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Under review as a conference paper at ICLR 2027

From Knowing to Doing: A Memory-Controlled Benchmark for LLM Trading Agents on Stock Markets

Abstract

Evaluating whether large language model (LLM) agents can profit in capital markets is increasingly framed as end-to-end trading: place an agent in a historical market, let it trade, and measure portfolio returns. This setup is vulnerable to two evaluation failures. First, long backtests often cover periods before the knowledge cutoffs of frontier LLMs, allowing memorized tickers, dates, prices, and market narratives to substitute for investment reasoning. Second, raw returns are a noisy proxy for the ability to select stocks, since positive performance may come from market beta, style exposure, or favorable regimes rather than stock-selection alpha. We introduce Knowing-To-Doing Financial Benchmark (KTD-Fin), an end-to-end trading benchmark based on price data that addresses both issues. To mitigate knowledge leakage when backtests cover periods before LLMs' knowledge cutoffs, KTD-Fin applies masking at the data layer to anonymize key identifiers and calendar information consistently across prompts and tools, limiting the cues agents can use to retrieve memorized market information while enabling controlled comparisons of identifier access. It also incorporates a Barra-style performance attribution framework that decomposes portfolio returns into market, style, and stock-selection alpha components. This finer-grained decomposition allows stock-selection ability to be assessed separately from market and style exposures that can confound evaluations based on raw returns. Across ten frontier LLM agents evaluated on the Chinese A-share CSI300 over a 2024–2026 trading window, masking changes agent rationales, pushing them away from narratives about specific companies and toward factor reasoning under anonymized identifiers. Attribution analysis further shows that LLM agents' cumulative returns under identifier masking are largely explained by market and style exposure, with negative stock-selection alpha for nine of ten agents under the full nine-factor specification. Cross-model replications reproduce behavioral differences; leave-one-factor-out attribution preserves closely aligned rankings. These findings suggest that financial LLM benchmarks should evaluate not only whether an agent makes money, but also which sources drive those returns. We provide KTD-Fin as a reproducible template for evaluating LLM trading agents with leakage controls and return attribution.

Primary area:
datasets and benchmarks
Keywords:
Large Language Model Agents, Stock Market Trading, Financial Benchmark Evaluation, Data Leakage, Performance Attribution

Reviews

Among:
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1234this paper, Top 4%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.33 over 3 reviews, above 96% of the others.
Reviewer_nc8JOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper proposes KTD-FIN, a Qlib-based trading benchmark on the CSI300 universe. It has two components: data-layer masking of tickers and dates (bright, stock-blind, date-blind, blinded), and a Barra-style attribution that splits returns into common, style and selection alpha. In the main experiment, ten LLMs trade under blinded × open-research from 2024-01 to 2026-04 and are compared against 18 Qlib baselines and CSI300. The authors report that masking shifts rationales from company narratives to factor reasoning, and that LLM returns are mostly explained by common and style exposure, with negative selection alpha for 9 of 10 models.

Critical strengths
  • The two problems it targets, memorisation in backtests and raw return as a proxy for skill, are important.
  • The execution rules are realistic, and model coverage is broad.
  • The paper is very easy to follow.
Critical weaknesses
  • Prior knowledge is not the same as look-ahead bias. Look-ahead bias means knowledge of realised future outcomes. Statements such as "Moutai, liquor leader" (Appendix A) could actually be point-in-time public knowledge that human investors can also use. Table 17 even finds such statements after the model's knowledge cutoff, where look-ahead is impossible. In this case, full masking also changes the task into price-only technical analysis.

  • Some results are inconsistent. Table 5 and Table 6 are different in both directions: GPT-5.5 is +61.3% by account vs. +36.9% by attribution, DeepSeek +1.4% vs. +18.6%. The effect of masking on returns flips sign across models (Table 2 vs. Tables 3 and 12).

  • No pre-/post-cutoff test. I think a cleaner test is to compare the bright and blinded gap before vs. after each model's knowledge cutoff, across several models. The paper has one model and one 43-day post-cutoff window, and does not report any model's cutoff. 43 days is also considered to be too short from my perspective. I would suggest using earlier models to have a larger post-cutoff testing period.

  • Minor: missing many related works. This field have been explored pretty much but many of them are not cited and discussed in the related work and for some of these existing studies, it would be valuable to explain how this paper builds upon them.

