Foundation Models and Fine-Tuning: Toward a New Generation of Models for Time Series Forecasting

Bertrand Pracca; Emilie Devijver; Eric Gaussier; Morad Laglil

REVIEW 3 major objections 5 minor 16 references

This paper claims that fine-tuning a pre-trained time-series foundation model on a target dataset can beat zero-shot forecasting, provided the adaptation strategy matches the model's scale—low-rank updates for large transformers, full weigh

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2026-08-01 03:26 UTC pith:FCHDSEVI

load-bearing objection The empirical study is systematic and worth publishing after major revision, but the abstract's 'consistently improves' claim is contradicted by the paper's own tables. the 3 major comments →

arxiv 2607.23146 v1 pith:FCHDSEVI submitted 2026-07-25 cs.LG

Foundation Models and Fine-Tuning: Toward a New Generation of Models for Time Series Forecasting

Morad Laglil , Bertrand Pracca , Emilie Devijver , Eric Gaussier This is my paper

classification cs.LG

keywords time series forecastingfoundation modelszero-shot learningfine-tuninglow-rank adaptationtransfer learningprobabilistic forecastingquantile loss

verification ladder T0 review T1 audit T2 compute T3 formal T4 reserved

The pith

A machine-rendered reading of the paper's core claim, the machinery that carries it, and where it could break.

This paper argues that post-pre-training fine-tuning can turn large time-series foundation models into better forecasters on specific datasets, and that the right adaptation strategy depends on model scale: low-rank adaptation works best for a 120M-parameter transformer, while full fine-tuning suits a compact mixer model. It pairs a review of architectures and training strategies with a large-scale empirical study spanning 23 datasets and 95 dataset/horizon configurations. The results show fine-tuning is generally—but not universally—beneficial: it helps most on medium and large datasets and on long horizons, while zero-shot remains competitive or superior on small datasets and in noisy domains such as nature and energy. The abstract's 'consistently improves' is stronger than the body's own 'generally beneficial' reading, and the paper's detailed tables document several configurations where every fine-tuning strategy degrades zero-shot performance.

Core claim

On the paper's own terms, the central empirical claim is that fine-tuning a pre-trained forecasting model on a target dataset—with the right adaptation regime—can improve both point and probabilistic accuracy over zero-shot application. Across 95 dataset/horizon configurations, two top-performing public models were adapted three ways: full weight updates, low-rank adaptation on all data, and low-rank adaptation on 20% of the data. The paper finds that the winning strategy tracks model scale: low-rank adaptation with full data is best for the 120M-parameter transformer (normalized quantile loss 0.364→0.357 on medium datasets and 0.310→0.301 on large ones), while full fine-tuning gives modest

What carries the argument

The argument rides on the contrast between three adaptation regimes, with Low-Rank Adaptation (LoRA) as the central mechanism. LoRA freezes a pre-trained weight matrix and adds a trainable low-rank update ΔW = BA with rank 8, so only a tiny fraction of parameters change; that is what lets a 120M-parameter model adapt without catastrophic overfitting. Full fine-tuning updates every weight and serves as the high-flexibility baseline. Measuring these two regimes against zero-shot under a fixed 4,000-gradient-step budget is what yields the paper's conclusions about model scale, dataset size, and domain noise.

Load-bearing premise

The load-bearing premise is that the models' pre-training exposure to part of the benchmark's training data does not materially distort the fine-tuning-versus-zero-shot comparison, because each model is compared only to its own fine-tuned version; the paper asserts this contamination is limited but does not measure it.

What would settle it

A direct check is in the paper's own tables: zero-shot beats every fine-tuning variant for the large model on small datasets (normalized quantile loss 0.423 vs 0.471 best LoRA) and in nature short-term (0.367 vs 0.381), so 'consistently improves' fails under a strict reading. A cleaner test would fine-tune on series from domains excluded from pre-training and verify whether adapted models still beat zero-shot on average.

Watch this falsifier. Get emailed when new claim-graph text bears on it.

If this is right

Practitioners with a large pre-trained forecasting model should prefer low-rank adaptation over full fine-tuning when target data is limited or noisy.
For compact models, full fine-tuning is the safer default; low-rank variants add little and can degrade accuracy.
Zero-shot remains the right baseline for small datasets and high-entropy domains; fine-tuning there can hurt.
Long horizons are where fine-tuning pays off most, because zero-shot long-horizon accuracy is weakest.
Because the study uses one fixed hyperparameter budget, reported gains are a floor; per-dataset tuning could shift the balance.

Where Pith is reading between the lines

These are editorial extensions of the paper, not claims the author makes directly.

