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Under review as a conference paper at ICLR 2027

Agentic Factor Engineering: Turning Investment Questions into Factors

Abstract

Factor construction turns investment ideas into numerical signals for quantitative investment. Automated methods can generate factor formulas and programs, but a single fixed formula cannot fully capture many investment judgments. For example, assessing whether a company's new capacity has begun to translate into deliveries requires examining disclosures, production data, and price records together. The key evidence differs across companies. We propose Agentic Factor Engineering, using investment questions to define natural-language factors. An executor agent follows common execution and scoring rules to read records, perform calculations, and assign each stock a score with supporting evidence. We also explore search over natural-language factors through return-guided evolution, using return evaluations and company cases to revise questions and expand the candidate bank. We then select ensembles from all generations using validation performance. Experiments on fundamental and technical factors in CSI300 and Nasdaq-100 support question-based measurement through formula comparisons, controlled evidence changes, and repeated execution. In chronologically held-out tests, selected ensembles achieve higher information coefficients (IC) and rank information coefficients (RankIC) than initial ensembles in three of four settings, suggesting predictive potential for this approach to factor construction.

Primary area:
foundation or frontier models, including LLMs
Keywords:
LLM Agents, Automated Factor Discovery, Quantitative Finance, Natural-Language Factors, Evolutionary Search

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_hFXmOpenReview ↗
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4(+1)
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Paper summary

This paper defines a factor as an investment question together with a fixed execution protocol. An agent reads the records available on the scoring date, may write code, and returns a score from 0 to 5 along with supporting evidence, counter-evidence, and missing information. A second loop rewrites questions from development-period returns and company cases. Candidates from every generation stay in a bank, and the set used at test time is chosen on a later validation window, then frozen. The empirical work has two parts. One asks whether the score measures the property named in the question: agreement with classic formulas, response to edited evidence, and stability across repeated runs. The other asks whether validation-selected ensembles predict returns better than the starting questions. On CSI 300 and Nasdaq-100, in both fundamental and technical settings, the selected ensemble improves IC and RankIC over the initial ensemble in three settings out of four. The test window is January to March 2026. The authors describe this as a feasibility result.

Critical strengths

1.The paper is clear about what a score is supposed to mean. Measurement and return prediction are set up as separate tests, and the write-up does not treat a high score as a claim about future profits. The formula comparison, the controlled evidence edits, and the repeated runs each answer a different question. The Amihud illiquidity question, where the agent ranks stocks in the opposite direction from the formula, is reported in the figure rather than dropped.

2.The execution protocol is concrete. The rubric, the tools, the token accounting, and the Zscaler trace make it possible to see the agent retrieve filings, compute a quantity, notice a sign error, and correct it before scoring. The case studies also keep the counter-evidence in the answer when the score is at the top of the scale.

3.The selection rule is more careful than keeping the question with the best in-sample IC. A question has to look acceptable on its weaker horizon, and the chosen set is fixed before the test months. The authors also state the setting that goes the wrong way: on Nasdaq-100 technicals, the selected ensemble is worse than the initial one on IC, RankIC, and spread.

Critical weaknesses

1.The out-of-sample results are not separable from noise. The test contains only three scoring dates, January through March 2026. The main table reports neither standard errors nor a test against the initial question set. Fundamental evaluation also uses 90-day returns, so labels from adjacent months overlap heavily. The Nasdaq-100 fundamental IC rises from near zero to about 0.10, the largest gain in the paper and the one most dependent on this short sample. The appendix reruns show that, with the question text held fixed, median validation fitness already moves by about 0.04. The validation gain of the leading Nasdaq-100 fundamental questions is about 0.04 as well.

2.The paper’s own comparison is unstable, and the gains do not clear a simple baseline. Relative to the initial question set, IC and RankIC improve in three of the four settings, but the CSI 300 long–short spread is essentially unchanged or lower, and the Nasdaq-100 technical ensemble is worse on IC, RankIC, and spread. The results may show only that selection sometimes rewrites the authors’ own initial questions. They do not show that the scores form a distinctive predictive signal.

3.Cutting off the files at the scoring date does not rule out information already present in the model weights. The executor is a general-purpose 2026 model, and the sensitivity runs use models from the same period. Retrieval is restricted to records available by the scoring date. The paper reports no knowledge cutoff, and it provides no control with an earlier-cutoff model or a retrieval-only setup.

