acceptodds
Under review as a conference paper at ICLR 2027

Threshold-Consistent Learning for Continuous Forecasting and Rare-Event Detection

12 views

Abstract

Continuous forecasting and rare-event detection are often treated as separate objectives in financial time-series forecasting, although they describe two aspects of the same future outcome. A regression model may achieve low prediction error while assigning insufficiently high scores to rare but decision-critical events, such as unusually large positive returns. We propose Threshold-Consistent Continuous–Discrete Learning (TCDL), a unified framework that jointly learns continuous return prediction and threshold-defined event states. The key idea is to couple the continuous prediction with a discrete state representation through a threshold-consistency objective, encouraging the predicted return and inferred event state to remain logically aligned during optimization. In this way, the continuous task preserves fine-grained numerical information, while the discrete task improves sensitivity to rare tail events. We evaluate TCDL across major global market indices against strong time-series forecasting baselines. The proposed method maintains strong regression accuracy while achieving competitive rare-event discrimination and substantially improving tail AUPRC over conventional regression and joint-learning objectives. Statistical significance tests and controlled ablations further isolate the contribution of the threshold-consistency mechanism. These results show that coupling continuous predictions with threshold-defined decision states provides a simple and effective learning paradigm for forecasting problems in which rare events are more consequential than average prediction error.

Primary area:
learning on time series and dynamical systems
Keywords:
threshold-consistent learning, continuous-discrete learning, rare-event detection, structured prediction, multi-task learning, time-series forecasting, financial time series

Reviews

Among:
Shape:
1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_L4ySOpenReview ↗
Rating
2(+1)
Confidence
3
Informativeness
1
Presentation
2
Soundness
2(+1)
Read review
Paper summary

The paper trains two heads together on nine equity indices: a regression head for the 4-day-ahead return, and a 61-class state classifier with an explicit right-tail class (return > 3%). A one-way squared hinge pushes the regression output above the tail threshold whenever the classifier predicts the tail class. The inputs are five tokens, obtained by 1-D K-means on the RMS magnitudes of overlapping OHLC windows. The evaluation covers two test periods and three seeds. It reports MSE/MAE and tail AUPRC/AUROC, with the regression output as the score, plus loss ablations and a backtest.

Critical strengths

Table 3 is a clean comparison: the same backbone with ten objectives, including a ground-truth hinge control. The proposed term improves the regression output's AUPRC over MSE+CE in both periods (0.111 to 0.146, 0.084 to 0.133). The protocol avoids leakage: the splits are chronological, and K-means and scaling are fit on training data only.

Critical weaknesses

My main concern is that the authors' own released run does not show the central claim (threshold-consistent coupling), and the other gains are marginal.

  1. The coupling does not do what the paper claims. I looked at the saved output of the released notebook (2021-2025, seed 1, default settings, with one extra dropout draw). The classifier predicts the tail class for 350 test samples, but the regression output exceeds 1.03 for only 3 of them. During training, the crossing rate stays at 1-3%. So the hinge acts as an upward bias on flagged samples, not as a consistency constraint. In the same run, the classifier's tail probability is a better tail score (AUPRC 0.154, AUROC 0.636) than the regression output (0.146, 0.621). The paper evaluates only the regression output, so it never shows that the coupling adds anything over using the classifier directly.

  2. The gains are small and the comparisons are uneven. The Random Walk has lower MSE in both periods (Table 2). TCDL's MAE advantage over it is 0.15% and 0.03%, and the paper does not test it, so the claim of a clear point-forecast advantage (L261-262) is not supported. Tail AUROC is about 0.59, and Autoformer has higher AUPRC in both periods. The baselines predict the close price with MAE loss and identity scaling, while TCDL gets normalised inputs and a standardised return target. There is also no volatility baseline, which is the obvious reference for 3% moves.

Questions for authors
  1. Please report tail AUPRC/AUROC with the classifier probability as the score, for MSE+CE and TCDL. Please also report the fraction of argmax-tail samples with r̂ > 1.03, for all seeds and both periods.

  2. The notebook's seed-1 tail metrics (0.146 / 0.621) are outside what Table 2's three-seed mean ± SD allows (0.1326 ± 0.0062 and 0.5896 ± 0.0121). Which code produced Table 2, and how large is the seed variance over more seeds?

  3. Please add per-index Diebold-Mariano tests against the Random Walk and a volatility baseline (realised volatility or GARCH-implied P(r > 1.03)). Does the score also rank left-tail events?