The abstract's 'consistently improves' overstates the body's own 'generally beneficial' pattern; a reader deciding whether to fine-tune should consult the per-domain tables rather than the summary line.
Since the models were pre-trained on part of the benchmark's training split, the fine-tuning gains may partly reflect fitting to distributions the model has memorized; a true transfer test would hold out entire domains from pre-training.
As these models scale toward billions of parameters, low-rank adaptation is likely to become the standard route, mirroring its role in language models.
The finding that full fine-tuning is unreliable for large models is entangled with the fixed budget; a per-dataset learning-rate search could change that conclusion.

Editorial analysis

A structured set of objections, weighed in public.

Desk editor's note, referee report, simulated authors' rebuttal, and a circularity audit.

Desk Editor's Note

The empirical study is systematic and worth publishing after major revision, but the abstract's 'consistently improves' claim is contradicted by the paper's own tables.

read the letter

The first thing to know: the abstract says fine-tuning "consistently improves forecasting accuracy over the zero-shot baseline," but the paper's own results say otherwise. Zero-shot wins on small datasets and in several domains (Nature, Energy) for both models on the primary MWQL metric. The paper itself admits in §3.4.3 that fine-tuning is "not universally beneficial," with zero-shot beating fine-tuning in 5/15 and 8/15 aggregated cells depending on metric. The headline claim is simply not supported.

That said, the empirical study is more solid than the abstract. This is a reasonably thorough comparison of full fine-tuning, LoRA full-shot, and LoRA few-shot across 95 configurations on GIFT-Eval, with both a large model (Chronos 2) and a compact one (TTM-R3-PT). The finding that LoRA is the best choice for Chronos 2 while FFT is better for TTM is a useful, non-obvious result. The domain-level analysis, especially the metric-dependent story on Energy, is also informative. The review portion is competent but not novel; it summarizes known architectures without adding new conceptual structure.

The soft spots are real but mostly fixable. First, the abstract must be rewritten to match the actual findings. Second, there are no significance tests—only means and stds over three seeds, which cannot tell us whether a 2% difference is meaningful. Third, the pre-training contamination is acknowledged but not quantified. The authors argue it is limited because each model is compared against itself, which is fair as far as it goes, but fine-tuning on data the model may have memorized makes the "improvement" harder to interpret. Fourth, there is no train-from-scratch baseline, which would help establish that pre-training is the source of any gain. Finally, no code or data are released, which limits reproducibility.

The paper is a useful dataset of empirical results, not a breakthrough. It deserves peer review because the study is carefully designed in many respects and the findings, once properly qualified, would be a useful reference for practitioners. A serious referee should push for a rewritten abstract, significance testing, and a more careful discussion of contamination. I would not cite it in its current form, but I would after those revisions. I'd bring it to a reading group to discuss the gap between claims and evidence—it's a good teaching case.

Referee Report

3 major / 5 minor

Summary. The paper reviews the main architectural families, pre-training objectives, and adaptation strategies of recent time-series foundation models (Chronos 2, TTM-R3-PT, TimesFM, Moirai, TiRex, TOTO, Timer-S1, etc.), then presents an empirical study of fine-tuning two publicly available GIFT-Eval leaders — Chronos 2 and TTM-R3-PT — across the GIFT-Eval train/test benchmark. The study compares zero-shot inference with full fine-tuning, LoRA full-shot, and LoRA few-shot, using normalized MAPE and MWQL aggregated by dataset size and by domain/horizon. The abstract claims that fine-tuning consistently improves over zero-shot, but the body reports a more nuanced picture: gains are concentrated in certain dataset sizes, domains, and metrics, with zero-shot remaining competitive or superior in many configurations.

Significance. If properly qualified, the empirical comparison is a useful contribution: it covers a large configuration space (15 univariate and 8 multivariate datasets, 95 configurations), uses both point and probabilistic metrics, and is transparent about pre-training contamination and fixed hyperparameters. The comparison between full fine-tuning and LoRA across two very different model scales is a practically relevant data point for practitioners. However, the headline claim is not supported by the results as reported, and the absence of statistical testing weakens even the weaker 'generally beneficial' conclusion. The review portion is competent and could be valuable as a survey component, but the empirical claims need substantial revision before the paper meets the standard of a journal publication.

major comments (3)