4.The measurement experiments do not test the factors that enter the final evaluation. Formula agreement, controlled evidence changes, and repeated execution are run on classic questions or on the initial questions. The evolution instructions ask for questions on which a higher score means a higher expected return, and they allow a stably negative question to be reversed outright. After such a reversal, the score tracks the rewritten return direction rather than the original investment judgment. Measurement validity and return prediction are therefore results about two different sets of factors, and the paper does not connect them.

Questions for authors

1.On each validation and test date, how many stocks receive a score? Is that the full index, or the development subsample of 300 agent tasks spread over the year? If the validation RankIC is computed on a thin cross-section, the selection rule is fitting a noisy statistic.

2.How many questions are retained, and are they rescored on the test dates under the frozen protocol? Please list the selected questions, including any whose meaning was reversed.

3.What is the pretraining cutoff of DeepSeek-v4-flash, and were the document summaries produced by a model that had already seen text from after the scoring date? The informative check is to rescore the test panel with a model whose cutoff precedes April 2024, or with retrieval only.

4.For the evolved questions that enter the test, is there a measurement check comparable to the formula agreement figure? In particular, after a question is reversed so that its RankIC changes sign, what property does the score still measure?

3 comments

Thank you for the careful reading and these comments. A factor here is the investment question plus a fixed execution protocol: the agent reads company materials and returns a score with checkable evidence, so factors can express ideas requiring several sources. Measurement consistency (formula agreement 0.821/0.728; strict P>B>N in 33/40; ICC 0.862/0.704) is tested independently of returns, and the return and evolution experiments ask whether such factors plug into a factor research workflow; the revision softens the return claims, as agent subjectivity, market complexity and low signal-to-noise make consistent returns difficult. We added a sampling-variation analysis, the selected-question list, the semantic-reversal explanation, the cutoffs and a retrieval-only baseline.

W1 & Q1. Short test period and overlapping labels; samples per date

Overlap between neighboring forward-return windows is ordinary in sequence experiments: rolling-origin evaluation advances the forecast origin step by step and reuses most of the preceding history as input, and sliding windows feed the same observations into many training examples, without the shared part ever including the outcome being predicted. Our metrics are computed within a single scoring cross-section, and the gaps between development, validation and test are wide enough that no outcome window straddles a stage boundary, so overlap cannot carry information from one stage into another.

Each scoring date has a few dozen samples; we use stratified sampling, fixed panels and per-date median RankIC, taking the weaker of the two horizons. As small cross-sections still fluctuate, we resample the 300 agent tasks 5,000 times, stratified by date and industry. Only NDX fundamental is clearly above sampling variation: its IC and RankIC differences (0.096, 0.082) are about twice the bootstrap SEs (0.026, 0.030); elsewhere they are below or near the SE. This matches the fitness change of about 0.04 under fixed question text (Elite ΔF 0.036 fundamental, −0.043 technical).

W2. The improvement is unstable; is it only a restructuring of the initial questions

Revising existing questions is itself part of factor development: we examine whether natural language can serve as the factor definition, so we do not require every descendant question to propose a new mechanism.

W3 & Q3. Future information in model parameters; cutoffs; earlier models or retrieval only

Public information and our own tests put the cutoff of DeepSeek-v4-flash at about May 2025 and that of Qwen3.6-35B-A3B, which writes the summaries, at about March 2025 (now in Appendix C, marked as approximate). Validation (Jul–Sep 2025) and test (Jan–Mar 2026) come after both, so final selection and test scoring should not use memorized information from those periods; development (Apr 2024–Mar 2025) lies inside the models' knowledge, as stated in the appendix. Earlier-cutoff models lack the capability for multi-source retrieval; later-cutoff models compress the available dates, lowering confidence on low-SNR data. The two cannot both be met, so development lies inside the knowledge range while validation and test follow the cutoff, leaving no direct leakage.

The retrieval-only baseline needs a program for mixed inputs, so we report it for reference only. It is strongest on NDX technical (IC 0.070, RankIC 0.071, close to Consolidated NL's 0.059/0.050) and near zero or negative elsewhere: it derives from agent-rewritten questions, and the technical setting is mostly structured market data, where programs have an advantage. Our gains come mainly from fundamental judgments.

