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Paper summary
The paper introduces FiRE, a financial time-series foundation model that combines generative pretraining with task-specific reward-guided adaptation. It addresses the cost of scaling discrete market representations and the mismatch between generative objectives and downstream financial metrics. FiRE encodes OHLCVA candlesticks into binary tokens using lookup-free quantization and combines a causal Transformer with conditional flow matching to generate all bits of each future token jointly. The authors further propose ReFLO, which scores sampled futures using verifiable financial rewards and constructs repulsive regression targets from continuations with below-average rewards, without requiring reward gradients or policy likelihoods. The framework is evaluated on financial forecasting across markets and frequencies, synthetic candlestick generation, and investment backtesting, with ablations examining representation capacity, generation mechanisms, and post-training feedback.
Critical strengths
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The architecture provides a practical approach to increasing market representation capacity. Combining binary tokens with joint flow-based generation avoids a vocabulary-sized classifier and sequential prediction within each token, while retaining autoregressive modeling across market timesteps. The tokenizer's candlestick-validity and directional objectives also incorporate relevant structure from financial data.
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ReFLO offers a flexible way to incorporate financial task feedback into a flow-based generator. Its repulsive regression updates do not require differentiable rewards or explicit policy likelihoods, making the approach compatible with the proposed architecture. Different reward functions allow the same pretrained model to be adapted separately to price, return, and volatility prediction.
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The empirical evaluation covers several aspects of financial modeling, including forecasting, synthetic data generation, and investment simulation with transaction costs. Comparisons include task-specific models, general time-series foundation models, and financial foundation models. The ablations on token width, prediction heads, sampling, and feedback signals provide useful evidence about the design choices and the gap between reconstruction quality and downstream forecasting performance.
Critical weaknesses
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The connection between ReFLO's local surrogate and the financial objective remains insufficiently established. Equations (10)–(11) show how the regression target encourages a denoising prediction to move away from a rejected token, but do not establish how this changes the probability mass assigned to low-reward continuations under the full sampler. Since the update acts on continuous token predictions while rewards are evaluated on complete decoded trajectories, the relationship between these two levels is important to the method's justification. An analysis or controlled experiment connecting the local update to changes in the generated distribution and expected reward would strengthen this contribution.
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The data splits and model-selection procedures are not specified clearly enough to assess out-of-sample validity. Appendix A.1.3 provides chronological splits for pretraining and standard forecasting, but refers to a separate fixed split for the main benchmark whose evaluation dates are not given in Appendix H.1. The date ranges used for forecasting and investment post-training, and the corresponding checkpoint-selection rules, also remain unclear. These details are particularly important because ReFLO computes rewards from realized futures. In addition, the main forecasting and investment tables report point estimates without variability across independent runs or confidence intervals accounting for temporal dependence, making the stability of the gains difficult to assess.
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The comparisons leave some ambiguity about the sources of the reported improvements. The post-training experiments compare different feedback signals, but lack conventional task fine-tuning or alternative reward-based adaptation from the same initialization with matched data and comparable compute. This limits the ability to distinguish the contribution of ReFLO's update rule from that of additional task supervision. In the investment experiment, FiRE and the baselines also construct ranking signals from different forecast horizons. Although the authors explain this choice and keep the trading protocol fixed, results at common horizons and an explicit validation-based horizon-selection procedure would help separate model improvements from signal-design choices.
Questions for authors
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Averaging continuous endpoints and then thresholding each bit need not preserve the learned joint token distribution. Have the authors examined how this aggregation affects dependencies between bits and the validity of decoded candlesticks as the sampling budget changes? Such an analysis would help explain the interaction between aggregation, the learned representation, and forecasting performance.
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In Table 2, FiRE achieves a better discriminative score than Kronos, while its train-on-synthetic, test-on-real forecasting scores are slightly lower. What explains this difference? In particular, which financial properties, such as heavy-tailed returns and volatility clustering, are preserved by the generated data, and which temporal dependencies appear most relevant to its predictive usefulness?
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Since price, return, and volatility adaptation use separate rewards, do these objectives exhibit positive transfer or interfere with one another? Evaluating each adapted checkpoint across the other forecasting tasks and synthetic-data generation would help clarify whether task-specific gains preserve the pretrained model's broader financial modeling capabilities.
8 comments
Response to Reviewer rxNC (2/6): Data Separation and Evaluation Reliability
Part 2/6 — W2: Temporal separation and evaluation reliability
W2: Temporal separation, model selection, and evaluation reliability.
