H100 GPU and one CPU core with throughput-oriented batching. CHRONOS-2 and TIREX-2 use BGAA in xhigh mode. Cold includes the full historical backtest (22,272 forward passes); warm reuses previously selected views. Multipliers are relative to each model’s frozen base; Passes gives the corresponding forward-pass count ratio. GPU denotes peak allocated memory in GiB, including weights. Batching substantially reduces verification overhead, which can be amortized across repeated forecasts.
We additionally evaluate longer horizons (–720) across five ETT/Weather datasets (Table 21). BGAA improves both normalized MSE and MAE on 18/20 dataset–horizon settings for CHRONOS-2 and 15/20 for Toto-2-313M, with gains persisting at , although they are not monotonic with horizon.
Table 21: BGAA generalizes to longer forecasting horizons. Normalized MSE and MAE for CHRONOS-2 and TOTO-2-313M on ETTh1, ETTh2, ETTm1, ETTm2, and Weather, with context length 2048 and horizons . denotes relative change versus the frozen base (negative is better; computed from displayed scores). Bold marks the better result within each comparison. BGAA improves both metrics on 18/20 and 15/20 dataset–horizon settings for CHRONOS-2 and TOTO-2-313M, respectively, with gains persisting at .
| Model | Normalized MSE Base | Normalized MSE BGAA | Normalized MSE | Normalized MAE Base | Normalized MAE BGAA | Normalized MAE | |
| CHRONOS-2 | 96 | 0.2405 | 0.2362 | −1.79 | 0.2723 | 0.2707 | −0.59 |
| CHRONOS-2 | 192 | 0.2920 | 0.2870 | −1.71 | 0.3105 | 0.3083 | −0.71 |
| CHRONOS-2 | 336 | 0.3328 | 0.3232 | −2.88 | 0.3402 | 0.3371 | −0.91 |
| CHRONOS-2 | 720 | 0.3901 | 0.3863 | −0.97 | 0.3827 | 0.3815 | −0.31 |
| TOTO-2-313M | 96 | 0.2386 | 0.2392 | +0.25 | 0.2673 | 0.2677 | +0.15 |
| TOTO-2-313M | 192 | 0.2867 | 0.2852 | −0.52 | 0.3055 | 0.3049 | −0.20 |
| TOTO-2-313M | 336 | 0.3241 | 0.3139 | −3.15 | 0.3354 | 0.3333 | −0.63 |
| TOTO-2-313M | 720 | 0.3830 | 0.3806 | −0.63 | 0.3793 | 0.3786 | −0.18 |
Table 21.
Matched controls isolate the role of gating and structured views. Averaging the full candidate pool without gating worsens MASE by 4.97%, whereas BGAA improves it by 0.95% on the same pool (Figure 4a). On BOOM, a lighter gate is active when fewer than backtest windows are available; median improvement is therefore up to 0.3% for 2929 such tasks, rises to 0.44% around , and increases further for larger buckets (Figure 4c).
Figure 4. (a) Ungated versus gated aggregation. (b) CDF of per-config MASE changes. (c) Gain as a function of backtest windows and horizon . The gate drives the gains and benefits from sufficient backtest evidence. (a) Ungated aggregation over the full candidate pool compared with the gated policy. (b) CDFs of per-config MASE changes for the policies in Table 3. (c) MASE improvement as a function of the number of available backtest windows and forecast horizon . When , a lighter gate is applied, since this accounts for a third of the benchmark tasks.
Compute-matched controls show that extra inference alone is insufficient. With and the pool and aggregation fixed, random selection worsens MASE by 4.82% and CRPS by 10.73%, while averaging jittered copies worsens MASE by 0.03% (Table 11). Restricted-family ablations further show that lookback-only and offset-only pools recover just 30% and 1% of the full-pool MASE gain, while cleaning-only views worsen MASE by 0.53% (Table 10). More importantly, a 22-view pool curated on CHRONOS-2/GIFT-Eval retains only 69% of the full-pool gain when transferred to other models and benchmarks, with a significant disadvantage (Table 14). These results support using a diverse, shared candidate pool rather than tuning a restricted pool for individual models or benchmarks. The verifier also remains useful with older evidence: backtests lagged by still improve MASE by 0.41%, compared with 1.60% at lag zero (Table 12). Further pool and aggregation ablations are reported in Table 9.
| pool tier | MASE | CRPS | policy | MASE | CRPS |
| base (no TTC) | 0.7043 | 0.4830 | margin (conservative) | 0.7019 | 0.4823 |
| crop core | 0.7005 | 0.4811 | top-2 Vincent | 0.6990 | 0.4792 |
| + micro views | 0.7007 | 0.4809 | top-3 Vincent | 0.6978 | 0.4780 |
| + 9 ideas families | 0.7000 | 0.4809 | CDF mixture top-3 | 0.6975 | 0.4778 |
| + mixture aggregation | 0.7001 | 0.4805 | spread-routed mixture | 0.6996 | 0.4796 |
| + decomposition family | 0.6975 | 0.4778 | tempvinc-mase | 0.6991 | 0.4798 |
| pool tier | MASE | CRPS | policy | MASE | CRPS |
| base (no TTC) | 0.7032 | 0.4838 | margin (conservative) | 0.7010 | 0.4822 |
| crop core | 0.7024 | 0.4827 | top-2 Vincent | 0.6998 | 0.4816 |
| + micro views | 0.7021 | 0.4821 | top-3 Vincent | 0.6993 | 0.4810 |
| + 9 ideas families | 0.7005 | 0.4820 | CDF mixture top-3 | 0.6984 | 0.4806 |
| + mixture aggregation | 0.6992 | 0.4814 | spread-routed mixture | 0.6990 | 0.4806 |
| + decomposition family | 0.6984 | 0.4806 | tempvinc-mase | 0.6997 | 0.4815 |
Table 9. Pool and aggregation ablations separate the sources of improvement. Left: nested pool ablations for CHRONOS-2 (top) and TOTO-2-313M (bottom) on GIFT-Eval, using CDF mixture top-3 unless otherwise noted. Right: aggregation ablations using the deployed pool on GIFT-Eval. Expanding the candidate pool generally improves MASE, while the aggregation rule determines the trade-off between MASE and CRPS. For CHRONOS-2, switching to the mixture is approximately MASE-neutral. The decomposition family provides the final MASE gain of the deployed configuration over the preceding pool.
| pool | MASE% | w/l | share | % | w/l | ||
| full pool | −1.60 | 9/5 | 0.011 | 100% | — | — | — |
| lookback-only | −0.48 | 8/2 | 0.037 | 30% | −1.13 | 7/6 | 0.065 |
| offset-only | −0.02 | 3/4 | 0.100 | 1% | −1.58 | 10/4 | 0.001 |
| cleaning-only | +0.53 | 3/5 | 0.484 | −33% | −2.12 | 10/4 | 0.030 |
Table 10. Restricted-pool controls (CHRONOS-2, gated top-2 Vincent, subset scope). “share” denotes the fraction of the full-pool gain recovered by each restricted pool. The right block reports paired full-vs.-control comparisons on the same configs. We use these paired tests for the main comparison, since a restricted pool can recover part of the aggregate gain while still underperforming the full pool on the same examples.
| arm | vs base (MASE) | vs base (CRPS) | BGAA vs arm (MASE) | ||||||
| w/l | w/l | w/l | |||||||
| BGAA top-2 | −0.76 | 63/29 | < 0.001 | −0.79 | 64/29 | 0.02 | — | — | — |
| random- | +4.82 | 35/60 | +10.73 | 31/63 | −5.58 | 77/20 | |||
| noise- | +0.03 | 47/50 | 0.079 | −0.05 | 45/52 | 0.86 | −0.80 | 65/32 |
Table 11. Compute-matched controls (CHRONOS-2, GIFT-Eval, , ). The left block compares each control with the frozen base. The right block reports the paired comparison between BGAA and that control on the same configs. We use the latter as the main test, since a control may improve over the base while still underperforming the gated selection rule. All significance tests use paired Wilcoxon tests across configs.
| lag () | MASE% | CRPS% | (MASE) | Jaccard vs lag 0 |
| 0 | −1.60 | −1.54 | 0.011 | 1.00 |
| 1 | −1.23 | −1.45 | 0.043 | 0.59 |
| 2 | −1.71 | −1.07 | 0.015 | 0.48 |
| 4 | −0.41 | −0.86 | 0.050 | 0.44 |
Table 12. Temporal robustness of the final selection policy (CHRONOS-2, CDF mixture top-3, subset scope, ). We progressively restrict the backtest to older windows. Jaccard reports the overlap between the admitted view set at each lag and the set selected at lag 0.
Table 14: Accuracy–compute trade-off and transferability of restricted candidate pools. Pools selected using Chronos-2/GIFT-Eval backtests are applied unchanged to other models and benchmarks. (a) MASE and WQL changes versus the frozen base (%; lower is better), with retained MASE gain and paired gap to the full pool (95% bootstrap CI). (b) Alternative pool-selection strategies across 90 model–configuration pairs, including regression risk and relative forward-pass cost. Smaller pools reduce compute but significantly lose accuracy relative to the full pool, particularly when transferred across models and benchmarks.
(a) Chronos-2/GIFT-Eval pool transferred across models and benchmarks
| Model / benchmark | Full pool (51) | Restricted pool (22) | Retained gain, top- (%) | ||||||
| MASE | WQL | MASE | WQL | Kept (%) | Gap [95% CI] | ||||
| CHRONOS-2, GIFT-Eval* | −4.34 | −3.99 | −4.34 | −3.99 | 100 | 0.00 | 57 | 42 | 43 |
| CHRONOS-2, fev | −7.83 | −5.85 | −4.36 | −4.25 | 56 | +3.70 [0.47, 8.42] | 32 | 25 | 33 |
| Toto-2, GIFT-Eval | −1.93 | −1.77 | −1.24 | −0.92 | 64 | +0.70 [−0.13, 2.15] | 47 | 16 | 5 |
| Toto-2, fev | −2.43 | −2.20 | −2.15 | −1.75 | 88 | +0.29 [−0.04, 0.68] | 74 | 80 | 34 |
| TiREX-2, GIFT-Eval | −1.69 | −1.74 | −1.22 | −1.38 | 72 | +0.48 [0.03, 1.12] | 57 | 65 | 57 |
| TiREX-2, fev | −4.69 | −5.64 | −3.97 | −4.69 | 85 | +0.75 [0.25, 1.33] | 39 | 55 | 50 |
| Transfer (75) | −3.74 | −3.46 | −2.60 | −2.61 | 69 | +1.18 [0.44, 2.20] | 43 | 42 | 37 |
| All (90) | −3.84 | −3.55 | −2.89 | −2.84 | 75 | +0.99 [0.36, 1.84] | 45 | 42 | 38 |
(b) Alternative restricted-pool selection strategies
| Pool selection | MASE | Kept (%) | Gap MASE [95% CI] | Gap WQL [95% CI] | Worst | Cost | ||
| Full pool | 51 | −3.84 | 100 | — | — | +1.38 | 0 | 1.00 |
| CHRONOS-2/GIFT-Eval | 22 | −2.89 | 75 | +0.99 [0.36, 1.84] | +0.73 [0.30, 1.23] | +2.80 | 0 | 0.60 |
| 20 | −2.83 | 74 | +1.05 [0.32, 2.09] | +0.79 [0.33, 1.32] | +2.80 | 0 | 0.57 | |
| 10 | −1.75 | 45 | +2.15 [0.92, 3.73] | +2.00 [0.93, 3.28] | +6.17 | 2 | 0.43 | |
| Same-pair LOO | 20 | −3.09 | 80 | +0.78 [0.25, 1.45] | +0.58 [−0.02, 1.23] | +4.10 | 2 | 0.53 |
| 10 | −2.11 | 55 | +1.78 [0.75, 3.00] | +1.17 [0.09, 2.39] | +25.10 | 3 | 0.34 | |
| Other-pairs LOO | 20 | −3.03 | 79 | +0.84 [0.28, 1.51] | +0.73 [0.05, 1.59] | +5.93 | 3 | 0.58 |
| 10 | −1.83 | 48 | +2.07 [0.72, 3.81] | +2.21 [0.94, 3.72] | +6.11 | 8 | 0.39 | |
| Random‡ | 20 | −2.40 | 62 | +1.49 [0.67, 2.35] | +1.29 [0.75, 2.18] | +4.39 | 1.2 | 0.47 |
| 10 | −1.61 | 42 | +2.30 [1.43, 3.11] | +2.07 [1.21, 2.92] | +4.50 | 1.5 | 0.27 |
Table 14.
