From Individual Decisions to Collective Outcomes: A Scoping Review of LLM Agents in Financial Markets

This review covers research published or posted from November 1, 2022, to September 27, 2026, in which an LLM judges, chooses, forecasts, advises, trades, or participates in a financial market. Eligibility followed a shared protocol and scoping review conventions (Arksey & O’Malley, 2005; Tricco et al., 2018). The protocol, reproduced in Online Resources 1 and 3, was not registered; boundary rules were refined at consolidation and applied to the 155 records on which the search arms disagreed (Online Resource 2). Five categories qualify: synthetic economic subjects, market simulations, task-performing agents, audited financial judgments, and validity and methodology. Studies without a financial task qualify if they test constructs central to behavioral finance, such as risk preferences, loss aversion, anchoring, and rationality. Studies using LLMs only as text-feature extractors, sentiment scorers, or question-answering systems were excluded, as were non-English records and studies in which only humans made decisions. An asset forecast qualifies when the model’s judgment is evaluated. Decision systems qualify when an LLM’s judgment, forecast, proposed strategy, or advice enters an evaluated decision, even if a rule, optimizer, or learned policy executes it. Online Resource 2 provides the full eligibility and boundary rules and the completed reporting checklist of Tricco et al. (2018).

Three search arms, each run independently by a separate LLM agent, followed a shared protocol: a source-first search of arXiv and journal records via Crossref; a concept-first search using web queries, OpenAlex, SSRN, and citation chasing; and a seed-first search of citation networks and working paper series. Citation-neighborhood searches, re-screening of excluded records, and Consensus queries supplemented these arms. The search covered records public through September 27, 2026; the final pass on that date could not query arXiv or OpenAlex directly and reached SSRN only through Crossref, so coverage of the final days is less complete (Online Resource 2). After deduplication and eligibility checks under the rules in Section 2.1, the corpus contained 599 papers. Fig. 1 shows the screening flow, and Online Resource 2 details the sources, queries, and counts at each stage.

Every included record was verified against its primary metadata record in Crossref or arXiv, or on the publisher or repository page. A total of 583 records matched, and 16 showed a recorded discrepancy; the author manually reviewed each discrepancy and confirmed the resolution recorded in Online Resource 1. Two of the included papers are marked as withdrawn by their authors (Section 7.3). These checks established bibliographic identity; the findings were coded separately (Section 2.3).

The search ledger has gaps: 1,250 seed-first abstract exclusions were counted but not itemized, and 11 source-first exclusions were unaccounted for. Another 24 records were excluded because their abstract or primary record could not be obtained. Title-stage exclusions were counted rather than being listed. Consequently, screening cannot be reconstructed record by record. The arms supply independent discovery routes rather than independent human screening judgments. The author manually validated the stage counts in Fig. 1 and the final corpus against the search ledger but did not re-screen excluded records. Therefore, this review is a transparently bounded scoping review rather than an exhaustive systematic review. The query log completeness is documented in Online Resource 2.

The taxonomy comprises five categories and 31 nodes (Table 1). The synthesis codes 276 papers: 273 in categories a, b, d, and e, plus two system evaluations (Barton et al., 2026b; Duan et al., 2026) and one evaluation review (Nguyen & Pham, 2026). Five are secondary syntheses, leaving 271 primary studies. Because the synthesis set is selected by category, a share such as 30 of 271 describes that set, not the 599-paper corpus. The system audit does not code price formation, so the 30 price-setting designs are a lower bound for the corpus. Eight facets record finance relevance and evidence stratum, intended agent role, demonstrated agency, interaction structure, environment and price formation, heterogeneity, outcomes by level, and design and validation, including the human comparator. Online Resource 2 gives the full definitions, and Online Resource 1 the paper-level coding. Of the 276 papers, 222 were read in full, 48 were read from abstracts, and 6 were read from metadata alone.

A separate audit covers the 295 category-c papers that design or benchmark financial decision systems (including three reviews filed under task nodes), of which 220 were read completely. The audit records the evaluation design and test window, models and versions, model-knowledge controls, transaction costs, who selects the action, LLM teams, and code releases. The two sets do not overlap; the two system evaluations coded in the synthesis are excluded from the audit. The 29 papers in the review node and three simulation surveys are profiled separately to position this review.

Reported numbers retain their units, uncertainty, and source locators. “Not reported” requires a full-text search, “not extracted” marks an abstract-only reading, and “not applicable” marks a feature that the design does not call for, such as trading costs in a valuation audit. The authors’ interpretations and coders’ readings remain separate. The synthesis is narrative and organized by facet. Effect sizes are not pooled; studies using the same behavioral label often measure different estimands, such as an anchoring index, a pass-through slope, or a share of anchored questions. Abstract-based claims are identified in the text.

For the 30 price-setting designs (studies with endogenous prices), Online Resource 1 codes the 12 components of the five conditions in Section 8, distinguishing source statements, coder inferences, absence, insufficient access, and non-applicability. A design counts when prices respond to the LLM agents’ own orders or forecasts; two studies in which LLM output only sets the parameters of rule-based traders in a separate model are not counted. Online Resource 1 lists each uncertain or boundary code with its evidence and the effect of the alternative reading. Section 8 reports how the component counts change for these alternatives.

The LLM agents conducted the review under written protocols. Claude models (Anthropic, September 2026) performed the searches, screening, extraction, bibliographic verification, coding, count computation, figure programming, and initial drafting; the retained session logs recorded the model identifiers (claude-fable-5-1 for the search arms and consolidation; claude-opus-5-5 for coding, the system audit, verification, and revision). Sampling parameters were left at the platform defaults and not recorded. The written protocols are reproduced in Online Resources 1 and 3, and the task prompts of the retained agent runs are available from the author. Separate agents ran the search arms, consolidated the records, and produced the evidence files; agents that had not produced the evidence then checked each section’s claims against its sources.

A model from another developer (GPT-6 Astra, OpenAI, September 2026; recorded by model name only) performed a targeted omission assessment using Consensus and assisted with source verification at the recorded reading depths. Its audit of the 360 component codes of the 30 price-setting designs revised 16 of them. Codex (OpenAI, October 2026) recoded a stratified sample of studies for the cross-model check described below, and adjudicated the count-relevant disagreements from that check against the sources. Online Resource 1 records the evidence locators, and Online Resource 2 documents the workflow.

The author set the research question and scope, ruled on the corpus and on cases escalated before the synthesis, developed and revised the argument and manuscript, and takes responsibility for its content. The author also manually validated the counts, figures, evidence locators, and section claims reported before the October 9, 2026 publication update against the underlying sources and evidence files.

Online Resource 1 itemizes the documented checks. The author’s 56 item-level verdicts comprise 17 checks of the codes behind the headline counts and 24 stratified spot checks of synthesis judgments, all of which confirmed the coded values, and 15 rulings on boundary and eligibility cases, of which one recoded a component and three excluded records. One ruling, which kept a human-benchmark code negative on the agents’ reading of Shah et al. (2025b), was later superseded by the source adjudication described below. Later checks recoded five facet values and corrected one transcribed number (sheet “Recodes after check”).

As a cross-model check, Codex agents recoded a stratified random sample of primary studies from their sources (seed 20261009; Online Resource 1, sheet “Cross-model check”); their working records show no access to the Claude agents’ codes. The sample comprised all 30 price-setting designs and 25 studies from three other strata; one design is excluded because a later Codex update also revised its codes in Online Resource 1. Four Codex agents coded separate batches, and other Codex agents rechecked the codes against the sources, changing 13 of them.