Thank you for highlighting the need to make these procedures explicit. We apologize for the unclear description of data splits and model selection in the original manuscript and have clarified these details in the paper.
Data separation and model selection. Both forecasting and investment ReFLO use the same historical training corpus as pretraining, with a cutoff of February 29, 2024. FiRE uses March–June 2024 for validation and selects checkpoints using the corresponding validation metrics. The main forecasting benchmark and investment evaluation both cover July 2024–December 2025, totaling 18 months. Importantly, computing rewards from “realized futures” does not mean using future information from the test period: these are observed continuations of historical training windows, entirely contained within the training split, with all reward targets ending before the training cutoff. No forecasting or investment test outcomes are used for parameter updates or checkpoint selection. We have clarified these chronological splits in Appendices A.1.3, H.1, and I.1, explicitly adding the evaluation dates of the fixed 62-task benchmark in H.1.
Forecasting reliability. We assess FiRE and task-specific FiRE + ReFLO on the central price-forecasting (PCC/SCC) and return-forecasting (IC/RankIC) tasks through 32 paired comparisons against competitive baselines. We use a paired moving-block bootstrap over evaluation dates, jointly resampling the same date blocks across models and market–frequency settings to account for temporal and cross-sectional dependencies. Within each bootstrap sample, we recompute the forecasting metrics and average equally across the 62 settings. We report pointwise 95% confidence intervals for score differences and apply Bonferroni correction across all 32 comparisons. This procedure is now specified in Appendix H.5.
The table shows comparisons against the strongest evaluated baseline for each metric. Entries are improvements over the baseline with 95% confidence intervals; positive values indicate better performance.
| Metric | Baseline | FiRE improvement [95% CI] | FiRE + ReFLO improvement [95% CI] |
|---|---|---|---|
| PCC | Kronos Base | 0.00230 [0.00158, 0.00302] | 0.00700 [0.00477, 0.00923] |
| SCC | Kronos Base | 0.00080 [0.00050, 0.00110] | 0.00740 [0.00457, 0.01023] |
| IC | Moirai 2.0 Small | 0.03330 [0.02013, 0.04647] | 0.03820 [0.02257, 0.05383] |
| RankIC | Kronos Base | 0.01640 [0.01366, 0.01914] | 0.02010 [0.01670, 0.02350] |
All 32 improvements are positive, all 95% confidence intervals exclude zero, and the Bonferroni-adjusted -values are at most . These results provide clear statistical support for the gains over the strongest evaluated baselines. Additional evaluations across different test periods also retain the performance advantages, supporting their temporal stability. The complete paired comparisons appear in Appendix H.5 and Figure H.1.
We additionally conducted three independent post-training runs for each of the price, return, and volatility objectives; all three runs per objective improve their targeted metric. Full training curves, cross-run means, and standard deviations appear in Appendix F.6, Figure F.1, and Table F.2.
Investment reliability. For each model, we select the forecast horizon with the highest validation ESR among 5, 15, and 30 trading days (15 days for FinCast and Kronos Base; 30 days for Sundial, FiRE, and FiRE + ReFLO), and fix it for test evaluation. At the selected horizon, we evaluate Sundial, Kronos Base, FiRE, and FiRE + ReFLO using five sampling seeds, keeping the checkpoint, sampling budget, test period, and trading protocol fixed. We report means and sample standard deviations to quantify sampling-induced variability. FinCast’s inference is deterministic, so its results are reported without a standard deviation. Higher AER and ESR indicate better performance.
| Model | AER (%): mean ± SD | ESR: mean ± SD |
|---|---|---|
| FinCast | 9.38 | 1.00 |
| Sundial | 10.25 ± 1.03 | 0.83 ± 0.10 |
| Kronos Base | 11.03 ± 2.04 | 0.98 ± 0.17 |
| FiRE | 13.65 ± 1.10 | 1.20 ± 0.09 |
| FiRE + ReFLO | 16.98 ± 1.40 | 1.50 ± 0.12 |
FiRE outperforms all three external baselines in mean AER and ESR, with each baseline evaluated at its validation-selected horizon. ReFLO further improves AER by 3.33 percentage points and ESR by 0.30 over pretrained FiRE, corresponding to relative gains of 24.4% and 25.0%. These repeated evaluations confirm FiRE’s advantage in average investment performance and the additional gains from ReFLO.
Response to Reviewer rxNC (3/6): ReFLO Attribution and Investment Horizons
Part 3/6 — W3: ReFLO attribution and investment horizons
W3: Attribution of the gains.
