{"id":"bb4a6afd-65cc-402b-9304-4342c48e2a95","arxiv_id":"2610.10232","paper_version":1,"verdict":"CONDITIONAL","confidence":"HIGH","novelty_score":6.0,"correctness_risk":"low","formal_verification":"none","parameter_count":3,"one_line_summary":"Fifteen chatbots receive nearly uncorrelated persuasiveness rankings across nine published evaluation methods, so a single persuasion score says little outside its own test.","lead":"Nine published tests of how persuasive an AI chatbot is rank the same fifteen chatbots very differently, agreeing only weakly with each other. The disagreement tracks what task a test sets and whether the chatbot is willing to do it, not how the test scores persuasion, a finding regulators and developers should weigh when reading any single persuasion score.","discovery_kind":"new_application","skeptic_critique":{"model":"deepseek/deepseek-v4-flash","headline":"The weakest point is adaptation fidelity: without at least one full original-form rerun, low agreement may characterize the shared harness rather than the published methods.","rationale":"The reader's strongest claim — weak agreement among the reliable methods, mean Spearman rho 0.252, with sampling noise unlikely to explain it — is supported within its stated scope. The reliability planning, resampling intervals, disattenuation, placebo capability check, and Westfall-Young correction are all handled carefully, and I found no internal inconsistency in the reported statistics. The single load-bearing concern is adaptation fidelity, the same assumption the reader identified: the paper's central generalization says something about published evaluation methods, but the measured disagreement is between adapted versions, and no original-form rerun was performed (b183). This is not a concealed flaw; the authors state it plainly. The problem is that the spot checks in Section 3.7 substitute alternative judges and persuadees within the shared harness and therefore cannot establish that the adaptations are ranking-neutral. A targeted original-form rerun of two heavily modified methods would resolve whether the finding survives. If original-form and adapted rankings correlate strongly, the weak-agreement conclusion stands; if not, the paper should be read as an evaluation of its own harness rather than of the published approaches. I would therefore keep the reader's CONDITIONAL verdict; I see no grounds to reject, since the claims are carefully hedged and the statistics are sound. The refusal contribution is somewhat fragile — one cell (Claude-Fable-5.1 on MakeMeSay) accounts for 0.054 of the 0.090 total effect — but the authors treat the refusal analysis as part of the exploratory RQ2 picture, and it is not the central load-bearing claim.","tokens_in":26477,"tokens_out":8069,"duration_ms":54082,"concrete_test":"After code release, rerun at least two methods with the largest deviations from their originals — Rationale (fixed GPT-4 reference instead of the original comparison) and either False Claim or Reduce Meat (fixed persuadee instead of self-play) — in their full original configurations on the same fifteen models, or on five capability-spanning models plus the Gemma-3-27B/Qwen3-32B close pair if budget binds. Compute Spearman rho between each method's original-form and adapted rankings, and the mean pairwise rho of the original-form runs. Original-form versus adapted rho >= 0.8 per method and an original-form mean pairwise rho near 0.25 would settle the adaptation concern; a large ranking flip or mean rho above roughly 0.5 would require re-scoping the headline to the adapted harness.","verdict_should_be":"UNCHANGED","load_bearing_attack":"The RQ1 result is internally coherent, but its generalizing force depends on an untested premise: that the shared-harness adaptations preserve each method's ranking behavior. Every method was altered (Section 3.1, Appendix B): a single pinned persuadee and judge replace the original agents; Rationale is scored against one fixed GPT-4 rationale rather than compared pairwise as in the original; Reduce Meat, False Claim, and Mislead Debate no longer let the evaluated model play its own persuadee; messages are token-capped at 512; and temperatures differ for some methods. The authors explicitly state that no method was rerun in its full original form (Limitations, b183). The Section 3.7 robustness checks — second judge, second persuadee, temperature 0, human verdicts for Rationale — test variation within the adapted design, not the mapping from adapted to original designs. If, say, fixed-reference scoring for Rationale or removing self-play in False Claim changes which models rank high, the mean rho of 0.25 would be a property of this harness, and the headline \"persuasion is in the eye of the evaluation\" would overstate what has been shown about published evaluation approaches. This is an external-validity gap rather than an internal inconsistency; the authors are transparent about it, but they do not test the direction that matters.","agreement_with_reader":"agree"},"referee_report":{"model":"deepseek/deepseek-v4-flash","summary":"This paper asks whether published