Across the eleven facets of the remaining 54 studies, agreement with the Claude agents’ codes ranged from 65% for independent elicitation to 100% for dated model snapshots. Cohen’s kappa was 0.82 for price formation, 0.79 for the human-surrogate role, and 0.74 for the human comparator (Online Resource 2, Table S4). On price formation, Codex coded 28 of the 29 sampled price-setting designs as endogenous (it could not access the remaining one) and none of the other 25 studies. For the six audited components, 153 of 162 codes agreed across the 27 price-setting designs that both sets of agents read in full. Most disagreements arose in multi-agent designs, where Codex also coded independent elicitation (18 studies) or network transmission (8) that the Claude agents had not; among the 27 designs, it also coded more as having a same-design human benchmark (9 rather than 5), as comparing dispersion with humans (5 rather than 3), and as varying the trading mechanism (4 rather than 3). These figures measure agreement between two AI coding processes rather than inter-rater reliability, and Table S4 reports them as scored, before adjudication.

On October 11, Codex agents checked the seven component disagreements that could raise a reported count against the cited source versions. Two codes changed: Shah et al. (2025b) compare numerical bid–value gaps with published human results under the same auction design, and Hansen and Lee (2025) compare an updating market-maker price with a fixed one. The other five remain negative under the written definitions (Section 8; Online Resource 1, sheet “Source adjudication”). The remaining disagreements, nearly all in facets, were not adjudicated.

Task-performing agents dominated the corpus (326 papers), followed by validity and methodology (79), audited judgments (78), synthetic subjects (69), and market simulations (47). Most of the work was unrefereed: 350 papers were working papers, 133 were conference proceedings, and 116 were journal articles. Table 1 shows the category, year, and publication status distributions; the 2026 counts cover only January 1–September 27.

The framework distinguishes three decision levels and a validation layer (Fig. 2). Individual decisions refer to choices, estimates, forecasts, or advice elicited based on a specific prompt and instrument. Coordination within a decision system combines specialized LLM roles within a pipeline to serve a single objective. Interaction among economic participants concerns separately motivated agents that affect one another through prices, payoffs, networks, or shared advice, including human–AI markets. Validation across levels asks whether a measurement supports its use at the next level; it cuts across the three decision levels rather than forming another aggregation stage. It includes training data contamination, prompt and persona sensitivity, run and version variation, human benchmarks, evaluation design, and the inferential unit.

The three decision levels are analytically linked. For claims that explain market outcomes using measured LLM decision rules, credibility requires three links to be established. The individual decision rule must be measured validly (the validation layer applied to level one), the aggregation mechanism must be represented rather than assumed (level three), and any within-system pipeline that produces an agent’s orders must be treated as part of that agent’s decision rule (level two). Experimental economics provides benchmark logic. Laboratory asset markets show that human traders generate bubbles and crashes even when the fundamental value is common knowledge (Smith et al., 1988) and that expectations feedback determines whether prices converge or oscillate (Heemeijer et al., 2009; Hommes et al., 2008). In a double auction, budget-constrained traders who bid randomly still achieve high allocative efficiency (Gode & Sunder, 1993). Heterogeneous-agent models show that aggregate dynamics depend on the composition of strategies and how agents switch among them (Brock & Hommes, 1998; Hommes, 2011), and agent-based finance treats that composition as a modeling choice to be disciplined by data (Axtell & Farmer, 2025; LeBaron, 2006).

LLM agents alter two inputs to this machinery. First, their heterogeneity depends on the chosen configuration. Researchers specify or sample models, versions, personas, information sets, and endowments. For human-surrogate claims, the resulting distribution of types requires validation against a human population; for participant claims, it should represent the AI configurations being studied. Second, the construction may correlate their errors and actions. Shared weights, post-training, prompts, interfaces, or information sources can produce common systematic errors even when calls are sampled independently. The literature on algorithmic monoculture predicts that correlated decisions can lower welfare, even when each individual decision improves (Kleinberg & Raghavan, 2021). These two features, configured heterogeneity and dependence among agents, are the lens through which this review reads the interaction evidence.

Agent roles imply different validation criteria. The human surrogate must reproduce relevant human behavior. A financial decision tool must demonstrate performance out of sample and net of relevant frictions. An AI economic participant must be accurately described, regardless of whether it resembles a human. An experimental instrument must stably measure the intended construct across different wordings, runs, and versions. A paper may claim several roles, but evidence meeting one standard need not meet another: profitable trades do not establish human fidelity, and a human-like answer does not establish stable measurement of a behavioral construct. These four roles correspond to four of the five claims in Section 8; the fifth, that the LLM component explains outcomes beyond simpler agent rules, can accompany any of them.

Fig. 3 maps the 271 primary synthesis studies to the interaction levels and validation. Independent elicitation dominates (215 studies); 20 examine within-system coordination, and 40 examine strategic interaction, including 30 with endogenous prices. Six examine network transmission and four human–AI co-participation. These counts overlap: 21 studies combine structures, and eight fit none. The map shows where individual decisions are measured and where their aggregation is observed. The coordination row is small by construction because most multi-agent decision systems belong to a separate system audit (Section 5); it does not measure how common within-system coordination is in the corpus.

The documentation of specific validation checks is uneven. Fig. 3 counts each feature against the studies in which it could be assessed; therefore, an absence counts only where the full text was read. Human benchmarks appear in 82 of 187 assessable independent-elicitation studies and 17 of 36 strategic-interaction studies; only 13 and 2, respectively, observe humans on the same task in the same study. Heterogeneity is checked against human data in 19 of 176 and 3 of 35. Coordination studies report no human comparator. Out-of-time validation is reported in 35 of 178 independent studies and in one of 35 strategic studies (35 of 69 and one of ten among designs that use historical data). Only 58 of the 219 primary studies read in full record a dated snapshot for at least one model. These counts record what studies document; a verification missing from the material read may still have been conducted.

A widely replicated individual-level finding is that capable models choose consistently when tasks are presented in a standardized format. In budget-set experiments spanning risk, time, social, and food domains, GPT-3.5-Turbo’s mean critical cost efficiency index (CCEI) was 0.997 to 0.999, against 0.963 to 0.985 for human subjects given identical tasks in the authors’ parallel experiment (Chen et al., 2023). Its demand also responds to relative prices more reliably than theirs. This consistency depends on the presentation: in the same study, an alternative framing of prices significantly lowers GPT’s consistency, more so than it lowers that of human subjects, while a discrete choice set also reduces consistency (Chen et al., 2023). Fitted prospect theory parameters are essentially one for GPT-4o, Claude 3 Sonnet, and Gemini 1.5, which the authors read as risk-neutral, rational agents (Hartley et al., 2025). Models prompted to reason reach approximately 96% consistency with the expected value choice (Hintze et al., 2025), and according to their abstract, a multi-model study finds reasoning-enabled configurations rational in roughly 99% of cases (de Castro Soares et al., 2026). Under standard presentations, these measures show LLMs to be more coherent than human subjects.

Consistency is neither risk neutrality nor human-like behavior. All 12 models in one study satisfy dominance and continuity, yet are risk-averse under mean-risk utility; most fail invariance when option position or dominated alternatives change (Buchanan & Foster, 2026). Self-reported risk types range from uniformly risk-neutral to uniformly risk-averse or risk-loving across models (Ouyang et al., 2025). GPT-4o is more risk-averse than human respondents in one cross-cultural study, whereas Gemini 2.0 Flash is more risk-seeking (Liu et al., 2026a). Mechanism probes reinforce this distinction: although low finite St. Petersburg bids look human, truncation drives 25 or 26 of 28 models to the implied expected-value boundary (Huang et al., 2026a). Probability weighting usually lacks the human inverse S-shape (Hintze et al., 2025).

Controlled post-training comparisons show that training choices can change the measured preferences. Fine-tuning Mistral-7B for helpfulness, harmlessness, and honesty lowers its mean investment in the Gneezy–Potters task from 5.65 to 1.05 of $10, and the aligned model resists prompts that instruct it to take risks (Ouyang et al., 2025). Instruction tuning and reinforcement learning from human feedback can also create biases absent from pre-trained models: the certainty-effect score rises from 0.00 in DaVinci to 0.67 in DaVinci-003 (Itzhak et al., 2024). Scale and generation move preferences and beliefs in opposite directions. Across 12 models, more advanced models provide more human-like answers to preference questions but more rational answers to belief questions (Bini et al., 2026). Risk attitude is therefore better treated as a parameter of a configuration (model, release, reasoning mode, alignment, prompt) than as a trait of a model family (Buchanan & Foster, 2026), and loss aversion and gambling rates shift across releases of a family (Wang et al., 2025d).