W4, Q2 & Q4. Measurement checks and semantic reversal; questions kept; the list

Semantic reversal rewrites a question rather than flipping the sign of a score. The agent sometimes ignores direction, so two phrasings of one idea can give ICs of opposite sign; rather than compare |IC|, we have the agent state the opposite hypothesis when a question shows a persistent negative relation, so a high score means a more positive expected return. Five final questions were reversed: CSI300 technical #1 and #2; NDX fundamental #1 (leverage expansion to deleveraging) and #5 (leverage reversed with a risk constraint); and NDX technical #4 (volume expansion to a 20-day contraction). The rest keep their direction. We keep 12 questions per setting, re-executed on the test-date materials; the full text is in Appendix E.3, Table 11.

On the measurement checks: the factor is the question itself, and it can express any property stated in natural language, not only those a formula can capture. Formula comparison asks whether a score ranks stocks as the matching formula does, so it needs a formula to compare against, and the classical questions have one; most final questions instead combine unstructured sources (filings, news, sell-side text) and involve judgment, so no formula defines their target, which is why we define factors by questions.

Thank you for the authors' response. My main concerns are addressed, And I think the experiment and ablation are enough to support the papers declare. However, there are fewer factor formulas released by the authors, so it is less likely to check the real expression to understand the economic logic. However I think the work is well organized and expressed and I am willing to update my score, good job.

Thank you very much for your thoughtful follow-up and your willingness to update your score. We sincerely appreciate the time and care you have put into reviewing our work. Your feedback has helped us strengthen the experimental evidence and clarify the scope of our claims.

We also appreciate your suggestion regarding factor interpretability. Making the economic intuition behind each factor directly accessible is indeed one of the motivations for our natural-language formulation. For reference, the full text of all 48 selected questions is provided in Appendix E.3 (Table 11).

Thank you again for your constructive feedback and encouraging assessment.

Reviewer_6tZ1OpenReview ↗
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2
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3
Informativeness
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Paper summary

The paper turns an investment question into a factor. An executor agent reads each company's records, answers the question, and returns a 0–5 score plus supporting and counter-evidence. A reflection agent and an evolution agent then revise the question bank using returns, and a factor bank keeps every generation for selection on a separate validation period. The main evaluation compares the starting questions with selected questions in fundamental and technical domains.

Critical strengths

Measurement validity is tested independently of predictive validity, and neither test uses future returns. Formula agreement shows the score tracks its intended property (Figure 2), while the controlled-evidence test shows it responds to relevant evidence but not irrelevant identifiers ( Figure 3). The measurement protocol therefore remains informative even where predictive results are mixed.

Run-to-run reliability is measured. Five runs give ICC of 0.862 for fundamentals and 0.704 for technicals, with score correlations of 0.824 and 0.695 . This gives a scale for judging whether Table 2 differences exceed run-to-run variation, which most factor papers do not provide.

Critical weaknesses

Nothing separates evolution from selection, so the central claim is not established. Consolidated NL is defined as questions selected from the factor bank using validation performance, and the bank keeps every generation, including the 12 starting questions. Picking the best questions by validation RankIC could raise test IC even if evolution did nothing, and Table 2 has no selection-only row that picks from the starting questions alone. The gain from Initial to Consolidated therefore cannot be attributed to the evolution loop.

The paper does not report how Table 2 handles run-to-run variation. Table 1 gives ICC of 0.862 and 0.704 over five runs, but the paper does not carry that reliability over to the IC comparison in Table 2. A reader therefore cannot tell whether small IC changes are signal rather than noise. The NDX technical decline, where all three metrics fall, is also left without diagnosis.

Questions for authors

Can you add a selection-only baseline that picks the top questions from the 12 starting questions by validation score, with no evolution?

Can you carry the Table 1 reliability over to the Table 2 comparisons, so we can tell whether small IC changes exceed run-to-run variation?

When should someone use the evolution loop rather than selecting from the starting questions by validation RankIC, and would that advice survive a change of executor?

1 comment

Thank you for the careful reading and for these constructive comments. The paper keeps the investment question itself, together with a fixed execution protocol, as the definition of a factor: the agent reads company materials and returns a score with checkable evidence, so that a factor can express investment ideas that need several sources. Measurement consistency is tested by formula agreement (0.821 and 0.728), controlled evidence (strict P>B>N in 33/40) and repeated execution (ICC 0.862 and 0.704), all independent of return evaluation; the return and evolution experiments then ask whether such factors can be plugged into a factor research workflow. In this revision we have further softened the claims about returns: the subjectivity of agent execution, the complexity of financial markets and the low signal-to-noise ratio of financial data make consistent returns difficult, and we leave that question to future work.