Historical selection also compares favorably with stronger forecast-combination baselines. On a targeted 30-configuration subset, BGAA achieves the largest aggregate MASE and WQL improvements and substantially fewer
severe regressions than historical top-1 selection and cross-validated convex combinations (Table 13). Although its mean advantage over L2-regularized combinations is not statistically significant, BGAA requires far fewer candidate forecasts at application time.
| BGAA | Top-1 | Base + top-1 | L2-convex | L2-anchored | ||||||
| MASE | WQL | MASE | WQL | MASE | WQL | MASE | WQL | MASE | WQL | |
| CHRONOS-2, GIFT-Eval | −4.34 | −3.99 | −0.96 | +0.46 | −2.10 | −1.56 | −3.27 | −2.66 | −2.96 | −2.75 |
| CHRONOS-2, fev | −7.83 | −5.85 | −4.34 | −0.71 | −6.71 | −4.09 | −3.65 | −1.87 | −4.05 | −1.86 |
| Toto-2, GIFT-Eval | −1.93 | −1.77 | +0.22 | +1.53 | −1.14 | −0.53 | −2.39 | −2.29 | −2.59 | −2.03 |
| Toto-2, fev | −2.43 | −2.20 | −1.65 | −0.92 | −2.26 | −1.95 | −3.95 | −1.63 | −3.24 | −1.19 |
| TiREX-2, GIFT-Eval | −1.69 | −1.74 | −1.42 | −0.40 | −0.91 | −0.68 | −2.49 | −2.91 | −2.96 | −2.86 |
| TiREX-2, fev | −4.69 | −5.64 | −2.55 | −2.86 | −2.82 | −2.97 | −2.05 | −3.36 | −2.25 | −3.30 |
| All (90) | −3.84 | −3.55 | −1.79 | −0.49 | −2.68 | −1.97 | −2.97 | −2.45 | −3.01 | −2.33 |
| Gap to BGAA | — | +2.11 | +1.20 | +0.91 | +0.86 | |||||
| 95% CI | [0.45, 4.04] | [0.22, 2.35] | [−0.48, 2.61] | [−0.57, 2.59] | ||||||
| Worst config | +1.38 | +27.39 | +6.54 | +12.30 | +12.30 | |||||
| Configs > 3% worse | 0 | 6 | 3 | 8 | 5 | |||||
| Candidates used | 2.8 | 1.0 | 1.0 | 13.2 | 6.3 |
Table 13. BGAA versus alternative forecast combiners under matched historical evidence. All methods use identical candidate forecasts and backtest windows on 30 configurations (15 GIFT-Eval, 15 fev-bench) across three TSFMs. Top: MASE and WQL changes versus the frozen base (%; lower is better; best per row in bold). Bottom: Aggregate MASE gap to BGAA (95% bootstrap CI), worst regression, configurations degrading by more than 3%, and mean additional forecasts used. BGAA achieves the best aggregate accuracy and robustness while using fewer forecasts than the regularized alternatives.
Most configurations do not regress. Table 3 shows that 61%, 69%, and 70% of configurations on GIFT-Eval, BOOM, and fev-bench, respectively, are equal to or better than their frozen base under the deployed policy, and 95%, 92%, and 94% of configurations show no statistically significant regressions. The worst regressions are 8% on GIFT-Eval and 7% on fev-bench. On BOOM, the larger negative tail is driven by a small number of near-constant series for which the scaled metric is unstable. These are empirical observations, not consequences of the backtest guarantee, which does not extend to unseen forecast horizons or benchmark-level metrics (§ 3).
Interpretation and supporting evidence
The results above establish that BGAA improves frozen forecasters, but do not explain why re-presenting the same observed history can produce useful alternatives. We therefore ask: what kind of model behavior would make structured views useful rather than merely different? The argument below is not required by BGAA and is not an accuracy theorem. Instead, a restricted transport result provides a concrete interpretation that yields empirical predictions we test across the four models.
A deterministic view adds no observations. Nevertheless, a frozen forecaster can return a different predictive distribution when the same history is presented in another representation. Let be an idealized distribution over complete trajectories and let denote the conditional future -quantiles under trajectory distribution , and write for the column of the frozen forecast at level .
Assumption 1 (PFN idealization). For an observed context , the frozen model returns the conditional quantiles under : .
Now let be a fixed strictly increasing bijection applied pointwise, and let be the trajectory distribution obtained by applying pointwise to trajectories drawn from . Let denote its marginal over contexts.
Proposition 1 (Transport identity). Under Assumption 1, for -almost every context and .
For this restricted class of transformations, forecasting a transformed history and mapping its quantiles back is equivalent to prediction under a transported trajectory distribution. This does not imply greater accuracy, nor do we claim that released TSFMs satisfy Assumption 1 exactly. None of our non-identity deployed views satisfies all of the proposition’s conditions: Rank-to-Gaussian is context-fitted and clamped, crops and offsets alter the observations presented to the model, and differencing is not pointwise and uses an approximate quantile-path reconstruction. The full statement, proof, and scope are in Section A.3. Proposition 1 instead provides a tractable case where re-presenting the same observations changes the effective predictive distribution without adding information, motivating us to ask whether BGAA’s broader views induce similarly structured changes.
This yields a testable hypothesis: if structured views systematically change a frozen model’s forecasting behavior rather than acting as arbitrary ensemble noise, then which views help should depend on the model, individual views should induce repeatable changes in representation space, and these changes should produce recognizable forecast-level signatures. We test these predictions below; full protocols and results are in Section E.
Useful view families depend on both the model and the data. Across the six model pairs, Kendall’s between per-family solo-gated benefit vectors ranges from 0.01 to 0.35, indicating weak agreement on which transformations are beneficial (Table 26). For example, differencing is strongest for CHRONOS-2 (−0.85% MASE) but slightly hurts TiREX-2 (+0.01%), while lookback is most effective for PATCHTST-FM-R1 and TOTO-2-313M (Table 25). Transformation preferences also vary across domains (Figure 10a) and with series characteristics such as seasonality, trend strength, autocorrelation, and volatility (Table 27). However, these statistical relationships do not provide a reliable alternative to historical verification: feature-based routers trained leave-one-configuration-out fail to outperform historical top-1 selection at matched application cost (Table 28). Furthermore, a pool curated on CHRONOS-2/GIFT-Eval excludes 30–41% of the views selected in other model–benchmark pairs (Table 15). Together, these results motivate using a diverse, shared candidate pool with historical verification rather than relying on model-specific pool tuning or statistical characteristics alone.
Table 15: Model- and benchmark-dependent view selection. Views selected by full-pool BGAA in at least 3 of 15 configurations, with selection frequencies in parentheses. Distinct counts views selected at least once; Outside is the fraction of selections absent from the 22-view Chronos-2/GIFT-Eval pool. † denotes an excluded view and the seasonal period. Across transfer settings, 30–41% of selected views lie outside the source-model pool.
| Model / benchmark | Selected views (frequency) | Distinct | Outside |
| CHRONOS-2, GIFT-Eval* | (7), (6), rankgauss (5), multiseason (4) | 22 | 0% |
| CHRONOS-2, fev | (5), (5), diff1† (4), lookback† (3), rankgauss (3), multiseason (3) | 24 | 30% |
| Toto-2, GIFT-Eval | recursive (5), (3) | 27 | 34% |
| Toto-2, fev | winsor (4), recursive (4), multiseason (3), diff1† (3), rankgauss (3), (3) | 22 | 41% |
| TiREX-2, GIFT-Eval | supportfloor† (3), nonneg† (3), (3) | 27 | 40% |
| TiREX-2, fev | rankgauss (5), recursive† (4), (4), winsor (3), (3), multiseason (3) | 25 | 36% |
Table 15.
Table 25. Solo-gated family benefit in (15 config GIFT-Eval test subset; more negative is better; 0 indicates that the family was never admitted). Each column gives the family-level fingerprint for one model; pairwise agreement between these fingerprints is reported in Table 26. Bold marks the best-performing family for each model. The preferred family differs across models, and TIREX-2 has the flattest profile: its best family yields about a quarter of the gain of TOTO-2-313M’s best family. Notably, diff is the strongest family for CHRONOS-2 but slightly hurts TIREX-2.
Table 26. Cross-model agreement between family fingerprints. We report Kendall’s between the fingerprints in Table 25, with permutation -values. Agreement is well below 1 for every model pair, indicating that useful families are not ranked consistently across models. The two pairs involving TIREX-2 and a model whose profile is dominated by lookback or diff are not significantly different from zero agreement. This is consistent with a model-specific ranking of view families, with some shared signal from families that are broadly useful.
| Characteristic | Tercile | CHRONOS-2 | TOTO-2-313M | TiREX-2 |
| Seasonality | Low | diff −6.4 [−12.2, −0.9] BGAA −6.9 | winsor† −3.2 [−13.7, +4.4] BGAA −1.7 | offset† −0.4 [−1.7, +0.5] BGAA −2.4 |
| High | decomp −4.3 [−7.6, −1.7] BGAA −5.6 | decomp −1.5 [−3.2, +0.1] BGAA −1.2 | multideseason −2.0 [−4.4, +0.6] BGAA −3.4 | |
| Trend strength | Low | decomp −2.6 [−5.4, −0.6] BGAA −4.1 | decomp −1.2 [−2.1, −0.2] BGAA −0.9 | multideseason −1.4 [−3.2, +0.4] BGAA −2.0 |
| High | decomp −2.9 [−6.0, −0.5] BGAA −8.1 | winsor† −2.5 [−11.0, +3.7] BGAA −2.1 | multideseason† −0.9 [−3.7, +0.8] BGAA −4.1 | |
| Lag-1 autocorr. | Low | decomp −2.0 [−3.9, −0.3] BGAA −2.0 | winsor† −1.8 [−5.5, +0.3] BGAA −1.3 | multideseason −0.7 [−1.8, +0.2] BGAA −1.7 |
| High | diff −5.7 [−10.9, −0.8] BGAA −7.7 | decomp −1.2 [−3.2, +0.6] BGAA −1.7 | multideseason† −2.6 [−6.3, +0.5] BGAA −5.8 | |
| Volatility | Low | diff −5.4 [−10.9, −0.3] BGAA −7.6 | winsor† −1.9 [−11.9, +5.1] BGAA −1.5 | offset† −0.3 [−1.5, +0.4] BGAA −2.6 |
| High | decomp −3.0 [−5.1, −1.2] BGAA −4.0 | decomp −1.8 [−3.9, −0.1] BGAA −2.7 | winsor −0.4 [−1.0, −0.0] BGAA −1.7 |
Table 27. View-family preferences across time-series characteristics. For the lowest and highest terciles of four statistical characteristics, we report the hindsight-best family and its MASE change versus base (%, 95% bootstrap CI). The second line in each cell gives the corresponding BGAA improvement on the same windows. Results cover 30 configurations (15 GIFT-Eval, 15 fev-bench) across three TSFMs. Negative changes indicate improvement; † marks effects not replicated on both benchmarks. Preferred transformations vary across models and series characteristics, motivating adaptive view selection.
| Selection method | CHRONOS-2 | TOTO-2-313M | TiREX-2 |
| Historical top-1 + identity | −4.4 | −1.7 | −1.9 |
| −2.8 | +2.0 | +1.3 | |
| Global view router | +1.7 [0.3, 3.3] | +3.7 [1.5, 6.4] | +3.2 [1.4, 5.5] |
| Four-characteristic router | −1.5 | −0.7 | +2.8 |
| +3.0 [0.0, 7.8] | +1.1 [−0.7, 2.7] | +4.6 [1.6, 9.0] | |
| Best of 12 routers (post hoc) | −4.3 | −1.6 | +2.8 |
| +0.2 [−1.1, 1.2] | +0.1 [−2.6, 2.1] | +1.3 [−0.8, 3.7] | |
| BGAA (; reference) | −6.1 | −2.2 | −3.2 |
Table 28. Historical verification versus statistical-feature routing. MASE change versus the frozen base (%; lower is better) over 30 configurations (15 GIFT-Eval, 15 fev-bench). Routers are trained leave-one-configuration-out. For each router, the second line gives its paired MASE log-ratio gap to historical top-1 selection (95% configuration-bootstrap CI; positive favors the gate). The best-of-12 row is selected post hoc and is not a deployable model-selection procedure. BGAA with is shown as a reference with a larger application budget. No tested router consistently outperforms historical verification at matched application cost.
Figure 10. Summary of the mechanism analyses in § 6. (a) Admitted families vary across domains. (b) Individual views induce consistent displacement directions. (c) These displacements can align with different modes of each model’s rollout distribution. Figure 9 visualizes the same effect in a rollout-based proxy for each model’s learned forecasting behavior.
Views induce systematic, model-specific changes. Across 626 GIFT-Eval contexts, we compare view-induced displacements with rollout samples from each model, used as a proxy for its learned forecasting behavior. Some views move contexts consistently: diff and smooth have directional consistency of 0.75–0.78, versus 0.04–0.07 for crops and offsets (Table 30). Different views are also non-redundant, with mean absolute pairwise displacement cosine of 0.36–0.48 (Table 31). Finally, diff aligns with a mode of each model’s rollout distribution (cosine +0.92 to +0.97), but with different modes across models (Table 32 and Figure 9). These patterns indicate repeatable, model-specific effects rather than arbitrary perturbations.
| view | CHRONOS-2 magnitude | CHRONOS-2 consistency | CHRONOS-2 95% CI | TIREX-2 magnitude | TIREX-2 consistency | TIREX-2 95% CI |
diff | 6.61 | 0.773 | [0.761, 0.785] | 13.29 | 0.781 | [0.768, 0.793] |
smooth_ma7 | 2.86 | 0.768 | [0.753, 0.781] | 7.27 | 0.752 | [0.734, 0.770] |
jitter_0.002 | 1.21 | 0.504 | [0.457, 0.548] | 4.43 | 0.456 | [0.413, 0.499] |
sdiff | 2.19 | 0.417 | [0.391, 0.442] | 5.43 | 0.490 | [0.463, 0.517] |
rankgauss | 1.23 | 0.341 | [0.310, 0.371] | 2.22 | 0.348 | [0.319, 0.376] |
winsor_0.05 | 0.54 | 0.337 | [0.312, 0.362] | 0.93 | 0.388 | [0.364, 0.411] |
deseason | 1.07 | 0.269 | [0.238, 0.299] | 2.47 | 0.293 | [0.256, 0.326] |
lookback_0.5 | 0.35 | 0.067 | [0.050, 0.084] | 0.73 | 0.065 | [0.049, 0.082] |
offset_8 | 0.04 | 0.045 | [0.032, 0.058] | 0.05 | 0.040 | [0.029, 0.052] |
seasontile | 0.07 | 0.045 | [0.031, 0.059] | 0.13 | 0.048 | [0.035, 0.063] |
Table 30. Directionality in feature space: does a view induce a consistent displacement across contexts? magnitude is , consistency is with a 95% bootstrap CI. Read the two columns together; see the caveat below.