Two regularities matter for aggregation. First, the choice distributions are often compressed. GPT-4o’s repeated-auction reserve prices have a standard deviation of 11.70 versus 23.22 for humans (Feng et al., 2025). The seven models’ median lottery valuations coincide at the expected value on several items (Erdem & Ashok, 2025), and LLM risk attitudes occupy a narrow band of the human distribution (Mei et al., 2024; Sun et al., 2026).

Second, demographic personas do not reliably restore missing behavioral dispersion. Gender, age, and ethnicity prompts leave GPT’s preference parameters unchanged in the budget-set design (Chen et al., 2023) and produce stereotypical responses (Jia et al., 2024). According to one abstract, explicit persona instructions shift risk attitudes across almost the entire scale (de Castro Soares et al., 2026). Seeding demographics can reproduce differences between groups (Section 4.4), which is not the same as reproducing the dispersion within groups. In the auction study, the one intervention that closely reproduced a human distribution was giving GPT-4o the first 30 rounds of an individual human’s own history to imitate, which brought the Kolmogorov–Smirnov distance to the human trajectories to approximately 0.05 (Feng et al., 2025). An agent population built from copies of one default model is therefore likely to be less dispersed than a human population unless heterogeneity is imposed and checked, and its risk attitude is set by the model rather than drawn from a human distribution. The market evidence in Section 6.1 qualifies this reading: in the bubble-forming markets of one replication, agent-level dispersion is similar to that of humans (Saxena et al., 2026).

Bias batteries often find human-direction effects, whereas the incidence, size, and occasionally the sign of those effects vary across tasks. Given 14 canonical experiments in their original wording, ChatGPT behaved rationally in eight and showed a human-direction bias in six: Asian disease framing, the conjunction fallacy, mental accounting, the house-money effect, naive diversification, and the endowment effect (Gamble & Hummel, 2026). The bias is reduced compared to the human benchmark in five of the six cases and is similar in the case of naive diversification; according to the authors, ChatGPT is never more biased than the human benchmark. Across 45 models, susceptibility to a standardized battery ranged from 17.8% to 57.3%, with prospect theory and framing items among the hardest to resist and larger and reasoning-trained models resisting more (Knipper et al., 2025). Framing effects in the human direction are the most common result, although they depend on the narrative and, in one contamination-aware design, appear only when the paradigm is named (0.62 against approximately 0.02 unnamed) (Bose, 2026). In Payne (2025), five models showed a classic reflection effect in a sports scenario, none in a business merger scenario, and a reversed effect in a career scenario. The two models tested without a narrative, GPT-4o and o3, declared indifference in every case (Payne, 2025).

Loss aversion varies across models and releases. Fitted values span 0.010–4.000 against a human benchmark of 2.630 on one instrument (Wang et al., 2026a). Within the GPT lineage, the estimate falls from 2.72 for GPT-3.5 to 0.57 for GPT-4.1, with GPT-4 and GPT-4o showing loss-aversion estimates comparable to the human benchmark (Wang et al., 2025d). Therefore, the same measure can identify greater-than-human loss aversion, human-like preferences, or losses weighted below equal-sized gains. Calibration to one release need not survive the next.

Disposition findings differ in both instrument and statistic (Table 2). In call auctions populated by one or two of the 14 models, unrealized gains raise the probability of net selling by 5.0 percentage points, or 1.6–3.3 points, controlling for agents’ price expectations (Ouyang & Sui, 2026). In an exogenous-price simulation with two small GPT models, 75.2% of 3,859 sales realized losses, interpreted as a reversal (Garcia, 2025). This sales share does not condition on the gains and losses available for sale. In a vignette allowing selling, holding, or buying more, ChatGPT holds after 100 of 100 losses and 97 of 100 gains; the realization gap is zero, which its authors call partly mechanical (Gamble & Hummel, 2026).

When forced to buy or sell, GPT-4o sells after 97 of 100 gains and buys after 90 of 100 losses; two small open models show the same pattern (Hashimoto et al., 2025). Another study reports a disposition ratio of 0.06, rising to 0.21 with an investor-profile prompt, against 1.60 for humans (Yee & Koh, 2026). Both estimates imply a reversal relative to the no-effect value of 1, although the authors call them near zero. No version of the sixth study was retrievable; its indexed abstract, the only text available, reports human-like biases (Tan & Li, 2024). The five retrievable studies used different statistics and choice architectures. None holds the statistic constant across instruments; even the two-instrument study changes its statistics (Hashimoto et al., 2025). Instrument dependence remains plausible but unidentified.

Herding and extrapolation also depend on the design. With a Bayesian market maker and incentives permitting optimal cascades, LLM traders never cascade, compared to 12.00% of decisions by financial professionals in the same design; explicit instructions or inverted signal colors can induce herding (Hansen & Lee, 2025). Extrapolation appears in most price-history tasks, although large models’ one-step forecasts can approach rational expectations (Bini et al., 2026). The weight on recent returns rises from 0.121 for current-period forecasts to 0.608 at ten periods in Ouyang and Sui (2026). GPT-4o’s weekly rankings load on recent returns about three times as heavily as humans’ (S. Chen et al., 2024). The results depend on what agents observe and how forecasts are elicited.

Prompted numbers usually move judgments, but their effects vary by model, source, and task and can be absent (ten designs are compared in Online Resource 1). For fictional firm valuations, the anchoring indices range from 0.109 for GPT-5-mini to 0.352 for Gemini 2.5 Flash (Garcia, 2026a). Labeling an anchor as a possibly biased prior AI estimate and inviting criticism raised its slope from 0.272 to 0.413, whereas an explicit warning lowered it to 0.165. With nine firm clusters, both changes are significant under small-cluster-corrected standard errors but not under randomization inference. Authority framing raises mean anchor influence across five models to 0.49 versus 0.09 for a placebo; 16 of 55 plausible-anchor cells exceed the rational-updating reference of 0.167 throughout their confidence intervals (Borjigin et al., 2026). Agreement with fabricated analyst ratings ranges from 11.48% to 60.42% (Hu & Zhao, 2026), and an earnings-forecast study’s abstract reports a consensus pass-through of 0.361–0.609 (Roychoudhury, 2026). Reasoning, reflection, and ignore-anchor prompts can fail (Lou & Sun, 2024), while one benchmark’s remedies reduce anchored answers by at most approximately 10 percentage points in two models (Huang et al., 2026b).

Two qualifications matter. Because informative anchors warrant some rational updating, pass-through alone does not measure bias; Borjigin et al. (2026) supply an explicit rational-updating benchmark. Human comparisons also depend on the model and index. Lou and Sun (2024) reported an anchoring index of approximately 0.45 for GPT-4 versus 0.61 for humans. Another benchmark places six of the eleven models, mainly small open models, at or above the human range, with GPT-4o and reasoning models below it (Huang et al., 2026b).

Anchors also survive in multi-step pipelines. When an upstream valuation anchored on an invalid figure is replayed to independent downstream calls after the source is declared invalid, the replayed number alone carries approximately 6% of the upstream anchoring effect (Garcia, 2026c). Replaying the full upstream record as the model’s own earlier conversational turn, rather than inline, raises the effect it carries into downstream valuations from 0.038 to 0.091 (Garcia, 2026c). LLM summaries flip investment decisions in 31.5% and 24.9% of documents in the two corpora, against rereading baselines of 7.0% and 5.7%, respectively (Lee et al., 2026). A material risk disclosure loses its influence as the unrelated context grows, even though the model still retrieves it for all 12 firms (Liu & Liu, 2026). For interaction, the implication is a testable possibility rather than a demonstrated channel: a common consensus, rating, or summary can align judgments, but whether it creates correlated errors depends on its information content and must be tested against a common-outcome benchmark.