Assessing Look-Ahead Bias in Stock Return Predictions Generated by GPT Sentiment Analysis, JFDS 2024 Time Machine GPT, Findings of NAACL 2024 Lookahead Bias in Pretrained Language Models, ICML 2025 The Memorization Problem: Can We Trust LLMs' Economic Forecasts?, arXiv 2025 Can LLM-based Financial Investing Strategies Outperform the Market in Long Run?, KDD 2026 Look-Ahead-Bench: A Standardized Benchmark of Look-ahead Bias in Point-in-Time LLMs for Finance, arXiv 2026 When Agents Trade: Live Multi-Market Trading Arena for LLM Agents, WWW 2026 Summoning the Oracle to Slay It: Mitigating Look-Ahead Bias in Financial Backtesting with Large Language Models, EMNLP 2026 Evaluating LLMs in Finance Requires Explicit Bias Consideration, ICML 2026

Questions for authors

See the weakness section. My main question is basically: How would you decouple look-ahead bias and prior knowledge?

3 comments

Thank you for recognizing the research question, execution rules, and clarity of the paper, and for identifying where the return statistics and temporal comparisons need clearer presentation.

W1 / Q1. Prior knowledge and look-ahead bias. We agree that a publicly known fact such as “Moutai is a liquor leader” differs from knowledge of subsequently realized returns. Our leakage concern is the latter: memorized outcomes from the backtest period. Stock identities and dates provide cues through which either type of knowledge can enter an agent's decisions. KTD-FIN holds market observations fixed while varying access to these cues throughout sequential trading. W10's explanation audit measures identity-conditioned company references after the anchor model's stated cutoff. The revised Introduction and §4.4 clarify this distinction.

W2. Return definitions and masking effects. Tables 5 and 6 report different statistics:

TableDaily-return aggregationAcross seeds
5Compounded account returnMedian
6Sum of daily common, style, and selection contributionsMean

For example, two daily returns of +10% compound to +21% but sum to +20%. Their difference depends on the return path. In the seed-level examples, GPT-5.5 has a compounded account return of 61.3% and a daily account-return sum of 55.0%; DeepSeek has corresponding values of 1.4% and 11.2%. Cross-seed means and medians introduce a separate aggregation difference. Section 4.1 and Appendix S now define these conventions, and Table 6 labels “Port” as “Add. sum” to distinguish it from compounded account return.

Tables 2, 3, and 12 cover different models and window collections; the anchor uses five seeds and the additional model comparisons use three. Masking tests identifier dependence, whose return effect varies across models and market windows. We distinguish this from the behavioral evidence: across 30 matched model/mode/window comparisons, mean absolute changes are 18.7 percentage points in capital utilization and 15.7 points in abstention (§4.2). Return comparisons are reported by model and window, while the explanation audit directly examines the information cited in trading decisions.

W3. Temporal comparisons across models. Thank you for recommending a broader temporal comparison. We expanded the ''doubao-seed-1-6-251015'' evaluation to eight windows, including a longer window from 2025-11-03 to 2026-02-02. Using the version's October 2025 release as the temporal reference, Appendix R, Table 23 now reports six pre-release and two post-release windows:

WindowDatesRelease groupBright (%)Blinded (%)Bright − blinded (pp)
P12024-04-01–2024-06-05Pre-release−4.07−2.93−1.14
P22024-07-25–2024-09-25Pre-release−3.72−7.74+4.02
P32024-10-21–2024-12-13Pre-release−9.03−2.97−6.07
P42024-12-06–2025-02-14Pre-release−4.58−3.36−1.23
P52025-03-03–2025-05-09Pre-release−2.26−8.06+5.80
P62025-07-14–2025-09-19Pre-release−1.88−7.38+5.50
P72025-11-03–2026-02-02Post-release−0.91+1.59−2.50
P82026-02-02–2026-04-10Post-release+2.14−1.95+4.09

We also disaggregated the Step-3.5-Flash, GPT-5.4-mini, and hy3 experiments in Tables 2 and 3 into pre- and post-cutoff periods. Across these three models, bright’s return advantage generally diminishes after the cutoff.

