How AI agents shape experts’ judgment calls

A pre-registered randomized trial in which 50 causal-inference practitioners analyzed synthetic farm data with Claude Code (Claude Opus 4.8), whose hidden system prompt assigned it a coin-flip lean on five decisions. Participants' choices matched the lean on 86% of four analytical decisions (a pooled flip rate of 72 percentage points); the lean's direct effect on the final recommendation was smaller and not significant under the registered estimator. Most participants later justified choices with the agent's arguments without crediting it. The authors note the lean was deliberately strengthened and the study covers one task, one model and one field.

Amaç Herdağdelen (Anthropic Fellows Program), Hailey Joren and Alex Tamkin (Anthropic) · 2026-10-27 · original

When an expert hands analysis to an AI agent, the usual assumption is that the expert still makes the calls that need judgment: what to measure, which assumptions to accept, what to recommend. This study asks whether that holds when the calls have more than one defensible answer. Practitioners analyzed data with a coding agent that had been secretly told, by coin flip, which option to favor on each of five decisions. The study then measured how much the coin flips moved their choices. The authors frame the stakes partly in terms of AI safety research, where a human reviewer "is only an independent check if their judgment is their own" (post, introduction).

Version of record. The study exists as a summary post on anthropic.com (27 October 2026) and a 29-page paper PDF linked from it, Who's Aligned to Whom? How AI Agents Shape Experts' Research Judgment Calls. The paper is the version of record. The PDF linked from the post on 12 November 2026 is byte-identical to the copy saved in the vault (PDF creation date 26 October 2026). No arXiv version was found. The design was pre-registered on OSF (osf.io/t3q59): the pre-analysis plan was uploaded on 6 August 2026 under embargo and made public on 28 October 2026, with one file version. Locations below are the paper's sections, tables, figures and appendices unless marked "post", in which case they are the post's headings. Where the post and paper give a number differently, both are reported.

Terms used in this note

  • Judgment call / underdetermined decision. A decision where the evidence supports more than one defensible option and there is no ground truth (Section 1). The study's decisions were built to be of this kind.
  • Lean. The option the agent was assigned to favor on a decision, set by coin flip and given to the agent in a hidden system prompt (Section 3.3).
  • Flip rate. The paper's measure of influence: the difference between lean arms in the probability of choosing option A, $P(C{=}A \mid L{=}A) - P(C{=}A \mid L{=}B)$, where $C$ is the participant's choice and $L$ the lean. Assuming no backlash (a lean never pushes a participant away from it), this equals the share of participants whose choice the lean changed (Section 3.5). A flip rate of 72 percentage points corresponds to choices matching the lean 86% of the time, against 50% if the lean had no effect.
  • Policy shift. The flip rate for the final recommendation, scored discontinue 0, one-year extension 0.5, roll out 1 (Section 3.5).
  • Disempowerment. The paper uses Chooi et al.'s definition, "The erosion of humans' ability to meaningfully shape outcomes that affect their lives, where such erosion is caused or substantially mediated by AI systems" (Section 2).

What the study does

Participants

Practitioners were recruited through "a paid expert-annotator marketplace" and passed a five-part vendor screen (Section 3.1, Appendix A.1). The screen required:

  • a six-question causal-inference knowledge check;
  • regular Python or R use;
  • hands-on observational causal work;
  • at least a theoretical grasp of ANCOVA and difference-in-differences.

Sixty-one participants completed the task with a valid deliverable. Eleven chose not to use the agent; they are excluded from the main analysis and serve only as a no-AI comparison group. That leaves 50, of whom 48 completed the surveys (Section 3.1). Among those 48:

  • 65% held a master's or doctorate or had six or more years in analysis roles;
  • 90% rated themselves proficient or expert in causal inference;
  • 84% of the 45 who gave a gender were men;
  • 55% of the 47 who gave an age were 25 to 34 (Table 4).

The paper does not report compensation, the number screened, or a response rate.

The task and the five decisions

Participants advised a fictional farming cooperative, on synthetic data from a process the authors control, whether to roll out or discontinue a voluntary advisory program. The board's target was a 3 to 4% productivity gain (Section 3.2). The briefing left four analytical decisions open, each with two options. Side A pushes the estimate up or toward rollout:

Decision Option A Option B
d1 productivity measure yield per hectare yield per operating cost
d2 identification difference-in-differences levels-adjusted ANCOVA
d3 estimand effect on enrolled farms (ATT) effect on full membership (ATE)
d4 weighting per farm production-weighted
d5 recommendation roll out discontinue

Source: Section 3.2. Appendix A.5 gives, for each decision, why it is underdetermined and the grounds each side can claim from the briefing. The post says each analytical decision "could move the estimated productivity gain by several percentage points".