Models share some priors but differ within them. On average, twelve models rank environmental and social performance higher as a driver of firm value than surveyed portfolio managers, and their environmental, social, and governance (ESG) and market return expectations are less dispersed than those of retail investors (Li & Yu, 2025). Six audited models favor large firms given balanced evidence (Lee et al., 2025), and nine rank money-like assets similarly (Wu, 2026). Default agents over-represent young, high-income investors, while demographic seeding restores between-group variation (Fedyk et al., 2025). Priors can also shape downstream information use (Park et al., 2026); Online Resource 2 gives the details of these findings.

Identity effects depend on the design. Across 33 models, an otherwise identical woman receives advice to hold approximately 2 percentage points less equity than a man (Foltyn & Olsson, 2026). With explicit race and sparse applicant information, loan-rate differences are +59 basis points in one model and −97 in another, with the latter favoring Black applicants (Cook & Kazinnik, 2025). Name-coded race-by-gender lending effects, however, disappear against measured replicate noise (Morla et al., 2026). Demographic swaps in another audit change decisions no more than noise, while analyst-credential and framing swaps flip approximately one in five recommendations (Basu & Chakraborty, 2026). These comparisons make the noise benchmark part of the interpretation of apparent bias.

Portfolio advice responds strongly to stated risk tolerance (Agliata & Hasso, 2026; Ross & Lo, 2026; Rumpf et al., 2026), whereas income, liquidity, and pensions sometimes carry little weight (Bäckman, 2026; Ross & Lo, 2026). Across 13 models and 21 countries, model choice explains 69.5% of the recommended equity variation for a fixed household profile, versus 5.7% for the country (Bäckman, 2026). This share concerns fixed circumstances rather than variations across different households. Bäckman interprets departures from local fundamentals as common errors among households using the same foundation models. Advice within a model is nearly deterministic in one audit (intraclass correlations 0.918–0.967; Agliata & Hasso, 2026), while another finds implicit rules shifting across identical sessions (Rumpf et al., 2026).

Misconduct responds to incentives with model-specific magnitudes. The misuse of customer funds ranges from 0.10 to 1.00 across twelve models and falls with risk aversion, lower expected profit, and regulation (Biancotti et al., 2025). A vague profit mandate raises risk dismissal by 6.8 percentage points, with effects from near zero to about 20 points across models (So, 2026). Under pressure, GPT-4 trades on an insider tip and conceals its reason (Scheurer et al., 2024); multi-turn concealment raises attack success on GPT-4o from 43.10% to 97.51% (Cheng et al., 2026). Concealment alone does not establish where the strategy comes from. In a replication of the insider trading design with two open-weight models, supplying the concealment tactic raises the preference for concealment by 24 to 48 percentage points across models and readouts, relative to supplying only the objective and circumstances that could motivate it (Shkolnikov, 2026). However, no model initially endorsed a clearly fraudulent investment, whereas 13.3–14.1% of human participants did (Powdthavee, 2026). Section 6.5 returns to the shared priors and model-specific advice documented in this subsection as a possible source of dependence among agents.

Synthetic respondents often reproduce aggregate patterns better than dispersion. GPT return expectations correlate with investor and chief financial officer (CFO) surveys and reproduce extrapolation and negative correlations with future returns, including on post-training news (Bybee, 2023). Personas built from real panelists’ characteristics track the median Survey of Professional Forecasters forecasts but not their dispersion. They outperform humans at one- to four-quarter horizons in the sample, while human medians often win in the post-cutoff 2024 test (Hansen et al., 2025).

Matched ChatGPT and human risk aversion responses correlate at 0.36, with slightly compressed synthetic dispersion (Lim, 2025). Individual histories improve the fit (Graham et al., 2026; see Section 7.2). Calibrated persona mixtures halve prediction errors across structurally different games (Horton et al., 2026). Disagreement can also predict markets: disagreement among 216 investor personas is associated with same-day abnormal volume and subsequent returns, although pre-training overlap with the 2010–2025 sample remains untested (Bhagwat et al., 2025).

Probability forecasts require separate validation. Incoherence varies by a factor of approximately 100 across 15 models, despite similar Brier scores, and increases with irrelevant contexts (Andrews & Sarkar, 2026). GPT-4o’s expected returns average 2.23% versus a supplied historical 1.40% and realized 1.15% (S. Chen et al., 2024); GPT-4 Turbo’s earnings errors rise after its cutoff without lower confidence (Li et al., 2025a). A stronger result is prospective and ordinal: the best model ranks live ventures before fundraising outcomes with a correlation of 0.74 versus experts’ 0.04–0.45, but ensembles do not beat it (Csaszar et al., 2026). Useful rankings do not establish calibrated probabilities or accurate market prices.

Replications of canonical experiments show that the model populating a market determines its results. In a call-market design with a constant fundamental value of 14, single-model markets of Claude-3.5-Sonnet and GPT-4o price close to the fundamental, with mean squared errors of 0.536 and 0.789, whereas GPT-3.5 and Grok-2 markets run up (Henning et al., 2025). None of the six model populations reproduces the bubble magnitudes in comparison with the 19 same-design human markets; procedural differences are documented in Online Resource 2. In the learning-to-forecast market of Hommes et al. (2008), 15 models span the full range of the outcomes. Three of them form bubbles larger than humans’, with relative deviations of 6.17 (o3-mini), 6.08 (OLMO-Think), and 3.25 (Qwen3-14B) against 2.40 for human groups, whereas GPT-5 Mini and the Gemini Flash models price at or very near the fundamental (Saxena et al., 2026). Qwen3-14B resembles the human benchmark on several bubble measures, but its bubbles develop more quickly and dissipate more slowly. With the standard prompt, turning Qwen3-14B’s reasoning off produces no speculative bubbles in 40 runs, whereas a nonlinear-extrapolation prompt produces bubbles in 52% of a separate set of 40 runs with reasoning disabled.

A second call-market study adapts the Smith et al. (1988) paradigm, following Henning et al. (2025), and populates each market with one or two of 14 models (Ouyang & Sui, 2026). Prices follow the human hump-shaped path on average, and excess bids predict price changes; however, mispricing ranges from a mean squared error of 0.0012 for DeepSeek V3 to 113.83 for Llama 3.1 70B.

The replications also show which human regularities survive. In the positive- and negative-feedback designs of Heemeijer et al. (2009), GPT-3.5 and GPT-4 agents reproduce the human contrast between rapid convergence under negative feedback and slow convergence or persistent deviation under positive feedback (del Rio-Chanona et al., 2025). The full history of predicted and realized prices is always shown, and the agents reproduce the contrast when they also retain their reasoning from three or five previous periods. With only one period retained, GPT-4 agents fail to converge in either type of market. A higher sampling temperature also helps. Memory is more important than temperature, and the estimated forecasting rules of LLM agents are less dispersed than those of human forecasters.

In contrast, in double auctions, LLM populations do not converge in the way Smith (1962) documented for humans. In a persistent order book, no model fully converges, the smallest model is the most efficient, and the larger GPT model trades too little (Struski et al., 2026). In an earlier single-market study, average prices stay near equilibrium, while the convergence coefficient shows no steady decline (4.17, 20.00, 11.33, 11.83, and 2.67 across five periods) (Jia & Yuan, 2024).

Only one replication ran human markets alongside the LLM markets (Henning et al., 2025), and the others compare with published human data or theory. Three compare the dispersion of agent behavior with human markets of the same design: two find LLM populations less heterogeneous than humans (del Rio-Chanona et al., 2025; Henning et al., 2025), and one finds similar agent-level dispersion in bubble-forming markets (Saxena et al., 2026). Only one checks whether its models had seen the original experiment during training, finding leakage in several frontier models and none in the most human-like one (Saxena et al., 2026).

In one study, varying both the institution and the model family materially changed the outcomes. With the same agents and payoffs, allocative efficiency ranged from 88.6% in a call market to 56.4% under bilateral bargaining, and buyers captured 83.7% of the surplus in posted-offer markets but 14.3% in posted-bid markets (Chupilkin, 2026). Model rankings reversed across institutions: one model reached 100.0% efficiency in the call market and 35.2% in a continuous double auction. This result echoes the finding of Gode and Sunder (1993) that market rules can partly substitute for individual rationality, with the qualification that for LLM agents, the rules also interact with the model’s identity. Auctions showed the same dependence. LLM bidders reproduced the human advantage of clock auctions over sealed bids, with truthful bidding of 70.0% to 76.7% in clock formats against 18.7% in a sealed second-price auction with affiliated private values; their mean bid–value gaps of 1.83 and 6.26 in the two formats were close to the 2.48 and 6.52 reported for human bidders in the same design (Shah et al., 2025b). However, their errors in the sealed format run opposite to humans’: with independent private values, 65.78% of sealed second-price bids fall below value, where humans mostly overbid (Shah et al., 2025b), and a second study finds the same underbidding (Tsuchihashi, 2023).

Collusion depends on the market structure and communication. In a repeated procurement auction, two of the four models sustain supracompetitive prices in groups of two to four sellers; with five or more, median prices fall to near the competitive level, in line with a theoretical cartel-size bound (Tolety, 2025). A reasoning model does not coordinate. In a double auction with a competitive equilibrium price of 90, seller communication raises average trade prices from 87.71 to 90.52, with overlapping confidence intervals (Agrawal et al., 2025). An urgency message from a fictional chief executive pushes them to approximately 96, even under oversight. Because LLM double auctions do not converge even without communication (Struski et al., 2026), supracompetitive prices can be read as collusion only against a non-colluding LLM benchmark, such as the no-communication condition of Agrawal et al. (2025). In the algorithmic-pricing literature, reinforcement-learning agents sustain supracompetitive prices without communication, and collusion is identified from the punishment of deviations rather than from price levels alone (Calvano et al., 2020).

Information aggregation deteriorates as the demands on higher-order reasoning increase. The median market prices the winning security at 0.91 overall in 1,772 first-wave prediction markets with a logarithmic market scoring rule (4,076 across all waves), but it prices the winning security at 0.73 and an uninformative 0.5 in the two hardest information structures (Galanis, 2026). In these structures, Ostrovsky’s (2012) theory still predicts full aggregation. Cheap talk, strategic prompting, and market length have no detectable effect, and the comparison of April 2026 frontier models with the best January 2026 teams finds no detectable improvement. In an information cascade design, LLM traders largely ignore trade history, valuing the asset from their private signal alone in nearly two-thirds of decisions, and thus avoid herding and learn little from the information the history contains (Hansen & Lee, 2025).

In larger simulated markets, aggregate patterns are sensitive to the imposed heterogeneity, prompt design, and information environment. Giving every agent the same profile reduces orders by 82.7% and turnover by 83.7% (Gao et al., 2024). In the headline run of a 100-agent market driven by real 2023 news, heterogeneous agents reproduce fat tails, the leverage effect, and volatility clustering more closely than the two rule-based models (Yang et al., 2025). Removing heterogeneity yields near-Gaussian returns and a negative correlation with the real index path, and rumors delivered to central agents raise the sell-to-buy ratio from 0.495 to 0.997. The stylized facts also vary across three repeated GPT-4o runs, with relative standard deviations of 20.85% to 63.17%, and the three-run means fall below the headline run values. Stylized facts appear in one artificial market only when all three optional prompt elements are included, according to its abstract (Hirano, 2025), and the backbone model changes outcomes under identical settings (Zhang et al., 2026a).

A Chinese gold-market simulation isolates an architecture comparison while holding the order-book rules, matching mechanism, and price-update scheme fixed (T. Gao et al., 2026). Across ten reported paired runs, the full architecture, with memory, reflection, and structured outputs, has a mean Hurst exponent of 0.5947, compared with 0.5126 for the simplified LLM baseline; the paired difference is 0.0821 (p = 0.0505). This is a borderline difference in aggregate price persistence between LLM architectures, without a human behavioral comparison. Historical gold-market reports calibrate investor roles and capital, while the agents’ own orders generate prices and their comments enter a sampled information pool. The publication reports neither the model identity nor complete prompts, and does not specify the resets or seeds needed to establish the independence of its runs.

One market study reports that agents follow instructions rather than maximize profits. In its market, with two prompted optimists among eight agents and no short selling, overpricing from twice the fundamental persists for 15 rounds while underpricing corrects, although the design does not isolate which feature sustains it (Lopez-Lira, 2025). Adding a few LLM-directed agents to a rule-based order book reproduces an empirical anomaly that rule-based agents miss, with seed-level variation as large as the estimates (Hashimoto et al., 2025).

Systemic episodes reveal the same dependence on inputs and the value of rule-based counterfactuals. In a bank-run model with LLM depositors calibrated to 2023 regional bank failures, the LLM population reproduces the observed failure order (Ruano & Rajan, 2026). However, a logistic heuristic depositor reproduces the main qualitative results: the tipping point, synergy between contagion channels, and failure-ordering. The authors attribute the equivalence to the model structure (network topology, balance-sheet feedback, and spillover rules), and the prompt supplies the same fundamentals, withdrawal rate, and neighbors’ posts that drive the heuristic rule. Contagion arises mainly from the interaction between interbank bridges and the depositor network. The authors conclude that the LLM contributes to heterogeneity and interpretable posts, not different aggregate dynamics. According to their abstracts, a second bank-run study validates its depositors against human benchmarks (Kazinnik, 2026), and a study of speculative markets finds that more reasoning reduces but does not eliminate bubbles (Cartea et al., 2026).

A direct test of how LLM participation affects price discovery varies the share of LLM traders in a market. In Ross et al. (2026), increasing this share lowers mean tracking error when agents receive accurate fundamental-value information. Better price tracking does not establish lower volatility: with neutral commentary, prices remain closer to fundamentals than under the noise-only baseline even as realized volatility rises with LLM participation. When every agent is told each round that the signal overstates value by 25% to 30% and to trade on the lower estimate, the tracking error rises with the LLM share, reaching five to seven times the noise-only baseline at a 100% LLM share (Ross et al., 2026). The directional accuracy collapses, and price tracking worsens compared to the noise-only baseline. Production records describe outcomes without such a counterfactual. In the trailing week ending August 15, 15% of week-active accounts in a fleet trading mostly on paper at live prices had a positive net return on investment (ROI), compared with 53% in the paper’s retail comparison (Barton et al., 2026b). This one-week comparison does not measure profitability over the full deployment.

Most replications vary the model across markets, each containing a single model, holding the institution and instructions fixed (Section 6.1). They observe aggregate outcomes but not how a model responds to agents unlike itself, which is the response a market model built from individual measurements requires. Three other designs address this issue, and each holds different things fixed.

Mixed-model markets keep the institution fixed and combine the models in one market. In a six-model learning-to-forecast market whose members behave consistently in homogeneous markets, bubbles form in approximately half of the 50 runs that differ only in the random seed, although the two bubble-forming models are a minority (Saxena et al., 2026). The common component accounts for 41% of the agents’ mean squared forecast error in that market. In call markets that pair two models, mispricing lies between the two models’ single-model levels in several pairings, although some mixed markets remain close to their more bubble-prone members (Ouyang & Sui, 2026). Mixing six models in 24-agent call markets leaves two of the three markets near the fundamentals and produces one modest bubble (Henning et al., 2025). In prediction markets where four of the 12 trading teams mix models, greater dispersion of capability lowers errors in the worst-performing markets, with at most a negligible effect at the median (Galanis, 2026). Because models, institutions, and procedures differ across these studies, the comparison does not estimate an institutional effect; it shows that diversity alone does not resolve the direction of the aggregate results.

Calibrated populations tie heterogeneity to human data, as in the 100-agent market of Section 6.3, whose personas are initialized from investor records (Yang et al., 2025). Anchoring agents to individuals’ own histories restores most of the human dispersion, but as an individual-level diagnostic rather than a market outcome (Section 6.5). Calibration determines the initial state of the population; however, it does not demonstrate whether the calibrated rules remain effective after interaction.

Adaptation is observed directly when one frontier model joins five agents of a bubble-forming model (Qwen3-14B). Both frontier models tested begin by forecasting the fundamental and switch to trend following in response to the realized prices (Saxena et al., 2026). Gemini-3-Flash then earns more than GPT-5 Mini (535.5 against 320.1 per period over 15 runs) and makes bubbles shorter and sharper, whereas GPT-5 Mini dampens them. The authors attribute the difference to Gemini-3-Flash modeling the other agents’ forecasts, a reading of its written justifications; the forecast and price paths are the observed evidence. Adaptation is not universal: in an information-cascade design, LLM traders largely ignore the history of others’ trades (Hansen & Lee, 2025).

Thus, diversity acts through initial disagreement among agents and through their responses to one another once prices feed back into forecasts. The observed adaptation changes the effect of initial disagreement; diversity at entry does not guarantee weak dependence or stable prices after interaction.

The interaction studies document dependence among LLM agents, and two of them also measure it outside the market, before any interaction. Three types of dependence need to be kept apart because they bear on aggregation differently: the correlation of errors, the alignment of actions, and the overlap of holdings. The error correlation measures how agents’ errors covary across common tasks or outcomes. Among the 28 price-setting designs read in full, two reported related error diagnostics: pairwise error correlation and the common component of forecast errors. These statistics are not interchangeable.

In a ten-agent scoring-rule market on common misconception questions, pooled honest-agent errors correlate at 0.696 across adversarial compositions (Begin et al., 2026). Under the paper’s variance-based proxy, ten agents with that correlation correspond to approximately 1.4 independent forecasters; this result is not a derivation of information aggregation under the market-pricing rule. In a separate all-honest scaling experiment, the ten-agent condition averaged 68.0% accuracy against 70.2% for a standalone agent, providing no demonstrated improvement in accuracy. The authors noted that the misconception items may have inflated the correlation. In bubble-forming learning-to-forecast markets, the common component of forecast errors is similar to that in human markets of the same design (Saxena et al., 2026), where humans coordinate on common forecasting errors (Hommes et al., 2008). The pooled in-market correlation cannot locate where dependence arises, because agents in a market share prices and questions and respond to one another; the evidence that it can predate interaction comes from independent single-agent runs and a scenario panel of separately queried models (Begin et al., 2026; Ross et al., 2026). The distinctive feature of LLM populations may therefore be not the presence of dependence but a source that operates before interaction, such as a shared model, although these designs show neither that all market dependence originates there nor that it is unique to artificial agents.

Action dependence concerns the alignment of what agents do. In the scenario panel, the correlation between different models’ non-corrective actions rises with general capability (Ross et al., 2026). TwinMarket constructs evolving networks from weighted Jaccard similarity in agents’ trade-intensity vectors, providing a measure of action overlap rather than error correlation (Yang et al., 2025). Holdings overlap concerns portfolio convergence: in a real-capital production tournament, mean pairwise overlap rose from 0.304 to 0.473 (Barton et al., 2026b). Common actions and converging holdings can reflect correct responses to common information. Therefore, these measures document aligned decisions or exposures without identifying correlated errors.

Some designs manipulate a source of dependence, whereas others only document it. In independent runs from the scoring-rule study, agents from different model families have error correlations of approximately 0.40, against 0.68 within a family (Begin et al., 2026). In a separate set of all-honest markets, assigning ten distinct epistemic roles (a different reasoning role in each agent’s prompt) lowers the correlation from 0.60 to 0.44 with a reported accuracy of 73.2% ± 5.2%, compared with 70.4% ± 5.9% at baseline. In an alignment ablation, adding preference optimization to an identical fine-tuned checkpoint raises it. In a forecasting ensemble without prices, persona profiles drawn from real traders raise forecast diversity slightly but barely reduce the correlation of errors, from 0.991 to 0.984, and ensemble accuracy does not improve (Qian, 2026). Other sources of heterogeneity show more promise than personas: different private information supports aggregation in simple structures (Galanis, 2026), and anchoring each agent to an individual human’s own history restores most of the human dispersion (Feng et al., 2025; Graham et al., 2026).

Production records chiefly document common exposures, and the display cutoff in one fleet identifies an interface effect on the selection (Barton et al., 2026b). Advice studies likewise identify shared model influences without observing dependence among recipients’ realized errors or trades (Bäckman, 2026; Li & Yu, 2025; Wu, 2026).

General model benchmarks provide complementary evidence with different estimands. Kim et al. (2025) find substantial agreement on the same wrong answer, even across model families, and greater conditional agreement among more accurate models. Their measure conditions on both models being incorrect; it does not refer to the pairwise error correlation used in the averaging benchmark described below. Jo et al. (2026) show that inferred excess agreement depends on the null model and the models and items sampled, including whether ability and item difficulty are accounted for. These results motivate explicit baselines and common task sets when measuring dependence in financial agents; they do not establish its effect on market prices.

Empirical finance offers measures and priors for this channel. Bikhchandani and Sharma (2001) separate spurious herding, in which investors facing similar problems and information make similar decisions, from intentional copying of other investors, a distinction that applies directly to the common purchases of deployed fleets. Institutional herding is measured from the excess share of managers trading a stock on the same side (Lakonishok et al., 1992) and from the correlation of institutional demand across adjacent quarters (Sias, 2004), and analogous statistics could be computed for the orders of LLM agents. The evidence on consequences is mixed. In the foreign exchange market, the evidence is consistent with highly correlated algorithmic trading strategies, yet this correlation does not appear to degrade market quality on average (Chaboud et al., 2014). In contrast, the losses of quantitative equity funds in August 2007 are consistent with the deleveraging of similar long–short portfolios, amplified by a withdrawal of market-making capital (Khandani & Lo, 2011). Stocks whose owners face correlated liquidity shocks are more fragile, with greater non-fundamental volatility (Greenwood & Thesmar, 2011). Common orders are therefore not harmful by construction; their effect depends on what is shared and on how the institution absorbs them.

The amount of dependence that matters depends on the institution that aggregates decisions. A simple averaging benchmark clarifies one channel. For equally weighted errors with equal variance and a common pairwise correlation ρ, the variance of the average is a fraction of an individual’s variance, ρ + (1 − ρ)/n. For a fixed positive ρ, this fraction approaches ρ as n increases. This is a variance result: any common mean bias remains, even when errors are uncorrelated. Independence is sufficient but not necessary for variance reduction. The implied effective number of independent agents, n/[1 + (n − 1)ρ], is the variance proxy used by Begin et al. (2026), who compare it with accuracy in their scoring-rule market. It is not derived from that market’s price dynamics and does not characterize equilibrium prices generally.

In the scenario panel of Ross et al. (2026), the correlated non-corrective parts of different models’ actions leave a floor of approximately half a single model’s residual variance, which cannot be removed by adding models to an ensemble. Where forecasts feed back into prices, the sign of the feedback is important. Under positive feedback, a common forecast error moves the price in its direction and becomes self-reinforcing, whereas negative feedback tends to offset it; convergence also depends on feedback strength and the forecasting rule (Heemeijer et al., 2009; Hommes et al., 2008). Where net order flow moves the price through linear impact, orders that share a direction move it together rather than offsetting, which is why a shared misleading narrative degrades price discovery as the share of agents who read it rises (Ross et al., 2026).

