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Under review as a conference paper at ICLR 2027

Beyond Regression: Probabilistic Ranking for Financial Forecasting

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Abstract

Financial time-series forecasting is commonly formulated as point regression, although minimizing prediction error does not necessarily produce effective ranking or discrimination of rare, decision-relevant movements. We propose a probabilistic market-state forecasting framework that represents both historical patterns and future returns in discrete spaces. Historical OHLC patches are quantized into tokens and encoded by a lightweight causal Transformer, while upward- and downward-oriented target codebooks define future return states predicted through dual classification heads. The probabilities of selected extreme states are aggregated into directional scores for return ranking and tail-event identification. Experiments on ten major equity indices across multiple chronological periods show consistent improvements over regression-based forecasters in rank correlation and the identification of extreme upward and downward movements. Ablation results show that input and target discretization provide complementary benefits. Furthermore, decision-level fusion combines the state probabilities with existing regression forecasts, improving both ranking quality and point-error metrics. These results demonstrate that discrete return-state probabilities capture decision-relevant information that point-regression objectives alone do not adequately represent.

Primary area:
learning on time series and dynamical systems
Keywords:
Financial time-series forecasting, probabilistic forecasting, market-state prediction, return ranking, extreme-event detection, discrete tokenization, K-Means clustering, Transformer

Reviews

Among:
Shape:
1234this paper, Bottom 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.25 over 4 reviews, above 49% of the others.
Reviewer_HjXtOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
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3
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Paper summary

This paper investigates the limitations of traditional financial time-series forecasting methods, which primarily rely on point regression objectives and struggle to effectively identify extreme market movements and rank returns. The authors propose a probabilistic market-state forecasting framework that represents historical OHLC data and future returns as discrete states. Experiments conducted on ten major equity indices across different time periods demonstrate that the proposed method outperforms several regression-based forecasting models in return ranking and extreme-movement identification.

Critical strengths

S1: This paper points out that traditional financial time-series forecasting methods primarily optimize MSE or MAE, but lower prediction errors do not necessarily lead to better return ranking or extreme-event identification. The authors shift the research focus from continuous numerical prediction to probabilistic market-state modeling, making the forecasting objective more aligned with decision-relevant information in financial applications. This perspective offers a certain degree of novelty and provides a valuable research direction for financial time-series forecasting.

S2: This paper transforms the traditional regression task into a probabilistic classification task through historical price patch discretization, directional anchor selection, and dual target-state codebooks. Specifically, two independent state spaces for upward and downward movements are used to model market changes in different directions, enabling the model to generate corresponding prediction scores for extreme upward and downward events.

Critical weaknesses

W1: The paper mainly compares the proposed probabilistic classification framework with traditional regression models optimized using MAE. However, these two types of methods have different training objectives, and the regression models are not directly optimized for return ranking or extreme-event identification. Therefore, the observed performance improvements may partially result from better alignment between the training objective and evaluation metrics, rather than solely from the proposed model architecture. Although the paper compares several classification output formulations, it still lacks systematic comparisons with independently optimized binary classification, learning-to-rank, and other probabilistic forecasting methods.

W2: The paper lacks systematic experiments with different historical lookback window lengths and prediction horizons. Therefore, the applicability of the proposed model to more complex financial forecasting scenarios remains to be further validated.

W3: The paper constructs directional prediction scores by selecting the five cluster states with the highest or lowest average returns. However, extreme events in financial markets are typically rare, and the analysis in Appendix B.2 also shows that the selected Top-5 or Bottom-5 states contain very few samples in some training periods. In such cases, the cluster mean returns estimated from a small number of samples may be significantly affected by random fluctuations and outliers.

W4: The paper considers the dual-directional K-Means codebooks as one of its core designs. However, Figure 8 in Section 5.5 shows that simpler output formulations, such as equal-width discretization, dual binary classification heads, and a single three-class classification head, can also achieve competitive performance in return ranking and extreme-event identification. This makes the practical advantages of the dual-directional K-Means codebooks over simpler classification strategies less convincing. I hope the authors can further clarify the necessity of this relatively complex design and provide more direct comparisons to demonstrate its irreplaceable contribution.

If the authors can adequately address the above concerns and provide appropriate clarifications or additional experimental evidence during the rebuttal phase, I would be willing to reconsider and potentially raise my score accordingly.

Questions for authors

See Weaknesses

3 comments
AuthorsOpenReview ↗

Response to Reviewer HjXt (1/2)

We thank the reviewer for the constructive comments. We address each point below.