Figure 9. Views move the same contexts toward different regions of each model’s rollout distribution. We use ancestral rollouts from each model’s quantile head as a proxy for its learned forecasting behavior and visualize the resulting 20-dimensional shape-feature space with joint t-SNE. Colored points are rollout samples, grouped by -means mode; black points are real GIFT-Eval contexts; arrows show the mean displacement induced by each view. We use the same contexts and views for both models, but diff moves toward different rollout modes: for CHRONOS-2, a low-iqr_over_std, high-step_max mode with mass 0.07; for TIREX-2, a high-kurtosis, high-skew mode with mass 0.02. This provides the geometric counterpart to the fingerprint result. t-SNE preserves local neighborhoods, but distances should not be interpreted metrically.
| model | feature space mean | feature space |off-diag| | feature space max | embedding space mean | embedding space |off-diag| | embedding space max |
| TIREX-2 | 0.42 | 0.90 | 0.54 | 0.85 | ||
| CHRONOS-2 | 0.36 | 0.81 | 0.55 | 0.97 | ||
| PATCHTST-FM-R1 | 0.48 | 0.96 | 0.44 | 0.97 | ||
| TOTO-2-313M | 0.40 | 0.84 | 0.33 | 1.00 |
Table 31. Non-redundancy of view displacements. We compute the cosine similarity between the mean displacement directions induced by different views. Values near 0 indicate that two views move contexts in different directions, while values near ±1 indicate similar or opposing directions. For each model and representation space, we report the mean and maximum absolute off-diagonal cosine. For CHRONOS-2 in feature space, the maximum is the diff–sdiff pair (0.81).
| model | top mode for diff | cosine | mass |
| TIREX-2 | high kurtosis / high skew | +0.97 | 0.02 |
| CHRONOS-2 | low iqr_over_std / high step_max | +0.97 | 0.07 |
| PATCHTST-FM-R1 | high tail_frac_2sig / high seasonal_peak_freq | +0.96 | 0.05 |
| TOTO-2-313M | low iqr_over_std / low mad_over_std | +0.92 | 0.08 |
Table 32. Destination of the diff displacement. For each model, we report the rollout mode most aligned with the mean diff displacement, together with the cosine between that displacement and the direction from the real-context centroid to the mode centroid. The alignment is strong for all four models, but the target mode differs across models, as also shown in Figure 9. Mode names are based on the cluster’s most distinctive features, and “mass” denotes the fraction of rollout samples assigned to that mode.
The structure persists in forecast space. The final prediction is that a view’s effect should remain recognizable in the forecast itself. On a 15-configuration subset, diff widens predictive intervals by a log-ratio of +2.10 to +2.25, with the same sign on 14–15 of 15 configurations (Table 33). This is a property of the complete forecasting view, including its cumulative-sum pull-back, rather than only of the transformed input. The broader signature analysis in Section E.4 shows the same family-level structure across the other forecast statistics and models.
| family | CHRONOS-2 width | CHRONOS-2 sign | CHRONOS-2 shift | CHRONOS-2 cov | TIREX-2 width | TIREX-2 sign | TIREX-2 shift | TIREX-2 cov |
| diff | +2.249 | 0.93 | 0.555 | +0.185 | +2.103 | 1.00 | 0.516 | +0.144 |
| sdiff | +0.398 | 0.87 | 0.578 | +0.034 | +0.375 | 0.93 | 0.507 | +0.015 |
| recursive | −0.461 | 0.93 | 0.068 | −0.178 | −0.548 | 1.00 | 0.050 | −0.202 |
| fft | −1.328 | 0.93 | 0.868 | −0.676 | −1.541 | 0.93 | 0.753 | −0.714 |
| rankgauss | +0.004 | 0.60 | 0.144 | −0.029 | −0.002 | 0.53 | 0.125 | −0.008 |
| jitter | 0.000 | 0.80 | 0.004 | +0.001 | 0.000 | 0.80 | 0.004 | 0.000 |
| lookback | 0.000 | — | 0.036 | +0.003 | −0.002 | 0.60 | 0.045 | 0.000 |
| offset | 0.000 | — | 0.002 | 0.000 | 0.000 | — | 0.000 | 0.000 |
Table 33. Forecast signatures by view family for CHRONOS-2 and TIREX-2 (15 configs each). width is the log-ratio of predictive interval width relative to the base, sign is the fraction of configs with the reported sign, shift is the scale-normalized median shift, and cov is the change in coverage. Families that materially change the forecast distribution do so consistently, while the remaining families have much smaller effects.
Taken together, this evidence forms a consistent chain: useful views differ by model, individual views move contexts in repeatable and distinct directions, and those changes remain visible in the resulting predictive distributions. This evidence strengthens the interpretation that structured views expose different behaviors of the same frozen TSFM rather than merely being generic ensembling. It does not establish causal prior transport: the rollout distributions are proxies for learned forecasting behavior, and we do not intervene on the models’ pretraining distributions.
Limitations and future directions
This section focuses on the main limitation revealed by our diagnostics: historical backtesting supports reliable config-level selection, but provides much weaker guidance for individual forecast windows. We also discuss what this means for future test-time compute methods.
The backtest guarantee in Section A.1 is deliberately limited: it controls loss on historical gate windows, not on future forecasts. The key question is therefore whether historical rankings remain informative at deployment. At the configuration level, on CHRONOS-2/GIFT-Eval, the median Spearman correlation between backtest and realized view rankings is 0.63 per configuration, but only 0.25 per forecast window (Figure 5). Configuration-level selection also benefits from pooling historical evidence across series. On 41 GIFT-Eval configurations, pooled selection outperforms independent per-series selection on average across all three tested models, particularly when individual series have limited backtest evidence (Table 24). Together, these findings support pooling historical evidence for more reliable configuration-level verification, while highlighting the harder problem of identifying which view will help on a particular future window using only its observed context.
Figure 5. Backtest rankings are strong per configuration but much weaker per forecast window. For CHRONOS-2 on 93 GIFT-Eval configurations, median Spearman between leak-free backtest and realized view rankings falls from 0.63 per configuration to 0.25 per window. Results use 8,313 sampled windows and MASE.
| Model | Series/config | Configs | Series | Backtests/series | Per-config MASE | Per-series MASE | Gap [95% CI] |
| CHRONOS-2 | Low (2–7) | 17 | 114 | 47 | −0.26 | +0.69 | +0.94 [−1.27, 4.41] |
| Medium (21) | 7 | 147 | 18 | −0.88 | −1.01 | −0.13 [−1.17, 1.09] | |
| High (30–42) | 6 | 204 | 12 | −0.48 | −0.69 | −0.21 [−0.95, 0.39] | |
| Very high (118–156) | 11 | 1,507 | 3 | −2.15 | −0.67 | +1.50 [0.50, 2.70] | |
| All (41) | 41 | 1,972 | 3–47 | −0.91 | −0.17 | +0.74 [−0.32, 2.34] | |
| TiREX-2 | Low (2–7) | 17 | 114 | 47 | −0.47 | +0.07 | +0.54 [−0.22, 1.56] |
| Medium (21) | 7 | 147 | 18 | −0.05 | −0.28 | −0.23 [−0.78, 0.31] | |
| High (30–42) | 6 | 204 | 12 | −0.05 | +0.53 | +0.58 [−0.55, 2.05] | |
| Very high (118–156) | 11 | 1,507 | 3 | −1.62 | −1.15 | +0.48 [0.08, 0.88] | |
| All (41) | 41 | 1,972 | 3–47 | −0.65 | −0.25 | +0.40 [−0.01, 0.89] | |
| TOTO-2-313M | Low (2–7) | 17 | 114 | 6 | −0.69 | +0.84 | +1.52 [0.31, 3.05] |
| Medium (21) | 7 | 147 | 6 | −0.56 | −0.76 | −0.20 [−0.82, 0.44] | |
| High (30–42) | 6 | 204 | 3 | −0.14 | +0.04 | +0.18 [−0.82, 0.90] | |
| Very high (118–156) | 11 | 1,507 | 1 | −0.98 | +0.01 | +0.99 [−0.05, 2.29] | |
| All (41) | 41 | 1,972 | 1–6 | −0.66 | +0.22 | +0.89 [0.23, 1.67] |
Table 24. Configuration-pooled versus per-series historical view selection. Results on 41 GIFT-Eval configurations (1,972 series) across three TSFMs, grouped by the number of series per configuration. MASE changes are relative to the frozen base (%; lower is better). Gap is the paired per-series minus per-config MASE log-ratio difference (95% configuration-bootstrap CI); positive values favor per-config selection. Backtests/series reports the historical evidence available to individual selectors. Per-config selection performs better on average across all three models, with the largest reliable gains when per-series evidence is sparse.
Hindsight selection confirms that the best-performing view can vary substantially across windows. The backtest’s top-1 contains the realized best view for 19% of configurations but only about 11% of individual windows, and its per-window top-1 recovers only about 27% of the hindsight-available MASE gain (Figure 6). Cross-fitted analyses likewise indicate that better fixed per-configuration choices remain possible (Table 22). These quantities are diagnostic rather than deployable targets: hindsight uses the realized future, and the cross-fitted splits remain temporally dependent (Section D.3). They therefore show where the current verifier loses information, not how much improvement a future context-only selector could necessarily recover.
| model | all 97 configs realized (Table 1) % | 53 configs long enough to cross-fit realized % | label-ranked gate % | realized / label-ranked ratio | best-view gain (x-fit) % | per-window hindsight % |
| CHRONOS-2 | 1.07 | 1.32 | 2.06 | 0.64 | 4.10 | 19.4 |
| TIREX-2 | 0.32 | 0.50 | 1.21 | 0.41 | 1.48 | 16.6 |
| PATCHTST-FM-R1 | 0.19 | 0.41 | 1.20 | 0.34 | 1.42 | 17.5 |
| TOTO-2-313M | 0.66 | 0.61 | 1.16 | 0.52 | 1.37 | 16.6 |
Table 22. Verification headroom is much larger at the forecast-window level. CRPS improvement over the frozen base in %. The first “realized” column uses all 97 configs; the others use the 53 configs that can be cross-fit. The label-ranked gate keeps the deployed policy fixed but ranks views with held-out labels. The reported realized/label-ranked ratio is the realized improvement divided by the label-ranked improvement. The best-view gain (x-fit) selects one view per config on one half of its windows and evaluates it on the other. The per-window hindsight selection selects the best view per window using its realized labels. These label-based quantities are diagnostics, not deployable verifier targets.
Figure 6. Agreement between backtest and hindsight view rankings for CHRONOS-2 on GIFT-Eval. (a) Fraction of configs whose realized best view lies in the backtest’s top-. Ranked per config, the backtest’s top-1 contains the best view for 19–20% of configs and its top-3 for 31–33%, well above both the most-selected-view heuristic (10% at ) and random selection (1.3% at ). The top-1 hit rate is therefore about 15× chance. Ranked per window, the top-1 hit rate falls to about 11%. (b) Share of the hindsight MASE gain recovered by the top-: the per-config top-1 recovers 32–33%, while the per-window top-1 recovers about 27%. Because the per-window target depends on the realized outcome, we use it only as a diagnostic rather than as an achievable target for a verifier that observes only .
Our evaluation is also limited to univariate forecasting, and BGAA incurs additional inference cost, primarily from evaluating candidate views on historical windows (Table 6). The main open question is whether information available before the forecast can support more accurate window-specific selection without making verification prohibitively expensive. This could require better window-level signals, better candidate views, or both. Other promising directions include: learned verifiers that predict useful views from context and view features; verification-set design that selects informative past windows; and adaptive budgets that spend more compute when views disagree.