1. ReFLO's contribution beyond additional training and task supervision
Thank you for this suggestion. Using return forecasting as a representative task, ReFLO outperforms continued pretraining, both supervised adaptation baselines, and all three alternative reward-based methods. All methods start from the same pretrained FiRE checkpoint and use the same training windows with matched total window exposure. Configurations and checkpoints are selected by validation performance and evaluated under the same test settings. Reward-based methods additionally use the same return reward and candidate-sampling budget.
Continued pretraining retains the original flow-matching objective, testing whether additional generative training alone produces the gains. For direct task supervision, we train the same small MLP return head either with the backbone frozen or with both the backbone and head updated. This tests whether changing the readout or adapting the representation through return regression is sufficient. We also compare AWM [1], Flow-GRPO [2], and DiffusionNFT [3] with ReFLO using the same return reward and evaluation protocol.
ReturnScore is the average of return IC and RankIC; higher is better.
| Method | ReturnScore ↑ |
|---|---|
| Pretrained FiRE | 0.0765 |
| Continued pretraining | 0.0710 |
| Frozen backbone + return head | 0.0796 |
| Task-supervised fine-tuning | 0.0788 |
| AWM | 0.0803 |
| Flow-GRPO | 0.0670 |
| DiffusionNFT | 0.0812 |
| ReFLO | 0.0840 |
Both supervised controls improve over pretrained FiRE, with head-only training slightly outperforming joint backbone–head fine-tuning. AWM and DiffusionNFT also improve the score, while continued pretraining and Flow-GRPO reduce it. ReFLO exceeds all of these alternatives, showing that its gains go beyond those obtained from additional generative training, direct return supervision, or the alternative updates using the same reward.
ReFLO performs best: its ReturnScore gain over pretrained FiRE is 9.80%, compared with 6.14% for DiffusionNFT, the strongest alternative—a 59.6% larger improvement. Its advantage over the supervised controls and methods using the same reward supports the contribution of ReFLO's update rule beyond additional training and task supervision.
2. Model selection and forecast horizons in the investment experiment
Thank you for raising this concern. For supervised baselines that require training, we already use validation-based model selection: training covers January 2011–February 2024, and validation covers March–May 2024. For each architecture, we select the configuration with the lowest validation return MSE and apply early stopping. This procedure is explicitly described in Appendix I.1.
To directly test whether the investment advantage comes from different forecast horizons, we added comparisons at common horizons of 5, 15, and 30 trading days for all models, keeping the trading protocol fixed. Both FiRE and FiRE + ReFLO outperform the evaluated external baselines in AER and ESR at all three common horizons.
The table below shows the strongest external baseline at each horizon alongside the two FiRE models. Each entry reports AER (%) / ESR; higher is better for both metrics.
| Forecast horizon | Strongest external baseline | FiRE | FiRE + ReFLO |
|---|---|---|---|
| 5 trading days | FinCast: 8.01 / 0.86 | 8.895 / 0.903 | 10.588 / 1.022 |
| 15 trading days | Kronos Base: 11.16 / 1.080 | 12.740 / 1.199 | 12.701 / 1.420 |
| 30 trading days | Sundial: 10.38 / 0.830 | 13.77 / 1.203 | 17.50 / 1.50 |
FiRE's advantage persists even at the five-day horizon originally used by the baselines. FiRE + ReFLO achieves the best ESR at all three horizons, further showing that its risk-adjusted return advantage is not confined to the original 30-day setting. The original difference in forecast horizons therefore does not explain this advantage.
The complete model-by-horizon comparison is now included in Appendix I.5 and Table I.2. The common trading protocol and supervised model-selection procedure are specified in I.1 and I.3.
References
[1] Advantage Weighted Matching: Aligning RL with Pretraining in Diffusion Models. ICML 2026.
[2] Flow-GRPO: Training Flow Matching Models via Online RL. NeurIPS 2025.
[3] DiffusionNFT: Online Diffusion Reinforcement with Forward Process. ICLR 2026, Oral.
Response to Reviewer rxNC (1/6): ReFLO and Trajectory Rewards
Part 1/6 — W1: Local updates and trajectory rewards
Thank you for your careful review and constructive suggestions. We address your three weaknesses and three questions in six numbered replies, with targeted experiments and explanations.
Both new experiments use price-path forecasting RL tasks. Each complete decoded OHLC trajectory is scored by its temporal Pearson and Spearman correlations with the realized future, averaged equally over the two correlations and valid OHLC fields. Expected reward is estimated by scoring individual trajectories and then averaging their rewards.