In response to your comments, we added a selection-only control and a run-to-run analysis. Together they establish measurement consistency, separate evolution from selection, and quantify the uncertainty of the test results.

W1, Q1 & Q3. Whether the gains come from evolution or from selection; when to use evolution

We added a selection-only control: within the 12 initial questions only, Top-3/6/12 are selected by the same validation score as the final ensemble (Top-12 is Initial NL).

Location: Appendix E.2, Selection-Only Baseline, Table 7 (Spread in %)

SettingEnsembleICRankICSpread
CSI300 Fund.Initial Top-30.0830.0324.56
Initial Top-60.0630.0033.66
Initial Top-12 (Initial NL)0.0940.0395.63
Consolidated NL0.1020.0525.61
CSI300 Tech.Initial Top-30.015-0.0090.48
Initial Top-60.028-0.0100.48
Initial Top-12 (Initial NL)0.0570.0180.52
Consolidated NL0.0630.0430.17
NDX Fund.Initial Top-30.0420.0353.81
Initial Top-6-0.053-0.051-0.95
Initial Top-12 (Initial NL)0.0020.0003.17
Consolidated NL0.0980.0827.84
NDX Tech.Initial Top-30.0590.0492.34
Initial Top-60.0540.0402.04
Initial Top-12 (Initial NL)0.0720.0642.30
Consolidated NL0.0590.0501.65

Consolidated NL attains the highest IC and RankIC in three of four settings (CSI300 fundamental, CSI300 technical, NDX fundamental), and selection within the initial questions varies across settings: there is no clear evidence that selection alone identifies good factors. The two steps play different roles. Evolution uses development-period return feedback and company cases to rewrite questions and widen the candidate pool; selection uses only the validation period, to test persistence outside it, which is also a standard guard against overfitting. The 12 initial questions were designed for coverage, so they are few and heterogeneous, leaving little room for selection, and their validation ordering need not carry over to the test period. On when to use evolution: if the initial questions already embed enough prior experience, validation-period selection alone suffices and also checks for overfitting; if coverage has to be extended, or development-period feedback written into the questions, evolution supplies the candidates and validation-period selection tests their generalization. As results differ across executors (main-text Fig. 6, Appendix E.3), we recommend treating the executing model as part of the protocol, re-scoring and re-selecting after any change.

W2 & Q2. Reliability of repeated execution; the decline on NDX technical

The run-to-run standard deviation comes from five independent executions on identical scoring inputs. On that scale, the IC and RankIC differences for NDX fundamental (0.096 and 0.082) are several times the run-to-run SD, whereas in the other settings the differences are comparable to it. NDX technical does decline (IC 0.072→0.059), and the change lies within the run-to-run SD (Initial NL IC SD 0.047); technical signals are sensitive to the market environment, and the pipeline selects by per-question fitness rather than ensemble performance, so we regard this setting as one of the limitations of the current mechanism.

Table 6 (left) omitted for the 5,000-character limit; see Appendix E.2.

Reviewer_LwH9OpenReview ↗
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2
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2
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Paper summary

This paper proposed a new method for generating trading strategies in an LLM agent system, turning the problem into "Agentic Factor Engineering (AFE)" paradigm, which takes investment questions in natural language as factors and use the aggregated factor evaluation over a set of such factors as the evaluation of a stock. The paper employed an executor agent to score a stock on a given set of factors, then the evaluator agent uses the aggregated scores (actually the ranked scores) to generate a feedback of the performance of this set of factors, then the reflection agent and evolution agent choose either to adjust the set of factor or to use such a set as the factor bank in downstream trading.

An experiment is conducted on CSI300 and NDX data, examining whether factor scores are related to returns and how questions evolve in fundamental and technical domains together with model sensitivity analysis. Results show that the IC of AFE is higher than numeric methods, while the RankedIC is usually not as good. while in 3 out of 4 cases the consolidated AFE factors behave better than the initial factors. However, the spread (avg of top 20% - avg of bottom 20%) of consolidated factors outperforms the initial ones only in NDX-fondamental group out of all 4 groups.

Critical strengths
  1. The natural language factors are more flexible than numerical ones, making it capable to encounter and use the information of stocks which the classical numerical data cannot cover or hard to be numerically measured.

  2. There is a closed loop on choosing and refining those natural language factors.

  3. LLM scoring can contain also the human-readable scoring reasons, which are useful in backtrack analysis and decision explanation.

  4. The expeirment contains multiple conditions on multiple datasets.

Critical weaknesses
  1. The paper reported a historical investment return data in experiment, but only 1 out of 4 shows improvement in spread (between top-scores and bottom-scores) than the initial factors. This may indicate that the evolution loop of factor bank may fail to be profitable in most cases. So whether this system is suitable to be applied in real trading is still questionable.

  2. The factor aggregator is too limited: the paper chooses factors (questions in natural language) according to each factor's performance on dataset, and the aggregation simply follows the average of ranked scores on all factors. In fact, the factors may affect in a nonlinear and combined way while such factor-choosing and aggregating method cannot handle. The factor-choice may allocate similar (and redundant) single factors which behave better, while missing the factor-combinations which are not strongly related to return but only behave well in a combined way (usually nonlinear, like A*B or (1-A)(1-B) ).

  3. The granularity of scoring (between 0 to 5) is coarse, which may not be capable to distinguish stocks when the stock-bank is large. In other words, since the LLM-facors and numerical factors are both available, it is necessary to conduct an experiemnt on comparing the performance of pure LLM-factors and that of the combination of both LLM-factors and numerical factors.

  4. The sensitivity test may also contain the sensitivity on initial factors, searching rounds and factor-bank size.

  5. The testing time-span (5 / 15 days on techinical and 30 / 90 days on fundamental) is relatively short, the factors generated may not reflect long-term properties.

Questions for authors
  1. How to exclude the data leakage? I mean, when we are using LLMs to score on investment questions, the future status / information of the stock / company may occur in training data. So it is not clear whether the LLM generates scores according to purely given information or also according to their training data.

  2. The scores across stocks / companies may not be comparable enough? Scores may be affected by how much the key information is known. A simple 0-5 score may not contain the confidence / certainty.

1 comment

Thank you for the careful reading and these comments. A factor here is the investment question plus a fixed execution protocol: the agent reads company materials and returns a score with checkable evidence, so factors can express ideas requiring several sources. Measurement consistency (formula agreement 0.821/0.728; strict P>B>N in 33/40; ICC 0.862/0.704) is tested independently of returns; the return and evolution experiments only ask whether such factors plug into a factor research workflow, and the revision softens the return claims, as agent subjectivity, market complexity and low signal-to-noise make consistent returns difficult. We added cross-question correlations, the combination with numerical factors and the cutoffs.

W1. Spread improves in only one setting; applicability to real trading

We agree that Spread is the raw historical return difference between the top and bottom groups, before turnover, transaction costs and risk controls, and should not be read as strategy return. The paper tests the feasibility of a factor representation and pipeline, distinguishing "application potential" from "direct deployment"; we therefore report all four settings, including the weaker NDX technical one (NDX fundamental Spread rises from 3.17% to 7.84%). Applications differ in their reliance on Spread: index-enhancement portfolios care about cross-sectional ranking, long-short portfolios about the two tails, so a single setting does not settle application value.

W2. Simple aggregation, possible redundancy, missed non-linear combinations

The aggregation uses only the per-question validation ranking and an equal-weight average of percentile ranks, with no search for non-linear complementarity; we kept it transparent so differences come from the question representation rather than a fitted model. The mean absolute correlation of the final sets falls for CSI300 technical (0.259→0.229) and NDX fundamental (0.271→0.162) and rises for CSI300 fundamental (0.392→0.513) and NDX technical (0.318→0.386), with the share of |ρ|≥0.8 moving the same way. This shows that per-question selection does not consistently change redundancy, nor systematically compress diversity; controlling redundancy explicitly needs ensemble-level objectives at selection, which is future work (Appendix E.3).

W3 & Q2. Coarse 0–5 scale; LLM factors versus LLM plus numerical factors; comparability

Granularity: LLM scores concentrate on a few scale points even with a wider scale, so a finer scale need not discriminate better; per-question scores do cover all levels 0–5 (Appendix Table 5), and averaging the percentile ranks of 12 questions discriminates more finely than a single score.

Comparability: each question is answered within the available data under one rubric (supporting evidence in 99.9% of responses), and aggregation uses within-date percentile ranks, so scale differences across companies and dates do not enter the score; the agent also reports information gaps (73.8%) and confidence (71.6% at 4–5). Confidence weighting and dropping scores below 3 change little (IC falls slightly in three of four settings): confidence is high overall and does not track predictive value.

Combination: mixing Consolidated NL with the six classical numerical factors of the domain at weights λ and 1−λ, the fundamental domain exceeds either component alone at intermediate λ (CSI300 IC 0.031 at λ=0, 0.120 at 0.5, 0.102 at 1; NDX 0.019 at 0, 0.105 at 0.75, 0.098 at 1), whereas in the technical domain pure natural-language has the highest IC (0.063 and 0.059). As the executor can call programs, natural-language factors can in principle cover what formulas express (Appendix E.2).

W4. Sensitivity to initial factors, search rounds and bank size

The cumulative discovery curve (Appendix Fig. 10) grows steadily and has not saturated by round 5, with the candidate bank traced in main-text Fig. 5; limited by cost, we stopped at round 5. The initial factors determine the ideas each domain covers and should have some effect, but testing this requires redoing the whole experiment, so we leave it to future work.

W5. Short holding horizons

30/90 days for fundamental and 5/15 for technical is already long in the factor literature. Longer horizons leave fewer scoring dates and worsen label overlap, and returns are more exposed to the macro environment and company events, which makes the signal harder to isolate.

Q1. Excluding future company information from LLM pretraining

As in our reply to Reviewer 2 (W3): the cutoffs are about May 2025 for DeepSeek-v4-flash and about March 2025 for the summary model, both before validation and test, while development lies inside their knowledge (Appendix C). Earlier-cutoff models lack the agent capability and context length needed here; later-cutoff models compress the available dates. Since the two cannot both be met, development lies inside the knowledge range while validation and test follow the cutoff.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Summary of Rebuttal and Revisions

Dear Area Chair and Reviewers,

We sincerely thank the AC and reviewers for their careful reading and constructive discussions. We would like to briefly summarize the paper's contributions and the main updates during rebuttal.

Key contributions. We introduce natural-language factors defined by investment questions and a fixed execution protocol, enabling agents to measure economic properties that are difficult to express through fixed formulas. Importantly, we evaluate whether the resulting scores reflect their intended properties independently of return prediction, through formula agreement (mean Spearman 0.821/0.728), controlled evidence changes (strict P>B>N in 33/40), and repeated execution (ICC 0.862/0.704). This separation of measurement validity from predictive performance was recognized as a strength by reviewers 6tZ1 and hFXm. We further demonstrate the feasibility of integrating these factors into an evolution-and-selection workflow.

Major concerns addressed. During rebuttal, we provided additional experiments and clarifications:

  1. Evolution versus selection: We added a selection-only baseline (Appendix E.2, Table 7), against which Consolidated NL achieves higher IC and RankIC in three of four settings.
  2. Evaluation reliability: We clarified overlapping return windows and added run-to-run standard deviations and bootstrap standard errors to quantify uncertainty. Given agent-executed scoring and the low signal-to-noise ratio of financial data, we position the return experiments as preliminary evidence of feasibility rather than proof of stable profitability, with NDX fundamentals showing the clearest improvement.
  3. Data leakage: We documented approximate model knowledge cutoffs: the validation and test periods fall after them, while the development period lies within them, a trade-off between agent capability and available dates that we state in the appendix. We also added a retrieval-only reference baseline.
  4. Interpretability and robustness: We clarified semantic reversal, examined cross-question correlations and combinations with numerical factors, and provided all 48 selected questions in Appendix E.3.

Reviewer feedback. We are encouraged that Reviewer hFXm indicated that their main concerns were addressed and that the experiments and ablations support the paper's claims. We appreciate this feedback and the constructive comments from all reviewers.

Broader significance. Factor investing is a demanding testbed for LLM agents: signals must be evidence-backed and judged out of sample under low signal-to-noise. More broadly, our work demonstrates a framework for evaluating whether agent-generated scores reflect their intended properties, independently of their downstream predictive performance. We believe this measurement perspective is relevant to agent-based research in other noisy, evidence-intensive domains.

We thank the AC and reviewers again for their time and consideration.

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

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