  4. How were the defaults (0.5, 0.1, 60) chosen? They give the best test AUPRC in all six groups of Table 6.

  5. For the backtest, please compare against random-timing overlays with the same activation rate and against baseline signals, with a significance test.

Related work that may be of interest: Ding et al. (KDD 2019) and NEC+ (Li et al., AAAI 2023).

6 comments
AuthorsOpenReview ↗

Response to Reviewer L4yS (1/2)

We mean no offense and simply wish to state the following facts honestly. After completing this paper, we gave it to large language models (e.g., ChatGPT and Claude) for a pre-submission review. However much we emphasized these points, the models consistently made the same two misreadings:

  1. They assumed that the crossing loss is meant to change test-time predictions. The paper never discusses test-time crossing; throughout, the crossing term is a training-time penalty within the loss (Section 4).
  2. They kept asking for a comparison with the classification head. The paper is about the regression head: a single continuous forecast with low point error that also identifies right-tail states and ranks observations. The classification head outputs probabilities and cannot provide a point forecast at all, so comparing the two is outside the scope of this paper.

We found both misreadings, in full, in this review. Reading it late at night, we admit that our blood pressure went up.

W1. The coupling does not do what the paper claims

Reviewer: only 3 of 350 predicted-tail test samples cross 1.03 and the training crossing rate is 1–3%, so the hinge is an upward bias rather than a consistency constraint; the classifier's tail probability is a better score, and the paper never shows what the coupling adds over the classifier.

(1) Training-time penalty, not a test-time constraint. Section 4 defines the crossing term as "only a training-time penalty" that transfers state information "without forcing threshold-consistent predictions toward the decision boundary." It shapes the regression head during training; the paper never reports or claims a test-time crossing rate. What we claim and evaluate at test time is whether the regression output ranks right-tail events higher (AUPRC/AUROC), and these rank-based metrics do not require predictions to exceed 1.03. Because MSE remains the dominant term, predictions stay shrunk toward the mean, so few cross 1.03 even when their ranking improves. Counting test-time crossings therefore does not evaluate the mechanism.

(2) A low crossing rate means the constraint is active. The loss acts precisely on predicted right-tail samples that have not crossed the threshold. A crossing rate of 1–3% means the penalty acts on about 97% of them in every epoch, and their mean squared shortfall decreases from 0.603 to 0.433 (about 28%) during training (see our response to Reviewer xxSR, Q1).

(3) What the coupling adds. With the same backbone, classification head and CE loss, adding the crossing loss raises the AUPRC/AUROC of the regression output from 0.1106/0.4706 to 0.1464/0.5935 (2015–2019) and from 0.0842/0.4596 to 0.1326/0.5896 (2021–2025), with nearly unchanged MSE; the same hinge applied to ground-truth tail samples yields smaller gains (0.1252/0.5532 and 0.1124/0.5848; Table 3), so the benefit comes from conditioning on the model's own predicted state.

W2. Small gains and uneven comparisons

Reviewer: Random Walk has lower MSE; Autoformer has higher AUPRC; the baselines use different targets, losses and scaling; there is no volatility baseline.

Each comparison must be read against both goals of the paper: low point error and informative tail ranking.

(1) Random Walk cannot rank or identify tail events. It predicts r=1r=1 for every sample, so its AUROC is 0.5 and its AUPRC equals the tail rate (hence N/A in Table 2); its low MSE reflects the concentration of four-day return ratios near 1 (Section 5.1). Pure point-error minimization drifts toward this flat forecast, the failure mode motivating the paper (Section 3). TCDL matches its point accuracy (MSE within 0.000005 and 0.000003, lowest MAE in both periods) while also ranking tail events. Significance tests are therefore run against the learned baselines, the only models that can serve both purposes: the MSE and MAE gains are significant against all eight in 2015–2019 and six of eight in 2021–2025.

(2) Higher AUPRC comes at a much larger point error. Autoformer's higher AUPRC (0.1503, 0.1684) comes with about three times TCDL's MSE (0.001616 vs. 0.000522; 0.001303 vs. 0.000488), and TimeXer's (0.1404 in 2021–2025) with larger MSE and MAE. Such models favor one goal at the expense of the other (Section 5.1).

(3) Same target, same evaluation. All models predict the four-day-ahead close, and all tail metrics use the regression output. The objective differs because it is the factor under study; with identical inputs, normalization and backbone (Table 3), tail AUPRC rises from 0.0923 (MSE only, i.e. the same model trained as a standard regressor) to 0.1464 and from 0.0864 to 0.1326.

(4) Volatility models address a different task. They forecast the scale of returns, not the return itself, and provide neither a point forecast nor a direction-specific ranking.