Thinking modes provide a controlled test-time compute ladder. All four modes draw from the same fixed augmentation catalogue and use the same BGAA procedure; only the test-time compute budget changes. Lower-compute modes evaluate nested subsets of the catalogue. (a) Budget parameters: denotes the number of forward passes per backtest window, and is the median number of gate windows. Gate and apply costs are reported relative to the base run, with gate% denoting the fraction of total cost spent on gating. (b) Candidate families: entries show the number of degrees included at each mode. The sets are nested. The resulting total cost and performance for each mode are reported in Table 5.
| candidates | gate | aggregate | cost split, CHRONOS-2 | ||||||||
| mode | families | views | top- | gate | apply | gate% | |||||
| low | 7 | 9 | 9 | 1 | 24/24 | 24 | 1 | 2 | 0.05 | 2.07 | 1.7 |
| medium | 11 | 19 | 19 | 6 | 32/48 | 48 | 2 | 2 | 0.37 | 2.15 | 10.4 |
| high | 13 | 31 | 36 | 16 | 64/96 | 64 | 3 | 3 | 1.81 | 3.66 | 28.0 |
| xhigh | 15 | 51 | 58 | 16/128 | 128 | 3 | 3 | 4.14 | 2.87 | 51.7 |
| family | passes/view | low | medium | high | xhigh |
| supportfloor | 0 | 1 | 1 | 1 | 1 |
| nonneg | 0 | 1 | 1 | 1 | 1 |
| rankgauss | 1 | 1 | 1 | 1 | 1 |
| winsor | 1 | 1 | 1 | 1 | 1 |
| multideseason | 1 | 1 | 1 | 1 | 1 |
| recursive | 2–4 | 1 | 1 | 2 | 2 |
| lookback | 1 | 3 | 6 | 10 | 18 |
| diff | 1 | — | 1 | 1 | 1 |
| jitter | — | 1 | 1 | 1 | |
| jitternorm | — | 1 | 1 | 1 | |
| offset | 1 | — | 4 | 7 | 14 |
| sdiff | 1 | — | — | 1 | 1 |
| decomp | 1 | — | — | 3 | 3 |
| fft | 1 | — | — | — | 3 |
| seasontile | 1 | — | — | — | 2 |
| jitter seeds | — | 1 | 2 | 3 |
On yearly configs (period = 1), decomp contributes 1 degree, so high/xhigh present 30/50 views there.
Table 6.
Conclusion
In this paper, we show that test-time compute can improve frozen time series foundation models without retraining or future labels. BGAA generates forecasts from multiple views of the same context and uses a leak-free rolling-origin backtest to select which views to aggregate. With one fixed pool and policy, BGAA improves all 12 model–benchmark combinations, with MASE gains of 0.5–1.0% on GIFT-Eval, 1.7–5.9% on BOOM, and 1.3–5.0% on fev-bench. Mechanism experiments show structured, model-dependent view effects and consistent forecast signatures, supporting our prior-transport interpretation. The main remaining limitation is window-level selection: backtest rankings are strong at the configuration level but much weaker per window, with median Spearman correlation 0.63 versus 0.25 for CHRONOS-2 on GIFT-Eval. This motivates better window-specific selection alongside improved candidate views.
AI Use Statement
We used large language models as coding and writing assistants during the development of BGAA and while writing the paper. The initial base implementation of BGAA was developed primarily by the authors. LLMs were used to scale the implementation, reproduce benchmark pipelines, configure environments, refactor code, and support model-and benchmark-specific integration. LLMs were also used for TIREX-2-specific kernel modifications to improve evaluation efficiency on H100 GPUs. The paper was primarily written by the authors. LLMs were used to review the text, check consistency with the final implementation, and compress the manuscript. The compression was done line-by-line or paragraph-by-paragraph rather than by regenerating the manuscript as a whole. Every resulting line was reviewed by the authors before inclusion, and any incorrect, ambiguous, or overstated language introduced during compression was revised manually. We take full responsibility for the implementation, experiments, analysis, theoretical claims, and final text of the paper.
Theory and proofs
Section A.1 proves the backtest-dominance property used in § 3. Section A.2 gives the aggregation results behind Vincent and CDF-mixture aggregation and states which aggregator each score covers. Section A.3 formalizes the transported-prior interpretation tested in § 6.
The backtest referee
This section gives the formal statement and proof of the gate guarantee summarized in § 3.
Fix a dataset configuration . Let id denote the identity view, which returns the base forecast, and a candidate view. On gate window , let be the loss of view , averaged over the rolling forecast origins in that window. The gate uses absolute error of the median forecast for *-mase policies and the mean pinball loss over for *-crps policies. Windows with are excluded; let be the set of usable windows and their number. Define the mean per-window loss relative to the base as
The relative improvement of candidate is . The margin rule requires , where is the minimum improvement, and a win on at least a fraction of usable windows. Top- keeps the candidates with largest positive . Both rules require at least usable windows.
Let denote the admitted candidate set and the resulting aggregate, with loss . The aggregate assigns weight to the base and nonnegative weights to admitted candidates, with
If , the policy returns the base forecast. The result below depends only on the gate losses and aggregation rule, not on the underlying forecaster.
Theorem 2 (Backtest dominance). Suppose that, on every usable gate window, the aggregate loss satisfies
This holds for Vincent averaging under pinball loss or absolute error of the median forecast. More generally, if is exact CRPS, CDF mixing also satisfies the required inequality. If , let
be the smallest improvement among admitted candidates. Then
Under the margin rule, ; under top-, . If , the aggregate equals the base.
Proof. For a non-empty admitted set, the assumed aggregation inequality holds on each usable gate window. For Vincent averaging, it follows from convexity of pinball loss; absolute error of the median forecast is proportional to the pinball loss. For CDF mixing under exact CRPS, it follows from Theorem 3. Since on every usable window, dividing by and averaging gives:
The empty-set case follows directly from returning the base forecast.
Theorem 2 applies to the gate windows and to the mean per-window relative loss used by the gate. It does not guarantee improvement under the benchmarks’ reported aggregation rules, which generally differ from and can weight configurations or forecast errors differently. It also does not guarantee improvement on the future forecast horizon without assumptions linking the backtest to that horizon. Thus, we measure horizon performance directly in Table 1 and 3. Table 12 probes the backtest-to-horizon link itself: when the gate’s evidence is restricted to observations at least lag before the forecast start (lag ), the horizon MASE gain of the Vincent top-2 policy stays at 0.4–1.7% even though the admitted set changes substantially (Jaccard 0.44–0.59 against lag 0), on a 15-config GIFT-Eval test subset for CHRONOS-2.
Note: The theorem covers the Vincent top3-mase policy. It does not cover the deployed mixtop3-mase, since CDF-mixture quantiles are not convex combinations of member quantiles. Similarly, the *-crps gate uses mean pinball loss over rather than exact CRPS, so CDF mixing under that gate does not inherit the exact-CRPS guarantee. The positive margin , win-fraction threshold , and minimum-window requirement are robustness checks against small or noisy backtests, not finite-sample guarantees on the forecast horizon.
Aggregation
This section gives the full aggregation result summarized in § 3.
Let be the CDFs of forecast distributions, with weights and , where the weights are determined independently of the realized outcome . Multi-horizon scores average the corresponding one-step scores, so the result below applies at each horizon. In our implementation, each is the interpolated CDF constructed from the model’s nine-quantile forecast (Section B). Vincent averaging combines quantiles level by level, while CDF mixing averages the predictive distributions.
Theorem 3 (CRPS decomposition for CDF mixtures). Let
be the mixture CDF, and assume the member forecasts have finite CRPS. Then, for every realized outcome ,
where indexes the forecast value. The diversity term depends only on the forecast distributions, not on .
Proof. For outcome , define
where is the indicator function. Since , the weighted-mean identity gives
Moreover, . Integrating both sides over and using the definition of CRPS gives the result.
Since the diversity term is non-negative, the CRPS of a CDF mixture is no worse than the weighted average CRPS of its members for every outcome, with equality when all positive-weight member CDFs agree almost everywhere. The term can also be computed without labels, giving a label-free measure of forecast disagreement and motivating the spread-routed policy in Section B.
This identity applies to the mixture itself, before we read it back as a nine-quantile forecast for deployment. It is specific to exact CRPS.
The guarantee in Theorem 2 requires the aggregation rule to be convex in the score used by the gate. Vincent averaging satisfies this condition for the absolute-error score used by *-mase and for pinball loss. CDF mixing satisfies it for exact CRPS. Our *-crps policies instead rank views using mean pinball loss over , so their CDF-mixture variants do not inherit the exact-CRPS guarantee.
The deployed mixtop3-mase policy similarly combines a MASE gate with CDF mixing, and thus does not inherit formal backtest dominance on either MASE or CRPS. We use it because it gives the best mean MASE in the policy ablation. The corresponding Vincent policy, top3-mase, uses the same gate and admitted set and is covered by the backtest guarantee in Theorem 2.
Restricted transport interpretation
A trajectory is , with context and future . Let denote an idealized trajectory distribution associated with the frozen model, a context, and the reported quantile levels. We write for the vector of conditional -quantiles of the future given under trajectory distribution , and for the corresponding model forecast, the column of at level .
Assumption 1 (PFN idealization). Given a context , the frozen model returns the conditional future quantiles under :
The PFN interpretation motivates this idealization [20]. Pretrained probabilistic forecasters such as Chronos motivate asking whether an analogous interpretation is useful for TSFMs [2], but we do not assume that it holds exactly. We use it only to motivate a mechanism with observable predictions, which we test in § 6.
Proposition 1 (Transport identity). Let be a fixed strictly increasing bijection applied pointwise, and define its trajectory-level extension
Let be the distribution of for , and let denote its marginal distribution over contexts. Here, and are also applied coordinatewise. Under Assumption 1, for -almost every context and every ,
Thus, forecasting the transformed context and mapping its quantiles back is equivalent to prediction under the transported trajectory distribution .
Proof. Let and define . By the definition of ,
Since applies coordinatewise,
Because Euclidean trajectory space is standard Borel, regular conditional distributions exist. Now fix a context . Since is a bijection, corresponds exactly to . Also,
coordinatewise. Therefore, for -almost every , the conditional distribution of given is obtained by applying coordinatewise to the conditional distribution of given . Because is strictly increasing, conditional quantiles transform coordinatewise:
Finally, Assumption 1 gives
Substituting this into the previous display yields
which is the claimed identity. □
Observation-map views. Lookback crops and patch-phase offsets do not satisfy the transport construction. Instead, they change the information presented to the model without changing the frozen forecaster. The gate treats them like any other candidate, and Theorem 2 does not require a transport interpretation.
Scope of the transport interpretation. Proposition 1 applies only to fixed pointwise strictly increasing bijections. The identity view satisfies these conditions trivially, but none of our non-identity deployed views satisfies them all exactly. Rank-to-Gaussian is the closest case, but it is fitted to the current context and clamps forecasts to the observed range. Lookback and offset views instead change the observation map. The remaining families are structured perturbations motivated by the same picture rather than exact transported trajectory distributions.
Differencing requires one additional caveat. Its pull-back constructs a level- path by cumulatively summing level- increment forecasts. Since the quantile of a sum is not generally the sum of its marginal quantiles, the resulting fan need not correspond to a transported posterior predictive. This can widen intervals with horizon, so part of the diff effect in Table 33 comes from the pull-back itself. This does not affect Theorem 2, which treats each view as a forecast-generating policy.
Selection over transported views. For views satisfying Proposition 1, the backtest can be interpreted as selecting among forecasts induced by different transported trajectory distributions. We use this exact case to motivate the broader structured-view interpretation. The gate ranks views by predictive loss; its weights are not Bayesian model probabilities.
The view catalogue
What makes a legal view. A view must (i) use no information beyond the available context, (ii) return a forecast fan on the original data scale, through pull-back, restriction, or output post-processing, and (iii) change something that is not removed by the model’s per-instance normalization. Requirement (iii) excludes affine warps: with RevIN-style normalization, rescaling and shifting the context are exact no-ops, which we verified empirically before constructing the pool.
Two views are free. nonneg and supportfloor post-process the identity fan rather than re-running the model, so they require zero additional forward passes in both the gate and apply steps once the identity forecast is memoized. Together they account for 16% of rank-weighted admits, giving them the largest admit share per additional pass in the pool and motivating their inclusion in the cheapest thinking mode in Table 6.
Families that were tried and rejected. For completeness, we also report families that were evaluated but not included in the deployed candidate set. These include detrending, STL decomposition, coarse resampling, motif retrieval (using either raw or model-embedding distance), regime/changepoint crops, anomaly cleaning, ARIMA-residual views, log-difference and reflected log-difference, moving-average and EWMA smoothing, despiking, and power transforms. Smoothing is informative: Section E.3 finds that its context displacement points away from the measured modes of the models’ rollout distributions, a pattern consistent with moving contexts away from regions favored by the frozen model.
How rejection was decided, and why it is not post-hoc. Every family, whether deployed or rejected, was evaluated using the same procedure before deployment decisions were made. We constructed the family’s full degree grid, gated it solo (that family plus the identity) using the leak-free backtest, and scored the resulting policy against the CHRONOS-2 base on a labelled 15-config subset of the GIFT-Eval validation split. A family was admitted to the deployed tier only if its solo-gated was negative and its worst-config regression was bounded on this CHRONOS-2 validation subset. This is the only stage at which labels informed a design choice: the pool was then frozen before any test-split evaluation or evaluation with the other models, and neither BOOM nor fev-bench was used for an admit/reject decision. Rejected families were evaluated under the same protocol and continue to be measured by it; harmful variants (smooth, ewma, and winsor above the smallest degree) remain in the ranking pool but are excluded at deployment. Their reported results are therefore regenerated under the same protocol rather than taken from a one-off sweep. § 6 reports the resulting per-family fingerprints across all four models.
Two families appear only in the fingerprint. Table 25 also gates two fixed-pool families that are not in the deployed tier. changepoint is the regime crop listed above: it finds the strongest single mean shift in the most recent of the context, , and starts the context at that break if the shift exceeds 0.5 standard deviations. warp resamples the context by linear interpolation to round points and back to , with , , and averages 3 seeded draws. Both resamplings span the whole context, so the round trip keeps every time index in place.
Aggregation details. Let be the admitted set, the identity fan, and the weight on the base. The first three rules assign uniform weight to the base and admitted members, giving ; the soft-gate instead reweights the admitted set.
Vincent (quantile averaging). at each level . Since each member is monotone in , their weighted average is also a valid quantile fan.