W4. Related work. Thank you for these references. We have added the suggested work on temporal isolation, point-in-time models, look-ahead detection, and live-market evaluation. Related Work now explains how KTD-FIN builds on these directions through consistent information control across sequential agent–tool interactions and return attribution.

Thanks for the rebuttal. I will raise my overall assessment to 3 given that the requested experiment is added.

Thank you for revisiting our work and for your helpful suggestions.

Reviewer_6mraOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper introduces KTD-FIN, a benchmark for LLM trading agents that combines stock and date masking with factor-based return attribution. It evaluates ten LLMs and eighteen ML baselines on the CSI300, with additional experiments on masking, information access, and factor sensitivity. The main findings are that identifier access changes trading behavior, and that positive LLM returns can coexist with negative stock-selection contributions under the chosen attribution model.

Critical strengths
  1. The benchmark addresses a useful question: what does a profitable LLM backtest actually tell us? Applying masking consistently across prompts and tool outputs is a practical contribution. Combining this with return attribution gives a more informative evaluation than a return leaderboard alone.
  2. The experimental coverage is substantial. The additional model replications, post-cutoff window, and factor sensitivity analysis help establish the scope of the findings. I also appreciate that the paper explicitly recognizes style allocation as potentially useful, rather than treating all factor-driven returns as uninteresting.
Critical weaknesses
  1. I’m not convinced the masking experiments isolate the historical leakage that motivates the paper. Hiding stock identities removes ordinary company knowledge as well as potentially memorized future information. The examples in Section 4.4 show that visible tickers elicit company descriptions, but those descriptions could have been available before the trading date. This establishes an effect of identifier access. It leaves unclear how much the benchmark corrects performance inflated by knowledge of future outcomes, which is a central reason given for introducing it.
  2. The attribution analysis is missing an important reference point. The eighteen ML baselines are compared on raw returns, but the paper’s main argument is that raw returns are insufficient. What happens when the same attribution is applied to these baselines? The authors acknowledge this omission, but I think it belongs in the main evaluation. Without it, the negative LLM residuals are harder to interpret. The stable rankings across factor specifications are useful evidence, though they do not resolve the sensitivity of alpha signs to the factor choice.
Questions for authors
  1. What evidence separates the removal of memorized future information from the removal of company knowledge that was already available at the simulated trading date? I would like to understand which conclusions about leakage the current experiments support.
  2. Could you apply the same attribution to a few representative Qlib baselines using their existing trading trajectories? Whether strong baselines also have negative selection contributions would materially affect my interpretation of the main result.
5 comments

Thank you for recognizing the evaluation question and experimental coverage. Your questions help us clarify the evidence and provide the missing baseline reference.

W1 / Q1. Company priors and future-outcome memory. Thank you for asking us to distinguish these information sources. W10 provides a post-cutoff reference for identity-conditioned explanations. Across its 43 trading days and five seeds, explicit company or sector descriptions occur in 14/215 bright steps and 9/215 date-blind steps, versus 0/215 under stock-blind and blinded.

These results show that identity-conditioned company references persist after the anchor model's stated cutoff. Over historical windows, masking changes access to both company priors and potential future-outcome memory. The bright–blinded return gap therefore measures performance sensitivity to ticker/date cues. The revised Introduction and §4.4 clarify this distinction.

KTD-FIN addresses the need to compare newly released frontier models over a long, common historical window when their cutoffs differ or are undisclosed. The underlying price histories, feature definitions, and execution rules are shared, while ticker/date cues vary consistently across prompts and tools. This provides a controlled setting for examining how agents turn supplied market observations into research, portfolio decisions, and execution.

W2 / Q2. ML baseline attribution and interpretation of residuals. Following your suggestion, we applied the same nine-factor decomposition to all 18 Qlib baseline trajectories using the shared trading period and aggregation convention. Eleven baselines have negative selection contributions. Positive examples include SFM (+12.6%), MLP (+11.9%), Transformer (+8.8%), ADARNN (+7.0%), and KRNN (+5.9%); negative examples include LightGBM (−9.4%), DoubleEnsemble (−9.9%), and Linear (−23.3%). Appendix P reports the complete table.

