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Paper summary
The paper studies rhetorical misalignment: loss in decision quality attributed to the linguistic presentation of AI-provided information. A motivating study collects 939 responses from 162 participants with self-reported medical training or experience on USMLE-derived questions. It reports improved aggregate accuracy after AI assistance, alongside harmful correct-to-incorrect revisions and qualitative accounts consistent with several cognitive biases. The paper then defines a utility gap between ideal rational and behavioral decision policies and implements two DeepSeek-V3.1-based simulators prompted to follow Bayesian reasoning or exhibit cognitive biases. Experiments compare their accuracy and disagreement across model-generated explanations, including explanations constructed from a shared claim pool, naturalistic generations, and post-training variants.
Critical strengths
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A consequential evaluation target grounded in human observations. Studying the quality of downstream decisions, including harmful revisions despite overall improvement, is more informative than reporting model accuracy alone. The human study provides concrete motivating evidence: 939 responses from 162 participants, with accuracy increasing from 45.7% to 57.5% (p. 3). Reporting helpful and harmful changes separately is useful because a net improvement can coexist with important failure cases.
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An explicit attempt to hold information fixed and distinguish theory from simulation. The shared-claim-pool experiment addresses an important confound, and the paper explicitly acknowledges that a prompted rational simulator is only an approximation (pp. 7–9). The multiple model and training-variant comparisons could become a useful screening methodology if semantic preservation, statistical reliability, and the simulator's interpretation are established.
Critical weaknesses
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The evidence does not identify the central presentation-only causal claim. In the human experiment, participants answer before and after reading AI analyses; the reported design does not include a randomized content-matched alternative framing or a no-AI reconsideration condition. The 19 harmful revisions following a correct model answer are important observations, but answer correctness does not establish that every supporting claim is factual or that rhetoric, rather than ambiguity, content, or ordinary reconsideration, caused the revision. Rationales are collected after the correct answer is revealed, further limiting causal interpretations of the coded mechanisms. The controlled simulation also does not fully resolve this issue. Table 8’s claim-pool construction examples change “pathognomonic” to “characteristic” and add “body image distortion” to an explanation originally mentioning denial. This preprocessing changes diagnostic strength or explanatory content. These are source-to-pool examples, so they do not by themselves show that every final model-versus-neutral contrast differs in content; however, they also do not validate the assumed semantic equivalence. Actual paired outputs and a preservation audit are needed. Tables 2–3 do not explicitly report both the model and neutral representations and their paired difference, despite Section 4.2 claiming that this contrast isolates a causal effect. Consequently, the conclusion that human decisions were worsened through language use alone is stronger than the evidence presented.
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The proposed measure is not sufficiently validated, and central numerical results are inconsistent. The ideal policy conditions on the full information pair (X0, X1), although an arbitrary utterance map need not preserve that information. Unless sufficient information is recoverable from the message, its gap from a message-limited listener can include information loss. Even with lossless messages, a gap under one representation can reflect generic policy or reasoning differences rather than presentation-specific harm. Appendix E explicitly instructs the behavioral simulator to exhibit six biases; an LLM's subsequent labeling of its reasoning mainly tests prompt compliance. Appendix D does not establish known-posterior Bayesian accuracy, calibration, action-level framing invariance, or correspondence with human framing effects. Table 6 reports high targeted-bias classification rates even for the rational simulator (0.69–0.86 under the biased framings), without a clear operational interpretation or uncertainty.
The numerical problems independently undermine the measurement. For common paired trials, the accuracy difference must equal P(rational correct, behavioral wrong) minus P(rational wrong, behavioral correct). In Table 2, DeepSeek-V3.1 has accuracy difference 89.2% − 89.8% = −0.6 percentage points, whereas the directional columns imply 1.9% − 1.1% = +0.8 points. Other discrepancies include Gemini (−0.6 versus −0.3 points) and Tülu-SFT (+5.8 versus +5.0 points); these exceed rounding tolerance. Moreover, the human-study totals and conditional counts need reconciliation: using the stated 939 equally weighted trials, 45.7% initial accuracy requires 429 initially correct trials; 19 harmful changes at a 5.6% conditional rate implies 337–342 initially-human-correct/model-correct trials, and 32 helpful changes at a 17.4% conditional rate implies 184 initially-human-wrong/model-wrong trials. Thus the model-correct count must be 663–668 (70.61%–71.14%), whereas the reported 65.0% implies 610 trials. These ranges allow rounding to one decimal place and assume that the statistics share a sample and weighting. No uncertainty intervals or formal tests support the claimed differences or the statement that larger models do not yield significant controlled gaps. These issues prevent reliable interpretation of the proposed metric and model comparisons.
Questions for authors
The following are clarification or evidence requests that could materially change the assessment, rather than suggestions for unrelated future work.
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Numerical reconciliation: Please provide the per-model paired correctness contingency counts underlying Tables 2–4, identify every denominator or exclusion, and reconcile Table 2's accuracy differences with its directional correctness columns. For the human study, please provide the initial-human-correctness × model-correctness × final-human-correctness counts and reconcile the conditional percentages/counts with 939 trials, 45.7% initial accuracy, and 65.0% model accuracy. Were different subsets used?
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Identification: Where are the paired results for the model representation and its neutral counterpart specified in Section 4.2? Please provide that contrast and evidence that the two preserve all decision-relevant claims, uncertainty, and recommendation content, including how Table 8's semantic changes are handled. Is there a human content-matched framing comparison? If not, would the authors restrict the human-study conclusion to descriptive evidence and avoid claiming identified human harm from language alone?
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Simulator validity: What evidence distinguishes the reported gap from baseline differences induced by the rational/behavioral system prompts? Please clarify Table 6's neutral-condition metric and provide action-level framing effects and an objectively computable Bayesian benchmark, with uncertainty. Can the measured effects be reproduced with another simulator or related to human effects on matched items? Please also clarify the information-sufficiency assumption connecting the utterance map to conditioning on (X0, X1).
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Statistical support: What are the exact sample sizes, repeated-generation settings, and confidence intervals for each comparison? Please use paired analyses for simulator outcomes, account for repeated participants and questions in the human study, and explain the inferential basis and multiplicity treatment for model-size and training-stage comparisons. A nonsignificant result should not be interpreted as evidence of negligible effect without an equivalence analysis or sufficiently informative interval.