CDF mixture. , where each is the interpolated CDF of its nine-quantile fan. We invert the mixture on a shared grid by pooling and sorting the members’ quantiles, evaluating on this grid, and reading back the 9 deployed levels by linear interpolation. Theorem 3 applies exactly to before this nine-quantile read-back. Its quantiles are not convex combinations of member quantiles, so the MASE-gated mixture is not covered by Theorem 2 on MASE or CRPS (Section A.2); the Vincent policy over the same admitted set, top3−mase, is the variant covered by the historical-backtest guarantee in Theorem 2.
Spread-routed mixture (routemix ). For each window, compute the pairwise-CRPS spread among admitted members, normalized by the window’s own label scale. Use the CDF mixture when and Vincent otherwise. We report , with as the reported safe alternative. The statistic is a label-free disagreement measure closely related to the diversity term in Theorem 3, but differs in both the routing set and scale normalization.
Temperature soft-gate. over the admitted set, with set to the spread of admitted backtest scores. We report this policy for completeness but do not deploy it: it gives the best CRPS and the worst MASE in Table 9.
Policies are named <rule><k>-<objective>, where the suffix denotes the backtest ranking objective: mase uses median absolute error, while the legacy crps suffix uses the nine-level pinball sum rather than exact CRPS. The deployed policy is mixtop3−mase.
Compute ladder and additional controls
We provide the additional details supporting § 5: the thinking-mode ladder and compute accounting used for the compute frontier, together with the pool, policy, rival, compute-matched, and temporal-robustness controls from § 5. The BGAA procedure itself is defined in § 3.
Thinking modes and the compute frontier
We use the four thinking modes in Table 5 to trace the compute–performance frontier in Figure 2. Across modes, we vary only the test-time compute budget: the number of candidates scored by the gate, the number of gate windows and folds, and the number of views retained for aggregation. All modes draw from the same fixed candidate catalogue and use the same selection procedure and frozen model; lower-compute modes evaluate nested subsets of that catalogue.
| mode | cand | cost | MASE% | CRPS% | worst% | TIREX-2 cost / MASE% | PATCHTST-FM-R1 cost / MASE% | TOTO-2-313M cost / MASE% |
| base | 0 | 1.00× | — | — | — | 1.00× | 1.00× | 1.00× |
| low | 9 | 2.40× | −0.44 | −0.52 | +5.62 | 2.79× / +0.02 | 2.40× / −0.45 | 2.28× / −0.27 |
| medium | 19 | 3.03× | −0.49 | −0.69 | +5.67 | 3.08× / −0.07 | 3.01× / −0.20 | 2.49× / −0.20 |
| high | 31 | 5.07× | −0.59 | −0.57 | +7.92 | 5.72× / −0.39 | 4.90× / −0.47 | 6.48× / −0.46 |
| xhigh | 51 | 9.46× | −0.97 | −1.07 | +7.92 | 9.54× / −0.45 | 8.38× / −0.49 | 8.32× / −0.68 |
Table 5. Thinking modes define a compute ladder over a fixed candidate catalogue (GIFT-Eval, 97 configs). Across modes, we vary only the test-time compute budget: the number of candidates scored by the gate, the number of gate windows and folds, and the number of views retained for aggregation. Each mode evaluates a nested subset of the same candidate catalogue, and the selection procedure is fixed. Cost is reported in forward passes relative to the no-test-time compute baseline. The left block gives the full CHRONOS-2 results; the right block reports cost / MASE% for the other three models. low and medium use mixtop2-mase, while high and xhigh use mixtop3-mase; these are compute-scaling variants for the frontier rather than changes to the deployed primary policy.
Compute accounting. Figure 2 and Figure 3 and Table 5 place the test-time compute ladders and published systems on a common compute axis. We use a conservative accounting scheme so that the comparison is consistent across models and compute budgets.
Figure 3. Pareto curves for accuracy vs computational cost. (fev-bench, 100 tasks). Lines are our test-time compute ladders over a frozen model, cheapest rung first; stars are published models on fev-bench. A rung sits at its model’s measured 1× benchmark PFLOPs times the measured forward-pass ratio (base+gate+apply)/base. As in Section C.1, charging each extra pass at the base-pass cost is a conservative accounting convention for models with variable-length computation, since some views shorten the context.
Compute axis. For each model, the 1× point is its measured benchmark PFLOPs for a full GIFT-Eval sweep, using the same profiling table for our models and the published baselines. We place each test-time compute rung at , where is the forward-pass ratio recorded during evaluation. We charge every additional pass at the measured cost of a base pass. This can overestimate computation for models that process shorter transformed contexts more cheaply. However, TIREX-2 pads every input to its full context window, so shortened contexts do not reduce its per-call model computation. We retain the same accounting convention across models and compute budgets for consistency.
Interpretation of the compute estimate. The axis measures estimated FLOPs rather than wall-clock time and does not account for parallel batching. Charging shortened-context views at the full base-pass cost is conservative for models with variable-length computation, but not for fixed-length models such as TIREX-2. The gate cost can also be amortized across multiple evaluation forecasts from the same configuration. We therefore distinguish this estimated-FLOPs accounting from the measured latency and memory reported in Section C.2.
Paired and published baselines. The ladder values come from our test-time compute runs over the 97 GIFT-Eval configs, while the published stars use the reported benchmark results from the compute table. We keep these sources separate. For example, our paired TOTO-2-313M base is 0.7032/0.4838, compared with 0.7028/0.4814 in the published table, while our PATCHTST-FM-R1 base is 0.7052/0.4820, compared with 0.7069/0.4829. We use the base from each test-time compute run to anchor its corresponding ladder, so the hollow base marker does not necessarily coincide exactly with the published star.
Chronos-2 configurations. Our test-time compute results use Chronos-2 with cross-learning disabled, corresponding to the univariate 22.05 PFLOPs configuration. Since that row does not have a published benchmark score, we use our base evaluation to anchor the ladder. We show the standard cross-learning-enabled Chronos-2 separately at 22.83 PFLOPs. The two configurations have nearly identical compute, so this comparison separates gains from cross-series conditioning from gains obtained by spending the same budget on test-time compute. On GIFT-Eval, the cross-learning-enabled model performs better.
Compute scaling on fev-bench. Figure 3 shows the same compute–accuracy analysis on fev-bench. Across all four frozen models, increasing the test-time compute budget improves over the corresponding single-pass baseline on both MASE and SQL. The size of the gain varies across models and metrics. The larger-budget CHRONOS-2 and TiREx-2 settings give the strongest MASE improvements, while the other two models still improve consistently over their own bases.
Thus, we use fev-bench as a second check that the compute–accuracy trade-off extends beyond GIFT-Eval, rather than as evidence that a single model defines the Pareto frontier in every setting. As in Figure 2, each rung is placed using the model’s measured benchmark PFLOPs multiplied by its measured forward-pass ratio, (base + gate + apply)/base, following the conservative accounting described above.
Measured Latency and Memory
We complement our estimated-FLOPs analysis with wall-clock latency and peak GPU-memory measurements on an 80GB H100 using one CPU core. We use synthetic contexts representative of the median GIFT-Eval configuration (, context lengths 648–696), with throughput-oriented batching for all models. Batch sizes are capped at 128, 512, and 256 for CHRONOS-2, TiREx-2, and Toto-2-2.5B, respectively. Cold BGAA includes historical backtesting, candidate forecasts, view transformations, and CDF aggregation, while warm inference reuses the previously selected views. GPU memory includes model weights; component-based latency estimates agree with end-to-end replays within 8% for CHRONOS-2 and TIREX-2, and within 2% for Toto-2-2.5B.
An implementation detail affects TiRex-2’s computational cost. Its g itfeval-zs checkpoint pads every input to a fixed length of 8192 + 928 = 9120 time steps, corresponding to 285 patches of length 32. Consequently, even much shorter contexts and lookback views incur approximately the same model computation per forward call. Unlike models that benefit from shorter transformed contexts, TiRex-2 therefore cannot reduce its per-call cost through context cropping. This also contributes to its relatively high historical backtesting latency.
Table 7 shows that the practical cost of BGAA depends strongly on forecast volume and thinking budget. At , CHRONOS-2+BGAA requires 7.02–14.3 seconds across its four modes, compared with 28.5 seconds for Toto-2-2.5B, even including historical selection. Its peak GPU memory is approximately 21× lower (0.48 versus 10.30 GiB).
However, Toto-2-2.5B retains better absolute GIFT-Eval accuracy than CHRONOS-2+BGAA. Conversely, TIREX-2+BGAA achieves lower MASE (0.6940 versus 0.6956) but requires more wall-clock time at the xhigh budget (114 versus 28.5 seconds). Table 8 further shows that batching reduces historical backtesting from 5.4 minutes to 4.5 seconds for CHRONOS-2 and from 20.7 minutes to 40 seconds for TIREX-2. Cold-start overhead remains substantial for isolated forecasts but can be amortized over repeated predictions. These results distinguish estimated inference FLOPs from practical latency and demonstrate that verifier-guided inference can offer a favorable accuracy–efficiency trade-off in high-throughput forecasting workloads.
Controls and ablations
We use the following controls to test alternative explanations for the observed gains. In Table 11, we compare the gate against random-, noise-, and identity- baselines at matched using paired tests. Table 10 restricts the candidate pool to specific view families, while Table 12 progressively ages the backtest windows to test whether the gate mainly exploits the most recent regime.
Table 9 separates the effects of the candidate pool and the aggregation rule. The pool ablation is nested: crops and offsets recover 56% (CHRONOS-2) and 17% (Toto-2-313M) of the final MASE gain, adding the ideas-tier families improves further, and the decomposition family contributes an additional 0.37% relative MASE improvement for CHRONOS-2 and 0.11% for Toto-2-313M. The aggregation ablation shows a trade-off between average improvement and regression frequency. Among the fixed top- policies, the CDF mixture gives the best mean MASE. The spread-routed variant gives up some of this gain but improves the win/loss count (63/29) and reduces the worst regression relative to the deployed mixture. Theorem 3 motivates the label-free spread statistic used by this policy, but its exact CRPS identity applies to the mixture CDF before the nine-quantile read-back, not necessarily to the reported CRPS after read-back. Finally, the temperature soft-gate improves over the base and is competitive on CRPS, but underperforms the CDF mixture on MASE.
Rival controls
We restrict the candidate pool to lookback-only, offset-only, and cleaning-only views, while keeping the same gated top-2 Vincent policy on CHRONOS-2. We use the same evaluation subset and report paired comparisons between each restricted pool and the full candidate pool.
Compute-matched controls
This control tests whether the gain comes simply from spending more inference compute. We keep the candidate catalogue fixed to the deployed tier (the identity plus 51 non-identity candidates, 52 total views at period 24), use the same members per window, the same equal-weight Vincent aggregation with the base, and the same glounts scoring. The only change is how the members are selected. For random-, we average over three seeds to reduce variance from a single random draw.
First, noise- gives no statistically significant gain. Averaging tiny-jitter copies of the identity () worsens MASE by 0.03% (), while improving CRPS by 0.05% (). This suggests that generic variance reduction does not explain the overall effect. The gated policy still performs substantially better head to head, by 0.80% MASE.
Second, random- performs worse than the base forecast, by 4.82% MASE and 10.73% CRPS. This is expected for a broad candidate pool that contains views which can be poorly aligned with a given series (Section E.3): uniformly sampling from the pool often includes harmful candidates. We therefore do not report a “share of gain recovered” for this arm, since the corresponding ratio would be negative. The result also shows that additional test-time compute is not useful by itself; without selection, it can degrade performance.
Note: the reference arm in this experiment is gated top-2 Vincent rather than the deployed mixtop3-mase policy. This gives a MASE improvement of −0.76%, compared with −0.97% for the deployed policy in Table 1 on the same 97 configs. We use the simpler top-2 Vincent policy for all arms so that the selection rule is the only factor that changes across the comparison.
Temporal robustness
We test how sensitive the gate is to the recency of its backtest evidence. For a given lag, we restrict the backtest to observations at least lag before the forecast start, while the final forecast still uses the full context. If the gate mainly relies on the most recent regime, we would expect its performance to deteriorate quickly as the lag increases.
The gain persists across lags, ranging from −0.41% to −1.71%, and is significant at lags 0, 1, and 2, with borderline significance at lag 4 (), even though the admitted set changes substantially. This suggests that the gate is exploiting a signal that is not limited to the most recent regime. We do not interpret the non-monotonic pattern across lags as evidence that older backtest windows are better. CRPS improvements decline with lag, while MASE shows a non-monotonic pattern and remains the metric used to rank the policy.
Forecast Combination Under Matched Historical Evidence
To isolate the contribution of historical selection and aggregation, we compare BGAA against four alternative combiners using identical candidate forecasts and backtest windows. The 30 configurations (15 GIFT-Eval, 15 fev-bench) were selected beforehand for high augmentation potential, ranked by the deployed gated MASE gain averaged over the three models with at most two per dataset family. This is because view effectiveness can only be compared across series characteristics where views actually change the forecast; this oversamples datasets where views matter, so effect sizes are larger than on a typical configuration. Thus, this is a targeted subset rather than a representative benchmark sample. Top-1 selects the historically best view using BGAA’s ranking statistic and identity fallback; base + top-1 averages it with the identity forecast. L2-convex fits per-quantile nonnegative, sum-to-one weights by minimizing backtest pinball loss with an penalty, while L2-anchored penalizes deviation from the identity weight vector. Both select regularization by five-fold cross-validation on historical evidence.