GroupModelsPositive selectionMedian selectionMean selection
LLM agents101/10−14.30%−26.24%
Qlib baselines187/18−5.15%−4.64%

These descriptive summaries use the displayed model-level contributions under the same factor specification. Negative residuals extend beyond LLMs, while positive residuals are achievable in this price-based environment. The baseline distribution provides a concrete reference for interpreting the LLM results. Attribution reports realized return sources; market and style allocation can themselves represent useful investment capabilities.

We also agree that ranking stability and sign stability require separate reporting. Appendix O gives ranking correlations of 0.964–1.000 but negative counts of 6/10–10/10. Our additional 200-subset analysis has mean correlation 0.976, with 93.5% of subsets at or above 0.95; signs vary mainly among the higher-ranked models. Appendices O and Q report rankings and sign counts separately.

Thank you for the response and additional experiments. The attribution results for the 18 Qlib baselines address my second concern. The first concern remains partially unresolved. The post-cutoff results demonstrate the use of company knowledge, but do not establish the impact of memorized future outcomes on trading performance. The revision clarifies this limitation. I have updated my rating from 2 to 3.

Thank you for your encouraging feedback on our work and our response.

We agree that it is difficult to separate the effects of company knowledge and memory of future outcomes on returns. Our original aim was to study how agents trade using price data alone, so we masked both company identifiers and dates in the blinded setting.

We are exploring a broader backtest with financial statements and analyst reports. The challenge is reconstructing exactly what information from each source was available at each trading decision.

However, we are starting to apply Barra attribution to the date-blinded and stock-blinded (ban company knowledge)trajectories to see if we can find more interesting results, though this may take some time.

Reviewer_qDrQOpenReview ↗
Rating
4(+1)
Confidence
4
Informativeness
3
Presentation
3
Soundness
3(+1)
Read review
Paper summary

This paper presents KTD-FIN (Knowing-To-Doing Financial Benchmark), an end-to-end benchmark for evaluating LLM trading agents that addresses two pervasive flaws in existing trading benchmarks: knowledge leakage from overlapping training data and historical backtest periods, and the use of raw returns as a noisy proxy for stock-selection ability. The benchmark features four masking conditions (bright, stock-blind, date-blind, blinded) that anonymize stock identifiers and calendar dates consistently across prompts and tool outputs, paired with a Barra-style cross-sectional return attribution framework that decomposes portfolio returns into common , style, and stock-selection alpha components. The authors evaluate ten frontier LLMs on the Chinese CSI 300 universe over 2024–2026, alongside eighteen Qlib-trained ML baselines. Key findings include:

  1. Masking shifts agent reasoning from company-specific narratives to factor-based reasoning, with measurable effects on capital utilization, turnover, and abstention rates.
  2. LLM returns are largely driven by market and style exposures, with nine of ten agents exhibiting negative stock-selection alpha under the full nine-factor model.
  3. Performance rankings remain highly stable across leave-one-factor-out attribution specifications. Overall, the work argues that trading agent benchmarks should measure not just profitability but also the sources of returns, and provides a reproducible template for leakage-controlled evaluation with return decomposition.
Critical strengths
  1. Rigorous masking methodology for leakage control. The four-level masking design, applied consistently across both prompts and tool outputs, represents a significant methodological advance for historical evaluation of learning agents. The accompanying identity recovery tests quantify how much information remains inferable from masked price patterns, providing empirical validation of the blinding procedure. This approach addresses a fundamental and widely acknowledged problem in LLM benchmarking and is readily generalizable to other sequential decision domains.
  2. Attribution-based evaluation as a conceptual advance. Moving beyond raw return metrics to decompose performance into market, style, and stock-selection components is an important conceptual shift for trading agent benchmarks. The finding that most LLM agents show negative selection alpha despite positive total returns is a striking and consequential result that challenges the standard interpretation of trading benchmark scores. This framework sets a new standard for how financial agent performance should be evaluated and reported.
Critical weaknesses
  1. Narrow data modality limits the scope of inference. The benchmark is restricted to price/volume data and technical factors, omitting the unstructured textual data where LLMs have a comparative advantage over traditional quant models. As a result, the benchmark primarily tests technical trading ability rather than the broader information-processing capabilities that distinguish LLMs. This makes it difficult to disentangle "LLMs are bad at stock selection" from "LLMs have no advantage when given only price data."
  2. Attribution analysis is incomplete and under-explored. Return attribution is only applied to LLM agents, not to the ML baselines, leaving open the question of whether negative selection alpha is an LLM-specific phenomenon or a general result of price-only trading in this market. Additionally, the attribution model uses only nine technical style factors and excludes industry factors and fundamental factors. It is therefore possible that part of what is labeled "style" or "common" would be classified as selection alpha in a richer factor model, and the negative alpha result may partially reflect incomplete factor coverage rather than absent stock-picking skill.
  3. Market-specific design limits generalizability. The trading environment is highly specific to the Chinese A-share market . While this is appropriate for a CSI 300 benchmark, it means the behavioral findings and performance numbers cannot be directly generalized to US or global equity markets with different settlement rules, short-selling, and no daily price limits.
Questions for authors
  1. Data modality expansion: The benchmark currently uses only price/volume-derived features. Why were news articles, earnings reports, and fundamental data not included, given that LLMs' purported advantage lies in processing unstructured textual information? Are there plans to add these modalities in future versions?
  2. ML baseline attribution: Was return attribution also performed on the eighteen Qlib baseline models? If so, what are their selection alpha values, and how do they compare to the LLM agents? If not, would adding this comparison not strengthen the paper's conclusions about LLM-specific performance patterns?
  3. Industry-level identity leakage: Under stock-blind and blinded settings, agents could potentially infer industry membership from cross-stock price co-movement. Have you tested for industry-level identity recovery, and does industry-level leakage affect the interpretation of the masking results?
  4. Factor model robustness: The negative selection alpha result could be sensitive to factor model specification. How sensitive are the alpha magnitudes and signs to the number and choice of factors? Have you tested attribution with industry factors or fundamental factors, and if so how do the results change?
  5. Cross-market generalizability: Are there plans to extend KTD-FIN to other markets with more standard global trading conventions (T+0 settlement, short selling allowed, no daily price limits)? How do you expect the core findings might change?
3 comments