1. From the local surrogate to trajectory reward. Following Appendix F.3, we connect ReFLO's local regression to reward-guided reweighting of complete trajectories. Fix a history h and its realized future. Let p0(S∣h) be the current distribution of complete continuations, Rh(S) their decoded trajectory reward, and ah(r)=E[ω−∣Rh(S)=r] the expected negative advantage. Since ah(r) is nondecreasing in reward, the reference distribution
=\frac{p_0(S\mid h)\exp\\!\left(\eta a_h(R_h(S))\right)}{Z_\eta(h)}$$ gives lower-reward continuations a stronger penalty and higher-reward continuations more relative weight. Here $\eta>0$ controls the strength of reweighting, and $Z_\eta(h)$ normalizes the distribution. This reweighting improves the full-trajectory reward distribution. Its expected reward is nondecreasing, while the probability below any fixed reward threshold $r_h$ is nonincreasing: $$\frac{d}{d\eta}\mathbb{E}_{q_\eta}[R_h] =\operatorname{Cov}_{q_\eta}\\!\left(R_h,a_h(R_h)\right)\geq0, \qquad \frac{d}{d\eta}\Pr_{q_\eta}(R_h\leq r_h)\leq0.$$ The connection to ReFLO is through the corresponding conditional denoiser. Let $u$ collect the history, generated prefix, noisy token and flow time, and let $e$ be the clean token. In the population analysis of Appendix F.3, with $f_0(u)=\mathbb{E}_{p_0}[e\mid u]$ and $a=a_h(R_h(S))$, the ReFLO regression solution and the denoiser induced by $q_\eta$ satisfy $$f_{\mathrm{ReFLO},\eta}(u) =f_0(u)+\eta\operatorname{Cov}_{p_0}(e,a\mid u) =f_{q_\eta}(u)+O(\eta^2).$$ **ReFLO therefore matches both the direction and magnitude of the leading denoiser change induced by reward-improving trajectory reweighting.** This connects the local token update to a change in the complete-trajectory distribution, whose expected reward and low-reward probability follow the directions above. The complete theoretical derivation is provided in Appendix F.3. **2. One actual update.** Across three runs, we evaluated zero, half, and full strength of the first accepted parameter update on 124 feedback histories per run, using 512 fresh trajectories per history and strength. Averaged across the three runs, the full step increased mean reward by **0.001052** [0.000074, 0.002031] and reduced probability at or below each history’s independently calibrated initial 20th-percentile reward by **0.199 percentage points** [0.052, 0.346]. Half-step point estimates lay between the endpoints. All comparisons rerun Gaussian-initialized Euler16 with $K = 1$, token thresholding, each continuation’s own autoregressive prefix, and the frozen decoder, using paired source noise. **3. Distribution after 1 and 12 updates.** Separately, we evaluated all three runs at updates 0, 1, and 12 on a fixed benchmark of 768 histories across eight market–frequency settings. Each history’s quintile boundaries were fixed using 128 independent baseline trajectories. Another 128 trajectories per model/history measured probabilities in these unchanged ranges. | Fixed baseline reward range | Before (%) | After 1 update (%) | After 12 updates (%) | Change (12−0), pp [95% MC interval] | |---|---:|---:|---:|---:| | 0–20% | 20.41 | 20.27 | 20.28 | −0.14 [−0.42, +0.14] | | 20–40% | 19.60 | 19.61 | 18.49 | −1.11 [−1.41, −0.81] | | 40–60% | 19.71 | 19.69 | 17.71 | −2.00 [−2.31, −1.70] | | 60–80% | 19.64 | 19.86 | 18.82 | −0.83 [−1.13, −0.53] | | 80–100% | 20.64 | 20.58 | 24.71 | +4.08 [+3.79, +4.36] | Mean trajectory rewards at updates 0, 1, and 12 were **0.037745, 0.038528, and 0.065886**. The first-step benchmark change was small and its interval includes zero: +0.000784 [−0.000300, +0.001867]. By update 12, mean reward increased in all three runs, with a mean increase of **+0.028141** [0.025610, 0.030672]. The clearest accumulated effect is increased high-reward probability and expected reward. Results give equal weight to settings and runs. All intervals are pointwise 95% paired Monte Carlo intervals. The trajectory-reweighting derivation and its assumptions are now presented in **Appendix F.3 (Connection to Trajectory Rewards)**.