AuthorsOpenReview ↗

Response to Reviewer L4yS (2/2)

Q1. Classifier-probability metrics and the fraction of argmax-tail samples with r̂ > 1.03

Reviewer: report classifier-probability AUPRC/AUROC for MSE + CE and TCDL, and the fraction of argmax-tail samples with r̂ > 1.03 for all seeds and both periods.

Both requests rest on the two misreadings described above: the classifier cannot provide a point forecast, so its tail metrics fall outside the scope of the paper, and the crossing loss is a training-time penalty, so the test-time crossing fraction does not measure the mechanism (W1). Nevertheless, the requested fraction is higher with the crossing loss even at test time, where the loss is not applied:

PeriodModelSeed 1Seed 42Seed 1337Mean
2015–2019MSE + CE5.4%6.9%4.7%5.7%
2015–2019TCDL9.0%5.2%8.3%7.5%
2021–2025MSE + CE0.5%0.0%0.0%0.2%
2021–2025TCDL0.6%0.4%2.2%1.1%

The fraction remains small, as expected for a soft training-time penalty with weight 0.1 under a dominant MSE term; what the paper claims is the improved ranking of the regression output (Table 3).

Q2. Which code produced Table 2, and how large is the seed variance?

Reviewer: the notebook's seed-1 metrics (0.146/0.621) fall outside what Table 2's mean ± SD allows.

The released notebook is the code that produced Table 2, including the extra dropout call noted by the reviewer. We have uploaded the training log (backtest_2021_seed1.log) and the per-sample test predictions (test_predictions.csv) of the Table 2 run for 2021–2025, seed 1. They show the same model with 178,558 parameters and give AUPRC/AUROC of 0.1370/0.6036; together with seeds 42 (0.1255/0.5825) and 1337 (0.1353/0.5828), this yields exactly 0.1326 ± 0.0062 and 0.5896 ± 0.0121. The outputs saved in the released notebook come from a Google Colab run, whereas Table 2 was run on a local CPU (macOS, Python 3.9, PyTorch 2.8.0). PyTorch does not guarantee identical results across platforms even with fixed seeds, which is why we report three-seed statistics; within a fixed environment, the seed variance is the SD reported in Table 2 (0.0062 for AUPRC in 2021–2025). The Colab run is better than ours, so Table 2 does not reflect a selection of favorable runs.

Q3. Diebold–Mariano tests, a volatility baseline and left-tail ranking

Reviewer: per-index Diebold–Mariano tests against Random Walk, a volatility baseline, and whether the score also ranks left-tail events.

The paper does not claim to beat Random Walk in point error; it claims to match it while providing tail ranking, which Random Walk cannot provide: its AUROC is 0.5 and its AUPRC equals the tail rate (6.7% in 2021–2025) (W2), so a test of equal accuracy would not change the conclusion. A GARCH-implied P(r>1.03)P(r>1.03) gives no point forecast and rises with predicted volatility, so it scores large falls as highly as large rises. Left-tail ranking is outside the design: the task targets right-tail opportunities, with a single explicit right-tail state and a one-sided crossing loss.

Q4. How were the defaults (0.5, 0.1, 60) chosen?

Reviewer: the defaults give the best test AUPRC in all six groups of Table 6.

They are a priori round values (the classification term at half the weight of the regression term, a small weight for the auxiliary crossing term, and an intermediate vocabulary size), fixed before the sensitivity analysis and shared by both periods and all nine markets; Table 6 is a post-hoc, one-at-a-time analysis around them. The defaults lead only in AUPRC: in 2021–2025, other values give lower MSE (0.000484 vs. 0.000488), lower MAE (0.015774 vs. 0.015831) and higher AUROC (0.5953 vs. 0.5896), which a configuration tuned on test data would not do. The AUPRC lead is also often within seed variation (e.g., λcls = 0.10 gives 0.1322 ± 0.0095 vs. 0.1326 ± 0.0062).

Q5. Random-timing overlays, baseline signals and significance

Reviewer: compare the backtest against random-timing overlays with the same activation rate and against baseline signals.

The backtest illustrates the economic use of the regression output, and Section 5.5 concludes only that the scores "may provide useful information for dynamically adjusting exposure"; models are compared on the forecasting and tail metrics in Table 2. A random-timing overlay cannot raise the Sharpe ratio: applying the 0.5× overlay in a fraction pp of periods independently of returns gives at most (1+0.5p)/1+1.25p<1(1+0.5p)/\sqrt{1+1.25p}<1 times the Buy-and-Hold Sharpe ratio (about 0.99 at p=0.1p=0.1), before transaction and borrowing costs reduce it further. The TCDL overlay instead raises the average Sharpe ratio in all six settings of Table 4 (0.4333 → 0.4401–0.4603; 0.5307 → 0.5418–0.5783; +1.6% to +9.0%) despite costs, so the gain reflects signal timing rather than extra exposure.