Table 13 shows that BGAA achieves the largest aggregate MASE (−3.84%) and WQL (−3.55%) improvements. Its advantages over top-1 and base + top-1 are statistically significant, whereas the differences from L2-regularized combinations are not. However, BGAA has a substantially smaller worst regression (1.38% versus 6.54–27.39%), no configurations degrading by more than 3%, and uses only 2.8 additional forecasts on average, versus 6.3–13.2 for the regularized methods. This suggests that historical admission followed by simple aggregation offers a favorable accuracy–robustness–compute trade-off without fitting combination weights to historical outcomes.
Transferability of Restricted Candidate Pools
To examine whether the candidate pool can be pruned without sacrificing transferability, we construct restricted pools using only CHRONOS-2/GIFT-Eval backtests, ranking views by their selection frequency (ties broken by positive backtest gains and reciprocal rank). We then apply these pools unchanged to the other models and benchmarks on the same 90 model–configuration pairs as Table 13. Only the candidate set changes; the backtest windows, scoring, top-3 aggregation, and evaluation forecasts are held fixed. We additionally compare pools selected by leave-one-configuration-out ranking within the same model–benchmark pair or across other pairs, and 200 randomly sampled pools. The source pair is in-sample by construction, since the 22-view pool contains every view selected there.
Table 14 shows that the 22-view pool retains only 69% of the full-pool MASE gain on the 75 transfer configurations, with a significant disadvantage of +1.18 log points (95% CI [0.44, 2.20]). Even excluding the three largest gaps, the disadvantage remains +0.47 [0.23, 0.76]. Pools selected through leave-one-configuration-out procedures retain approximately 79–80% of the gain at roughly 53–58% of the forward-pass cost, but remain significantly worse than the full pool on MASE. Table 15 explains this transfer loss: 30–41% of selected views in the other model–benchmark pairs are absent from the source-model pool. Thus, smaller pools offer meaningful computational savings, but a diverse shared pool avoids excluding transformations that become useful for other models or datasets, without requiring deployment-specific pool tuning.
Full results and verification diagnostics
This section collects the full results underlying § 5 and the verification analyses from § 7. We include the cross-model policy grid for each benchmark, the complete official BOOM leaderboard corresponding to the excerpt in Table 2, the per-domain breakdown, the cross-fitted headroom and ranking results, and a small set of qualitative forecast examples illustrating how BGAA changes the prediction on selected successful windows. Compute-ladder, gate-ablation, and matched-control analyses are kept with their underlying experiments in Sections C.1 and C.3 rather than duplicated here.
| system | MASE | CRPS | note | ||||
| TOTO-2-313M + BGAA | 0.575 | 0.350 | ours | ||||
| Toto-2-2.5B | 0.581 | 0.349 | published | ||||
| Toto-2-1B | 0.582 | 0.349 | published | ||||
| Toto-2-313M | 0.585 | 0.351 | published | ||||
| Toto-2-313M base | 0.585 | 0.353 | our reproduction | ||||
| Toto (v1) | 0.617 | 0.375 | published | ||||
| TiRex-2 + BGAA | 0.619 | 0.376 | our run | ||||
| TimesFM-2.5 | 0.632 | 0.382 | published | ||||
| TiRex-2 base | 0.642 | 0.386 | our run | ||||
| MOIRAI-2-small | 0.672 | 0.427 | published | ||||
| benchmark | configs | final policy: equal or better | final policy: no sig. regression | final policy: worst | conservative (routemix05-crps): equal or better | conservative (routemix05-crps): no sig. regression | conservative (routemix05-crps): worst |
| GIFT-Eval | 97 | 61% | 95% | −8% | 67% | 93% | −6% |
| BOOM | 6750 | 69% | 92% | −199% | 85% | 95% | −98% |
| fev-bench | 100 | 70% | 94% | −7% | 77% | 97% | −6% |
Table 2. BGAA on Toto-2-313M (313M) exceeds the published larger members of the same family on BOOM MASE. Excerpt of the full recomputed leaderboard (Table 18). This table compares accuracy; model size alone does not establish inference-compute efficiency after adding BGAA.
| system | MASE | CRPS | system | MASE | CRPS |
| TOTO-2-313M+BGAA | 0.575 | 0.350 | moirai_2_small | 0.672 | 0.427 |
| toto_2.0_2.5b | 0.581 | 0.349 | moirai_1.1_base | 0.710 | 0.428 |
| toto_2.0_1b | 0.582 | 0.349 | moirai_1.1_large | 0.720 | 0.436 |
| toto_2.0_313m | 0.585 | 0.351 | moirai_1.1_small | 0.729 | 0.442 |
| TOTO-2-313M base | 0.585 | 0.353 | timesfm_2.0_500m | 0.725 | 0.447 |
| toto_2.0_22m | 0.601 | 0.363 | chronos_bolt_base | 0.726 | 0.451 |
| toto (v1) | 0.617 | 0.375 | chronos_bolt_small | 0.733 | 0.455 |
| TiREX-2+BGAA | 0.619 | 0.376 | timer | 0.796 | 0.639 |
| toto_2.0_4m | 0.624 | 0.377 | time_moe_200M | 0.881 | 0.643 |
| CHRONOS-2+BGAA | 0.626 | 0.380 | time_moe_50M | 0.806 | 0.649 |
| timesfm_2.5_200m | 0.632 | 0.382 | visionts | 0.988 | 0.673 |
| TiREX-2 base | 0.642 | 0.386 | autoarima | 0.824 | 0.736 |
| PATCHTST-FM-R1+BGAA | 0.641 | 0.388 | seasonalnaive | 1.000 | 1.000 |
| chronos_2 | 0.641 | 0.392 | autotheta | 1.123 | 1.018 |
| CHRONOS-2 base | 0.655 | 0.394 | autoets | 0.842 | 1.975 |
| PATCHTST-FM-R1 base | 0.681 | 0.407 |
Table 18. Full official BOOM leaderboard (6750 scaled tasks from the 7413-task benchmark; DataDog seasonalnaive baseline; shifted geometric mean with ). We recompute all 23 published systems using DataDog’s evaluation pipeline and verify the reproduced scores against the published leaderboard. Bold rows are our runs. Table 2 shows the corresponding excerpt used in the main text.
Benchmark-level results
Table 16: GIFT-Eval results across four models and four policies (97 configs; geomean of metric/seasonal-naive). We report and MASE win/loss counts relative to each model’s own base; all MASE comparisons have . mixtop3-mase is the deployed policy. routemix05-crps gives the best win/loss ratio for PATCHTST-FM-R1 and TIREX-2, but with a smaller mean gain. top3-mase has the best win/loss ratio for CHRONOS-2 while routemix05-crps has the best win/loss ratio for TOTO-2-313M. On MASE, PATCHTST-FM-R1 and TIREX-2 are the only models for which top2-mase strictly outperforms the deployed policy.
| model | policy | MASE | CRPS | MASE% | CRPS% | w/l |
| CHRONOS-2 | base | 0.7043 | 0.4830 | — | — | — |
| CHRONOS-2 | top2-mase | 0.6990 | 0.4792 | −0.76 | −0.79 | 63/29 |
| CHRONOS-2 | top3-mase | 0.6978 | 0.4780 | −0.93 | −1.04 | 65/27 |
| CHRONOS-2 | routemix05-crps | 0.6996 | 0.4796 | −0.67 | −0.70 | 63/29 |
| CHRONOS-2 | mixtop3-mase | 0.6975 | 0.4778 | −0.97 | −1.07 | 55/38 |
| TIREX-2 | base | 0.6972 | 0.4791 | — | — | — |
| TIREX-2 | top2-mase | 0.6937 | 0.4776 | −0.50 | −0.33 | 57/33 |
| TIREX-2 | top3-mase | 0.6939 | 0.4772 | −0.46 | −0.39 | 57/33 |
| TIREX-2 | routemix05-crps | 0.6949 | 0.4775 | −0.33 | −0.33 | 62/28 |
| TIREX-2 | mixtop3-mase | 0.6940 | 0.4776 | −0.45 | −0.32 | 54/38 |
| PATCHTST-FM-R1 | base | 0.7052 | 0.4820 | — | — | — |
| PATCHTST-FM-R1 | top2-mase | 0.7009 | 0.4810 | −0.61 | −0.21 | 62/30 |
| PATCHTST-FM-R1 | top3-mase | 0.7020 | 0.4818 | −0.45 | −0.05 | 62/30 |
| PATCHTST-FM-R1 | routemix05-crps | 0.7036 | 0.4810 | −0.21 | −0.21 | 67/24 |
| PATCHTST-FM-R1 | mixtop3-mase | 0.7018 | 0.4811 | −0.49 | −0.19 | 64/28 |
| TOTO-2-313M | base | 0.7032 | 0.4838 | — | — | — |
| TOTO-2-313M | top2-mase | 0.6998 | 0.4816 | −0.49 | −0.46 | 60/31 |
| TOTO-2-313M | top3-mase | 0.6993 | 0.4810 | −0.55 | −0.58 | 60/31 |
| TOTO-2-313M | routemix05-crps | 0.6990 | 0.4806 | −0.60 | −0.66 | 58/29 |
| TOTO-2-313M | mixtop3-mase | 0.6984 | 0.4806 | −0.69 | −0.66 | 60/32 |
Table 16.
Energy contains the largest number of configs and improves for all four models, while Healthcare is the most consistent domain by win/loss count (at most one loss for every model). Web/CloudOps is flat or harmful on GIFT-Eval (except TOTO-2-313M), but the same pattern does not appear on BOOM, which consists entirely of observability data and shows large overall gains in Table 1. One relevant difference is the amount of available backtest evidence: the Web/CloudOps configs in GIFT-Eval are relatively short, whereas the BOOM tasks provide substantially more windows for the gate. This comparison is descriptive and does not isolate history length from domain effects.
Benchmark comparability notes.
BOOM. Our BOOM results are directly comparable to the public leaderboard. We evaluate the full official universe of 7413 dataset×term tasks and use DataDog’s evaluation code, which produces the 6750-task scaled set, replaces non-finite raw metrics by column means, normalizes by the published seasonal-naive run, and then computes the shifted geometric mean with . We also recompute all 23 published systems through the same pipeline and verify the resulting scores against the BOOM leaderboard; for example, TOTO-2-313M approximately reproduces at 0.585/0.353.
Note: our evaluations are univariate, whereas published leaderboard entries use each model’s native configuration, although our TOTO-2-313M base approximately reproduces the published TOTO-2-313M result for the same checkpoint. Also, the 663 tasks with zero seasonal-naive score, which the leaderboard handles separately, are not part of the scaled table reported here.
| model | policy | SQL | WQL | MASE | SQL skill | MASE skill | SQL w/l |
| CHRONOS-2 | base | 1.3416 | 0.2193 | 1.6332 | 0.438 | 0.312 | — |
| CHRONOS-2 | routemix05-crps | 1.2882 | 0.2179 | 1.5593 | 0.447 | 0.324 | 71/23 |
| CHRONOS-2 | mixtop3-mase | 1.2836 | 0.2163 | 1.5513 | 0.447 | 0.325 | 56/38 |
| TiREX-2 | base | 1.3653 | 0.2275 | 1.6192 | 0.426 | 0.305 | — |
| TiREX-2 | routemix05-crps | 1.3460 | 0.2266 | 1.6098 | 0.431 | 0.309 | 64/27 |
| TiREX-2 | mixtop3-mase | 1.3436 | 0.2263 | 1.5989 | 0.430 | 0.309 | 54/39 |
| PATCHTST-FM-R1 | base | 1.3150 | 0.1956 | 1.5852 | 0.446 | 0.328 | — |
| PATCHTST-FM-R1 | routemix05-crps | 1.2778 | 0.1954 | 1.5386 | 0.455 | 0.338 | 70/22 |
| PATCHTST-FM-R1 | mixtop3-mase | 1.2845 | 0.1954 | 1.5461 | 0.455 | 0.338 | 65/27 |
| Toto-2-313M | base | 1.3881 | 0.2151 | 1.6652 | 0.433 | 0.316 | — |
| Toto-2-313M | routemix05-crps | 1.3687 | 0.2156 | 1.6467 | 0.437 | 0.318 | 60/33 |
| Toto-2-313M | mixtop3-mase | 1.3622 | 0.2133 | 1.6444 | 0.439 | 0.319 | 56/37 |
Table 17. fev-bench results across all four models (all 100 tasks; fev-native raw metric means and skill relative to the published seasonal-naive baseline, where higher is better). SQL is the primary fev metric and is used for the paired win/loss counts; every test-time compute row has is statistically significant against its corresponding base. routemix05-crps again trades some mean improvement for a substantially better win/loss ratio, e.g., 64/27 versus 54/39 for TiREX-2.
Ordered by CRPS, as the leaderboard is. BGAA moves every one of our four models up the table. TOTO-2-313M with test-time compute (0.575) is the best MASE of any zero-shot row here.
fev-bench. We report fev-bench using its native raw metric means together with skill relative to the published seasonal-naive baseline. Temperature-family policies achieve higher skill but worse raw-mean CRPS and do not produce results for 8 short-horizon tasks. The deployed mix, route, and top- policies improve both raw means and skill across all 100 tasks.