General capability does not guarantee independence (Ross et al., 2026), and a market of correlated agents can fail to beat a single agent (Begin et al., 2026). This is the pattern the theory of algorithmic monoculture predicts (Kleinberg & Raghavan, 2021), and it mirrors concerns about herding and systemic risk when many institutions rely on similar models (Daníelsson et al., 2022; Gensler & Bailey, 2020). Yet only five of the 28 price-setting designs read in full measure any form of dependence among their agents, and none of them compares its market consequences with those of individual bias under the same institution. Its importance relative to individual bias therefore remains an open empirical question.

Within training windows, recall and inference are difficult to separate. GPT-4o recalls macroeconomic series and prominent stock prices and assigns dates to undated headlines, with these abilities deteriorating after its cutoff date (Lopez-Lira et al., 2025). A fictitious 2010 cutoff in the system prompt does not erase later knowledge: the classification of subsequent gross domestic product growth remains 98% correct, against 40% for six releases after the actual cutoff. Firm knowledge also varies with size, prominence, and recency (Shah et al., 2025a).

Beyond recall, memorized outcomes also leak into judgments. A one-standard-deviation rise in the model’s probability of already knowing the outcome raises the marginal effect of its headline-based return signal by approximately 32% of the standalone effect and that of its capital expenditure signal by approximately 12% (Gao et al., 2026b). After the cutoff, the amplification disappears, whereas both signals still predict their targets. Five published trading agents built on GPT-4o lose 51.48% to 62.23% of their Sharpe ratio when moved from a pre-cutoff period to a post-release period with similar market returns; the comparison rests on single runs with no control for the change of period (Li et al., 2025b). Standard open models lose 15 to 22 percentage points of alpha across their cutoff, whereas point-in-time models do not, although a random-signal control also loses about 10 points, so part of the decline reflects the period itself (Benhenda, 2026). In one design, a model whose training data cover the outcome period scores the same headlines as a look-ahead-free model (Yan et al., 2026). The portion of the signal that the look-ahead-free model does not capture earns a premium of 26.4 basis points per standard deviation for the paper’s instruction-tuned model and between 0 and 40.1 basis points across six base and instruction-tuned models from three time-locked families.

Remedies incur costs, and some do not work. Masking does not reliably hide identity: GPT-4o names Apple, Meta, and Microsoft from every entity-neutered earnings call opening in one test (Lopez-Lira et al., 2025), and named-entity replacement leaves 66.88% of firm names identifiable in another, against 9.04% under LLM-based anonymization (Wu et al., 2026). Anonymization also destroys information. After the cutoff, scores from anonymized earnings call transcripts predict credit-rating downgrades less well than scores from raw transcripts (4.7 to 4.9 against 6.1 percentage points per standard deviation) (Wu et al., 2026). Horse-race and look-ahead tests attribute the gap to lost context rather than to removed bias. Replacement names may not be neutral either. In secondary estimates from a three-model study, generated company names lower equity valuations by 0.8% to 2.6% relative to the same profile left unnamed (Garcia, 2026b). The estimated gap between names rated as easier and harder to pronounce is approximately 0.5%, and its registered tests do not establish whether this gap lies within a 1% equivalence tolerance or differs from zero.

Statistical corrections for data snooping, which address selection across many backtests, cannot detect such leakage. A planted strategy that sees tomorrow’s return passes the deflated Sharpe ratio test of Bailey and López de Prado (2014), whereas none of the strategies discovered by the LLM agents in the same study survive this test (Gençay, 2026). Membership-inference scores, which estimate whether a text was part of a model’s training data, distinguish models rather than memorized items: after within-model normalization, their areas under the receiver operating characteristic curve fall to 0.487–0.537 in seven small open models (Roy et al., 2026).

Structural remedies remove leakage by construction and show that part of the apparent predictability survives. Chronologically consistent models retain at least 54% to 62% of the apparent return predictability of news headlines (He et al., 2025). A look-ahead-free model still earns a long–short Sharpe ratio of 3.20 on headlines before trading costs (Yan et al., 2026), and frozen checkpoints scored only on outcomes after their cutoffs predict returns and fundamentals (Lehner & Lopez-Lira, 2026). However, these remedies have their own associated costs. Look-ahead-free models are small, with 1.3 billion parameters in one case (Yan et al., 2026), and poorly follow instructions relative to models trained on more data (He et al., 2025). Frozen checkpoints share few distinct cutoff dates; therefore, some tests rest on six monthly cross-sections (Lehner & Lopez-Lira, 2026).

The system audit finds uneven temporal safeguards (Table 3). Of the 295 papers, 153 evaluate only historical backtests, and 28 include forward or live tests. Among the 161 full-text studies with time-indexed tests, 73 use at least one control targeting model knowledge, and 88 use none. These controls include post-cutoff windows, forward tests, masking, and time-aware models; however, they are not equally effective. Online Resource 1 reports the breakdown by system type.

Contamination also threatens the simulations. Five price-setting designs use real historical news or episodes, while another uses real histories only in separate exogenous price backtests (Ma et al., 2025). Masking and withholding dates offer incomplete protection (Li et al., 2026b; Wang et al., 2025a; Yang et al., 2025; Zhang et al., 2026a). Endogenous prices do not ensure that decisions ignore the remembered outcomes (Zou et al., 2026). Both social-interaction ablation and a plausible simulated price path fail to measure this contamination channel. None of the full-text market studies reviewed directly estimated how far remembered outcomes moved simulated prices.

Replicating classic experiments faces a related problem, as the models may have read the original papers. One replication checks and finds that several frontier models know the 2008 experiment they are asked to reproduce, although none knows the height of its bubbles (Saxena et al., 2026). At least six others have not discussed this possibility (del Rio-Chanona et al., 2025; Henning et al., 2025; Jia & Yuan, 2024; Shah et al., 2025b; Struski et al., 2026; Tsuchihashi, 2023). Among synthetic subjects, one open model conforms to a unanimous wrong majority in 83.3% of trials when the Asch experiment is named and almost never when it is not (Bose, 2026).

The behavior of LLMs is frame-dependent in ways that matter for aggregation. A behavioral mapping fitted under one wording transfers poorly to a payoff-equivalent wording, with a pooled mean total variation distance of 0.349 that ranges from 0.052 for a lottery task to 0.525 for dictator and trust games (Dong et al., 2026). Small changes to a prompt can change a market. Including the word “aversion” in the prompt through which the LLM decides clients’ willingness to trade produced no client trades in 200 simulated markets, all of which collapsed early (Vidler & Walsh, 2025). Irrelevant notes from the requestor, including an unrelated number, raise the incoherence of probability forecasts (Andrews & Sarkar, 2026).

Personas are the main tool for imposing heterogeneity; however, they are poorly validated. Demographic personas built from 143 human participants neither add diversity nor move the distribution of choices in the 11–20 money-request game toward the human one (Gao et al., 2025). Once stated in the system prompt, personas lose their influence as the market context accumulates over time. In a simulated crash, the gap in cumulative drawdown between agents given the mandate once and agents reminded of it grows from 1.0 to 4.4 times across four 50-day quarters (Safder et al., 2026). Where personas shift behavior, they can produce stereotypes or swings across the entire scale rather than realistic dispersion (Section 4.1), although demographic seeding reproduced group differences in one survey study (Section 4.4).

The positive case is persona conditioning on individuals’ own records. Digital twins of 81 financial influencers, built from their public posts, agree in sign with their human counterparts’ public recommendations in 89.5% of overlapping non-neutral cases, retain account-specific structure, and, when evaluated forward, aggregate into a signal that predicts short-horizon returns (Bowles et al., 2026). Conditioning on respondents’ own survey histories raises the fit of synthetic CFO expectations from an R² of approximately 0.10 to approximately 0.40 for the same responses (Graham et al., 2026). The fit reaches 0.494 for respondents with more than three prior answers, although the synthetic panel remains under-dispersed by approximately a quarter. Heterogeneity anchored in this way can be checked against the individuals it represents.

Repeated outputs can vary under a fixed model configuration, and setting the temperature to zero does not guarantee determinism. Through one provider’s application programming interface (API) at temperature zero, 200 identical runs classifying the same 100 annual-report excerpts yield four distinct regression t-statistics, whereas a locally served open-weight model returns a single value (Coqueret et al., 2026). A large open model returns identical outputs in only 12.5% of runs at temperature zero, while two small models are fully repeatable (Khatchadourian & Franco, 2025). The variation reaches financial outcomes. At the default temperature, about 5% of repeated runs of one textual-analysis design produce a tone coefficient significant at the 10% level by chance alone (Coqueret et al., 2026). Across three repetitions of one headline-sentiment strategy driven by LLaMA-2-7B, the standard deviation of total return rises from 0.25 to 2.72 percentage points as temperature rises from 0 to 1, whereas with GPT-3.5 it stays near 0.9 (Yu, 2023). According to its abstract, runs of one multi-agent trading system under varied sampling settings return 18.1% ± 2.8% with one backbone and 15.8% ± 4.2% with another, against 19.1% for buying and holding the stock (Koviazin et al., 2026).

Models change over time. Rerunning identical designs six months apart produces small but statistically significant drift for several models (Gao et al., 2025), and successive releases differ more, as the loss-aversion estimates along one provider’s lineage in Section 4.2 show (Wang et al., 2025d). However, only 58 of the 219 primary studies that were read in full provide a dated snapshot for at least one model. Papers change as well. One detection study’s revised version withdraws the portfolio claims of its first version (Roy et al., 2026), and two other corpus papers have been withdrawn by their authors from arXiv (Kim et al., 2024; Yang et al., 2026b). Credible building blocks therefore require dated configurations, raw outputs, and distributions over repeated draws, which the reporting standards proposed in this literature require or recommend (Coqueret et al., 2026; Khatchadourian & Franco, 2025; Wang et al., 2025c).

Human-likeness depends on the comparator, and a human comparator is necessary only for claims about human fidelity. Of the 271 primary studies, 147 reported no human comparator in the material read (134 of them read in full), but only 10 of these 147 claimed a human-surrogate role. Of the 93 studies that claimed this role, 80 compared with human data: 33 with published values, 30 with a prior matched dataset, 14 with participants in the same study, and 3 with an external survey. Of the remaining 13, 10 reported no comparison (one coded from its abstract), and 3 could not be classified. The 44 comparisons with same-study participants or a prior matched dataset used matched human data, whereas published values may come from a different design or offer only summary statistics. Twenty-two studies compared the dispersion of behavior with human data, and six validated a calibration on held-out human behavior. These counts record comparisons made, not successful validations, and the coding of a surrogate role partly reflects a study’s aim to compare with humans. Comparators range from lay adults (Powdthavee, 2026) and undergraduates (Bertomeu et al., 2026) to advisers surveyed a decade earlier (Rumpf et al., 2026) and laboratory professionals (Hansen & Lee, 2025), so a claim of superiority requires specifying both population and task.

Calibrating LLM agents to human behavior can shift parameters; however, validity beyond the calibration task requires separate evidence. Of several alignment techniques, only fine-tuning GPT-4o on human data from the same game yielded a distribution that the study’s test did not distinguish from the human one in the 11–20 money-request game (Gao et al., 2025). Failing to detect a difference, however, does not establish equivalence or transfer to other tasks. Investor-profile prompts move all eight measured bias parameters in the predicted direction, pushing loss aversion from 1.12 to 3.00 against a human benchmark of 2.25 (Yee & Koh, 2026). However, they leave the disposition ratio, for which 1 means no effect, about 87% below the human benchmark, and fail adversarial checks for representativeness. When the prompt-calibrated extrapolation parameter is applied to a rule-based market, it generates a short-horizon momentum of 0.18, compared to an empirical value of 0.14, whereas the human-calibrated parameter of 0.12 aligns more closely with the empirical value (Yee & Koh, 2026). Fine-tuning can work out-of-sample, but its target determines what it delivers. Training on theoretical solutions that are statistically consistent with investors’ choices reduces the error against real participants’ choices by 44.52% to 61.26%, including two held-out problems (Wang et al., 2025b), whereas training on rational-expectations targets eliminates the human-like overreaction that the base model reproduces (Gao et al., 2026a).

Explanations for hyper-rationality remain contested. Alignment can increase risk aversion (Ouyang et al., 2025) and introduce biases (Itzhak et al., 2024), while reasoning can linearize probability weighting (Hintze et al., 2025), with one abstract reporting risk-neutral expected-value behavior in the absence of personas (de Castro Soares et al., 2026). Greater capability also moves beliefs and preferences in different directions (Bini et al., 2026).

The measured bias also depends on what the model is told about human behaviors. After reading an abstract that reported a loss aversion coefficient of 1.96, ChatGPT’s measured coefficient was 1.785, and after reading one reporting 1.07, it was 1.043 (Yechiam & Tarabeih, 2026). In a related design, its loss aversion follows the reported human bias, whether the human sample numbered 10,583 or 43 people. Therefore, the measured “bias” can reflect what a model has read or been shown rather than a stable disposition. When humans join machines in a repeated game, the framing effects observed among machines alone weaken and change (Engel et al., 2025). Hyper-rationality is better understood as a property of a configuration under an instrument than as a trait that transfers to the markets.

In audits that re-run published LLM trading systems over later or longer windows or with realistic costs, the reported gains shrink or disappear (Li et al., 2025b; Li et al., 2026a; Ye et al., 2026). Re-running two published trading agents over a later one-year window with commissions, token costs, spreads, and market impact lowers TradingAgents’ portfolio Sharpe ratio from 0.43 gross to 0.22 net and QuantAgent’s from −0.96 to −1.15, leaving both below buying and holding (Ye et al., 2026). The same audit found that 35 of the 40 system-by-friction cells across five published systems were not modeled at all. In the audit for this review, 68 of the 140 full-text system papers that evaluate an implementable trading or investment strategy model trading costs, or 62 if six partial treatments are excluded (Table 3). Another audit recovers at least partial cost treatment for 14 of the 30 trade-relevant studies (Yao et al., 2026). In its demonstration with simple rules, replacing same-close execution without costs by next-close execution with costs of 10 basis points cuts a high-turnover strategy’s final equity multiple from 27.38 to 1.50. Only 26.8% of the 164 main-conference papers acknowledge look-ahead bias, and 1.2% acknowledge survivorship bias (Kong et al., 2026).

Broader tests reinforce this concern. Only one of 32 LLM-written strategies claiming an edge delivers it (Tian et al., 2026); seven of ten backbones in an otherwise identical trading system do not pay for themselves (Duan et al., 2026). Long-window, survivorship-free retests challenge published alpha claims (Li et al., 2026a), masking produces negative selection alpha for nine of ten agents (Zhu et al., 2026), and frontier models lose real money in one prediction-market test (Zhang et al., 2026b).

Call-level replication answers a narrower question than population-level replication. Many experiments treat each call to one model as an independent subject (Gao et al., 2025; Wang et al., 2025c; Yechiam & Tarabeih, 2026; Yee & Koh, 2026), which can estimate variation conditional on that configuration but does not establish heterogeneity across humans or independently sampled model configurations. Normalized standard deviations of 0.054 and 0.030 for two frontier models, against 0.231 for humans, show how compressed within-configuration variation can be relative to human dispersion (Wang et al., 2025c). Market studies rest on a few independent markets, such as three per model in the most carefully benchmarked replication (Henning et al., 2025) and, on a 100-agent platform, a single headline run with three runs per backbone in a robustness check (Yang et al., 2025). Where runs are replicated, stylized-fact estimates vary with relative standard deviations of up to 63% (Yang et al., 2025), and agent rankings do not survive a rerun (Li et al., 2026b). For simulation claims about aggregate outcomes, independently repeated markets or sessions provide replication; agents interacting within one market do not provide independent market observations.