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Under review as a conference paper at ICLR 2027

Cross-Asset Graphs in Reinforcement-Learning Trading: Derivation, Validation, Decision-Relevance and Reporting

Abstract

Reinforcement-learning traders increasingly condition on a graph over assets and report gains from doing so. Two questions go unasked: nobody applies multiple-testing control to the thousands of candidate edges a graph is selected from, and nobody reports how much the graph changes what the agent does. This paper addresses both. For a mean-variance-with-costs reward under an approximate factor model , it proves that the reward decomposes exactly into per-asset terms, pairwise terms supported precisely on , and one rank-one global term, so the validated graph is not an architectural choice but the coupling structure the reward already has. It also bounds the value error by the false-discovery rate of edge selection and fixes the construction's scope by a third-order criterion. On 116 US large caps over 3,772 trading days that coupling changes a median of 0 of 116 actions, and forty pre-registered studies leave it intact, including two regimes built to revive it, a second architecture, and a published system whose released code was run. The mechanism is measurable and does not depend on the agent: the graph's information is contemporaneous at daily resolution, with out-of-sample of 0.0907 same-day against 0.0030 for a degree-matched random graph, but -0.0010 at one day's lag, for every structure tried. Same-day co-movement is a risk fact, and risk enters the decision marginal one order in position size below alpha and cost. That diagnosis names a remedy, which the paper tests: in an objective with no return term, the same edges as sparse precision support beat a density-matched random support out of sample by -10.42% in realised volatility. A pre-registered adversarial pass that nets out sector structure retains 48% of that effect and 27% on log-likelihood, and the retained figures are the ones claimed. This research recommends three numbers, which no graph-RL paper currently reports: the count of actions the graph changes, the fraction of decisions beyond any graph's reach, and the number of seeds the comparison can resolve (19,261 here against a cap of 100).

Primary area:
reinforcement learning
Keywords:
reinforcement learning, graph neural networks, portfolio optimization, factored value functions, multiple testing, false discovery rate, negative results, reproducibility, covariance estimation

Reviews

Among:
Shape:
1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_aw5dOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
1
Soundness
1
Read review
Paper summary

This paper focuses on RL-based trading algorithms with condition on graphs. Many theoritical results are offered such as reward decomposes exactly into per-asset terms. Experiments on medium size US stock datasets are conducted to further demonstrate the findings of this paper.

Critical strengths

RL-based portfolio management is decent topic.

Critical weaknesses
  • The motivation of this work is poor. As far as I know, graph-based information is not widely used for RL-based trading algorithms. The two gaps mentioned do not make sense to me at all.
  • The flow of this work is very hard to follow with poor writting. There are lots of typos or formatting issues.
  • The setting and formulation of this work is not realistic (e.g., 3 choices of actions is far too simple)
  • The experiment part are useless for me. Toy experiment on US stocks with no baseline can not support the statement in this paper.
  • The overall quality of this work is far below the bar of ICLR.
Questions for authors

N/A

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

This paper asks whether a statistically validated asset graph changes an RL portfolio agent’s decisions. It shows that a mean–variance reward under a factor model decomposes exactly into per-asset, pairwise and market terms. On that basis, it places FDR-validated residual-correlation edges as pairwise terms in a factored Q-function. On 116 US large caps, the graph changes a median of 0 of 116 actions, because its information is contemporaneous and enters only through the small risk term. The result holds across around 40 pre-registered studies, including a reproduction of HATS.

Critical strengths
  1. Rigorous design with a useful diagnostic. Counting how many actions the graph changes, compared within the same state, avoids seed noise and is a better first question than a performance ablation. Matched random-graph controls, both BY and BH, and open reporting of voided runs make the negative result credible.

  2. Diagnostic on a published system. The gated HATS reproduction shows that its graph is decision-irrelevant: 95% of books are unchanged and 98–99.7% of decisions are beyond any graph's reach. It also identifies concrete bugs in the released code. This is the most transferable contribution.

Critical weaknesses
  1. The negative result seems calibration-driven and is overgeneralised. With γ=3\gamma = 3, gross 1×1\times and w∼1/Nw \sim 1/N on daily returns, the risk terms are tiny by construction. The paper's own results show the graph mattering at high leverage, under binding risk budgets and in the minimum-variance limit (§6.7). "Inertness" is therefore a property of one parameter region, not of daily equity data, and the γ\gamma sweep is not shown.