Generalization to Longer Forecasting Horizons
We evaluate whether BGAA’s improvements extend to longer forecasting horizons on five standard long-horizon forecasting datasets: ETTh1, ETTh2, ETTm1, ETTm2, and Weather. We test CHRONOS-2 and TOTO-2-313M at , using input contexts of 2048 steps and the same daily test origins across horizons. Each channel is normalized using training-split statistics, and performance is measured using normalized MSE and MAE. The frozen base and BGAA are evaluated on identical forecast windows.
Table 19: GIFT-Eval results for CHRONOS-2 across the deployed policy grid. Changes are relative to the base score of 0.7043 MASE / 0.4830 CRPS; “worst” denotes the largest regression on any single config. Bold marks the final deployed policy.
| policy | MASE | w/l | worst% | CRPS | w/l | ||||
| base | 0.7043 | — | — | — | — | 0.4830 | — | — | — |
| margin-mase | 0.7019 | −0.35 | 0.080 | 17/9 | +12.07 | 0.4823 | −0.15 | 0.980 | 15/11 |
| top2-mase | 0.6990 | −0.76 | <0.001 | 63/29 | +6.08 | 0.4792 | −0.79 | 0.021 | 64/29 |
| top3-mase | 0.6978 | −0.93 | <0.001 | 65/27 | +8.39 | 0.4780 | −1.04 | 0.002 | 66/27 |
| mixtop2-mase | 0.6991 | −0.74 | 0.020 | 58/35 | +5.67 | 0.4791 | −0.81 | 0.026 | 57/36 |
| mixtop3-mase | 0.6975 | −0.97 | 0.004 | 55/38 | +7.92 | 0.4778 | −1.07 | 0.004 | 60/33 |
| routemix05-crps | 0.6996 | −0.67 | 0.003 | 63/29 | +6.08 | 0.4796 | −0.70 | 0.004 | 67/26 |
| tempvinc-crps | 0.6997 | −0.66 | 0.005 | 59/33 | +7.22 | 0.4794 | −0.74 | 0.056 | 61/32 |
| tempvinc-mase | 0.6991 | −0.73 | <0.001 | 62/30 | +13.31 | 0.4798 | −0.66 | 0.039 | 65/28 |
| tempmix-mase | 0.6985 | −0.82 | 0.014 | 54/39 | +9.61 | 0.4789 | −0.84 | 0.045 | 56/37 |
Table 19.
Table 20: Per-domain CRPS change on GIFT-Eval under the deployed mixtop3-mase policy. We report the mean across configs in each domain, with win/loss counts in parentheses. This is the domain-level counterpart of the fingerprint analysis in Figure 10a and § 6: the pattern varies substantially across models. For example, Econ/Fin ranges from −4.00% for CHRONOS-2 to +1.53% for TIREX-2, while Web/CloudOps ranges from −1.12% for TOTO-2-313M to +2.46% for PATCHTST-FM-R1. Healthcare, sales, and energy are the only domains where all four models improve.
| model | Econ/Fin | Energy | Health | Nature | Sales | Transport | Web/CloudOps |
| CHRONOS-2 | −4.00 (4/2) | −0.40 (20/12) | −7.07 (4/1) | −1.16 (8/7) | −0.19 (3/0) | −0.17 (11/4) | −0.12 (10/7) |
| TIREX-2 | +1.53 (1/5) | −0.58 (19/12) | −5.50 (5/0) | +0.31 (6/9) | −0.22 (3/0) | −0.17 (9/6) | +0.37 (10/7) |
| PATCHTST-FM-R1 | −0.75 (3/3) | −0.54 (20/12) | −1.64 (4/0) | −0.34 (10/5) | −0.17 (3/0) | −0.63 (12/3) | +2.46 (11/5) |
| TOTO-2-313M | −0.87 (2/4) | −0.16 (20/12) | −5.52 (5/0) | −0.28 (8/7) | −0.42 (3/0) | +0.33 (8/6) | −1.12 (12/5) |
Table 20.
Table 21 shows that BGAA improves both metrics on 18 of 20 dataset–horizon settings for CHRONOS-2 and 15 of 20 for TOTO-2-313M. Aggregated MSE improves at every horizon for CHRONOS-2, with the largest relative reduction at (2.88%). For TOTO-2-313M, the improvement is also largest at (3.15%), although performance slightly regresses at . Both models retain improvements at , demonstrating that historical verification can remain useful for substantially longer prediction horizons. However, improvements are generally modest and do not increase monotonically with horizon.
Verification headroom and label-based diagnostics (Table 22) {#tab:capturability}
We retain the per-window pinball loss on the realized test horizon for every view and use it to construct three label-based diagnostics. The cross-fitted best-view gain selects one fixed view per config, using disjoint halves of the windows for selection and evaluation. The label-ranked gate keeps the deployed policy unchanged but replaces the backtest ranking with a ranking computed from labeled held-out windows. The per-window hindsight selection selects the lowest-loss view separately for each forecast window using that window’s labels. These diagnostics use future labels only for analysis; the deployed policy does not.
Evaluation protocol. We score all diagnostics with the same gluonts MASE and CRPS metrics used in Table 1 and apply the same aggregation procedure. Each reported value is the relative change in the aggregate metric with respect to the base forecast, computed over the same set of windows.
Windows. For each config, we use evenly spaced test windows from the evaluation sampler used for the main results. We evaluate the identity forecast together with every available non-identity view in the deployed catalogue on these windows and retain the per-window losses. For MASE, we drop windows with zero seasonal error to match gluonts.
Deployed policy. We evaluate the view set admitted by the deployed run using the deployed CDF mixture. This reproduces the per-config results underlying Table 1 to within relative error.
Cross-fitting split. We divide the windows into two contiguous halves and remove the windows closest to the split boundary so that selection and evaluation labels do not overlap. We then swap the two halves and pool the held-out evaluations. We require at least 8 retained windows per half, which leaves 53 of the 97 configs. On the remaining 44 shorter configs, the deployed policy improves by to across models.
Label-ranked gate. We keep the deployed top-3 selection rule but rank views using labeled test-window losses instead of backtest losses. The in variant ranks on the same half used for evaluation; the reported x-fit variant ranks on the opposite half.
Best-view gain. We select a single view, including identity, with the lowest CRPS on the selection half and evaluate it on the other half.
Per-window hindsight selection. For each evaluation window, we select the view with the lowest summed pinball loss using that window’s realized labels.
On the 53 cross-fittable configs, the deployed policy’s all-window and held-out improvements differ by less than 0.1 percentage points for every model.
Table 22 summarizes these diagnostics for each model. The realized/label-ranked ratio is the realized improvement divided by the improvement from the label-ranked gate on the same 53 configs. This measures how much of the gain available to the fixed policy is recovered by the leak-free backtest ranking. In-sample best-view selection is optimistic: it exceeds the cross-fitted gain by – (Table 23), which is why we use the split above. The label-ranked gate is less sensitive, with in-sample and x-fit results differing by at most 0.2 percentage points.
| model | CRPS best-view gain in | CRPS best-view gain x-fit | CRPS label-ranked gain in | CRPS label-ranked gain x-fit | CRPS realized | CRPS label-ranked gate (x-fit) | MASE realized/label-ranked | MASE best-view gain in | MASE best-view gain x-fit | MASE per-window hindsight |
| CHRONOS-2 | 5.36 | 4.10 | 2.01 | 2.06 | 0.92 | 1.39 | 0.67 | 2.44 | 0.76 | 20.7 |
| TIREX-2 | 3.43 | 1.48 | 1.06 | 1.21 | 0.23 | 0.75 | 0.31 | 1.79 | 1.09 | 19.0 |
| PATCHTST-FM-R1 | 3.54 | 1.42 | 1.09 | 1.20 | 0.35 | 1.23 | 0.28 | 3.46 | 2.36 | 21.3 |
| TOTO-2-313M | 2.95 | 1.37 | 1.26 | 1.16 | 1.08 | 1.44 | 0.75 | 1.74 | 0.72 | 19.4 |
Table 23. Supporting diagnostics for Table 22. Results are reported on the same 53 cross-fittable configs as improvement over the base in percent (positive is better). selects and evaluates on the same windows, while -fit selects on one half and evaluates on the other. The MASE block reports the same diagnostics using the point-forecast metric.
For MASE, the realized/label-ranked ratio ranges from 0.28 to 0.75 across models. We therefore interpret this quantity as a ranking diagnostic, not as a ceiling: under distribution shift, labels from the opposite half can rank views worse than the recent backtest. The two halves are also contiguous and autocorrelated, and their contexts may overlap near the split boundary, so cross-fitting reduces label reuse without making the samples independent. The per-window hindsight best-view diagnostic should be read similarly. It uses the realized outcome and selects only among individual views; for CRPS, an aggregate can outperform every member (Theorem 3), so this hindsight best-view diagnostic is not an upper bound over aggregation policies.
Configuration-level versus window-level ranking. The ranking diagnostics show the same separation. On CHRONOS-2, the median Spearman correlation between backtest and realized view rankings is 0.63 when rankings are aggregated per configuration, but only 0.25 when computed per forecast window (Figure 5). The top- hit-rate and gain-recovery diagnostics show the same degradation at the window level (Figure 6). Because the per-window targets use the realized outcome, they quantify ranking difficulty and heterogeneity rather than an achievable target for a context-only verifier.
Why averaging more backtest windows does not solve window-level selection. The gate statistic averages relative loss over historical windows. Under the usual independent-noise heuristic, the sampling component of its standard error decreases on the order of . The configuration-level gate uses – windows, whereas a window-specific comparison based on a single realized window has no analogous averaging. This heuristic helps explain why configuration-level rankings are more stable, but it is not a finite-sample guarantee: the gate windows are dependent time-series samples, and the realized future window may come from a different local regime. More historical windows can stabilize a configuration-level average; they do not by themselves identify which view will be best on a particular future window.
Fine-grained weighting is not better supported by the current signal. The policy ablation is consistent with this limitation. The temperature-weighted gate uses more of the relative backtest-score information: it achieves the strong CRPS among the tested policies but the worst MASE (Table 9). Fixed top- instead uses the backtest primarily to identify a small set of promising views and is less sensitive to errors in their fine ordering. This is evidence about the policies tested here, not a general claim that weighting cannot help.
Pooled versus Per-Series Historical Selection
We investigate whether selecting views independently for each series improves over the deployed configuration-level gate. On 41 GIFT-Eval configurations containing 1,972 series, we compare the pooled gate, which ranks views using historical evidence shared across a configuration, against per-series selection using only each series’s own backtests. Both approaches use the same sampled historical evidence and candidate views; only the granularity of selection changes. For configurations with fewer than eight usable historical windows, we use the lighter gate described in the experimental setup, rather than requiring the standard eight-window minimum. We group configurations by series count to examine the effect of sparse per-series evidence, with 1–47 backtests available per series depending on the model and configuration.
Table 24 shows that per-config selection achieves better average MASE across all three models: −0.91% versus −0.17% for CHRONOS-2, −0.65% versus −0.25% for TiRex-2, and −0.66% versus +0.22% for Toto-2-313M. The clearest pattern appears in configurations with 118–156 series, where each series provides only 1–3 backtests: pooling significantly outperforms per-series selection for both CHRONOS-2 and TiRex-2. These findings suggest that sharing historical verification evidence across related series can improve selection reliability, particularly when individual series provide too little evidence for stable view ranking.
Qualitative examples
We additionally inspect a small set of forecast windows where the deployed BGAA policy improves over the frozen base model. These examples illustrate the behavior of BGAA, and each plot follows the same format. The left panel shows the base context together with the inputs or forecast-side transformations associated with the views admitted by the gate. The middle panel compares the forecasts produced by these views before aggregation, together with the resulting BGAA mixture. The right panel compares the base and final predictive distributions against the realized forecast horizon. This makes it possible to inspect how the admitted views alter the frozen model’s prediction and how their combination changes the final forecast in windows where BGAA is successful.
Figure 7. Qualitative examples for BGAA improvements. Selected forecast windows for which BGAA improves over the frozen base model. Each subfigure shows the admitted views, their candidate forecasts, and the resulting BGAA prediction relative to the realized horizon.
Figure 8. Qualitative examples for BGAA improvements. Additional successful forecast windows under the deployed policy.
Mechanism experiments: protocols and full results
This section gives the full protocols and results for the three mechanism analyses in Section 6: fingerprinting, prior geometry, and forecast signatures. When an experiment reuses forecast evaluation, we run it through the same evaluation pipeline used for the main results, with the same candidate pool, leak-free backtest, admission rules, aggregation, and scoring. We do not modify the deployed outputs for these analyses.
Experiments that restrict the candidate pool or change the selection rule are reported separately with the controls in Section C.3. Unless noted otherwise, the experiments in this section use a 15-config GIFT-Eval test subset used for selected mechanism and forecast-signature analyses rather than the full set of 97 configs.