automated LLM persuasion evaluation methods reach the same conclusions about which models are most persuasive. The authors adapt nine published methods — five rational-persuasion and four manipulation — to a shared harness with a single pinned persuadee (GPT-4.1-mini), a single pinned judge (GPT-4o), and documented prompt and token adaptations (Section 3.1, Appendix B), and run all nine on the same fifteen LLMs. RQ1 finds weak agreement: mean pairwise Spearman rho = 0.252 over the eight methods passing the 0.80 split-half reliability bar (0.235 over all nine), a disattenuated mean of 0.29 against a 0.7 convergent-validity reference, a highest pairwise rho of 0.73, and robustness checks (second judge, second persuadee, temperature 0, human verdicts for Rationale) that reproduce the main rankings (Sections 4.1–4.2). RQ2 attributes part of the disagreement to refusals: excluding refused or empty attempts raises the mean rho to 0.342, so refusals lower agreement by about a quarter, and an exploratory eighteen-axis analysis suggests the task type (rational vs manipulative) matters more than how a method scores persuasion, though no grouping survives the Westfall–Young correction (Table 5).","tokens_in":26722,"tokens_out":14381,"duration_ms":82296,"significance":"If the result holds, this is a timely, methodologically careful contribution: it is, to the authors' knowledge, the first side-by-side comparison of independently published persuasion evaluation methods on a common model set, and it speaks directly to manipulation-risk assessment under the EU GPAI Code of Practice and developers' safety frameworks. The RQ1 measurement is strong and, in an important respect, conservative: the shared persuadee, judge, and seed would tend to inflate agreement between methods, so the low observed agreement is unlikely to be an artifact of the harness inflating disagreement. The reliability gating with the ceiling argument, the disattenuation check, the leave-one-out agreement values, the bootstrap and jackknife intervals, and the placebo-controlled capability-removal analysis are all sound, and the human-judge validation of the Rationale method provides a concrete anchor. The authors are also commendably explicit about what is exploratory (RQ2 axes; adjusted p-values 0.23–0.39) and about the adaptation problem (Limitations, b183).","major_comments":[{"comment":"","section":"3.1, Appendix B, Limitations","authors_acknowledge":null,"authors_acknowledge_p":null},{"comment":"The claim that 'the effect of willingness on agreement is thus larger than the exclusion rule shows' (Section 4.3) rests on the conditional re-scoring of False Claim, in which paragraphs are classified as supporting or correcting the false claim by the pinned persuadee GPT-4.1-mini. The resulting swing in that method's mean agreement with the other reliable methods, from −0.26 to +0.38, is large, and no reliability figure for these labels (for example, inter-labeler agreement or a human-checked subset) is reported. Since this analysis is the main quantitative support for the ability-versus-willingness reading of manipulation scores, I ask that the label reliability be reported or the claim qualified accordingly.","section":"4.3","authors_acknowledge":null,"authors_acknowledge_p":null}],"minor_comments":[{"comment":"The sentence 'Excluding refused or empty attempts raises the mean only to 0.34 ... dropping the seven cells ... raises it to 0.36' lacks a clear subject for the second clause; rephrase to state that excluding, in addition, the seven cells with refusal or unreadable rates above a quarter raises the mean to 0.36.","section":"4.2","authors_acknowledge":null,"authors_acknowledge_p":null},{"comment":"The phrase 'lower agreement by about a quarter' should state its base, since 0.090/0.252 is 0.36 while 0.090/0.342 is 0.26; as written, readers may compute the wrong fraction.","section":"Abstract and 4.3","authors_acknowledge":null,"authors_acknowledge_p":null},{"comment":"The orange refusal bars only become visible from 5%, which makes all cells with smaller refusal shares look identical; a small table of refusal rates or a lower visibility floor would make the figure self-contained.","section":"Figure 2","authors_acknowledge":null,"authors_acknowledge_p":null},{"comment":"The run-to-run reliability column is not accompanied by the replicate conditions (temperature and seed of the replicate runs); one sentence in Section 3.7 would help interpret the gap between Mislead Debate's split-half reliability (0.74) and its run-to-run value (0.43).","section":"3.7 and Table 3","authors_acknowledge":null,"authors_acknowledge_p":null},{"comment":"The Conclusion restates the task-type split ('Together these produce a split by task type') without the qualifier, carried in Sections 4.3 and 6, that no grouping remains significant after correction; adding the adjusted-p qualifier there would prevent the indicative finding from being quoted as established.","section":"7","authors_acknowledge":null,"authors_acknowledge_p":null}],"recommendation":"major_revision","confidential_remarks":"The editor may wish to treat the requested calibration rerun as a feasibility question: a subset rerun of Rationale under pairwise judging, or of False Claim under a self-play persuadee, is substantially cheaper than a full nine-method rerun, so the major comment is actionable within the manuscript's budget. The paper fits the journal's scope well. One mild editorial note: the method sample is drawn from the authors' own review paper and online hub; the inclusion criteria are explicit and objective, so I do not see this as a disqualifying conflict, but it is worth being alert to in the revision process."