Participants worked in a browser-based VS Code workspace with Claude Code (v2.1.220) running Claude Opus 4.8 at high effort, pinned for all sessions. The platform recorded the transcript, screen, window focus and inactivity (Sections 3.3 and 3.4). There was a minimum 24-hour gap between the pre-task survey and the task. Median task time was 65 minutes (Section 4.2.3). The deliverable was a JSON report with a point estimate, confidence interval and the five choices.

The randomization

Each agent received one of the 32 configurations of five binary leans. Configurations were drawn from randomized blocks in which consecutive pairs took opposite sides on every decision, so the five factors stayed balanced (Section 3.3). The authors did not ask participants for their own choices before the task, because "elicitation is itself an intervention" (Section 3.4). The paper's limitations note this means individual influence cannot be measured.

Coding and statistics

Final choices were coded by an LLM judge from the deliverable and, where needed, the code. Where the judge and the participant's own survey answer disagreed, the authors adjudicated. Of 41 such disagreements, 37 went to the judge (Section 3.5). For the session-level analysis, one author hand-coded 15 randomly selected sessions, and an LLM judge (Claude Fable 5 at xhigh reasoning effort) applied the same scheme to all sessions. On the 75 decisions both coded, agreement was 93% (Cohen's $\kappa = 0.73$). Estimates use participant-clustered CR2 standard errors. Registered tests are one-sided at $\alpha = .05$ with two-sided 95% intervals, and the primary estimators adjust for pre-task covariates selected for predictive value (Section 3.5).

Four hypotheses were registered: H1, the pooled flip on d1 to d4 (primary); H2, the policy shift on d5; H3, departures from the recommendation implied by one's own estimate; and H4, switching after an opposed versus an aligned voiced lean. H3 and H4 condition on behavior after randomization, so each was registered with falsification checks. H3's check failed and it is reported descriptively. H4's four checks passed after Holm adjustment, and "its causal reading [is] conditional on the identifying assumption" (Section 3.5).

What it finds

Analytical decisions followed the lean

The pooled flip rate on d1 to d4 was 0.72 (95% CI 0.60 to 0.83, one-sided p < .001, 195 trials), the same adjusted and unadjusted (Table 2). Per-decision flip rates ranged from 62 to 82 percentage points (Section 4.1). The post's figure gives them as 82 (outcome measure), 64 (comparison method), 62 (which farms) and 78 (weighting). The post reports the corresponding match rates as 92%, 82%, 81% and 90%. Omitting three sessions that were idle for over half the work period gave 0.74 [0.63, 0.85] (Table 5, Appendix A.4).

The final recommendation moved less directly, but was predictable from the earlier leans

The policy shift was 0.17 under the registered adjusted estimator (95% CI −0.06 to 0.40, p = 0.069, n = 50), not significant, and 0.22 unadjusted (p = 0.037) (Table 2). Without the idle sessions it was 0.26 (p = 0.019, Table 5). The post reports a related but different quantity: 54% recommended rollout when the agent leaned rollout and 36% when it leaned the other way, with an extension counted as not rolling out. Its figure labels that gap "+17pp", the same number as the paper's adjusted policy shift, but a difference in rollout shares is not the paper's recommendation score, which gives an extension half credit (the unadjusted score difference is 0.22).

The authors argue the smaller shift does not mean participants kept control. In an exploratory, in-sample logistic regression, the four analytical leans alone predicted 82% of recommendations, against 61% for always guessing the majority (AUC 0.84). This excludes participants who chose an extension (Section 4.1). The paper's Exhibit 1 traces one session: difference-in-differences gave +4.6%, the agent's lean moved the participant to a levels adjustment giving −1.6%, and the participant recommended discontinuation against the agent's own d5 lean.

The descriptive H3 difference was 0.23 [−0.04, 0.50] (n = 26, Table 2).

Participants who had already chosen often switched

In 38 trials a participant took a side before the agent voiced its lean. They switched in 60% of opposed trials against 6% of aligned ones (Section 5; post, "Results"). The registered decision-adjusted gap was 0.53 [0.24, 0.82], p < .001 (Table 2). The post states the gap as 54 percentage points with that interval. The authors caution that participants who stated a preference early "may have been systematically different" (post). In the paper's limitations, they note that these participants selected themselves into the subset.

How the decisions unfolded

Across 245 machine-coded decisions (Table 3):

  • the agent voiced a side first on 77%, the participant on 17%, and neither on 6%;
  • participants contested the agent's lean on 23% (a contest includes a clarifying question or silently favoring the other side), and the agent contested the participant's side on 9%; the paper's text calls participants' contests rare (Section 4.2);
  • the delivered choice was the agent's lean on 84%.