Fingerprinting
| family | CHRONOS-2 | TIREX-2 | PATCHTST-FM-R1 | TOTO-2-313M |
| changepoint | −0.034 | 0 | 0 | 0 |
| decomp | −0.814 | −0.084 | −0.109 | −0.214 |
| diff | −0.849 | +0.012 | −0.537 | −0.264 |
| fft | −0.030 | 0 | −0.094 | 0 |
| jitter | −0.370 | −0.362 | −0.130 | −0.105 |
| jitternorm | −0.362 | −0.357 | −0.127 | −0.104 |
| lookback | −0.480 | −0.047 | −0.649 | −1.390 |
| multideseason | 0 | 0 | −0.065 | −0.035 |
| nonneg | +0.002 | −0.068 | −0.075 | −0.003 |
| offset | −0.080 | −0.016 | +0.002 | −0.980 |
| rankgauss | −0.317 | −0.180 | −0.529 | 0 |
| recursive | +0.015 | −0.213 | −0.347 | −0.207 |
| seasontile | −0.182 | −0.082 | −0.149 | 0 |
| warp | −0.397 | −0.113 | −0.104 | −0.270 |
caption:
:::
| model A | model B | perm. | |
| CHRONOS-2 | TIREX-2 | 0.089 | 0.350 |
| CHRONOS-2 | PATCHTST-FM-R1 | 0.297 | 0.078 |
| CHRONOS-2 | TOTO-2-313M | 0.352 | 0.049 |
| TIREX-2 | PATCHTST-FM-R1 | 0.223 | 0.148 |
| TIREX-2 | TOTO-2-313M | 0.012 | 0.480 |
| PATCHTST-FM-R1 | TOTO-2-313M | 0.148 | 0.253 |
caption:
:::
We evaluate each view family separately for each model by restricting the candidate pool to that family plus the identity and applying the deployed backtest gate unchanged. We then measure the resulting gain relative to that model’s own base forecast. Families are drawn from the full fixed pool, which overlaps the deployed tier in Table 4 but differs from it in four ways: it adds changepoint and warp, gates jitter and jitternorm over their full 7-degree grids () rather than the single deployed , merges sdiff into diff and suprsoftfloor into nonneg, and omits the cleaning views (smooth, ewma, winsor). To compare family preferences across models, we compute Kendall’s between the resulting 14-family benefit vectors. Permutation -values are estimated from random label shuffles.
| tier | family | # | passes | degrees, and how the fan is inverted |
| crop | identity | 1 | 1 | – (cached base forecast) |
| crop | lookback | 18 | 18 | keep the last samples, ; restriction map, no fan inversion |
| crop | offset | 14 | 14 | shift the patch grid by samples (patch_len = 16); restriction map |
| micro | jitter | 1 | 3 | additive noise, 3 seeded draws averaged in quantile space; median-neutral |
| micro | jitternorm | 1 | 3 | as above, rescaled to preserve the context’s scale |
| micro | winsor | 1 | 1 | clip at the 0.5% tails |
| ideas | diff | 1 | 1 | first differencing; cumulative-sum inversion along each quantile path (comonotone pull-back, an approximation; Section A.3) |
| ideas | sdiff | 1 | 1 | seasonal differencing at the config’s period ; seasonal cumulative-sum inversion |
| ideas | multideseason | 1 | 1 | remove the multiplicative seasonal profile at period ; multiply it back onto every quantile |
| ideas | seasontile | 2 | 2 | tile the last seasonal period, |
| ideas | fft | 3 | 3 | keep the top- frequencies, ; low-pass of the context only |
| ideas | rankgauss | 1 | 1 | empirical ranks Gaussian order statistics; invert through the context’s empirical quantile function, clamped to its observed range; context-fitted, degree 2 |
| ideas | nonneg | 1 | 0 | project the fan onto ; reuses the cached identity pass |
| ideas | supportfloor | 1 | 0 | project the fan onto the context’s observed support; reuses the identity pass |
| ideas | recursive | 2 | 6 | short-step rollout composed to , step fraction (2 and 4 sequential calls) |
| decomp | decomp | seasonal decomposition at the base period and its sub/super harmonics ; deduplicated, so 1–3 views per config |
Table 4. The deployed pool of views. Tiers are strictly nested, crop micro ideas ideas+decomp, which makes Table 9’s left column a decomposition rather than a list. “#” counts views; “passes” counts forward passes per window, which differs when a view is seeded (jitter/jitternorm average 3 seeded draws) or sequential (recursive_f0.5 needs 2 calls, recursive_f0.25 needs 4). Thus, the gate uses up to 58 passes for the identity plus 51 non-identity candidates (52 total views); where the decomposition family deduplicates to a single view, e.g. period-1 configs, this becomes 56 passes and 50 total views.
Why the fingerprint uses the full pool. We fingerprint the full fixed pool rather than the deployed tier, for three reasons. First, the deployed tier is itself the output of a label-informed admit decision (Section B). Fingerprinting only its survivors would select the family set on the quantity being compared. Second, that selection keeps the families that helped. It truncates the benefit vectors, and truncation typically pulls rank correlation toward zero, the direction our claim predicts. The full pool removes the truncation and makes the test harder. Restricted to the 12 families it shares with the deployed tier, mean cross-model falls from 0.19 to 0.15 (range to 0.33), and removing any single family keeps every pair at . Third, gating each family over its full degree grid measures it at the degree the gate prefers for each model, not at the one fixed for deployment (jitter’s single ). The grids are identical across models, so any advantage a larger grid gives is shared by all four columns and would tend to add agreement, not remove it.
The differences are also qualitative. TiRex-2’s strongest family is jitter (). lookback is strongest for PatchTST-FM-R1 () and Toto-2-313M (), but gives little gain for TiRex-2 (). Within Chronos-2, admitted families also vary across domains (Figure 10a), supporting the use of config-specific selection.
We distinguish two notions of cross-model agreement. The solo-gated benefit vectors above have Kendall in the range 0.01–0.35. In contrast, when we compute the same comparison using per-config admission patterns over full GIFT-Eval, the agreement is much higher (0.50–0.72). This is largely because admission is dominated by the two crop families, which are used by all four models. For the mechanism analysis, we therefore focus on agreement in realized family benefit rather than agreement in whether a family is admitted.
Series Characteristics and Feature-Based Selection
We investigate whether simple statistical properties can predict which transformation families are useful, using 30 configurations (15 GIFT-Eval, 15 fev-bench) across three TSFMs. For each series, we compute STL seasonality strength, linear-trend , lag-1 autocorrelation, and volatility lumpiness, then compare the lowest and highest terciles. Table 27 reports the strongest family in each group using the realized performance of an ungated identity–view mixture, alongside BGAA’s improvement on the same windows. For example, Chronos-2 favors differencing under low seasonality () but decomposition under high seasonality (), whereas TiRex-2 more often favors multideseasoning. These are retrospective associations: the best family is chosen using evaluation outcomes, and the confidence intervals are not adjusted for this selection. Several effects also fail to replicate across both benchmarks.
To test whether these properties provide a deployable alternative to backtesting, we evaluate feature-based routers trained leave-one-configuration-out. Table 28 compares them with historical top-1 selection at the same one-view application budget. Across the three models, the historical gate improves MASE by 1.7–4.4%, whereas the four-characteristic router ranges from a 1.5% improvement to a 2.8% regression. None of the 36 router variants improves average MASE over historical top-1 selection, and even the post-hoc best-of-12 routers do not consistently match it. Thus, statistical features help describe transformation preferences, but these simple predictors do not reliably replace the causal verification signal obtained from historical forecast errors.
Prior geometry
We use ancestral rollouts as a proxy for each model’s learned forecasting behavior, with short-step samples drawn by inverse-CDF sampling from the model’s own 9-quantile head. We study the resulting geometry by embedding both contexts and rollout samples in two spaces: a 20-dimensional shape-feature space and the model’s own embedding space. For each model, we standardize both using its rollout samples. We identify modes by applying -means to the rollout distribution and name each mode by its most distinctive features. For context and view , we define the displacement as , using GIFT-Eval contexts. Figure 9 shows the joint t-SNE projection; we also compute PCA, embedding-space, and three-dimensional projections.
Shape features. The 20 shape features capture temporal dependence, trend, spectral structure, distributional shape, and local variation (Table 29). We compute them from the last 512 points of each context or rollout after z-normalizing the series, making the representation invariant to level and scale. For each model, we standardize the features using the mean and standard deviation of its own rollout samples. We then fit PCA and the -means mode centroids in this model-specific standardized space. Thus, the coordinates of modes in each panel are defined relative to that model’s own rollout distribution.
| group | features | description |
| Autocorrelation and memory | acf1, acf2, acf5, acf10, acf_first_zero, pacf2 | Autocorrelation at lags 1, 2, 5, 10; first non-positive ACF lag up to 99 (scaled by 100); and lag-2 partial autocorrelation. |
| Trend and oscillation | trend_r2, turning_rate, crossing_rate | Linear-trend , frequency of sign changes in first differences, and frequency of crossings of the series mean. |
| Spectrum | spectral_entropy, seasonal_peak_power, seasonal_peak_freq | Normalized spectral entropy, power share of the strongest non-DC Fourier component, and its normalized frequency. The spectrum uses a Hann window. |
| Distribution shape | skew, kurtosis, iqr_over_std, mad_over_std, tail_frac_2sig | Skewness, excess kurtosis, normalized IQR and MAD, and the fraction of observations with . |
| Smoothness, jumps, and persistence | diff_std_ratio, step_max, runlen_mean | Relative first-difference variability, largest one-step change, and mean run length above or below the median. |
Table 29. Shape features used for contexts and model rollouts. We compute all features on z-normalized series using at most the last 512 observations. Bounded statistics are clipped and rescaled where needed so that no single coordinate dominates the representation.
Directionality. diff and smooth move contexts in similar directions across examples, with mean cosine 0.75–0.78, compared with 0.04–0.07 for crops and offsets (Table 30).
Interpreting the directionality results. We treat these results as a mechanism diagnostic rather than direct evidence of prior transport. The jitter control still shows non-trivial directionality (), because even small perturbations systematically change noise-sensitive features such as diff_std_ratio and turning_rate. We therefore also look at displacement magnitude and mode alignment. Within the same model, diff moves contexts 3.0–5.5× farther than jitter, while jitter is among the smallest non-crop movements in feature space and is the smallest displacement in the model embedding space for three of the four models. We also test whether each view moves toward a consistent rollout mode.
As we have clarified previously, these results should not be read as a literal application of Proposition 1. In particular, rankgauss is fitted to the context and diff acts across time. Crops and offsets behave differently as well: they induce only small shape-space displacements (magnitude 0.04–0.05 for offset_8 and 0.35–0.73 for lookback_0.5, versus 6.61–13.29 for diff (Table 30). This is expected because they change the observation map rather than the shape of the series, and this case is covered separately by Section A.3. Overall, we use the geometry to test whether the views induce structured, model-specific changes, not to establish causality.
Non-redundancy. Displacement directions from different views have mean absolute cosine 0.36–0.48 in feature space, indicating that the views make distinct changes (Table 31).
The extreme pairs are also consistent with the intended semantics of the views. For CHRONOS-2, the two differencing families are strongly aligned, , while the intentionally opposing deseason and smooth views have cosine . In contrast, jitter and lookback, which do not share a common mechanism, have only weak alignment, with cosine .
Mode movement and poorly aligned views. We also measure how strongly each view changes mode assignments, independent of its displacement direction. For each view, we compute the Jensen–Shannon divergence between its distribution over rollout modes and the corresponding identity distribution. On CHRONOS-2, with jitter at 0.019, we obtain diff 0.269, sdiff 0.106, rankgauss 0.054, smooth_ma7 0.050, deseason 0.042, winsor 0.022, lookback 0.019, and 0.001 for both offset and seasontile. TIREX-2 shows the same ordering at the top: diff 0.402, sdiff 0.157, and smooth_ma7 0.144, with crop-based views again near the bottom. smooth_ma7 is a useful counterexample. It moves contexts by an amount comparable to several useful views, but fig:10c shows little alignment with any rollout mode. Its largest mode cosine is only +0.03 over 20 modes for CHRONOS-2 and +0.13 for TIREX-2, with the remaining modes negatively aligned. Thus, large movement alone is not sufficient: smooth_ma7 changes the representation substantially without moving toward the rollout modes targeted by the useful views.
Forecast signatures
We characterize the forecast-level effect of each view family using three statistics: the log-ratio of predictive interval width, the median shift normalized by the label scale of each window, and the change in coverage. We compute these quantities over the test windows where the view is applied, first per family and config, and then aggregate using the median across windows and configs.
fft consistently narrows predictive intervals by −1.33 to −1.54, while lookback, offset, and jitter have little effect on interval width (Table 33). Part of diff’s interval widening comes from the cumulative-sum pull-back, which sums marginal quantiles across the horizon (Section A.3). Thus, the signature reflects the full view, not just the input transform.
We summarize the signatures in two ways. First, families are clearly distinct within each model. The between/within-family variance ratios for (width, shift, coverage) are [32.0, 10.4, 71.6] for CHRONOS-2, [25.9, 9.6, 76.0] for TIREX-2, [34.2, 10.0, 56.7] for PATCHTST-FM-R1, and [35.5, 9.9, 86.9] for TOTO-2-313M. Thus, across all four models and all three statistics, between-family variation is roughly 10–87× larger than within-family variation.
Second, the non-degenerate signatures are stable across models. Comparing CHRONOS-2 and TIREX-2, the per-family signature cosines range from +0.95 to +1.00 for the ten families with nonzero signatures (diff +1.00, sdiff +1.00, recursive +1.00, fft +0.99, jitternorm +0.97). The remaining four families: nonneg, offset, seasontile, and supportfloor, have a zero median signature on TIREX-2. They leave most windows unchanged, although they alter enough windows to be admitted occasionally (Table 25). Thus, their cosines are undefined rather than small. Since this cosine is computed from only three statistics, we use it as a consistency check rather than as strong evidence on its own. We also report the fraction of dropped windows due to non-finite fp16 values or zero label scale. The worst case is 0.47 for diff on CHRONOS-2; the median is 0.0, and 9/15 configs drop no windows.
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