  2. Limited relevance and novelty. The refuted construction is the authors' own (Table 1), and HATS is not an RL agent. The propositions are largely elementary, and Prop. 4 does not actually bound the value error by qq. §6.7 omits standard baselines (Ledoit–Wolf, graphical lasso). The dense study codes and the 41-page appendix make the claims hard to verify, and code is not provided.

  3. The mechanism rests on under-specified premises. The claim that alpha is O(1)O(1) and dominates depends on how μ\mu is estimated, which is not clearly stated, even though daily expected returns are of order 10−410^{-4} and noisy. The three-level action grid also makes the argmax essentially a sign decision, which favours inertness. The continuous relaxation is non-concave and solved only locally, so it does not fully remove this concern.

  4. Verifiability and internal consistency. The "pre-registrations" have no external registry or timestamps, so they cannot be checked. There are several inconsistencies: Fisher-z on residual correlations (§4.1) versus on partial correlations (App. L); the E8 row labelled as Prop. 3 but referring to Prop. 2; and seed counts acknowledged to be 2×2\times inflated (Remark 7) but reported uncorrected. Together these weaken confidence in a paper whose case rests on its own record-keeping.

Questions for authors
  1. How many actions change as γ⋅g\gamma \cdot g increases, and is the regime where validated edges beat random ones economically realistic?
  2. How is μ\mu estimated, and how sensitive is the alpha-to-risk ratio to that estimate?
  3. How does §6.7 compare with Ledoit–Wolf shrinkage and graphical lasso?
  4. Can Prop. 4 be stated as an explicit bound on ∣Q^−Q∣|\hat{Q} - Q| in terms of qq? If not, please revise the abstract.
  5. Will code and timestamped pre-registrations be released?
Reviewer_fdqKOpenReview ↗
Rating
1
Confidence
2
Informativeness
1
Presentation
1
Soundness
1
Read review
Paper summary

In this paper, the authors study whether a cross-asset graph changes the decisions of an RL trader. The motivation is that graph-based RL trading papers select edges from thousands of candidate pairs without multiple-testing control, and only report performance ablations. The authors use a mean-variance reward with transaction costs and a factor model for the covariance. They show that this reward splits into per-asset terms, pairwise terms on the support of the residual covariance, and one rank-one market term. They estimate the graph with Fisher-z tests on market residuals and a Benjamini-Yekutieli correction, and put it in a factored Q-function. They then count how many actions change with and without the pairwise terms. They also argue that the pairwise term is too small to change a discrete decision. Experiments use daily data on 116 US large caps. The paper reports that the graph changes almost no actions, and that the graph only helps in a minimum-variance allocation with no return term.

Critical strengths

The main measurement is simple and paired within each state, so it does not depend on training seeds. Counting how many actions a graph changes is a reasonable thing for graph-RL papers to report.

Critical weaknesses

I am not an expert in quantitative finance, so I review this paper mainly from an RL and deep learning perspective. For finance-specific points, I rely on what the paper itself says.

  1. The main negative result is built into the setup. By the paper’s own numbers, every risk term in the reward is small compared with the alpha and cost terms. The whole risk penalty is 0.064 times alpha (Figure 9). So the graph cannot change a decision for the same reason the covariance as a whole cannot. The paper admits this: the inertness belongs to the objective, not the graph (Section 6.4). Much of Section 6 then spends many experiments confirming an order argument already proved in Section 5.4. I do not see what the reader learns beyond that algebra.
  2. The paper does not test the systems it criticizes. The abstract and introduction criticize graph-based RL traders. But the paper’s own survey (Table 1) shows that no published system puts the graph in an action-value function, and Section 7 says published rewards are of a different type. So the negative result is about a construction the authors built themselves. The only published system they actually run is HATS, which Table 1 lists as not an RL method. Its reproduction also fails the authors’ own gate on 2 of 4 phases (Appendix G). To support the claims in the abstract, the paper would need to test at least one published graph-RL system under its own reward.
  3. There is very little RL in this paper. The main measurement is a property of the reward, not of a learned policy. Only 8 trained agents are checked (E1, Appendix L). The positive result in Section 6.7 has no agent and no learning at all (Appendix I). The learned ψ network is never given the edge strength (Appendix H), so it is unclear what the learned coupling can represent. For an ICLR paper framed around RL, I would expect the learning part to be central. Here it is an afterthought, and I am not sure what the ICLR audience gains from it.
  4. The abstract overclaims. It presents the minimum-variance result as the remedy, but by the paper’s own pre-registered rule this result is sector-driven, since it keeps only 27.0% of the log-likelihood gain after removing sectors (Appendix I). Appendix I also says that a shrinkage baseline is the comparison readers will want, and leaves it for future work. The abstract highlights a seed count of 19,261, but Remark 7 says the reported counts are twice what the paired formula gives. The abstract should state these limits plainly.
  5. The evidence is too narrow for the general claims. Section 7 itself lists the limits: one universe of 116 present-day large caps, daily data only, and a selection of names that has survivorship issues. Remark 5 says the 52 rolling windows amount to about 6 independent ones. I cannot judge how much each limit matters in finance. But together they make me unsure that the general statements in the abstract and conclusion hold beyond this one setting.
  6. The presentation is very poor, and I highly suspect that most of the text was generated by an AI or an automated research pipeline. The paper reads like an agent’s experiment log, not a paper. I list the evidence below. a. The paper says so itself in one place. Appendix M states that “the manuscript source is generated”, and that every number is loaded from a saved artifact at build time. Appendix B.5 says the same about the verification table. The AI-use statement only mentions coding assistance and drafting and editing text, which does not match a generated manuscript. b. Internal codes and file names leak into the text. Results are cited by study codes such as D1, D7b, E19b, E24b and T9c. Some codes are never defined anywhere. Figure 12 refers to “the C21 protocol”, Figure 17 to C24, Table 6 to C25, and the legend of Figure 15 to C27, but Table 6 only lists D and E studies. Appendix M lists script names like measure_c11_c15, benchmark_c18 and run_h4_pilot as the “execution order”. The text also cites file paths such as src/verify_n_invariance.py and results/tables/graph_timing.json, and a commit hash. A human author writing for readers would not leave these in. c. Much of the paper is a log of the process, not the result. It reports eleven void runs, two withdrawn verdicts and one corrected verdict (Section 6, Appendix L). It repeatedly narrates its own past mistakes. Remark 3 says an earlier version “asserted the opposite, and was wrong”. Appendix I says “an earlier draft of this appendix got that wrong”. Appendix K.8 has a heading for “the methodological choice this project got wrong most often”. Appendix B.5 describes a “deliberately failing” assertion that was kept so the verifier would catch a past error. Appendix M even has a paragraph on why no GPU was used, with an Amdahl’s law calculation. Appendix G says the authors read the HATS issue tracker in full and counted its issues, pull requests and forks. None of this helps the reader understand the result. d. The figures look like no one checked them. Figure 3 prints the threshold as 0.15000000000000002, which is a raw floating-point value. In Figure 12 the two subfigure titles run into each other (“the generous on ebecause the policy”), and the same happens in Figure 13 (“is weak Keep only”). The edge-count labels in Figure 13 overlap (“2260 edges1202 edges676 edges”), and the legends in Figure 8 sit on top of the curves. Most figure titles are full-sentence claims, e.g., “Training makes learned edges LESS consistent, out to 5,000 steps” (Figure 15). e. The writing style is typical of LLM text. Conclusions are given as short bold slogans instead of explanations, e.g., “That is the whole mechanism” (Section 5.4), “Neither published exact method survives contact with this graph” (Section 6.1), and “That deflated figure is the one claimed” (Section 6.7). Almost every paragraph in Section 6 has a bold sentence. The abstract alone contains more than ten numbers and a bold sentence. f. Finally, Appendix O says that “two incidents of fabricated citation content in a related project” made the authors check every citation, and it labels each reference as read, secondary or unread. Fabricated citations are a known failure of LLM-generated text, so this appendix suggests the same pipeline was used here. Frankly, it is absurd to send a paper in this state to ICLR. I have nothing against using AI to write. But if the authors want to hand the writing to a model, they should at least use a good frontier model, and then read what it produces. A pipeline that prints 0.15000000000000002 in a figure, cites studies that appear nowhere in the paper, and leaves its own script names in the appendix is not doing the authors any favors. Someone should have read this paper before sending it to reviewers. As it is, the authors ask reviewers to spend hours on a text they do not seem to have checked themselves. I could not verify most claims, because the main text cannot be followed without about 30 pages of appendix and the code is not available. The paper needs a full rewrite by the authors themselves, plus an honest statement of how AI was used in the research and the writing.
Questions for authors

● How was AI used for coding and writing? Did an AI agent design or run the experiments and write the whole paper? ● What are studies C21, C24, C25 and C27, which are referenced but not listed in Table 6?

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