Thanks for the reply and for uploading the log and predictions.

I recomputed the metrics from test_predictions.csv and get 0.1370 / 0.6036, which is consistent with Table 2, so I withdraw that concern. I also put the crossing-rate point too strongly, given that Section 4 describes a soft penalty, though I would still drop "logically aligned" from the abstract and conclusion.

My main remaining concern is the volatility baseline (my Q3), so I computed it from your files: trailing 20-day realised volatility at the forecast origin, no fitting (the date column in the CSV is the target date, so the origin is four trading days earlier). On the same 11,192 rows it gets AUROC 0.723 vs 0.604 for TCDL, and AUPRC 0.166 vs 0.137. Its AUROC is also higher in each of the nine markets (mean 0.693 vs 0.612). You're right that volatility isn't direction-specific: it ranks falls of the same size (r < 1/1.03) above chance too, at 0.641. But so does TCDL's output (0.562), and among the 1,520 moves beyond 3% either way, volatility separates rises from falls about as well (0.589 vs 0.546). For 2015-2019, I rebuilt the test set from the same price files (11,213 rows vs your 11,180) and get AUROC 0.749, vs 0.594 for TCDL in Table 2.

A simple non-learned score ranks the right-tail events better than the model, and I think the paper needs that comparison. I'm raising my score to 2 since the reproducibility issue is resolved, but I still lean towards rejection because of this.

Reviewer_o7PFOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

This paper propose Threshold-Consistent Continuous–Discrete Learning (TCDL), a unified framework that jointly learns continuous return prediction and threshold-defined event states. Its key idea is to couple the continuous prediction with a discrete state representation through a threshold-consistency objective, encouraging the predicted return and inferred event state to remain logically aligned during optimization. Consequently, the continuous task retains fine-grained numerical information, while the discrete task improves sensitivity to rare tail events.

Critical strengths

A practically relevant problem with a simple formulation. The paper addresses the mismatch between pointwise regression accuracy and threshold-based event detection. TCDL combines continuous forecasting, discrete state classification, and a threshold-consistency penalty without introducing a complex architecture, making the approach straightforward to implement.

Critical weaknesses
  1. The performance gains of TCDL in rare-event detection are not sufficiently significant. TCDL does not outperform the strongest baseline in AUPRC in either test period: Autoformer performs better in 2015–2019, while TimeXer performs better in 2021–2025. The paper also needs stronger evidence that the gains are robust to threshold choices, cross-market differences, and the evaluation protocol, particularly given the practical claims supported by the backtest.

  2. There is a potential issue with the crossing loss. If I understand correctly, the crossing loss is applied only to samples whose predicted class is already the right-tail state, with sample selection determined by a non-differentiable argmax. As a result, the selection mechanism provides no direct gradient signal to change which samples are selected, potentially limiting the loss's ability to improve tail-event recognition. Although the loss may still influence the classifier indirectly through shared representations, the paper does not sufficiently explain or empirically establish how this mechanism improves cross-task consistency and tail discrimination.

Questions for authors
  1. Does the crossing loss provide a meaningful learning signal to the classification head? Can the authors clarify exactly how the crossing loss improves tail-event discrimination rather than merely shifting the regression predictions of samples already classified as tail events?

  2. Is the improvement attributable to consistency itself or simply to an additional threshold-aware regression penalty?

  3. The experiments primarily use a fixed four-day return threshold of 1.03, corresponding to a 3% return. How sensitive is the method to the choice of the event threshold?

3 comments
AuthorsOpenReview ↗

Response to Reviewer o7PF (1/2)

We originally did not intend to submit a rebuttal, because the initial scores include a 1. Out of respect for the reviewers, however, we have tried our best to respond to the points where the paper has been misread.

W1. Gains in rare-event detection and their robustness

Reviewer: TCDL does not outperform the strongest baseline in AUPRC (Autoformer in 2015–2019, TimeXer in 2021–2025); stronger evidence is needed that the gains are robust to threshold choices, cross-market differences and the evaluation protocol.