[Abstract; §3.4.3; Tables 4 and 5] The headline claim that fine-tuning 'consistently improves forecasting accuracy over the zero-shot baseline' is contradicted by the paper's own results. Table 4 shows that on small datasets all fine-tuning variants degrade Chronos 2 performance (MWQL_n 0.423 zero-shot vs 0.471–0.577; MAPE_n 0.544 vs 0.612–0.732). Table 5 lists multiple domain-horizon cells where zero-shot remains best, e.g., Chronos 2 on Nature MWQL short/medium, Chronos 2 on Energy MWQL at all horizons, and TTM on Web/CloudOps MWQL short/medium. Section 3.4.3 itself concedes that zero-shot wins in 5/15 and 8/15 aggregated configurations. The abstract and conclusion must be rewritten to state that fine-tuning is generally but not universally beneficial and that the benefit depends on dataset size, domain, horizon, and metric.
[§3.4; Tables 4 and 5] No statistical hypothesis tests are provided for the central comparison. Fine-tuning results are reported as mean±std over three seeds, while zero-shot has a single value; no paired test or confidence interval over datasets is given. Many claimed differences are tiny: for example, Chronos 2 on Transport Long MWQL_n is 0.123 zero-shot vs 0.120 for FFT, while other cells in the same table have seed std as large as 0.147 (Web/CloudOps Medium MAPE). Without paired significance tests or across-dataset intervals, even the weaker claim that fine-tuning is 'generally beneficial' is not rigorously established.
[§3.2] The treatment of pre-training contamination is insufficient. The authors acknowledge that Chronos 2 and TTM-R3-PT were pre-trained on a subset of the GIFT-Eval training data, but assert that the impact is limited because each model is compared only with itself. This reasoning does not follow: if the pre-training corpus includes the target datasets, then fine-tuning gains may partly reflect adaptation to distributions the model has already memorized, rather than transferable improvement. The paper should quantify this effect, for example by reporting fine-tuning gains separately for datasets present in and absent from the pre-training corpus, or by validating on a separately held-out benchmark.

minor comments (5)

[§2.1, §2.3.2] The text says 'Equation 1 below' in Section 2.1, but the referenced equation appears much later in Section 2.3.2. Please renumber or move the definition so that cross-references are correct.
[Table 2] The '# Obs.' column contains repeated and ambiguous values, making it hard to recover the actual series length and total observation counts. Please reformat the table so each dataset has a clear series length and total observation count.
[Figure 5 caption] The caption ends with 'as proposed by GIFT-Eval in Figure 5,' which appears to attribute this paper's own figure to the GIFT-Eval benchmark. Please correct the attribution or rephrase.
[Throughout] Minor editorial issues: 'novel idea' should be 'a novel idea'; the LoRA reference cites 'Hu, yelong shen, ...' and should be normalized to 'Hu, Y., Shen, Y., ...'; several references use inconsistent 'and et al.' formats. Please run a careful copyedit.
[§3.3] Section 3.3 says hyperparameters are 'retained as default values,' but Table 3 reports specific values for batch size, LoRA rank, alpha, learning rate, and gradient steps. Please clarify which values are official model defaults and which were chosen by the authors, and state the batch-size adaptation rule for TTM-R3-PT more precisely.

Circularity Check

0 steps flagged

No circularity: the fine-tuning study is an empirical comparison with standard metrics; the abstract's 'consistently improves' overstatement is a correctness/accuracy concern, not a circularity.

full rationale

The paper makes no derivation-from-first-principles claim whose conclusion is equivalent to its inputs. The central empirical result is a direct comparison of zero-shot and fine-tuned forecasting models evaluated on a fixed benchmark (GIFT-Eval) with standard metrics (MAPE, MWQL). Fine-tuning optimizes a quantile loss that is related to MWQL, but the paper does not present this as an independent prediction; it is an evaluation set-up, and the paper itself reports that fine-tuning is 'not universally beneficial' (Section 3.4.3), acknowledging configurations where zero-shot wins. The only self-reference is footnote 1 pointing to the authors' earlier EGC 2026 paper as an 'extension and update'; this is not load-bearing for any empirical or theoretical conclusion. The acknowledged pre-training contamination (Section 3.2) is a limitation about benchmark interpretation, not a case of fitting a parameter and then renaming it a prediction. No equations are shown to be equal by construction, no fitted parameter is relabeled as a prediction, and no claim is justified solely by a self-citation. Therefore, no significant circularity is present; the abstract's universal 'consistently improves' claim is contradicted by the paper's own Tables 4 and 5, but that is an internal-evidence inconsistency, not a circular-reasoning defect.

Axiom & Free-Parameter Ledger

9 free parameters · 5 axioms · 0 invented entities

The paper is an empirical comparison; it introduces no new entities or fitted derivations. The main free parameters are the hand-chosen hyperparameters and the data-driven size thresholds. The key assumption is that the GIFT-Eval benchmark and the self-comparison protocol isolate the effect of fine-tuning despite pre-training contamination.

free parameters (9)

Learning rate (Chronos 2 FFT) = 1e-4
Fixed across all datasets; affects whether full fine-tuning overfits.
Learning rate (TTM-R3-PT FFT) = 1e-3
Fixed; chosen by hand, not tuned.
Learning rate (LoRA, both models) = 1e-5
Used for LoRA experiments; fixed.
Batch size (TTM-R3-PT) = 18–256 (adapted to dataset size)
Adapted by dataset, a choice that could affect results.
LoRA rank (r) = 8
Rank of low-rank adaptation; fixed.
LoRA alpha = 16
LoRA scaling factor; fixed.
Max gradient steps = 4000
Fixed computational budget; may under- or over-train.
Few-shot fraction = 20%
Proportion of training data used in LoRA-FewShot; arbitrary choice.
Dataset size quantile thresholds = 0.33 / 0.66
Used to split datasets into small/medium/large; data-dependent choice.