W1. Training objective and direct classification baselines.

Our central question is whether probabilistic market-state forecasting is better suited than point-error minimization to ranking next-day returns and identifying extreme moves. The objective alignment noted by the reviewer is therefore the effect we aim to test, rather than a confound. We do not claim that our model dominates all alternatives.

(1) Why MAE-trained regressors are the primary baselines. Financial forecasting models are routinely trained and selected by MSE or MAE, so whether this serves ranking and extreme-event identification is our central question (Section 1, lines 57–59). Figure 2 shows that lower MSE or MAE can coincide with weaker IC and AUROC. Proposition B.2 shows that MSE/MAE regression recovers the conditional mean/median, whereas the Bayes-optimal AUROC ranking is given by the event posterior; Proposition B.3 gives a counterexample where the MSE-optimal predictor inverts the tail ranking.

(2) Same-backbone binary and three-class classifiers support this conclusion. Section 5.5 fixes the input tokens and Transformer backbone and changes only the output layer. In 2015–2019 and 2021–2025, the dual binary head reaches Spearman ICs of 0.0422 and 0.0390, the three-class head 0.0442 and 0.0378, and our codebooks 0.0372 and 0.0364, all well above PatchTST, the strongest regression baseline (0.0317 and 0.0140; Table 9). The improvement thus comes from replacing point regression with probabilistic state prediction, not from one specific output design.

(3) What our codebooks add over direct classification.

  • High-confidence concentration. DP@1000 reaches 15.60% and 13.57%, versus 14.95% and 12.85% (dual binary) and 14.78% and 13.07% (three-class) (Fig. 8d).
  • Richer, reusable output. Binary and ternary heads are tied to the ±2% training labels. Our codebooks keep a distribution over 100 states per direction, which can be aggregated into different extreme-state events without retraining (Table 3), with Bayes optimality for the induced event (Theorem B.5).

(4) Other probabilistic and ranking methods. We already compare with Kronos, which predicts categorical distributions over discrete K-line tokens but decodes them into continuous prices. On 2025–January 2026, our model achieves a higher IC (0.0511 vs. 0.0153/0.0067) and higher AUROCs in both directions (Table 9). Out of respect for the reviewers' suggestions, we also added Gaussian NLL and quantile heads on the same input tokens and backbone (see our response to Reviewer kVbL, W1/Q1): our dual codebooks rank first in 6 of 12 entries, and all probabilistic heads remain far above the MAE-trained baselines.

W2. Lookback window and forecast horizon. Our model uses 10 trading days of daily index OHLC observations to forecast the next-day return. This follows the standard practice in financial forecasting, which differs from general time-series forecasting in this respect.

(1) One to two weeks of input and a next-day target are the mainstream setting. Unlike long-term time-series benchmarks, financial forecasting studies rarely evaluate multiple prediction lengths or input lengths. For next-day prediction, 10 trading days is a common choice: Shahabi Nejad and Ebadzadeh [1], Ding et al. [2], and Yoo et al. [3] use 10-day lookbacks for next-day price and movement prediction, and Wang et al. [4] use nine daily closes to predict the next index close. Such short-term tasks typically do not use more than two weeks of history, and our 10-day setting follows this convention.

(2) In finance, the horizon defines the task rather than its difficulty. In long-term forecasting, multiple horizons (e.g., T∈{24,36,48,60}T \in \{24,36,48,60\} for PatchTST on ILI [5]) measure how point error grows with lead time on the same series. In financial forecasting, changing the horizon changes the holding period and the event being ranked: a 2% next-day move and a 2% weekly move are different decision targets with different base rates. Fixing the next-day target lets all methods be compared on the same daily decision.

References
[1] Shahabi Nejad & Ebadzadeh, Stock market forecasting using DRAGAN and feature matching, ESWA 2024.
[2] Ding et al., Hierarchical Multi-Scale Gaussian Transformer for Stock Movement Prediction, IJCAI 2020.
[3] Yoo et al., Accurate Multivariate Stock Movement Prediction via Data-Axis Transformer with Multi-Level Contexts, KDD 2021.
[4] Wang et al., Stock market index prediction using deep Transformer model, ESWA 2022.
[5] Nie et al., A Time Series is Worth 64 Words: Long-term Forecasting with Transformers, ICLR 2023.

AuthorsOpenReview ↗

Response to Reviewer HjXt (2/2)

W3. Robustness of the Top-5 and Bottom-5 scores. In some training periods, the Top-5 and Bottom-5 states contain few observations (Appendix B.2). This raises the question of whether the resulting tail rankings are sensitive to random fluctuations or outliers in these small samples.

(1) The Top-5 and Bottom-5 scores deliver significant AUROC gains in both test periods. Table 9 reports upward and downward AUROCs of 0.8131 and 0.7557 in 2015–2019, and 0.7741 and 0.7082 in 2021–2025. In each period and direction, the AUROC gain over every evaluated point-forecasting baseline is statistically significant (Holm-adjusted p<0.05p<0.05). Appendix A.7 assesses these gains with a market-stratified moving-block bootstrap using 1,000 resamples and 20-trading-day blocks.

(2) Tail discrimination is similar when the score aggregates 40 states per direction. This comparison addresses how much the forecast depends on using only the five states at the extreme end of each training-set ordering. Figure 9 shows that expanding the aggregation from 5 to 40 states increases the number of selected training observations by more than a factor of 100 in each direction and period, with event purity of at least 99.82%. In Table 3, the largest absolute change across both test periods and directions is 0.0112 in AUROC and 0.0031 in AP.

The five-state scores therefore achieve significant out-of-sample gains in both periods, and those periods also show comparable tail discrimination when the probabilities of a much broader group of states are aggregated.

W4. Practical advantage of the dual-directional K-Means codebooks. We do not claim that this design is irreplaceable. As stated in Section 5.5, the probabilistic state framework is not tied to a particular output discretization, and the competitiveness of simpler discrete outputs further supports our central claim (see W1). The dual K-Means codebooks are the instantiation that performs best, with two concrete advantages.

(1) High-confidence event concentration (K-Means). Section 5.5 identifies high-confidence event concentration as the practical advantage of our codebooks (lines 466–475). Figure 8(d) directly compares K-Means with equal-width binning, two binary heads, and a single three-class head using the same input tokens and Transformer backbone. To compute directional precision (DP@N), we take the NN highest-scored observations for each direction, calculate the fraction that moved at least 2% in that direction, and average the two hit rates.

At N=1000N=1000, K-Means achieves the highest directional precision in both periods, reaching 15.60% in 2015–2019 and 13.57% in 2021–2025. At N=2000N=2000, K-Means also ranks first in 2015–2019 and is nearly tied with equal-width binning in 2021–2025 (10.51% versus 10.55%). These results suggest that the finer, data-adaptive states can place more realized extreme moves among a fixed number of high-confidence predictions, a distinction that aggregate metrics such as IC, AUROC, and AP do not fully capture.

(2) Dedicated directional codebooks (dual). Removing the downward branch (upward-only codebook) lowers Spearman IC from 0.0372/0.0364 to 0.0362/0.0303 in 2015–2019/2021–2025, and replacing the anchored dual codebooks with a shared K=200K = 200 codebook lowers it to 0.0354/0.0314 (Table 2). When the score aggregates 40 states, the dedicated downward codebook keeps downward AUROC at 0.7576/0.7194, whereas the bottom states of the upward codebook drop to 0.2484/0.2891 (Table 3).

Summary. The two components are supported by different evidence. The K-Means state construction is supported by high-confidence event concentration (DP@N, Fig. 8d). The dual-directional design is supported by the stability of the dedicated downward score under broader aggregation (Table 3) and by the ranking gain from dual-branch training (Table 2). Together with the same-backbone comparison in W1, these results show that probabilistic state prediction drives the main improvement over regression, and the dual K-Means codebooks further refine it.

I thank the authors for their detailed response, which has addressed most of my concerns. However, the paper still has some limitations, particularly the lack of systematic evaluations across different historical input lengths and forecasting horizons. In addition, I have carefully reviewed the comments from other reviewers and the authors' corresponding responses. Although the authors have clarified some issues during the rebuttal phase, I believe that the available evidence is still insufficient to fully resolve my remaining concerns. Therefore, I have decided to maintain my original score.

Reviewer_3kNSOpenReview ↗
Rating
3
Confidence
4
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

The paper provides a novel perspective on financial forecasting by combining point-wise regression with probabilistic state classification via rank fusion.

It challenges reliance solely on MSE/MAE by emphasizing ranking-based metrics (AUROC/AP) and demonstrates how adaptive codebooks can specifically target extreme market movements, offering a more nuanced understanding of tail-risk prediction in time-series data.

Critical strengths
  • Dual cookbooks enhance the ability to leverage both regression and directionality, improving discrimination of extreme events

  • Kudos to the authors for releasing hte code implementation, which fosters reproducibility

Critical weaknesses
  • The competitor approaches mostly covers transformer based and LLM models, leaving unconvered, for example, deep fusion model for stock market prediction, which combine with news headlines and time series data

  • Authors mentioned that codebooks are robust across M=5 to M=40, but using the upward codebook for both directions deteriorates sharply at M = 40 for downward events. This suggests that the model is sensitive to architectural or hyperparamrter choices and may not be generalizable or practical

  • There is no mention of computational cost, either theoretical or empirical

  • I could not find a portfolio simulation with simulated returns over time

  • I am a bit skeptical about AUROC being so high in the bar plot in Figure 5

Questions for authors

While the evaluation provides a thorough comparison against standard transformer and LLM baselines, it remains unclear how the framework stacks up against specialized deep fusion models for stock prediction that explicitly combine news headlines with high-frequency time-series data.

Furthermore, while the codebooks demonstrate stability across a range from M=5 to M=40, the sharp performance deterioration observed when applying the upward codebook to downward events at M=40 raises questions about structural robustness; to what extent does this sensitivity to hyperparameter choices limit the model's practical generalizability in real-world deployments?

One concern regarding real-world viability is the absence of any theoretical or empirical analysis of computational cost, leaving the actual training and inference overhead unquantified. Can the authors do something in this regard?

In regards to Figure 5, what validation safeguards were put in place for such stellar performance, and have the authors ruled out potential data leakage or evaluation issues?

3 comments
AuthorsOpenReview ↗

Response to Reviewer 3kNS (1/2)

With the rise of large language models, submitting to AI venues has increasingly become a lottery, and many review comments now read much like AI-generated text. Although our paper appears to have a low chance of acceptance, we are glad and honoured to receive the reviewer's positive assessment. In particular, we can tell that this review was written without the traces of AI generation, and we genuinely felt respected by it. We address each point below.

W1/Q1. Deep fusion models with news headlines.

Reviewer: While the evaluation provides a thorough comparison against standard transformer and LLM baselines, it remains unclear how the framework stacks up against specialized deep fusion models for stock prediction that explicitly combine news headlines with high-frequency time-series data.

Our central question is whether probabilistic market-state forecasting is better suited than point-error minimization to ranking next-day returns and identifying extreme moves, with the input information held fixed. All compared models therefore receive the same daily OHLC price history and differ only in how the forecast is formulated and learned. News–price fusion models address a different question: they add a second input modality, so a comparison with them would measure the value of additional information rather than the effect of the output formulation. Our dual-state output is also not tied to a price-only encoder and could replace the regression output of such a fusion model. We therefore view these models as complementary to, rather than competing with, our framework.

W2/Q2. Sensitivity at M=40M=40.

Reviewer: While the codebooks demonstrate stability across a range from M=5 to M=40, the sharp performance deterioration observed when applying the upward codebook to downward events at M=40 raises questions about structural robustness; to what extent does this sensitivity to hyperparameter choices limit the model's practical generalizability in real-world deployments?

We believe this concern arises from reading an ablated variant as the proposed model. In Table 3, the row that deteriorates sharply at M=40M=40 (marked × in the q−q^- column) is not our model: it scores downward events using the upward codebook alone, a variant included precisely to test whether the second codebook is necessary. The proposed model, which uses the dedicated q−q^- score, is stable from M=5M=5 to M=40M=40:

PeriodDownward scoreAUROC, M=5AUROC, M=40AP, M=5AP, M=40
2015–2019Dedicated q−q^- (ours).7557.7576.1236.1235
2015–2019Upward codebook only.7585.2484.1269.0231
2021–2025Dedicated q−q^- (ours).7082.7194.0900.0930
2021–2025Upward codebook only.7206.2891.0947.0245

The upward AUROC and AP of our model also change by less than 0.004 between M=5M=5 and M=40M=40 in both periods. As stated in Section 5.4, "the dedicated q−q^- score remains stable". The deterioration therefore shows why a single codebook cannot serve both directions, which is exactly the motivation for the dual codebooks; it does not indicate that the proposed model is sensitive to MM.

W3/Q3. Computational cost.

Reviewer: One concern regarding real-world viability is the absence of any theoretical or empirical analysis of computational cost, leaving the actual training and inference overhead unquantified. Can the authors do something in this regard?