(1) The paper does not claim the highest AUPRC. Its goal is a single continuous forecast with low point error that also ranks right-tail events, and Section 5.1 states that TCDL is competitive "without uniformly dominating the strongest baseline." The baselines with higher AUPRC obtain it at a much larger point error: Autoformer (0.1503 and 0.1684) has about three times TCDL's MSE (0.001616 vs. 0.000522; 0.001303 vs. 0.000488), and TimeXer (0.1404 in 2021–2025) has larger MSE and MAE (0.000536 and 0.016649 vs. 0.000488 and 0.015831). TCDL achieves the lowest point error while remaining competitive in tail discrimination, and in 2015–2019 its AUPRC is significantly higher than four of the eight learned baselines after Holm correction (Table 2).

(2) Cross-market differences. Cross-market consistency is assessed per index: each metric is averaged over seeds for each of the nine indices, and TCDL is compared with each learned baseline using a paired Wilcoxon signed-rank test with Holm correction (Section 5). The MSE and MAE gains are significant against all eight learned baselines in 2015–2019 and against six of eight in 2021–2025.

(3) Evaluation protocol. The protocol uses two chronological splits, a separate validation period for checkpoint selection, tokenizers and scaling fitted on training data only, and three seeds per configuration. Reviewers xxSR and L4yS both noted that this protocol is sound and avoids leakage.

W2. The argmax selection in the crossing loss is non-differentiable

Reviewer: the crossing loss is applied only to samples whose argmax class is the right-tail state; the selection is non-differentiable and gives no direct gradient, which may limit the loss's ability to improve tail-event recognition; the paper does not establish how it improves consistency and tail discrimination.

We agree that the argmax selection itself receives no gradient. This is intended, and we believe the concern arises from reading the crossing loss as a training signal for the classifier, which it is not.

(1) The crossing loss is designed to train the regression output, not the classifier. TCDL couples the two heads in one direction only: the classifier is trained directly by CE, and its right-tail prediction is used to supervise the continuous forecast. Section 4 states that the design "transfers discrete right-tail supervision to the continuous forecast," and that "the reverse direction is not enforced." Its gradient therefore flows into the regression head and the shared representation, which is exactly where it is meant to act. The hard argmax is deliberate: unlike probability weighting, it penalizes only samples that the classifier actually assigns to the right-tail state. The quantity the paper improves and evaluates is the tail discrimination of the regression output, not the classifier's recognition of tail events.

(2) The effect is established by controlled comparisons. In Table 3, MSE + CE uses the same backbone, classification head and CE loss and differs only by removing the crossing loss; adding it raises the AUPRC/AUROC of the regression output from 0.1106/0.4706 to 0.1464/0.5935 in 2015–2019 and from 0.0842/0.4596 to 0.1326/0.5896 in 2021–2025. Applying the same hinge to ground-truth tail samples instead of predicted ones yields smaller gains (0.1252/0.5532 and 0.1124/0.5848), showing that the benefit comes from conditioning on the model's own predicted state rather than from an additional threshold penalty. During training, the penalty acts on about 97% of the predicted right-tail samples in every epoch, and their mean squared shortfall decreases by about 28% (see our response to Reviewer xxSR, Q1).

(3) Giving the classifier a signal does not help. Appendix A.9 tests exactly this alternative: a bidirectional variant adds a regression-to-classification loss that pushes the classifier toward samples whose regression output crosses the threshold. It does not improve performance consistently: it is worse on all four metrics in 2015–2019, and in 2021–2025 its AUPRC drops from 0.1326 to 0.1282 (Table 8). Occasional regression crossings are too noisy to supervise the classifier, which is why TCDL keeps the one-way design.

AuthorsOpenReview ↗

Response to Reviewer o7PF (2/2)

Q1. Does the crossing loss give the classification head a meaningful signal?

Reviewer: does the crossing loss provide a meaningful learning signal to the classification head, and how does it improve tail-event discrimination rather than merely shifting the regression predictions of samples already classified as tail events?

We believe this question misses the central point of the paper. The crossing loss is not meant to give the classification head a learning signal; the classifier is trained by CE, and the crossing loss transfers its right-tail prediction to the continuous forecast (Section 4; see W2). The tail discrimination that the paper improves and evaluates is that of the regression output.

Shifting the regression predictions of predicted right-tail samples is therefore not a side effect but the mechanism itself, and it is not limited to the flagged samples. The gradient also flows into the shared representation and the regression head, which are applied to every sample, so the ranking of the regression output changes over the whole test set. During training, the penalty acts on about 97% of the predicted right-tail samples in every epoch, and their mean squared shortfall decreases by about 28% (see our response to Reviewer xxSR, Q1). This is what Table 3 measures: AUPRC and AUROC are computed over all test samples, and adding the crossing loss to MSE + CE raises them from 0.1106/0.4706 to 0.1464/0.5935 in 2015–2019 and from 0.0842/0.4596 to 0.1326/0.5896 in 2021–2025. Conversely, giving the classifier a signal from the regression output does not help (bidirectional variant, Table 8; see W2).

