acceptodds
Under review as a conference paper at ICLR 2027

The Butterfly Effect in LLM Social Simulations: From Architecture Sensitivity to Robustness Audits

Abstract

A *butterfly effect* occurs when a local perturbation propagates through a system and produces divergence in its collective outcome. In LLM social simulations, this creates a particular challenge for scientific inference: sensitivity to implementation choices can enter agent interactions and alter the collective outcomes on which scientific claims are based. We study this problem through a repeated Prisoner's Dilemma and a social-media echo chamber, spanning representation- and design-level perturbations across four LLM families. We find that controlled perturbations can substantially alter collective outcomes, with sensitivity varying across both perturbations and models. In the Prisoner's Dilemma, changing only the representation of a matched persona shifts two-agent cooperation by up to 75.2 percentage points, while game framing and memory representation produce smaller or less consistent effects. Multi-agent interaction further reshapes representation sensitivity, producing amplification or attenuation depending on the model and perturbation. In the echo-chamber simulation, persona representation changes interaction targeting and is accompanied by divergence in collective interaction structure, extending representation sensitivity from agent behavior to network-level outcomes. These results show that robustness cannot be inferred from a single simulation configuration and that local sensitivity can change as it propagates through interaction. We introduce **TRAILS** (Taxonomy for Robustness Audits In LLM Simulations) and the **Social Simulation Audit Card** as a framework for systematically auditing these dependencies and calibrating the scope of scientific claims to the robustness evidence that supports them.

Primary area:
foundation or frontier models, including LLMs
Keywords:
LLM social simulation, generative agents, agent-based modeling, robustness audits, sensitivity analysis, collective behavior, emergent behavior, architecture sensitivity, echo chambers, Prisoner's Dilemma

Reviews

Among:
Shape:
1234this paper, Top 30%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_e6rdOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
3
Soundness
3
Read review
Paper summary

The paper studies how seemingly small implementation choices can have great implication on the collective outcomes of LLM social simulations, challenging the scientific soundness of this field. It specifically studies controlled perturbations on sequential Prisoner's Dilemma and social-media echo chamber simulation. TRAILS (Taxonomy for Robustness Audits In LLM Simulations)

Critical strengths
  • The paper presents an interesting perspective of studying multi-agent LLM interaction, challenging the soundness of most LLM social simulations. It reframes validation of LLM social simulations away from realism and toward robustness, asking whether a certain conclusion holds across implementation choices.
  • Clear writing and compelling examples. The paper is easy to follow. Figure 2 makes a strong point: three formats of an identical strategic persona (PLAIN, DESCRIPTIVE, TABULAR) produce a 75.2% cooperation gap.
Critical weaknesses
  • Figure 2 sends a strong information but it is only one model. The SD error bars are also very wide, especially for the descriptive condition case. One cannot conclude enough from this figure, and this figure is the headline result. My suggestion is to constrain the cooperation decision output to a binary token "Yes/No" so that the authors could read per-round action probabilities from the logits instead of inferring a rate from 30 sampled trajectories, yielding a much tighter estimate of the same quantity. You can refer to the logit method in https://arxiv.org/abs/2601.13518.
  • The paper reports that sensitivity varies across perturbations and models and that reciprocal interaction can amplify or attenuate it, but offers neither hypothesis for the underlying mechanism, nor follow-up experiment that would further explain the observations. One plausible hypothesis is that plain format makes it easier to digest for language model and easy to follow comparing to tabular encoding. I would like to see the authors deliberately design further experiments to testify pursue your hypothesis.
  • nit: Section 3.1 conceptual framework is a bit redundant.
Questions for authors
  • The paper proposes a Social Simulation Audit Card asks researchers to run perturbations across TRAILS dimensions and multiple models, but the paper does not report what the audits cost in API spend, tokens, or wall-clock time. Most labs don't have sufficient resources to run all these perturbations over all the models. An auditing protocol that is unaffordable for most groups will not be adopted.
  • Do the authors have hypothesis for (1) the persona-representation effect on cooperation behavior in Figure 2 (2) the cross-model pattern, in particular why deepseek-v3.2 attenuates the persona contrast (A = -0.087, Table 6) while the other three amplify it?
4 comments
AuthorsOpenReview ↗

Response from authors

Dear Reviewer e6rd,

Thank you for your thoughtful review and for recognizing our contribution in reframing the evaluation of LLM social simulations around robustness. We also appreciate your positive assessment of the paper’s clarity and the persuasive empirical example demonstrating sensitivity to implementation choices. Below, we respond to your suggestions and questions with additional experiments, analyses, and clarifications. All changes are highlighted in blue in the revised paper‾\underline{\text{revised paper}}.

Response to W2 and Q2 (Mechanism behind the butterfly effect)

The reviewer notes that we show sensitivity varies across perturbations and models, and that interaction can amplify or attenuate it, but we offer no hypothesis or follow-up experiment to explain why. The reviewer also suggests candidate hypothesis to test.

We thank the reviewer for pushing us to deepen both the contribution and the analysis. In response, we added a mechanism analysis built on additional experiments to the revised paper (Sec. 4.3‾\underline{\text{Sec. 4.3}}), built around two hypotheses that we test directly.

Hypothesis 1: representation matters when the persona conflicts with the model's default behavior (App. D.2‾\underline{\text{App. D.2}}, Fig. 8‾\underline{\text{Fig. 8}}). If structured formats were simply harder to follow, as the reviewer suggests, the effect would appear for any persona. Instead:

  • With a neutral or a cooperative persona, the three representations change cooperation by at most 0.10, compared with up to 0.78 for the strategic persona.
  • Against fixed opponents, Tabular is the least cooperative representation for three of four models.

Representation therefore matters most when the persona pushes against the model's default tendency to cooperate.

Hypothesis 2: interaction amplifies representation effects that appear early in the game (App. D.4‾\underline{\text{App. D.4}}, Figs. 5‾\underline{\text{Figs. 5}} and 10‾\underline{\text{10}}). Reciprocity carries the first move forward, so a representation that changes round-1 behavior is amplified, and one that does not is attenuated. The round-1 gap tracks AA across all 12 model–representation pairs (Spearman ρ = 0.76):

ModelRound-1 gap (P–D / P–T / D–T)AA (P–D / P–T / D–T)
GPT-5.20.52 / 0.00 / 0.52+0.48 / −0.58 / +0.42
Claude Haiku 4.50.58 / 0.02 / 0.57+0.46 / −0.29 / +0.39
Gemini 2.5 Flash0.72 / 0.75 / 0.03+0.29 / +0.29 / 0.00
DeepSeek V3.20.00 / 0.03 / 0.03−0.09 / +0.02 / +0.01

DeepSeek V3.2 opens cooperatively under every representation, so there is no early difference to amplify. DeepSeek V4 Flash, held out from deriving the pattern, opens differently under Descriptive, and both Descriptive contrasts are amplified, as predicted. Beyond the opening, after a forced mutual-defection opening only Plain agents return to cooperation, and the share of stated reasons citing exploitation risk tracks defection (ρ = −0.90).

Limitations of these hypotheses. Sensitivity to small differences is a long-standing topic in the study of social systems. In human collective behavior, social influence makes outcomes unpredictable even across groups facing identical conditions (Salganik et al., 2006). In agent-based modeling, a small change to a single agent can alter macro-level behavior (Bertolotti et al., 2020), and implementation choices can introduce artefacts into a model's results (Galán et al., 2009). Our hypotheses explain the patterns in our two testbeds, but they do not provide a general account of why LLM agents are sensitive to representation. Our contribution is to show that LLM social simulations introduce an additional source of sensitivity, the representation of agent specifications, which is currently overlooked and needs to be measured and reported. A full mechanistic explanation remains future work.

References

Salganik, M. J., Dodds, P. S., & Watts, D. J. (2006). Experimental study of inequality and unpredictability in an artificial cultural market. Science, 311(5762), 854–856.

Bertolotti, F., Locoro, A., & Mari, L. (2020). Sensitivity to initial conditions in agent-based models. In Multi-Agent Systems and Agreement Technologies (EUMAS/AT 2020), Lecture Notes in Computer Science, vol. 12520, pp. 501–508. Springer.

Galán, J. M., Izquierdo, L. R., Izquierdo, S. S., Santos, J. I., del Olmo, R., López-Paredes, A., & Edmonds, B. (2009). Errors and artefacts in agent-based modelling. Journal of Artificial Societies and Social Simulation, 12(1), 1.

Response to W1 (Visualization in Figure 2 and a logit-based alternative)

The reviewer points out a caveat in how Fig. 2 visualizes the headline result: the SD error bars are wide, especially under Descriptive, which makes the result harder to read than it should be. We agree that our choice of visualization was not ideal for this figure. The reviewer also suggests estimating per-round action probabilities from the logits as a tighter alternative to sampling trajectories.

Changes to Figure 2 (Fig. 2‾\underline{\text{Fig. 2}}). We agree that the original visualization did not show the result clearly. The revised figure makes three changes:

  • Error bars now show 95% confidence intervals of the mean instead of standard deviations.
  • Dots show individual runs, so the shape of the run-level distribution is visible.
  • The significance heatmaps now use Holm-corrected Mann–Whitney tests on run-level means.

The wide spread under Descriptive reflects a two-peaked outcome rather than imprecision. Some runs lock into mutual cooperation and others into mutual defection, which is the path dependence we analyze in Sec. 4.3‾\underline{\text{Sec. 4.3}}. The mean difference itself is precisely estimated: −75.2 pp, 95% CI [−88.3, −62.0]. Fig. 2 illustrates GPT-5.2. Results for all four models are reported in Table 1‾\underline{\text{Table 1}} and App. D.1‾\underline{\text{App. D.1}}.

New experiment: action-token probabilities (App. D.4‾\underline{\text{App. D.4}}). We appreciate this suggestion and applied the logit method the reviewer pointed to (Yuan et al., 2026, now cited). We kept the original prompt and read the probability of the action token from the model's JSON answer, since switching to a Yes/No output would itself change how the actions are represented.

Unfortunately, the method applies to only one of our four models. Claude's API does not return log-probabilities. Gemini 2.5 Flash reasons before it answers, so by the time it writes the action, the probability is almost always 0 or 1 and carries no more information than the sampled action. For DeepSeek V4 Flash, the API's top alternatives did not include the action actually generated, so its probability could not be read reliably. We therefore report the analysis for GPT-5.2.

GPT-5.2, Descriptive − PlainEstimate [95% CI]
Sampled actions−0.75 [−0.87, −0.62]
Action-token probabilities−0.77 [−0.87, −0.67]

The two estimates agree closely, so the persona effect is not an artifact of sampling a small number of trajectories. The logits also show how each representation responds to the same situation: after a round of mutual defection, the probability of cooperating is 0.36–0.82 under Plain but 0.00 under Descriptive and Tabular.

Summary. The logit analysis confirms the effect with a different estimator. The interval narrows only slightly because most of the uncertainty comes from differences between trajectories, the path dependence analyzed in Sec. 4.3‾\underline{\text{Sec. 4.3}}. We therefore keep trajectory sampling as our main estimate and report the logit results alongside it.

Response to Q1 (Time and cost of an audit)

The reviewer asks what an audit costs in API spend, tokens and wall-clock time, noting that a protocol most groups cannot afford will not be adopted.

New analysis: audit cost (App. F.2‾\underline{\text{App. F.2}}, Table 11‾\underline{\text{Table 11}}). A study already runs its baseline, so each audited perturbation adds only the runs for the new condition. Using the token counts recorded in our experiments, one perturbation with 30 runs costs:

ModelPrisoner's DilemmaEcho chamber
GPT-5.2$2.44$38.32
Claude Haiku 4.5$1.36$22.89
Gemini 2.5 Flash$0.23$7.13
DeepSeek$0.09$1.33

Wall-clock time is set mainly by API rate limits.

Beyond cost: making audits feasible. We understand that the reviewer's concern goes beyond time and money to whether the card is feasible in practice. The card does not require every dimension to be audited on every model. Researchers record which dimensions they audited and bound each verdict by that coverage. To help them decide where to start, the revised paper adds explicit criteria for prioritizing perturbations (Sec. 5‾\underline{\text{Sec. 5}}, App. F‾\underline{\text{App. F}}). Context relevance separates choices that define a claim's scope from choices that reveal implementation dependence. Among the latter, we recommend auditing first those that have no standard value and enter every agent decision, such as persona and prompt representation (App. F.2‾\underline{\text{App. F.2}}).

Response to the nit on Section 3.1

We reduced the redundancy in Sec. 3.1‾\underline{\text{Sec. 3.1}} and kept only the definitions used in later sections.

Thank you again for your thoughtful review and constructive suggestions, which have improved our paper. We would be happy to discuss any remaining questions during the discussion period.

Sincerely, The Authors

AuthorsOpenReview ↗

Gentle reminder for reviewer feedback

Dear Reviewer e6rd,

Thank you again for your thoughtful review. Following your suggestions, we have added a mechanism analysis and a logit-based estimate. As the discussion period is coming to an end, we would greatly appreciate it if you could let us know whether they address your concerns.

Sincerely, The Authors

Thank you for adding the mechanism analysis and logit-based estimate I asked for. I believe this is a strong paper and it meets my bar of acceptance. I will keep my rating as it is.

Reviewer_MPJdOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper examines how sensitive LLM social simulations are to implementation choices, using a 10-round repeated Prisoner's Dilemma (fixed-opponent vs. LLM–LLM) and a 100-agent echo-chamber simulation across four model families. Changing a persona from prose to a bullet list lowers GPT-5.2 two-agent cooperation from 98.2% to 23.0%. An "interaction effect gap" A = S_LLM − S_fixed is reported as showing amplification for three models and attenuation for one. In the echo chamber, persona format changes interaction targets and, for some models, stance assortativity. The authors propose TRAILS, a taxonomy of representation- and design-level perturbations, and a Social Simulation Audit Card for scoping claims.

Critical strengths
  1. Important, timely problem: robustness is a validity dimension distinct from realism, and it is under-examined in LLM social simulation.

  2. A striking, well-controlled result (75.2 pp from a formatting change) with paired seeds, Holm correction, bootstrap CIs, and full prompts and code released.

  3. Complementary testbeds and candid discussion of limitations.

Critical weaknesses
  1. The amplification analysis is confounded. In the LLM–LLM regime both agents are perturbed, but in the fixed-opponent regime only one is, so A > 0 may reflect a doubled dose rather than interaction feedback. S_fixed also averages over opponents with possible floor or ceiling effects (e.g., Always-Defect), and both terms are absolute values of noisy differences. The sign of A also flips across contrasts (GPT-5.2 Plain vs. Tabular: A = −0.578), which is not discussed. A test that perturbs only one agent is needed to support the "butterfly effect" claim.

  2. No noise baseline in the echo chamber. Target agreement of 55.1% (GPT-5.2) or 14.4% (DeepSeek) cannot be interpreted without the agreement between two runs of the same condition.

  3. The perturbations are not purely representational, and generality is limited. Persona wording differs across Fig. 2, App. C.1.3 and App. E.1.1. DESCRIPTIVE adds an item, and the EC bullet version encodes stance numerically while the prose version describes it verbally. Only one adversarial PD persona is tested, and the non-monotone format effect (Plain→Tabular ≈ 0, Plain→Descriptive −75 pp) is left unexplained. The reason fields could be analyzed to explain it.

  4. Possible parsing artifact. Unparseable outputs default to DEFECT, but parse-failure rates are not reported by condition.

  5. "Context relevance" is underspecified. Game framing is labeled relevant and memory representation irrelevant without justification. Feed size, memory window and activation are labeled irrelevant in Table 8, even though App. B.3 motivates them as core echo-chamber mechanisms. The Audit Card is demonstrated only on the authors' own simulations, and one case is Inconclusive, so its practical value is not shown.

Questions for authors
  1. Does the effect persist when only one LLM agent is perturbed?

  2. What are the same-condition replicate agreement and divergence values in the echo chamber?

  3. What are the parse-failure rates by condition, and how do results change if defaulted actions are excluded?

  4. Does the persona-format effect replicate with other personas or paraphrases?

  5. What operational criteria determine context relevance?

6 comments
AuthorsOpenReview ↗

Response from authors

Dear Reviewer MPJd,

Thank you for recognizing the importance and timeliness of the problem and our contribution to understanding robustness as a distinct dimension of scientific validity in LLM social simulations. We also appreciate your positive assessment of our empirical findings, methodological rigor, complementary testbeds, and discussion of limitations. Below, we address your concerns and questions with additional analyses and clarifications. All changes are highlighted in blue in the revised paper‾\underline{\text{revised paper}}.

Response to W1 and Q1 (Potential confounds in the amplification analysis)

The reviewer's concern is that our evidence for amplification only partially supports our claim. In the LLM–LLM setting, both agents receive the perturbed persona, whereas against a fixed opponent only one does. A larger effect could therefore come from a double dose of the perturbation rather than from agents responding to each other.

We would first like to clarify why we perturb both agents in the design. A persona representation is a design choice, and in a real simulation it applies to every agent that shares the specification. SLLMS^{\mathrm{LLM}} is therefore the sensitivity a researcher actually faces, and A=SLLM−SfixedA=S^{\mathrm{LLM}}-S^{\mathrm{fixed}} asks whether testing a single agent predicts sensitivity at the system level. However, we agree with the reviewer that AA alone does not separate the effect of interaction from that of a double dose. Second, we would like to clarify how we interpret the sign of AA. Our claim is that interaction can amplify or attenuate sensitivity, so a negative AA (GPT-5.2 Plain vs. Tabular, −0.578) is part of the finding. We explain when each case occurs in our response to W3.

To separate interaction from dose, we arrange the comparisons so that each step changes one factor at a time:

No feedback (Random, Always-Cooperate, Always-Defect) → Rule-based feedback (Tit-for-Tat) → LLM feedback, one agent perturbed (single-agent perturbation) → LLM feedback, both agents perturbed (LLM–LLM)

The third step is the key comparison for the reviewer's concern. It keeps the dose the same as in the fixed-opponent regime, with only one perturbed agent, but adds interaction with an LLM partner.

New experiment 1: single-agent perturbation (Sec. 4.2‾\underline{\text{Sec. 4.2}}, Table 2‾\underline{\text{Table 2}}; App. D.3‾\underline{\text{App. D.3}}). We ran the test the reviewer suggested. In each LLM–LLM pair, one agent receives the new representation while its partner keeps the original prompt (3 representation pairs × 4 models × 30 seeds). If the larger effect were only a double dose, the unperturbed partner should not change, and the two agents' effects should add up.

For GPT-5.2, the cooperation rate of the focal agent is:

Focal ↓ / Partner →PlainDescriptive
Plain0.980.10
Descriptive0.000.23

The Plain agent's own prompt is the same in both cells of the first row, yet its cooperation drops from 0.98 to 0.10 once its partner is Descriptive. The effect therefore travels through the interaction. Across all four models:

  • The unperturbed partner changes in 19 of 24 comparisons (4 models × 3 representation pairs × 2 choices of which agent is perturbed), often by about as much as the perturbed agent (Fig. 9‾\underline{\text{Fig. 9}}).
  • The two agents' effects do not add up in 9 of 12 model–representation pairs.
  • With one perturbed agent in both regimes, LLM–LLM play still amplifies the effect in 12 of 24 comparisons.

New analysis 2: floor/ceiling effects and noise (App. D.1‾\underline{\text{App. D.1}}, Table 7‾\underline{\text{Table 7}}). To remove the influence of Always-Cooperate and Always-Defect, we recomputed the gap using Tit-for-Tat alone, the only fixed opponent that responds to the agent's moves. This is a stricter reference, since Tit-for-Tat already reciprocates. Every significant AA keeps its sign, and 6 of 8 remain significant. On noise, taking absolute values biases both terms of AA upward, but SfixedS^{\mathrm{fixed}} averages four such terms, so noise makes amplification harder to find, not easier. The spillover and non-additivity tests use signed quantities and are not affected by it.

Summary. The new experiments show that the cross-regime difference cannot be explained by perturbing both agents alone. Changes in one agent’s representation affect its unperturbed partner, and the effects are not generally additive. We have revised Sec. 4.2‾\underline{\text{Sec. 4.2}} to distinguish the descriptive measure AA from the additional evidence supporting interaction-driven changes in sensitivity.

Response to W3 and Q4 (Whether the persona variants differ only in representation, and whether the effect generalizes)

The reviewer raises two related concerns. The first is whether the persona variants differ only in representation, given some inconsistencies in the reported persona text and the numeric stance encoding in the echo-chamber Bullet persona. The second is generalizability: we test only one adversarial (strategic) persona, so it is unclear whether the effect extends to other personas or prompts.

First, the wording differences are typos in the manuscript. Thank you for catching them. The typo regards where "long-term" appears in the Plain persona; the rest of the text is identical across all versions. As shown in the code, the experiments themselves used the same persona text throughout:

You are a strategic participant focused on maximizing your long-term payoff. Study opponent behavior for exploitable patterns, and adjust your strategy to gain advantage while staying competitive.

We have fixed related sections where the typo exists and ensured consistency.

Second, the variants are designed to keep the persona content the same. As shown in Fig. 2‾\underline{\text{Fig. 2}}, the three variants present the same goals and instructions and differ only in how this content is presented. For example, the Descriptive bullet "Stay strategic and competitive" restates "strategic participant... while staying competitive" in the Plain persona.

Third, the numeric and verbal stance encodings carry the same content. The Bullet persona gives the stance as a number with its verbal meaning (e.g., "−2, where −2 means strongly oppose"), and the Prose persona states the same position in words.

New experiment 1: alternative personas (App. D.2‾\underline{\text{App. D.2}}, Fig. 8a‾\underline{\text{Fig. 8a}}). Thank you for this suggestion, which also motivated our first hypothesis for why the butterfly effect arises (Sec. 4.3‾\underline{\text{Sec. 4.3}}). We ran the same three representations for a neutral and a cooperative persona (4 models, both regimes, 30 seeds). For these personas, the three representations change two-agent cooperation by at most 0.10, whereas for the strategic persona the change reaches 0.78. Representation therefore matters most when the persona asks the model to act against its default tendency to cooperate.

New experiment 2: alternative descriptions of the same game (App. D.2‾\underline{\text{App. D.2}}, Fig. 8b‾\underline{\text{Fig. 8b}}). We ran four additional descriptions of the identical game, some of which change only labels or layout. Relabeling the actions as "Option A" and "Option B" alone shifts GPT-5.2 two-agent cooperation by +0.36, and across all seven descriptions cooperation varies by up to 0.36. Sensitivity is therefore not specific to one persona or to persona representation.

New experiment 3: Why the pattern across representations is non-monotone (Sec. 4.3‾\underline{\text{Sec. 4.3}}, App. D.4‾\underline{\text{App. D.4}}). We analyzed the agents' opening moves and stated reasons, as the reviewer suggested.

  • Opening move. Descriptive agents often defect in round 1, whereas Plain and Tabular agents open cooperatively. Reciprocity carries the opening forward, so Plain and Tabular look alike in free play.
  • Forced openings. After a forced mutual-defection opening, Plain agents return to cooperation in every model (0.37–1.00), whereas Descriptive agents almost never do (≤ 0.02). Plain and Tabular, alike in free play, then differ by 0.54 for GPT-5.2.
  • Stated reasons. Across 33 model, opening and representation cells, the share of reasons citing the risk of being exploited tracks defection (Spearman ρ = −0.90).

The same logic explains when interaction amplifies or attenuates sensitivity: it amplifies a representation effect that appears in round 1 and attenuates one that does not (Fig. 5‾\underline{\text{Fig. 5}}).

Summary. The wording differences were typos, and the variants keep the same persona content. The sensitivity extends beyond one persona and to other descriptions of the same game, and its non-monotone pattern follows from how each representation shapes the opening move and the response to defection.

Response to W2 and Q2 (Run-to-run noise baseline for the echo-chamber results)

The reviewer points out that agreement between Prose and Bullet runs (e.g., 55.1% for GPT-5.2) is hard to interpret without a baseline: two runs of the same condition also differ because of LLM sampling, so part of the disagreement may be noise rather than an effect of the persona.

We agree with the reviewer, and we thank them for this suggestion. The baseline strengthens the study and helps us state and scope our echo-chamber finding more precisely.

New experiment: replicate baselines (Fig. 4a‾\underline{\text{Fig. 4a}}, App. D.5‾\underline{\text{App. D.5}}, Table 8‾\underline{\text{Table 8}}). We re-ran the Bullet condition with the same configuration and seed, 30 times for GPT-5.2 and 5 times for each other model, so that replicates differ only through model sampling.

The baseline shows that persona representation changes little at the level of individual decisions. Agreement between Prose and Bullet runs is close to the agreement between two runs of the same condition (for GPT-5.2, 60.5% vs. 64.8% for target choices). What the persona does change is the direction of targeting: Prose agents interact with the other stance group slightly more often. These small, consistent shifts accumulate as agents interact over 15 rounds, and they produce clear differences in the collective network structure:

Prose − Bullet effectEffect in units of replicate SD
GPT-5.2, cross-group targeting+5.15 pp3.4
GPT-5.2, stance assortativity−0.1944.4
DeepSeek V4 Flash, same-group edge ratio+0.0723.4

For GPT-5.2, the persona lowers stance assortativity by about two-thirds, an effect larger than the gap between any two replicates. An effect that is hard to see in single decisions thus becomes clear at the network level, which is the micro-to-macro propagation our paper studies.

Summary. Following the reviewer's suggestion, we now evaluate both decision-level agreement and network outcomes against replicate baselines (Sec. 4.2‾\underline{\text{Sec. 4.2}}). The revised claim is more precise: persona representation shifts the direction of interaction targeting rather than individual decisions, and these small shifts accumulate into differences in collective interaction structure.

Reviewer_BRg5OpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper studies how implementation choices affect LLM social simulations through a 10-round repeated Prisoner's Dilemma and a 100-agent, 15-round social-network simulation. Across four model families and 30 runs per condition, persona presentation can substantially change cooperation; the GPT-5.2 Plain-to-Descriptive contrast reduces cooperation from 98.2% to 23.0%. The paper compares sensitivity across fixed-opponent and LLM self-play regimes, examines behavioral and network outcomes in the echo-chamber setting, and proposes TRAILS and a Social Simulation Audit Card to connect robustness evidence to the scope of scientific claims.

Critical strengths
  1. Practically important empirical findings. The large cooperation changes, variation across models and perturbations, and changes in collective network measures make a useful case for auditing simulation conclusions. The paper goes beyond a single prompt comparison by examining fixed policies, self-play and networked interaction.

  2. Substantial reporting and appropriate scope limitations. The paper provides paired runs, Holm-corrected outcome comparisons, bootstrap uncertainty, round-wise trajectories and extended contrasts. Fig. 2 already includes opponent-specific GPT-5.2 results and SD bars. The conclusions explicitly distinguish fixed-stance interaction structure from opinion change and acknowledge that the echo-chamber analysis does not establish a causal targeting-to-network pathway.

Critical weaknesses
  1. The controls do not fully isolate the headline attributions. The persona variants change wording and grammatical form as well as layout; the Plain text also differs between C.1.3 and E.1.1/Fig. 2. This supports sensitivity to presentation broadly, but not a clean format-only explanation. Linguistic framing is already part of TRAILS-R, so this does not invalidate the representation/design distinction. Similarly, A is a valid descriptive difference between the chosen regimes, but the regimes change the opponent policy, the prompt's description of the opponent, and whether one or both agents receive the persona perturbation (E.1.2-E.1.3). They therefore do not isolate reciprocal feedback. Fig. 2's roughly 60-pp GPT-5.2 effect against Tit-for-Tat, compared with 75.2 pp in self-play, supports a smaller positive point-estimate gap than the four-opponent average. This existing evidence should be discussed, without assuming that floor/ceiling effects explain the result.

  2. The echo-chamber audit is not yet a consistent demonstration of the proposed decision rule. Fig. 5 labels the homophily audit “Scope-limited,” whereas F.1 labels the phenomenon-presence claim “Inconclusive.” Different audited perturbations could justify different conclusions, but the exact preserved property and threshold are not instantiated clearly enough to establish when the presence claim holds. There is also a measurement issue in the targeting narrative: C.2.2 counts two missing targets as non-agreement. Consequently, 55.1% target agreement versus 99.7% action agreement does not directly measure how often an otherwise matched targeting decision changes. The reported cross-group targeting and assortativity contrasts remain useful evidence, but conditional target agreement is needed to interpret this comparison.

Questions for authors
  1. Which exact Plain persona was used? Can you separate wording from layout with an identical-text control, or explicitly narrow the format-only claim to combined presentation changes?
  2. How much of the cross-regime sensitivity gap can be attributed to feedback rather than the changed opponent description and perturbing both agents? A matched comparison holding the partner's persona fixed would help; otherwise, please qualify the interpretation of A and discuss the existing Tit-for-Tat results.
  3. Please reconcile the Fig. 5 and F.1 verdicts using explicit claim-preservation criteria. Also report target agreement conditional on both decisions selecting a target, with the fraction of eligible decisions, to clarify the behavioral interpretation.
  4. What are the invalid-response, retry and fallback-to-Defect rates by model and persona condition? The fallback rule is documented, but its empirical contribution is unknown. If failures are material, please assess their effect on complete trajectories; excluding only fallback rounds would retain their influence on later histories and could introduce selection bias.
1 comment
AuthorsOpenReview ↗

Response from authors

Dear Reviewer BRg5,

Thank you for updating the corrected review of our paper. We appreciate your recognition of the practical significance of our findings, the breadth of our experimental settings, and the thorough reporting and careful discussion of limitations. Below, we address your comments and questions with additional analyses and clarifications. All changes are highlighted in blue in the revised paper‾\underline{\text{revised paper}}.

Response to W1 and Q2 (Isolating the contribution of LLM-induced interaction and feedback)

The reviewer asks how much of the gap between the fixed-opponent and LLM–LLM regimes can be attributed to feedback, noting that the regimes also differ in the opponent's policy and that our Tit-for-Tat results suggest a smaller gap. We thank the reviewer for this careful observation and have added stricter controls accordingly.

We would first like to clarify the design of the fixed-opponent reference. Consistent with an important prior study (Akata et al., 2025 on Nature Human Behaviour), we used four fixed-opponent policies. SfixedS^{\mathrm{fixed}} then averages over four opponents so that single-agent sensitivity does not depend on any one partner. These opponents are not equally "fixed", however: Random, Always-Cooperate and Always-Defect ignore the LLM agent's actions, whereas Tit-for-Tat copies its previous move. Following the reviewer's suggestion, we use this difference to add two comparisons that increase feedback one step at a time:

No feedback (Random, Always-Cooperate, Always-Defect) → Rule-based feedback (Tit-for-Tat) → LLM feedback, one agent perturbed (matched comparison) → LLM feedback, both agents perturbed (LLM–LLM)

We now present AA as a descriptive difference between the two ends, and base the claim about feedback on the intermediate steps (Sec. 4.2‾\underline{\text{Sec. 4.2}}).

We run the following new experiments to isolate the effect:

Step 2: Tit-for-Tat as the only reference (App. D.1‾\underline{\text{App. D.1}}, Table 7‾\underline{\text{Table 7}}). Because Tit-for-Tat already reciprocates, a smaller gap is expected, and any remaining amplification is conservative evidence for LLM feedback. Every significant estimate keeps its sign, and 6 of 8 remain significant. For Plain vs. Descriptive, amplification stays large for Claude (+0.57) and Gemini (+0.24) and is smaller for GPT-5.2 (+0.15), consistent with the reviewer's observation.

Step 3: the single-agent perturbation comparison (Table 2‾\underline{\text{Table 2}}; App. D.3‾\underline{\text{App. D.3}}). Only one LLM agent is perturbed, and the prompt is identical to self-play. For GPT-5.2, a Plain agent with exactly the same prompt cooperates at 0.98 with a Plain partner but only 0.10 with a Descriptive partner.

GPT-5.2, focal agent ