acceptodds
Under review as a conference paper at ICLR 2027

R2 PT: Relation-Probed Dynamic Graphs with Regime Adaptive Evolutionary Factor Pruning for Quantitative Trading

Abstract

Recent large‑model‑driven factor mining combined with static graph neural networks for quantitative trading suffers from two critical drawbacks: static asset relation graphs ignore dynamic causal spillover among stocks, and one‑shot global factor selection overlooks factor validity shifting under different market regimes. To address these limitations, we present Relation‑Probed Trading (R²PT), a practical end‑to‑end trading framework. First, we design a relation probe module to build time‑varying directed asset graphs by fusing news text signals, lead‑lag statistical correlation and industry prior knowledge. Second, we introduce a regime‑aware evolutionary pruning mechanism, which adaptively screens effective factors conditioned on current market status. Moreover, we adopt overlapping stratified backtesting to mitigate phase artifacts caused by fixed rebalancing offsets. Extensive out‑of‑sample rolling experiments and ablation studies are conducted on both S&P 500 and CSI 300 constituents. Empirical results demonstrate consistent performance gain and verify the independent contribution of each core component. We further discuss survivorship bias and hyper‑parameter sensitivity as key limitations for real‑world deployment.

Primary area:
learning on time series and dynamical systems
Keywords:
Quantitative Trading, Factor Mining, Time‑Varying Graph Neural Network, Regime‑Adaptive, Evolutionary Feature Selection, Asset Relation Graph, Overlapping Backtesting

Reviews

Among:
Shape:
1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_YsCKOpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

R²PT combines dynamic asset graphs with HMM-conditioned evolutionary factor gating for quantitative trading. The graph integrates news co-occurrence, return lead–lag relationships, and industry structure. A relational attention scorer generates predictions, which are evaluated through overlapping-tranche portfolios. Experiments include walk-forward backtests on 68 S&P 500 and 60 CSI 300 constituents, transaction costs, and component ablations.

Critical strengths

The overlapping-tranche construction addresses sensitivity to arbitrary rebalancing phases. The two-market study also explicitly reports negative ablation results and limitations, helping readers assess where the framework provides useful evidence and where its benefits remain uncertain.

Critical weaknesses
  1. The temporal validity of the backtest requires clarification. Section 3.3 specifies Viterbi decoding, and Algorithm 1 decodes regimes over the full panel. If implemented as written, this can make historical state assignments depend on future observations, even with frozen HMM parameters. Although the paper states that fitting uses past data only, the refit description does not explicitly exclude unfinished forward-return labels from scorer training and stacking-weight selection. These are concerns about the documented procedure, not confirmed implementation bugs, but they could materially affect the main results.

  2. The incremental value of the evolutionary operators is not isolated. The "w/o evolution" ablation uses uniform weights over all factors, whereas the full method selects and weights a sparse subset. This comparison evaluates the pruning mechanism as a whole, rather than isolating mutation and crossover. A matched rolling top-P selector, with and without the same historical-weight smoothing, is needed to establish their added value. The authors also acknowledge that the paired return differences in Appendix E are statistically inconclusive. The evidence is therefore suggestive, but does not yet establish an advantage over simpler adaptive factor selection. Additionally, Figure 1 contains noticeable presentation issues, including overlapping text, labels extending beyond their boxes, and arrows with unclear connections. These problems make the overall pipeline harder to follow and reduce the clarity of the method's presentation. While secondary to the methodological concerns above, they further weaken the quality of the submission.

Questions for authors
  1. At decision date t, does regime inference use only observations available through t? Are scorer training and stacking-weight selection restricted to samples d satisfying d + H ≤ t? Please clarify how the implementation handles these information cutoffs and provide corrected backtest results if necessary.
  2. With P = 8, the same fitness-to-weight mapping, and the remaining training and evaluation protocol unchanged, how does the full gate compare with rolling top-P selection, with and without historical-weight smoothing? Please report the paired performance differences and confidence intervals accounting for temporal dependence.
1 comment
AuthorsOpenReview ↗

Response to All Reviewers

We thank all reviewers for the valuable feedback. We address the major concerns point by point:

To Reviewer YsCK

  1. Look-ahead bias: We remove offline Viterbi decoding for regime labeling and adopt online HMM filtering. Only information up to time t is used for trading decisions. All backtests are re-run, and we add an ablation to quantify the leakage effect.
  2. Ablations: New ablations are added to isolate the contributions of online regime modeling and evolutionary factor pruning, with comparisons against greedy top-K selection.
  3. Figure & hyperparameter: Workflow figures are revised for clarity. Controlled experiments for β and weight smoothing are supplemented in the appendix.

To Reviewer dUC6

  1. Cross-market performance: Our method works better on US large-cap markets but underperforms on CSI 300 due to persistent static factor premiums and high turnover frictions. We clarify this application boundary in the paper.
  2. Statistical inference: We adopt Newey-West HAC standard errors for Sharpe and IC to handle autocorrelated returns. Claims that lose statistical significance are weakened or removed.
  3. HMM collapse: We switch to a regularized 2-state HMM and add a 3-state robustness check. We also replace all "causal" claims with "predictive directed relation".

To Reviewer y32

  1. Overlapping IC autocorrelation: Newey-West correction is applied for overlapping forward returns in statistical testing.
  2. Forward-looking leakage: Same online HMM setting is used to strictly avoid future information.
  3. Significance: Results are re-evaluated after correction. Only statistically robust improvements are emphasized.

All revisions are marked in the updated manuscript.

Reviewer_yY32OpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

Please concisely summarize the paper, contributions, and validation as you understand them to be. R²PT combines dynamic graphs built from news, return lead–lag correlations, and industry links with HMM-conditioned factor gating for stock ranking and long–short trading. Predictions are stacked with an equal-weight factor prior, while overlapping ten-day tranches reduce rebalance-phase sensitivity. Walk-forward tests cover 68 US and 60 Chinese stocks over approximately 2.2 years with 10-bps one-way costs. The full model achieves Sharpe ratios of 0.28 and 0.27 and improves mean rank-IC over the static ensemble in both markets. However, the Chinese static ensemble has a higher Sharpe of 0.87, and no component-ablation mean-return gap is significant at 5%. Limited news coverage and US regime coverage further constrain interpretation, leaving incremental effectiveness preliminary.

Critical strengths
  1. Explicit reporting of important limitations and negative results. The paper reports statistically inconclusive ablation comparisons, negligible text-edge contributions under limited coverage, poor agreement between US regime names and rule-based labels, and a stronger static baseline on the Chinese panel. This reporting makes several limitations of the evidence visible and supports a more informed assessment of the framework.
  2. Evaluation that reduces sensitivity to rebalance phase. Overlapping tranches average across rebalance phases, addressing the substantial variation observed when the starting phase changes. The paper provides a linear-return argument for equivalence to averaging the single-phase strategies in the fully ramped regime. This is a useful evaluation feature because it reduces dependence on an arbitrary scheduling choice.
Critical weaknesses
  1. Incremental benefits and IC uncertainty remain insufficiently established. No component-ablation mean-return gap is significant at 5%. The full model barely exceeds the static ensemble’s US Sharpe (0.28 vs. 0.24) and trails it on CSI 300 (0.27 vs. 0.87). The no-text variant also contradicts the claimed best US risk-adjusted performance. Moreover, overlapping ten-day labels do not justify treating daily IC observations as independent or claiming a √H-fold standard-error reduction without dependence-adjusted analysis.
  2. Look-ahead safeguards remain unclear. Algorithm 1 describes full-panel state decoding; full-sequence Viterbi could use future observations despite frozen HMM parameters. While pruner fitness explicitly uses realized labels, equivalent cutoffs are unspecified for scorer training and stacking. Clarification is needed to establish that every prediction uses only information available at its decision date.
Questions for authors

Clarification requests:

  1. IC uncertainty and effective sample size. How were the claim of approximately 540 independent IC observations and the approximately √H-fold standard-error reduction derived? Please explain how temporal dependence from overlapping ten-day return labels was handled, and report dependence-adjusted confidence intervals for both mean IC and the paired IC differences supporting the claimed improvements. Appendix E reports intervals for daily-return differences, which concern a different statistic.
  2. Temporal information boundaries. At each decision date, does the HMM state used for prediction depend only on observations available by that date, or is it taken from Viterbi decoding over the complete panel? The pruner explicitly uses fully realized labels; please specify the corresponding label-availability cutoffs for scorer training and stacking-weight selection. If either procedure uses information unavailable at the decision date, how do the results change after enforcing these boundaries?
Reviewer_dUC6OpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper fuses three relation sources (dated news co-occurrence, one-day lead–lag, industry membership) into a time-varying directed asset graph, labels days with a four-state Gaussian HMM fitted on trailing data, evolves a per-regime gate that keeps 8 of 24 price/volume factors, and scores the cross-section with a one-layer relational attention model; the resulting book is dollar-neutral, quintile long–short, traded through overlapping tranches with 10 bps costs. Two panels (68 S&P 500 and 60 CSI 300 constituents), 2024-07 to 2026-09.

Critical strengths
  1. The evaluation discipline is better than most work in this area: walk-forward refitting, strictly causal fitness, decision-date graph snapshots, an explicit cost model, and a full ablation ladder.
  2. The observation that rebalance phase alone moves the test Sharpe between 0.15 and 0.77 is a useful warning, and the overlapping-tranche protocol is the right response to it.
  3. Null and negative results are reported rather than hidden.
Critical weaknesses
  1. The results contradict the claims. On the US panel the full system earns Sharpe 0.28 against 0.57 for an equal-weight market book; on CSI 300 it earns 0.27 against 0.87 for the authors' own static factor ensemble and 0.51 for the market. The abstract's "best risk-adjusted book among the eight signal variants" is therefore true only on the US panel; on the second panel the proposed machinery is the worst non-degenerate variant in the table. The "the market book only carries beta" defence does not apply to the static ensemble, which is dollar-neutral under the same protocol and beats R2PT by 0.60.
  2. Nothing is significant, by the paper's own tests. Every ablation gap has a bootstrap interval containing zero (largest: +2.4 bps/day, t = 1.6). With 2.2 years of daily returns the standard error of a Sharpe ratio is roughly 0.7, so 0.28 is statistically indistinguishable from zero; the paper never reports a confidence interval on the Sharpe ratio itself, only on return differences.
  3. The regime variable is degenerate on the US panel, which makes the central ablation uninterpretable. 502 of 550 test days are decoded as one regime, "bull" and "bear" never occur, and agreement with a transparent rule labelling is 0.4%. A near-constant label cannot support a 0.41 Sharpe gap attributed to regime conditioning (0.28 vs −0.13), and because regimes with fewer than 20 trailing days fall back to pooled fitness, both variants use pooled fitness most of the time. The paper states both facts but does not confront the contradiction.
  4. The text channel, which motivates Gap 1, is null. Removing the text edges changes the book by −0.07 bps/day, 95% CI [−0.36, +0.12]. "Validated by construction" is not evidence of value, and the data limitation (news covers only the final quarter) does not repair it — it means the premise is untested.
  5. The IC inference is incorrect. Overlapping H-day forward returns make the daily IC series autocorrelated to order H−1, so the effective sample is roughly n/H and the standard error of the mean IC is not reduced by √H. The ±0.007 figure used to arbitrate between variants is therefore too small, which matters because several conclusions rest on IC gaps of 0.002–0.004.
  6. The obvious baselines are missing. The support is 8 of 24 factors — a small combinatorial problem — so rolling greedy top-8, a gate with mutation and crossover disabled, and a random 8-support (to calibrate what noise produces) are the controls that isolate the value of evolution. The current control removes pruning altogether, so it cannot separate "selection helps" from "evolution helps". No regime-switching factor model (Ang & Bekaert 2002; Guidolin & Timmermann 2008) or factor-timing baseline is compared on the same factors.
  7. Minor: the Abstract's "causal texture" claim is not supported by one-day lead–lag correlations, which are substantially a microstructure artefact.
Questions for authors
  1. On CSI 300, why is R2PT the system of record when the static ensemble reaches 0.87 under the identical protocol?
  2. How often does the pooled-fitness fallback fire per regime, and what does the "no regime" ablation then remove?
  3. What is the confidence interval on the Sharpe ratio, and the minimum detectable Sharpe gap at 5% power?
  4. If the IC standard errors are recomputed with an effective sample of n/H, do the "graph matters" and "regime conditioning matters" conclusions survive?

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.