Q2. Consistency itself or an additional threshold-aware regression penalty?

Reviewer: is the improvement attributable to consistency itself or simply to an additional threshold-aware regression penalty?

This question is answered directly by a control already included in Table 3. The GT threshold hinge applies the same squared hinge to the regression output, but selects the penalized samples by the ground-truth right-tail label instead of the classifier's prediction. It is therefore exactly an additional threshold-aware regression penalty, without the prediction-conditioned consistency:

PeriodMSE + CEMSE + CE + GT threshold hingeTCDL
2015–2019 (AUPRC / AUROC)0.1106 / 0.47060.1252 / 0.55320.1464 / 0.5935
2021–2025 (AUPRC / AUROC)0.0842 / 0.45960.1124 / 0.58480.1326 / 0.5896

The threshold-aware penalty alone helps, but TCDL improves further in both periods, most clearly in AUPRC (+17% and +18%). Without CE, the GT hinge is weaker still (0.0927/0.5079 and 0.1033/0.5770). This holds even though the GT hinge uses the true labels, which carry more information than the classifier's predictions. The additional gain therefore comes from conditioning the penalty on the model's own predicted state, i.e. from the consistency itself, as stated in Section 5.2.

Q3. Sensitivity to the event threshold

Reviewer: the experiments primarily use a fixed four-day return threshold of 1.03; how sensitive is the method to the choice of the event threshold?

We chose the threshold to define the task, not as a tuning parameter, for three reasons.

(1) It defines a genuinely rare and decision-relevant event. A four-day horizon corresponds to forecasting, at Monday's close, the return through Friday's close. A rise of more than 3% over this window is rare: according to Table 5, it occurs in 11.37% and 10.95% of the pooled training samples and in only 6.95% and 6.68% of the pooled test samples of the two splits, with rates as low as 1.98% in individual markets. Higher thresholds would leave too few positive samples to learn and evaluate a tail state reliably.

(2) It corresponds to market-move levels used in practice. As noted in footnote 1, the 3% level reflects market-move levels used in some trading-control mechanisms.

(3) It is fixed a priori. The threshold is set before training and kept the same for both splits and all nine markets, and it is never adjusted on validation or test data (Appendix A.3).

The method itself does not depend on this specific value: the threshold enters only through the definition of the right-tail state and the crossing loss, and can be set to any decision-relevant level. Since the paper's contribution is the threshold-consistent coupling rather than the choice of a particular threshold, we kept the event definition fixed and focused the experiments on isolating the effect of the coupling (Tables 3 and 8).

Thank you for your response. Most of my concerns have been addressed. However, my main concern regarding the performance gains remains unresolved. After considering the other reviewers' comments, I decide to keep my original score.

Reviewer_xxSROpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper proposes TCDL, which jointly learns return forecasts and discrete market states, with an additional loss encouraging agreement between the two outputs. The experiments examine whether this approach improves the identification of large positive returns without sacrificing forecasting accuracy.

Critical strengths

The motivation is relevant: a model can achieve low average error while providing useful information about large market movements. I found the controlled loss ablations particularly helpful. They provide encouraging evidence that the proposed consistency term improves tail ranking over MSE and MSE+CE on the same backbone.

The chronological evaluation and validation-based model selection are also sensible. I appreciate that the authors report mixed results openly, including the strong Random Walk baseline and cases where competing models achieve better tail discrimination.

Critical weaknesses

First, the link between the motivation and the proposed constraint needs more explanation. Predicting a tail event and estimating the conditional mean are different tasks. The tail state can be the classifier’s most likely individual class without implying that the expected return exceeds 3%. The constraint may still be a useful learning bias, but describing this disagreement as a logical inconsistency seems too strong. Comparing the regression score directly with the classifier’s tail probability would help show what the coupling adds.

Second, the financial meaning of the threshold is unclear. A 3% move over four days is considerably more unusual in some markets and volatility regimes than others. Is the objective to identify an absolute return opportunity or an unusually large movement relative to market conditions? A clearer explanation, supported by a limited threshold-sensitivity analysis, would help. The focus on positive tails is reasonable for opportunity detection, although the broader rare-event claims should acknowledge this scope.