},"author_rebuttal":null,"desk_editor":{"model":"deepseek/deepseek-v4-flash","letter":"Short version: this is the first paper that actually runs nine independently published persuasion evaluation methods on the same fifteen models, and the headline result — weak rank agreement, mean Spearman rho about 0.25 — holds up under the paper's own reliability work. The load-bearing weakness is external validity: the shared harness changes every method enough that the measured disagreement may be a property of the harness, not of the published evaluation approaches. The authors know this and say it plainly, but they do not test the direction that matters.\n\nWhat is genuinely good: RQ1 is careful. Eight of nine methods clear the 0.80 split-half bar, the disattenuated mean (0.29) barely moves from the raw 0.252, and the robustness checks — second judge, second persuadee, temperature 0, human verdicts for Rationale — mostly reproduce the rankings. The bootstrap over sampling units and jackknife over models are the right tools here. The adaptation decisions in Appendix B are documented in unusual detail, including the places where the original methods had self-play or different scorers. The paper also deserves credit for keeping the RQ2 task-type story labelled as indicative; none of those groupings survive Westfall-Young correction.\n\nThe soft spots are real but proportionate. The stress-test concern is accurate: Section 3.7 varies judge, persuadee, and temperature within the adapted design; it does not compare an adapted method against its original form. The one near-exception, Mislead Debate without the token cap, is only a partial rerun and the authors report it as unreliable. So the right reading is: nine methods, as adapted, disagree. That is a meaningful result, but it is not the same as showing that the published evaluation approaches disagree. The abstract and title lean broader than the contribution statement, and the \"about a quarter\" refusal effect comes mostly from two cells — Claude-Fable-5.1 on MakeMeSay and two models on MakeMePay — though the paired bootstrap difference in Table 4 is solid. Two smaller issues: the code is promised but not released, and the API runs cannot be independently verified from the preprint.\n\nWho should read this: people building or reviewing safety evaluations, regulators trying to read manipulation scores, and benchmark methodologists. It gives them a reusable comparison template and a sensible vocabulary for separating reliability, agreement, capability, and willingness. I would cite it for the RQ1 result and the measurement design, and I would send it to peer review. The revision request should be: release the harness, and run at least one method in something close to original form, even on a few models, to show the adaptation is not doing the work.","headline":"First side-by-side comparison of nine persuasion evaluation methods; the weak-agreement result is credible within the paper's stated adapted scope, but the absence of any original-form rerun leaves a real external-validity gap.","tokens_in":27392,"tokens_out":2094,"would_cite":true,"duration_ms":15012,"reading_group":"yes","serious_thinker":"yes","would_accept_peer_review":true},"pith_extraction":{"msc":[],"pacs":[],"model":"deepseek/deepseek-v4-flash","headline":"Nine published persuasion evaluations, adapted to one shared harness and run on the same fifteen models, rank them with mean Spearman agreement of only 0.25, so a single persuasion score says little outside its own task.","keywords":["LLM persuasion evaluation","evaluation fragmentation","benchmark agreement","manipulation risk","refusal behavior","general capability","ability versus willingness","automated evaluation methods"],"falsifier":"Rerun the methods that disagree most, for instance False Claim and Subjective Opinion, which rank the models at $\\rho = -0.44$ under the harness, in their full original published form on the same fifteen models, with each method's own persuadee, judge, token limits, and scorer. If the original-form rankings correlate strongly, the fragmentation is an artifact of the adaptations; if they still diverge, the task-dependence is intrinsic. The paper already supplies a partial version: removing the 512-token cap raised Mislead Debate's reliability from 0.74 to 0.93, yet the uncapped ranking still differed from the capped one ($\\rho = 0.21$), leaving the harness's contribution unresolved.","tokens_in":27813,"feed_emoji":"🎭","tokens_out":11349,"duration_ms":58403,"temperature":0.7,"pith_summary":"This paper asks whether published