Thank you for recognizing the masking design, identity-recovery tests, and value of return attribution. Your questions help us clarify the evaluation objective and strengthen the comparison of return sources.

W1 / Q1. Price-based observations and historical information availability. KTD-FIN supports timely evaluation of newly released frontier models on a common, long trading window, despite heterogeneous or undisclosed knowledge cutoffs. Traceable price observations preserve a complete agent task involving retrieval, candidate comparison, portfolio management, and sequential execution. Adding historical text requires reconstructing what was actually retrievable at each decision: today's searches may return later-updated pages or retrospective summaries. Evaluation therefore needs archived as-of search contents, original publication dates, and availability dates. Fundamentals likewise require actual disclosure dates and revision histories, rather than reporting-period end dates. The revised Introduction clarifies the evaluation objective, and Limitations outlines the extension to historically aligned text inputs.

W2 / Q2. Return attribution for the Qlib baselines. We have extended the same nine-factor attribution, trading period, and aggregation convention to the existing trajectories of all 18 baselines (Appendix P). Eleven have negative selection contributions, while seven have positive contributions, including SFM (+12.6%), MLP (+11.9%), and Transformer (+8.8%). Thus, negative residuals occur beyond LLMs, while positive residuals are attainable in this price-based setting. The comparison strengthens the benchmark's purpose: similar account returns can have different sources. Contributions are additive; account returns are compounded.

ModelAccount return (%)Common (%)Style (%)Selection (%)Additive sum (%)
SFM+86.58+42.2+9.6+12.6+64.4
DoubleEnsemble+73.66+41.5+26.9−9.9+58.5
CatBoost+72.97+41.6+20.8−5.1+57.2
LightGBM+66.22+41.4+22.1−9.4+54.1
Transformer+60.35+43.2−3.1+8.8+48.9
LSTM+43.92+41.8+7.6−11.1+38.4
MLP+34.08+38.4−16.1+11.9+34.2
Linear+29.60+40.1+11.5−23.3+28.3
XGBoost+66.41+41.8+31.8−18.6+55.0
ADARNN+66.13+43.0+2.8+7.0+52.8
KRNN+62.09+41.2+3.7+5.9+50.7
Sandwich+56.57+40.4+11.7−5.2+46.9
…
GRU+34.05+42.4+6.6−17.4+31.5
ALSTM+22.67+43.6+0.4−20.9+23.0

Q3. Industry-level recovery. We evaluated five attackers on the same 51 stratified probes across 11 sectors, using the masked market context, candidate table, and stock snapshot available during trading. Eastmoney industry labels are mapped to 11 GICS-style categories. Top-1 accuracy ranges from 10.9% to 13.7%; all confidence intervals cover the uniform-random and majority-class references. The complete results have been added to Appendix K.

AttackerProbesSector top-1 accuracy (%)95% confidence interval (%)Uniform random (%)Majority class (%)
DeepSeek-V4.1-Flash5113.7[6.8,25.7]9.19.8
Claude Sonnet 5.55112.9[6.0,24.2]9.19.8
OpenAI GPT-6 Sol5112.2[5.5,23.0]9.19.8
Google Gemini 3.8 Flash5111.8[5.1,22.4]9.19.8
OpenAI GPT-6 Luna5110.9[4.4,21.0]9.19.8

W2 / Q4. Factor-number and factor-choice sensitivity. In addition to the leave-one-factor-out results in Appendix O, we re-estimated 200 random subsets retaining five to eight of the nine price-derived factors on fixed trajectories. Rankings remain closely aligned with the full specification, while signs vary most for models with smaller full-model residuals. The results show stable rankings and predominantly negative selection contributions across these tested specifications.

Statistic200 random subsets
Spearman correlation: mean/minimum0.976/0.891
Correlation ≥0.95 (%)93.5
Negative models: mean/median8.24/8
≥6 negative models (%)96.5
Negative cross-model mean selection198/200
All 10 models negative (%)43
≥9 models negative (%)46

Negative-selection frequencies were 100% for Gemini, DeepSeek, GLM, and Kimi; 98% for GPT-5.5; 96% for Step; and 44%, 49%, 62%, and 74% for Claude, Qwen, Doubao, and MiniMax, respectively. Industry and fundamental factors concern the evaluator's exposures and need not be agent inputs. Our current sensitivity tests examine price-derived specifications; evaluating broader specifications requires additional point-in-time exposure data. Selection alpha is defined relative to the specified factor model. Market timing, style allocation, and stock selection can each be valuable; attribution reports their realized contributions.

W3 / Q5. Other markets. CSI300 provides a real market with explicit execution constraints for matched comparisons. The masking interface and attribution procedure can be reused with market-specific execution engines. The revision strengthens the controlled comparisons in CSI300 and identifies additional markets as an extension of the benchmark.

I would thank the authors for the detailed response and huge efforts on additional experiments. My questions has been resolved and I will upgrade my rating to 4.

Thank you for your thoughtful review. We’re glad our response addressed your questions.

Comments on the paper

1 comment

Dear Area Chair and Reviewers,

Thank you for reading our paper closely and for returning to the discussion after the rebuttal. We appreciate your comments on the masking and attribution design and on the trading rules and range of models we evaluated.

We built KTD-FIN so that newly released trading agents can be compared on the same historical market. We vary whether agents see stock identifiers and dates in prompts and tool outputs, then trace their returns to market exposure, style exposure, and stock selection. In our CSI300 evaluation, masking changed how agents explained trades and allocated capital. Market and style exposures accounted for much of the ten agents’ returns.

  • Stock selection across baselines. qDrQ and 6mra asked how the 18 Qlib baselines fared under the same nine-factor model. Eleven had negative stock selection contributions and seven had positive ones, compared with nine negative contributions among the ten LLM agents (Appendix P).
  • Masking and factor choice. We tested whether five models could infer a stock’s industry from masked inputs. For each model, the 95% confidence interval for accuracy included the scores of both the random and majority-class baselines (Appendix K). Across 200 random factor subsets, some selection contributions changed sign, but the models ranked much as they did under the full specification (mean Spearman correlation 0.976, Appendix Q).
  • Company knowledge and memory. Following the discussion with 6mra and nc8J, we compared Doubao 1.6 across six windows before its release and two after (Appendix R). For Step-3.5-Flash, GPT-5.4-mini, and hy3, the return advantage of seeing stock identifiers and dates generally narrowed after each model’s knowledge cutoff.

We have also shortened the title to "KTD-FIN: A Memory-Controlled Benchmark for LLM Trading Agents on Stock Markets". We have marked the revisions in blue. Thank you again for helping us improve the paper.

Best regards,
The Authors

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