Third, the comparisons leave some uncertainty about where the gains come from. The external baselines use different targets and training objectives. A matched comparison with one or two representative models would be more convincing. Per-market ablation results would also help establish whether the pooled gains are broadly shared.

Finally, the backtest is a useful addition, but an exposure-matched benchmark would help separate signal quality from the effect of extra leverage. Execution timing should also be clarified, since the inputs include prices at the forecast-origin close.

Questions for authors

In addition to the above identified weakness:

  • How often does the tail-state constraint activate, and does it reduce disagreement between the heads?
  • Does the coupled regression score outperform the classifier’s tail probability?
  • Are the gains robust to the event threshold and to an exposure-matched trading comparison?
2 comments
AuthorsOpenReview ↗

Response to Reviewer xxSR (1/2)

Since another reviewer has recommended clear rejection, we hold no real hope for this submission and initially considered not writing a rebuttal. Out of respect for the reviewers' time and for our own work, we have nevertheless tried to answer each point of this review as carefully as we can.

W1. Link between the motivation and the constraint

Reviewer: predicting a tail state and estimating the conditional mean are different tasks; describing the disagreement as a logical inconsistency seems too strong; what does the coupling add?

We thank the reviewer for this point. We agree that predicting a tail state and estimating the conditional mean are different tasks, and the paper does not claim that an argmax right-tail prediction implies an expected return above 3%. The term "logically aligned" refers to the training objective: during optimization, the crossing term penalizes cases in which the classifier predicts the right-tail state while the regression output remains below the threshold (Section 4). It acts as a prediction-conditioned learning bias rather than a logical requirement, as the reviewer also suggests.

Role of the constraint. Our goal is a single continuous forecast that retains point accuracy while being informative about right-tail events. The regression output is therefore the evaluated tail score (Appendix A.2), as it is for all regression baselines in Table 2. The crossing term transfers the classifier's right-tail state information to this continuous forecast.

What the coupling adds. This is quantified in our response to Q2.

W2. Financial meaning of the threshold

Reviewer: a 3% four-day move is more unusual in some markets and volatility regimes than others; is the objective an absolute return opportunity or a move relative to market conditions? The rare-event claims should acknowledge the positive-tail scope.

Absolute return opportunity. The objective is to identify absolute return opportunities. Trading decisions and the backtest in Section 5.5 are evaluated in absolute returns, so an absolute threshold matches the decision directly. A common threshold also gives all nine markets the same event definition, which pooled training and pooled evaluation require. The threshold τ=1.03\tau=1.03 is fixed a priori and held constant across both splits and all markets (Appendix A.3); it is not tuned on validation or test data.

Market heterogeneity. We agree that a 3% move is rarer in some markets than in others, and Table 5 reports this directly. This heterogeneity is part of the task: a useful score should rank opportunities across markets with different volatility, not only within a single market. To check that the results are not driven by a few markets, Section 5 also compares TCDL with each learned baseline on per-index results using a paired Wilcoxon signed-rank test with Holm correction.

Relative thresholds and scope. A volatility-relative threshold defines a different task, namely identifying unusual moves rather than return opportunities. Because τ\tau defines both the right-tail state and the crossing loss, it would require redefining the right-tail state rather than re-evaluating the current model.

W3. Source of the gains

Reviewer: the external baselines use different targets and training objectives; a matched comparison with one or two representative models, and per-market ablation results, would help establish where the gains come from.

Same target and evaluation. All models in Table 2, including the external baselines, forecast the same four-day-ahead close Ct+4C_{t+4} (equivalently, rt=Ct+4/Ctr_t=C_{t+4}/C_t), and all tail metrics use each model's regression output as the score. The baselines are standard point forecasters (Appendix A.6); TCDL differs in its training objective, which is the factor under study.

Matched comparison. Table 3 isolates the objective: all configurations share the same tokenizer, backbone, regression head, target normalization and optimization settings, and differ only in the loss (Appendix A.7), including MSE only, i.e. the same model trained as a standard regressor. The tail AUPRC of the regression output rises from 0.0923 (MSE only) to 0.1464 in 2015–2019 and from 0.0864 to 0.1326 in 2021–2025, and none of the alternative objectives reproduces this gain. The gain therefore comes from the objective, not from the tokenizer or the backbone.

Per-market results. Cross-market consistency is tested per index with a two-sided paired Wilcoxon signed-rank test and Holm correction (Section 5): TCDL's lower MSE and MAE are significant against all eight learned baselines in 2015–2019 and against six of the eight in 2021–2025 (Table 2).