axioms (5)

domain assumption GIFT-Eval train/test split provides a valid evaluation of zero-shot and fine-tuned models.
The benchmark is treated as ground truth for comparing models; the authors acknowledge pre-training overlap with training split.
domain assumption Comparing each model's zero-shot to its own fine-tuned version mitigates the effect of pre-training contamination.
Section 3.2 argues contamination is limited in this comparison, but this is an assumption, not demonstrated.
domain assumption Arithmetic mean of metric ratios (normalized by Seasonal Naive) is an appropriate aggregation across heterogeneous datasets.
The evaluation aggregates normalized MWQL/MAPE with an unweighted mean, which can be dominated by easy/hard datasets.
domain assumption Fixed hyperparameters across datasets are representative of deployment and do not unfairly disadvantage any strategy.
The authors explicitly choose not to tune per dataset, which may bias against FFT on small data; acknowledged in §3.4.3.
standard math The MWQL approximation of CRPS is adequate and the quantile-loss training objective relates directly to it.
Equation (3) and following definitions; standard result in quantile regression.

pith-pipeline@v1.3.0-alltime-deepseek · 20308 in / 12619 out tokens · 108293 ms · 2026-08-01T03:26:24.622466+00:00 · methodology

0 comments

read the original abstract

Inspired by recent breakthroughs in large language models for natural language processing, foundation models have emerged as a promising paradigm for zero-shot time series forecasting, enabling accurate predictions on datasets never seen during pre-training. Ranging from tens to hundreds of millions of parameters, these models are pre-trained on vast and diverse collections of time series, learning generalizable representations that support both point and probabilistic forecasting. This approach alleviates the need for dataset-specific model design and manual tuning, offering a unified solution across forecasting problems. In this work, we review the main architectures, pre-training strategies, and optimization methods underpinning these models. We further investigate post-pre-training fine-tuning of selected foundation models to enhance their performance on specific datasets. Our empirical results demonstrate that this step consistently improves forecasting accuracy over the zero-shot baseline.

Figures

Figures reproduced from arXiv: 2607.23146 by Bertrand Pracca, Emilie Devijver, Eric Gaussier, Morad Laglil.

**Figure 1.** Figure 1: Timeline of representative time series forecasting models, from traditional statistical methods (ARIMA, HoltWinters) through deep time series models (DTSMs, 2012–2024) to the emergence of pre-trained time series foundation models (TSFMs, 2024–2026). Models are positioned according to their release date, which may precede the publication of the corresponding paper or technical report. foundation models for… view at source ↗

**Figure 2.** Figure 2: Illustration of the two main paradigms for time series foundation models. (a) Encoder-only: future patches are masked and appended to the input; the encoder processes all patches bidirectionally and predicts the masked positions. (b) Decoder-only: the model autoregressively predicts the next patch from preceding context using causal attention. Blue: input time series and its patches; red: neural layers (en… view at source ↗

**Figure 3.** Figure 3: Comparison of three forecasting strategies. (1) Serial forecasting (Timer-S1): the main blocks process the lookback series, then each STP block progressively predicts the next future patch with increasing computation depth. (2) Autoregressive forecasting: the model predicts one patch at a time and rolls its own predictions back as input. (3) Multi-token forecasting: Multiple patches are produced simultaneo… view at source ↗

**Figure 4.** Figure 4: Illustration from (IBM) of Low-Rank Adaptation (LoRA) (Hu et al., 2022). Left (during training): the pre-trained weight matrix 𝑊 ∈ ℝ𝑑×𝑑 is frozen, and a trainable low-rank perturbation Δ𝑊 = 𝐵𝐴 is added in parallel, where 𝐴 ∈ ℝ𝑟×𝑑 is initialized from a Gaussian distribution and 𝐵 ∈ ℝ𝑑×𝑟 is initialized to zero, so that the perturbation is initially null. The rank 𝑟 ≪ 𝑑 controls the number of additional train… view at source ↗

**Figure 5.** Figure 5: Average trend strength, seasonality strength, and spectral entropy across the seven domains of the GIFT-Eval benchmark. Higher trend and seasonality values indicate more structured and predictable series, while higher entropy reflects greater irregularity. Economic/Financial series exhibit the strongest trend (0.90), whereas Transport stands out with the highest entropy (0.63) and weakest trend (0.47), sug… view at source ↗

discussion (0)

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