automated methods for evaluating LLM persuasiveness reach the same conclusions when run on the same models. Adapting nine published methods to a shared harness, with one pinned persuadee, one pinned judge, and the same fifteen LLMs, it finds that the methods rank the models only weakly alike (mean Spearman $\\rho = 0.25$ over the eight reliable methods), with sampling noise an unlikely explanation. Two factors account for part of the split: models that refuse some tasks but not others lower agreement by about a quarter, and the type of task matters more than how a method scores persuasion, with rational-persuasion methods agreeing among themselves and manipulation methods agreeing neither with them nor with each other. The authors conclude that a persuasion score fuses a model's ability to persuade with its willingness to try, so a low manipulation score can mean stronger safeguards rather than weaker ability, and a single score describes one task rather than a portable property.","feed_headline":"LLM persuasion rankings barely agree across nine evaluation tests","feed_subtitle":"Eight methods rank fifteen models at mean agreement 0.25; task type and refusals drive the split.","key_machinery":"The load-bearing mechanism is the shared harness together with the decision to compare rankings rather than scores. Every method was adapted so that a single pinned persuadee (GPT-4.1-mini) and a single pinned judge (GPT-4o) play every role, messages are token-capped, and a refused or empty attempt is scored as zero; each method's own sampling units (claims, conversations, codewords) are resampled for confidence intervals, and each method's split-half reliability sets the ceiling on how much agreement it could possibly show. Against that ceiling, the paper compares methods by Spearman rank correlation over the fifteen models, applies the disattenuation correction $\\rho/\\sqrt{r_a r_b}$ to separate construct disagreement from noise, computes a capability score $C$ as the mean of z-scored MMLU-Pro and IFEval accuracies, and reruns the rankings with refused attempts excluded to isolate willingness from ability. The refusal-exclusion rule is the instrument that lets the authors decompose each score into ability and willingness.","core_discovery":"The paper's central claim is that automated LLM persuasiveness evaluation is fragmented rather than convergent: nine published methods, adapted to a shared harness and run on the same fifteen models, rank the models only weakly alike. Across the nine methods seven different models come first, and the mean pairwise Spearman correlation over the eight methods that clear the reliability bar (split-half at least 0.80) is $\\rho = 0.252$, with a model jackknife interval of [0.00, 0.50]; the disattenuated mean is 0.29, so sampling noise does not explain the disagreement. The paper attributes part of the split to refusals, since scoring a refused attempt as zero means models that decline some tasks and not others lower the mean agreement by about a quarter ($+0.090$, [0.06, 0.14]), and part to task type: the five rational-persuasion methods agree moderately among themselves (mean $\\rho = 0.56$), while the three manipulation methods agree neither with them (0.06) nor with each other (0.03), a pattern the authors call indicative given only eight methods. A capability analysis shows most rational-persuasion methods track general capability ($\\rho$ with the capability score $C$ from 0.58 to 0.90) while the manipulation methods do not, with False Claim's ranking driven by capable models declining its task (the share of declines correlates $\\rho = 0.76$ with capability). The interpretive conclusion is that a persuasion score combines ability with willingness: scored only on the attempts that support the false claim, False Claim ranks models by capability and agrees with the rational methods, and a low manipulation score may reflect stronger safeguards rather than weaker persuasive ability. LLM persuasion is therefore largely in the eye of the evaluation.","pith_inferences":["If the ability-willingness split holds, persuasion-risk regulation should ask at which training stage a score was produced: only evaluation of pre-safety-training models reads ability cleanly, while scores from released models are inseparable blends of the two.","Because several automated methods are modeled directly on human-study paradigms, the fragmentation logic is testable in human settings; running two of the same task designs with human persuaders on matched content would show whether the near-0.25 agreement is a property of automated harnesses or of the construct itself.","The near-zero agreement among the five API models may partly be a harness effect the paper itself flags as possible, since a shared weak persuadee can compress differences among strong persuaders; repeating the comparison with a more capable pinned persuadee would separate construct fragmentation from measurement compression.","The general lesson likely extends beyond persuasion: any capability evaluated through simulated interactive tasks, such as negotiation, deception, or flattery benchmarks, can be