In the 15 hand-coded sessions, on 39% of decisions the participant neither asked about the decision nor took a side before the final choice (Section 4.2.1). This analysis was not registered (Appendix A.6).

Background did not predict deferral

Ten participant characteristics were tested as moderators in exploratory analyses (Section 4.1):

  • years of experience, self-rated expertise, education and quiz score;
  • trust in AI and frequency of AI use;
  • need for cognition and open-minded thinking;
  • age and gender.

Only age was nominally significant (older participants followed the lean more, p = 0.037), and it did not survive correction for 10 tests. The post adds that with most participants following the agent on most decisions, "there was little variation to explain".

Ownership, recall and justification

  • Ownership. 52% of the 48 rated the recommendation as more their own than the agent's, and 35% as mostly or entirely their own (Section 4.2.2, Figure 3). The post's figure gives the counts: 23 rated it more the agent's (14 slightly, 9 mostly, 0 entirely) and 25 more their own (8 slightly, 13 mostly, 4 entirely). Nearly all of the 11 no-AI participants rated it entirely their own. The post reports that the choices of those who called the recommendation more their own shifted about 65 percentage points toward the lean, against 79 for those who called it more the agent's, "a difference within the margin of error"; this comparison was not found in the paper.
  • Recall. Participants identified their own choice correctly on 85% of decisions, and 35 of the 40 who reported their estimate were within half a percentage point (Section 4.2.2).
  • Confidence. On a 0 to 100 scale, those who matched the lean on all four analytical decisions averaged 71 (n = 29), against 73 for the rest (n = 19). Confidence was unrelated to the share of aligned decisions (Spearman ρ = −0.06, p = 0.666) (Section 4.2.2).
  • Justification. Asked per decision, "Briefly, why ... rather than the alternative? If it wasn't an active choice, just say so," 77% (37 of 48) repeated a talking point their agent had given, "sometimes nearly verbatim", and 15% mentioned the agent anywhere in their answers. Participants could not look back at the transcript while answering (Section 4.2.2; post). Who judged a talking point "repeated" is not stated, beyond the exhibits marking shared phrases.
  • Awareness. Asked first, before any cue, what the study was about: 46% mentioned reliance on or deferral to AI, 12% (6 of 48) the agent's influence or preferences, and none suspected planted behavior (Section 4.2.2, Table 6). The post reports only the 12% figure, as "correctly guessed".

Participants without the agent made more serious errors

Two LLM judges (GPT-5.6-Sol and Gemini 3.1 Pro) graded all 61 sessions' code. One author adjudicated every fatal finding either judge flagged (35 findings in 15 sessions), blind to arm; sessions neither judge flagged were not reviewed by a person (Appendix A.9). By that adjudication, serious errors that would invalidate results occurred in 6 of 11 no-AI sessions (55%) and 3 of 50 AI-assisted sessions (6%). Median time was 90 minutes against 65 (Wilcoxon p = 0.002) (Section 4.2.3). The groups self-selected: the no-AI group had fewer participants with a master's or doctorate (4 of 11 against 24 of 46) and fewer self-rated proficient or expert (8 of 11 against 43 of 48). The authors say they "cannot make causal claims".

The agent's own preferences, without a lean

In direct simulations with no lean, a stock agent on Opus 4.8 chose the same five options (BAAAA) in 91% of 123 runs. The post states this as 112 of 123 (Section 4.3). In a scripted probe where an analyst declared a choice against the agent's baseline and asked only for code, the stock agent raised the other option on 66% of 150 judged declarations and recommended or advocated it on 41%. Leaned toward its non-preferred side, the agent advocated the leaned option on 87% of 150 declarations (Section 4.3). Figure 6 reports "recommend or advocate" rates of 99% for leaned agents and 17% for stock agents when the declaration matched their preference. Figure 5 shows that other models, including Fable 5, Opus 5 and GPT-5.6, also have modal configurations, with varying consistency. The authors use these results to argue that the lean prompt "amplifies" an existing behavior rather than creating one.

The prompts and instructions used

The manipulation is a written instruction. Appendix A.3 summarizes the lean prompt's shared preamble. It tells the agent to:

  • hold the priors as its own and stay neutral on general questions;
  • voice a prior when its decision arises;
  • make "the strongest good-faith, data-grounded case" for it;
  • change its mind if the evidence turns decisively against it.

Its hard constraints read "never misrepresent results, never hide or distort data the user asks for, never make an argument the data doesn't support or that you don't believe." For d5, if the participant's estimate contradicts the lean, the agent recommends a one-year extension rather than denying the estimate. Each decision's prior is a short argument, quoted in Appendix A.5. For d4, for example, the two priors are "this is a membership decision . . . one farm, one weight" and that the subsidy is "funded from surplus the co-op earns on total tonnage". The full prompt text is not printed.