AuthorsOpenReview ↗

Response to Reviewer xxSR (2/2)

Q1. How often does the tail-state constraint activate, and does it reduce disagreement between the heads?

Reviewer: how often does the tail-state constraint activate, and does it reduce disagreement between the heads?

We clarify that this disagreement is a training-stage quantity: Lcross\mathcal{L}_{cross} penalizes, during training only, samples predicted as right-tail whose regression output remains below the threshold (Section 4). We report its activation from the training log of the released notebook (2021–2025, seed 1, 22,427 training samples):

Epoch110203040
Crossing rate among predicted right-tail samples0.0%1.4%1.9%2.8%3.1%
Mean squared shortfall [max⁡(0,τz−z^t)]2[\max(0,\tau_z-\hat z_t)]^20.6030.4610.4400.4310.433

Activation frequency. In the final epochs, about 2,200–2,300 training samples per epoch are predicted as right-tail, and about 97% of them remain below the threshold. The constraint is therefore active for roughly 2,150 samples per epoch, about 10% of the training set, comparable to the empirical right-tail rate (10.9%).

Disagreement. The mean squared shortfall of the penalized samples decreases by about 28% during training, so the term consistently reduces the gap between the two heads. Most penalized samples do not fully cross the threshold, which is by design: Lcross\mathcal{L}_{cross} is a soft penalty with a small weight (λcross=0.1\lambda_{cross}=0.1) that transfers right-tail state information to the continuous forecast "without forcing threshold-consistent predictions toward the decision boundary" (Section 4). Consistently, increasing λcross\lambda_{cross} to 0.2 does not improve tail discrimination (Fig. 6), and the effect of this transfer on the regression output is shown in our response to Q2.

Q2. Does the coupled regression score outperform the classifier's tail probability?

Reviewer: does the coupled regression score outperform the classifier's tail probability?

We first clarify that the paper does not claim that the regression output outperforms the classifier's tail probability. Our claim concerns the regression output itself: the crossing term makes the continuous forecast more informative about right-tail events (Section 5.2). Comparing two heads trained with different objectives is not an apples-to-apples comparison. What the coupling adds is isolated by comparing regression outputs trained with and without the crossing loss: MSE + CE uses the same backbone, classification head and CE loss but removes the crossing loss, and MSE + CE + GT threshold hinge applies the same hinge to ground-truth tail samples instead of predicted ones (Table 3):

PeriodObjectiveTail AUPRCTail AUROC
2015–2019MSE + CE0.11060.4706
2015–2019MSE + CE + GT threshold hinge0.12520.5532
2015–2019TCDL0.14640.5935
2021–2025MSE + CE0.08420.4596
2021–2025MSE + CE + GT threshold hinge0.11240.5848
2021–2025TCDL0.13260.5896

Compared with MSE + CE, adding the crossing loss raises the AUPRC of the regression output by 32% and 57% in the two periods, with nearly unchanged MSE. The GT threshold hinge adds the same threshold penalty without conditioning on the predicted state and yields smaller gains, indicating that the benefit comes from coupling the regression output with the model's own predicted state.

Q3. Are the gains robust to the event threshold and to an exposure-matched trading comparison?

Reviewer: are the gains robust to the event threshold and to an exposure-matched trading comparison?

Threshold. As discussed in W2, τ=1.03\tau=1.03 defines the task and is fixed a priori for both splits and all markets. The robustness of the resulting score to the decision threshold is shown by the backtest (Table 4): the signal threshold is set from validation predictions at three levels (Q90, Q95, Q98), and in all six period–level combinations the overlay improves both the average cumulative return and the average Sharpe ratio over Buy-and-Hold, from 0.3029/0.4333 to 0.3218–0.3419/0.4401–0.4603 in 2015–2019, and from 0.4555/0.5307 to 0.4779–0.5557/0.5418–0.5783 in 2021–2025.

Exposure matching. The Sharpe ratio separates signal quality from extra exposure, because extra leverage alone cannot raise it. Scaling exposure by a constant factor leaves the Sharpe ratio unchanged before financing costs, and adding leverage at times unrelated to the signal lowers it: if the 0.5× overlay is applied in a fraction pp of periods independently of returns, the Sharpe ratio is at most (1+0.5p)/1+1.25p(1+0.5p)/\sqrt{1+1.25p} times that of Buy-and-Hold, which is below one for any p>0p>0. The overlay nevertheless raises the Sharpe ratio in all six settings, despite the 0.1% round-trip cost and the 5% borrowing rate, so the improvement reflects the timing of the signal rather than additional exposure.

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.