expected to show the same task-dependence and the same conflation of willingness with ability."],"forward_implications":["A single persuasion score describes a model on one task and should not be read as a measure of persuasiveness across settings, even when refusals are set aside.","For the most capable models, which safety regulation targets, the choice of evaluation method may largely determine the ranking: agreement among the five API models is near zero (mean $\\rho = 0.00$).","Refusals, including indirect ones, should be reported separately from persuasive success, because a low manipulation score can reflect willingness to decline rather than inability to persuade.","Most rational-persuasion methods track general capability, so two methods can agree mainly because both measure capability; reporting a capability correlation alongside each persuasion score is necessary to read either.","Safety assessments should use several tasks chosen for the risk in question, particularly for manipulation, where different models decline different tasks and rankings diverge most."],"supporting_citations":[{"why":"Supplies the taxonomy and code links through which the nine evaluated methods were selected and adapted.","marker":"Dementaviciute et al. (2026)"},{"why":"Closest prior comparison; found manipulation rankings barely correlate across environments, the pattern this study extends to published methods.","marker":"Zaman et al. (2026)"},{"why":"Formalizes benchmark agreement testing and supplies the ten-model minimum and ranking-based comparison that justify the study design.","marker":"Perlitz et al. (2025)"},{"why":"Provides the method for measuring how closely a benchmark ranking tracks general capability, used for RQ3.","marker":"Ren et al. (2024)"},{"why":"Supplies the 0.7 convergent-validity reference against which the disattenuated agreement is read.","marker":"Carlson and Herdman (2012)"},{"why":"Provides the disattenuation formula used to estimate agreement without measurement noise.","marker":"Spearman (1904)"},{"why":"Source of the False Claim method and of the observation that capable models score low, attributed to alignment.","marker":"Ju et al. (2025)"},{"why":"Source of MakeMePay and MakeMeSay and of the practice of measuring ability alone on pre-safety-training models.","marker":"OpenAI (2024)"}],"fun_headline_variants":["Nine persuasion tests crown seven different LLM winners","LLM persuasion rankings depend on the evaluation, not the model","Persuasion scores reveal willingness, not just skill","Task type, not scoring, splits LLM persuasion rankings","Refusal behavior sways LLM persuasion rankings by a quarter"],"cache_read_input_tokens":0,"weakest_assumption_plain":"The load-bearing premise is that the weak agreement is a property of the published evaluation approaches, not of the shared harness every method was forced into: no method was rerun in its full original form, so the measured fragmentation could in principle be an artifact of the pinned agents, the token caps, or the changed scorers, and the authors test this only through spot checks rather than an original-form rerun.","fun_headline_variants_meta":{"raw":{"variants":["Nine persuasion tests crown seven different LLM winners","LLM persuasion rankings depend on the evaluation, not the model","Persuasion scores reveal willingness, not just skill","Task type, not scoring, splits LLM persuasion rankings","Refusal behavior sways LLM persuasion rankings by a quarter"]},"model":"deepseek/deepseek-v4-flash","effort":"low","cost_usd":0.000324,"raw_usage":{"cost":0.000324016,"is_byok":false,"cost_details":{"upstream_inference_cost":0.000324016,"upstream_inference_prompt_cost":0.000125776,"upstream_inference_completions_cost":0.00019824},"total_tokens":2016,"prompt_tokens":1308,"completion_tokens":708,"prompt_tokens_details":{"audio_tokens":0,"video_tokens":0,"cached_tokens":512,"cache_write_tokens":0},"completion_tokens_details":{"audio_tokens":0,"image_tokens":0,"reasoning_tokens":638}},"tokens_in":1308,"tokens_out":708,"cost_source":"openrouter_usage","duration_ms":5065,"image_pages":[],"temperature":1.0,"billed_attempts":1,"reasoning_tokens":638,"transport_provider":"openrouter","cache_read_input_tokens":0,"cache_creation_input_tokens":0},"cache_creation_input_tokens":0},"created_at":"2026-10-08T14:10:05.025918+00:00","model_set":{"reader":"deepseek/deepseek-v4-flash"},"falsifier":"Rerun the methods that disagree most, for instance False Claim and Subjective Opinion, which rank the models at $\\rho = -0.44$ under the harness, in their full original published form on the same fifteen models, with each method's own persuadee, judge, token limits, and scorer. If the original-form rankings correlate strongly, the fragmentation is an artifact of the adaptations; if they still diverge, the task-dependence is intrinsic. The paper already supplies a partial version: removing the 512-token cap raised Mislead Debate's reliability from 0.74 to 0.93, yet the uncapped ranking still differed from the capped one ($\\rho = 0.21$), leaving the harness's contribution unresolved.","supporting_citations":[],"review_version":1}