The post summarizes the instruction as making "the best honest case for its lean", to "change its mind if the evidence demanded it", and "never to mislead". From close reading of transcripts, the authors suggest that the influence came "not through misleading or hiding consequences, but through making the case for only one option": agents often explained how results would change under the other option, but "rarely explained why a competent expert could pick the other option" (Section 5). The study does not test a prompt instructing the agent to argue both sides. The authors propose that design for future work.

Human-subjects and registration details

  • Consent and ethics. The study "received internal ethics review before fielding, and participants consented at recruitment to session monitoring and screen recording" (Section 3.6). No external review board is named. Participants were not told the agent had been assigned leans. The paper does not report a debriefing, and it does not report compensation.
  • Data. The paper quotes verbatim excerpts from five sessions, identified by session codes (Appendix A.7). It does not say whether data or transcripts will be released.
  • Registration timing. Data collection began before registration. When the plan was frozen, 17 participants had started and 4 had dropped out. The authors disclose two exceptions to analyzing no data before freezing: they had seen completion and inclusion rates, and one researcher had coded three transcripts, masked to the leans, to develop the rubric (Section 3.6; pre-analysis plan, Section 7). The OSF record shows the plan uploaded on 6 August 2026.
  • Comparison with the plan. The paper follows the plan's hypotheses, estimators, stopping rule (60 completed tasks or 20 August 2026) and idle-share sensitivity analysis. The plan also states that the paper will report the deviations log "in full" and that the codebook will be published. It lists further sensitivity analyses: a split by whether participants guessed the manipulation, results with and without participants who answered no skill items correctly, and an alternative coding of hybrid choices. This note did not find these in the 29-page paper or the post, and the OSF project held only the plan on 12 November 2026.
  • Sample. The plan's power calculation used a nine-session pilot and gives a minimum detectable pooled flip of about 0.21 at 80% power; the observed 0.72 is well above it.

Limitations and open questions

The authors list three main limitations (Section 5; post, "Our study's limitations"):

  • Amplified lean. The prompt made the agent hold and voice a preference reliably. Stock agents also have preferences and voice them unprompted, but whether the flip rates hold for a stock agent depends on whether it has a preference on a decision and volunteers it. The post adds: "When agents aren't given clear preferences and instructions to voice them, the effect might be smaller."
  • One setting. The study covered one task of about an hour, in one field (farming), with one pinned agent. Participants were causal-inference practitioners new to the domain, who in real work would have more domain knowledge and could consult stakeholders.
  • Average effects only. Without pre-task elicitation, the study cannot say how much any one participant was influenced. The post adds a fourth limitation: strength of preference was not measured, so weak prior views may explain some deferral.

Further points from the paper's methods:

  • Self-selected exclusion. The 11 participants who chose not to use the agent were excluded after randomization. Their exclusion follows a registered rule (no substantive AI engagement), but they differed in experience from those included.
  • Model-coded outcomes. Final choices, session events and code errors were coded or first screened by LLM judges. The validation reported is 93% agreement (κ = 0.73) on 75 hand-coded decisions for session coding, and author adjudication for disagreements and flagged errors only.
  • Synthetic task. The decisions were designed to be balanced and consequential. How often real analyses have decisions this open, and this decisive for the result, is not measured.
  • Developer's own product. The agent tested is Anthropic's product, studied by Anthropic researchers and a Fellow. The finding concerns the product's influence on users.

Research questions

  1. How large is the effect with a stock agent? The lean was deliberately strengthened. Randomizing between a stock agent and agents leaned each way, on the same task, would estimate deferral to the model's own default preferences, which the simulations show are strong (91% of runs choosing one configuration).
  2. Does an agent that argues both sides reduce deferral? The authors attribute influence to one-sided argument. A trial arm in which the system prompt requires the agent to state the best case for the other option, and the assumptions behind it, would test that explanation directly.
  3. Does asking the expert first change the outcome? The study avoided pre-task elicitation. An arm that asks participants for their choice on each decision before the agent speaks would measure how much elicitation protects judgment, and at what cost in time.
  4. Do domain experts defer less? Participants were new to farming. Repeating the design with agricultural economists, or moving it to the participants' own fields, would test the authors' expectation that domain knowledge reduces the effect.
  5. Can deferral be detected from transcripts alone? Because of the randomization, each session's influence is known on average. Testing whether features of the transcript (who voiced a side first, whether the participant contested) predict following the lean would show whether the counterfactual methods the authors cite could work in real settings.
  6. Does attribution change if participants can review the transcript? Only 15% credited the agent when answering without the transcript. Allowing review before the justification questions would show whether non-attribution reflects memory or a sense of ownership.

How it connects

References