Table 1 reports the size of every compared model. Our model has 0.178M trainable parameters, the smallest among all methods. The learned baselines are 1.6× to 47.5× larger (Autoformer 0.291M, FEDformer 0.381M, PatchTST 0.403M, iTransformer 6.329M, TimeXer 8.445M), and Kronos-small and Kronos-base are 138.9× and 575.4× larger (24.7M and 102.3M).

AuthorsOpenReview ↗

Response to Reviewer 3kNS (2/2)

W4. Portfolio simulation.

Reviewer: I could not find a portfolio simulation with simulated returns over time.

The paper does not include a portfolio simulation, by design. Our claims concern return ranking and tail-event identification, which we evaluate directly with Spearman IC, Kendall's τ, AUROC, AP, AUPRC, and DP@N on the ten indices (Section 5, Table 9). A portfolio simulation would add choices that are independent of the forecasts, such as position sizing, rebalancing frequency, transaction costs, and tradability across markets, so its outcome would reflect these choices as much as forecast quality. Moreover, there is currently no satisfactory way to run a portfolio backtest on the indices themselves. In many markets an index cannot be traded directly; exposure must be obtained by trading its constituent stocks or index ETFs, which introduces replication costs, tracking error, and differences in trading hours and market access. Whether a backtest built on such proxies reflects realistic trading conditions is itself debatable.

W5/Q4. Validation safeguards for Figure 5.

Reviewer: I am a bit skeptical about AUROC being so high in the bar plot in Figure 5. In regards to Figure 5, what validation safeguards were put in place for such stellar performance, and have the authors ruled out potential data leakage or evaluation issues?

We thank the reviewer for checking this carefully. The following safeguards are in place:

  • Chronological splits. Three non-overlapping train–validation–test splits (1999–2008 / 2009–2014 / 2015–2019, 2005–2014 / 2015–2020 / 2021–2025, and 2009–2018 / 2019–2024 / 2025–January 2026), with early stopping on the validation period only.
  • Causal normalization. Each 11-day sequence is normalized by its value on the last historical day, so no future observation enters the input (Section 4).
  • Training-only fitting. The input codebook, the directional anchors, the target codebooks, the cluster ordering, and the Top-5/Bottom-5 state sets are all learned from the training split and remain fixed during validation and testing (Section 4; Appendix A.2).
  • Robustness. Results are averaged over three seeds, and significance is assessed with a market-stratified moving-block bootstrap with Holm correction (Appendix A.7). On the most recent split, 2025–January 2026, the upward AUROC remains 0.7517.

Finally, in addition to the released code and data, we have uploaded the test-set predictions to the anonymized repository, so the reported metrics can be inspected and recomputed directly.

Thank you for the fruitful rebuttal. I believe the authors should integrate the new sensitivity results and the discussion of computational costs into the PDF. Also, regarding W1/Q1, I find the motivation for not comparing with them reasonable, but I think it would be useful to integrate such studies into the related work because, at least in my perception, they are very popular approaches in the recent literature. Overall, I find the responses helpful, and I remain supportive of the paper.

Reviewer_TF2dOpenReview ↗
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2
Confidence
2
Informativeness
2
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2
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Paper summary

This paper proposes a probabilistic market-state forecasting framework that replaces point-wise regression with discrete state prediction for financial return ranking and extreme-event identification. It employs a causal Transformer with dual directional classification heads to predict upward and downward market-state probabilities. Experiments on ten equity indices report generally stronger performance in return ranking and tail-event identification against the evaluated forecasting baselines, while ablation studies and rank-fusion experiments examine the effectiveness and complementarity of the proposed approach.

Critical strengths

(1) The paper provides a meaningful alternative to conventional point-wise financial forecasting by explicitly targeting return ranking and directional tail-event identification. The dual directional state prediction framework is well motivated and offers a task-oriented perspective that is relevant to practical financial forecasting. (2) The experiments cover ten equity indices, multiple chronological splits, and several forecasting baselines. Ablation studies and statistical significance tests further support the empirical evaluation. Moreover, rank-fusion experiments show that the proposed method provides complementary information and improves the performance of existing regression models.

Critical weaknesses

(1) The anchor-selection criterion is not sufficiently justified. Anchors are selected using full-patch representations containing next-day information, whereas the forecasting model only uses historical patches. Better separability in the former does not necessarily imply better predictability from historical inputs. (2) The theoretical analysis does not sufficiently connect the proposed state probabilities to actual extreme-return events. The theoretical guarantee concerns codebook-defined events rather than the ±2% thresholds used in the experiments. The practical significance of the discrepancy bound on held-out data remains unclear. (3) The five learned regression baselines use MAE for point forecasting, whereas the proposed method directly optimizes directional classification. Comparisons with external methods specifically designed for return ranking or event prediction are missing, making it difficult to establish its advantages over task-aligned alternatives.

Questions for authors

(1) Can the authors compare the proposed anchor selection with fixed anchors or alternatives based only on historical patches? How do these choices affect forecasting performance? (2) Can the authors report held-out purity and coverage of the selected states for the ±2% events? How many extreme events fall into unselected states, and how stable are these results across different codebook fits? (3) Have the authors considered comparisons with methods specifically designed for return ranking or directional event prediction? Such comparisons would help establish the advantages of the proposed approach.

3 comments
AuthorsOpenReview ↗

Response to Reviewer TF2d (1/2)

We thank the reviewer for the constructive comments. We address each point below.

W1/Q1. Anchor-selection criterion. We would like to clarify the role of the anchors. They are used only to construct the target states, and we do not use them to argue for predictability.

(1) The angular transformation is applied only to the output. We believe the concern may arise from Section 4B, which states that anchors are selected from "full-patch geometric representations." This angular representation of all ten patches (Eq. 2) is used only to score candidate anchors on the training split and is never fed to the model. The model input consists of the nine historical tokens obtained by Euclidean K-Means on the raw patches (Section 4A), so it involves no angular transformation and does not depend on the anchors. After selection, the anchors are fixed and used only to define the target space: the next-day close ratio C~i\tilde C_i is mapped by gb(C~i)g^b(\tilde C_i), on which the target codebook is fitted (Section 4C.1). Defining target states from next-day information is analogous to defining class labels from future returns, and no future information enters the input.

(2) The Fisher criterion is a target-quantization criterion. We do not claim that separability in the full-patch representation implies predictability from historical inputs. The criterion selects anchors that separate extreme from non-extreme samples in the transformed representation (Section 5.4). Proposition B.6 shows that the anchor sets the local weight wa(y)w_a(y) of the quantization, which determines how codebook resolution is allocated across return levels. Whether the resulting states can be predicted from history is evaluated out of sample.

(3) Out-of-sample effect of anchor choices.

  • Removing the directional anchors (shared K=200K=200 codebook) lowers Spearman IC from 0.0372/0.0364 to 0.0354/0.0314 in 2015–2019/2021–2025 (Table 2).
  • Selecting anchors from the target close alone instead of the full patch lowers IC to 0.0320/0.0298, upward AUROC from 0.8131/0.7741 to 0.7958/0.7479, and downward AUROC from 0.7557/0.7082 to 0.7360/0.7036 (Table 3).

Anchor choices are therefore validated by held-out forecasting performance. Among the evaluated options, the full-patch criterion yields target states that the model predicts best from historical inputs.

W2. Link between the theory and ±2% events. Appendix B is intended as a theoretical interpretation rather than a guarantee for the ±2% events: Theorem B.5 concerns the codebook-induced event, and Appendix B.2 states that qbq^b is not a calibrated probability of crossing 2%. Eq. 18 bounds the gap between qbq^b and the ±2% event posterior by two terms, contamination of the selected states and events falling into unselected states, which correspond to the purity and coverage reported under Q2 below.

The practical significance of this bound can be seen in Table 3. The Top-5 and Bottom-5 states represent a more concentrated event than the complete 2% tail (Appendix B.2), whereas the M=40M=40 states closely match the ±2% events on held-out data (Q2). Moving from M=5M=5 to M=40M=40 changes the AUROC and AP for ±2% events by at most 0.0112 and 0.0031. The ranking ability of qbq^b for ±2% events therefore does not hinge on the codebook-induced event matching the threshold event exactly.

Q2. Held-out purity and coverage of the selected states. We first clarify that the model does not predict which state a test observation belongs to. It outputs the summed probability of the selected extreme states, qib=∑k∈Sbpi,kbq^b_i=\sum_{k\in S^b}p^b_{i,k}, which serves as a ranking score. Purity and coverage are obtained by assigning realized test returns to the fixed states and therefore do not involve the model's predictions; the relation between qibq^b_i and ±2% events is measured by the held-out AUROC and AP (Table 9). We nonetheless report these statistics as requested, using the M=40M=40 states, which contain more test observations than the Top-5 and Bottom-5 states.

Test periodDirectionPurity (seed 42)Coverage (seed 42)Purity (6 seeds)Coverage (6 seeds)
2015–2019Up100%61%100.0 ± 0.0%69.3 ± 12.6%
2015–2019Down100%87%100.0 ± 0.0%83.1 ± 4.3%
2021–2025Up99.7%84%99.7 ± 0.0%76.9 ± 4.7%
2021–2025Down100%92%96.1 ± 9.6%86.5 ± 11.5%

Seed 42 is the codebook used in the paper; the last two columns report the mean ± standard deviation across six K-Means initializations of the target codebooks (seeds 42 and 0–4). For the codebooks used in the paper, purity is at least 99.7%, and 61–92% of the realized ±2% events fall into the selected states, so the remaining 8–39% fall into unselected states. The six-seed columns show how stable these results are across codebook fits.

AuthorsOpenReview ↗

Response to Reviewer TF2d (2/2)

W3/Q3. Comparison with task-aligned methods. Our central question is whether probabilistic market-state forecasting is better suited than point-error minimization to ranking next-day returns and identifying extreme moves. MAE-trained regressors are therefore the primary baselines by design, as point-error minimization is the prevailing objective in financial forecasting. We do not claim that our model outperforms every method designed for these tasks.

Directional event prediction. Section 5.5 compares two standard directional event-prediction formulations under the same input tokens and Transformer backbone: a dual binary head trained with BCE on the ±2% events and a three-class head trained with CE for downward, neutral, and upward movements.

  • Return ranking. In 2015–2019 and 2021–2025, the dual binary head reaches Spearman ICs of 0.0422 and 0.0390, the three-class head 0.0442 and 0.0378, and our codebooks 0.0372 and 0.0364, all above PatchTST, the strongest regression baseline (0.0317 and 0.0140; Table 9).
  • High-confidence event concentration. DP@1000 reaches 15.60% and 13.57% for our codebooks, compared with 14.95% and 12.85% for the dual binary head and 14.78% and 13.07% for the three-class head (Fig. 8d).

These task-aligned classifiers confirm that probabilistic outputs improve over regression, while our codebooks place more realized extreme events among the most confident predictions.

Continuous distributional baselines. Out of respect for the reviewers' suggestions, we also added continuous distributional baselines, a Gaussian NLL head and a quantile (pinball-loss) head, on the same discrete input tokens and Transformer backbone (see our response to Reviewer kVbL, W1/Q1). Our dual codebooks rank first in 6 of the 12 reported entries, including DP@1000 in both test periods, and all probabilistic heads remain far above the MAE-trained baselines.

Thank you for the detailed rebuttal and additional experiments. The clarifications address several of my concerns. However, the theoretical connection to actual extreme-return events remains limited, and the task-aligned baselines outperform the proposed method in return ranking. Therefore, while I appreciate the authors' efforts, I will maintain my original rating.

Reviewer_kVbLOpenReview ↗
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2
Confidence
3
Informativeness
2
Presentation
2
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2
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Paper summary

The paper proposes a discrete market-state forecasting framework to address the mismatch between point-forecasting accuracy and return ranking or extreme-movement detection. It discretizes historical price patterns and future returns using K-means codebooks, with separate directional target representations derived from optimized anchors. A shared Transformer predicts upward and downward state distributions, which are aggregated into ranking and tail-event scores. Experiments on ten equity indices report improvements over regression baselines in rank correlation and tail-event detection metrics. The paper also presents ablation studies, a rank-fusion strategy, and theoretical analyses interpreting the proposed approach.

Critical strengths
  1. The paper prevents data leakage by fitting all adaptive components on training data only. Improvements are evaluated across multiple periods with statistical significance tests and out-of-pretraining comparisons. This rules out the usual in-sample selection / lucky-seed explanation, so the ranking and tail-detection gains are credible as real signal rather than evaluation artifacts.

  2. The ablations identify input discretization as a major contributor to performance and demonstrate the benefit of directional codebooks, particularly for downward tail-event detection.

Critical weaknesses
  1. Missing distributional regression baselines. The paper compares primarily against point-forecasting models trained with MAE, without considering quantile or probabilistic regression alternatives. Consequently, it remains unclear whether the improvements come from discretization or simply from better alignment between the training objective and evaluation metrics.

  2. Lack of probability calibration. Although the method is presented as probabilistic forecasting, the proposed directional scores are not calibrated to actual tail-event probabilities. Without calibration analysis, their interpretation as meaningful event probabilities remains questionable.

Questions for authors
  1. Could you add a continuous distributional baseline (e.g., Gaussian NLL head, pinball/quantile loss, or CRPS) using the same discrete input tokens and Transformer backbone, scored for ranking/tail the same way?

  2. Please report calibration (reliability diagram / ECE) of q⁺, q⁻ against the ±2% events. Given B.2's disclaimer, is any claim beyond ranking defensible?

2 comments
AuthorsOpenReview ↗

Response to Reviewer kVbL

We thank the reviewer for the constructive comments. We address each point below.

W1/Q1. Continuous distributional baselines. Our central question is whether probabilistic market-state forecasting is better suited than point-error minimization to ranking next-day returns and identifying extreme moves. This claim rests on the comparison with point regression; it neither requires nor would be overturned by comparisons with other methods. We do not claim that our output formulation outperforms every probabilistic alternative. We nonetheless appreciate the reviewer's suggestion and ran the requested experiment.

Setup. We keep the discrete input tokens, the causal Transformer backbone, the training protocol, and the seeds (1337, 2337, 3337) unchanged, and replace only the dual classification heads:

  • Gaussian NLL head: predicts the mean μ\mu and standard deviation σ\sigma of the next-day return; tail scores are P(R≥0.02)P(R\ge 0.02) and P(R≤−0.02)P(R\le -0.02).
  • Quantile head: trained with the pinball loss over seven quantiles from 0.05 to 0.95; tail scores are the 0.95 quantile and the negated 0.05 quantile.

As for our model, return ranking is evaluated with the upward score. Results are mean ± std over three seeds; ours are taken from Table 9 and Fig. 8d.

PeriodOutput headSpearman ICUp AUROCUp APDown AUROCDown APDP@1000
2015–2019Ours.0372±.0032.8131±.0046.1510±.0060.7557±.0006.1236±.004115.60%
Gaussian NLL.0381±.0018.8111±.0049.1487±.0011.7519±.0053.1265±.004714.88%
Quantile.0412±.0017.8144±.0041.1447±.0032.7536±.0032.1239±.004614.83%
2021–2025Ours.0364±.0036.7741±.0036.1336±.0057.7082±.0036.0900±.000613.57%
Gaussian NLL.0311±.0049.7725±.0034.1395±.0050.7208±.0067.0911±.002613.53%
Quantile.0321±.0039.7725±.0028.1399±.0026.7171±.0058.0893±.003313.43%

Summary. Our dual codebooks rank first in 6 of the 12 entries, including DP@1000 in both periods, while the continuous distributional heads remain competitive. All three probabilistic heads are far above the MAE-trained baselines, whose upward AUROC ranges from 0.5631 to 0.6325 in 2015–2019 (Table 9). This confirms that replacing point regression with probabilistic, tail-oriented prediction on discrete input tokens drives the improvement over regression. Among these probabilistic formulations, the dual codebooks provide the strongest overall performance. We will add this comparison to the appendix.

W2/Q2. Calibration of q±q^{\pm}. We may not have fully understood the intent of this question, since our model uses these probabilities only to rank observations. The claims of our paper concern return ranking and tail-event identification, and none of them relies on q±q^{\pm} being calibrated probabilities of the ±2% events.

(1) The contributions and all experiments depend only on the ordering of q±q^{\pm}. Spearman IC, Kendall's τ, AUROC, AP, AUPRC, and DP@N are invariant to any strictly increasing transformation of the scores, and rank fusion combines rank positions "without retraining or numerically calibrating either model" (Section 1, lines 63–65). No experiment interprets the magnitude of q±q^{\pm} as an event probability.

(2) q±q^{\pm} is not designed to estimate the ±2% event probability. By construction, qbq^b is the probability of entering the selected extreme states (Theorem B.5), as stated in Appendix B.2. A reliability diagram or ECE against the ±2% events would compare qbq^b with an event it is not defined to predict, so the resulting gap would reflect this difference in definition rather than the quality of the forecasts.

(3) Meaning of "probabilistic". In our framework, "probabilistic" refers to the form of the model output: a probability distribution over market states, learned with cross-entropy, a strictly proper scoring rule. The scores derived from these distributions are evaluated as ranking signals, as reflected in the title. We will make this scope explicit in the revision.

Thank you for running the additional distributional baselines and clarifying the calibration scope. Since the quantile head performs comparably to the dual codebooks on Spearman IC (0.0412 vs. 0.0372 in 2015–2019; 0.0321 vs. 0.0364 in 2021–2025), the advantage over standard probabilistic heads remains limited. I will keep my rating at 2 and encourage adding these comparisons and the q± scope clarification to the main text.

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

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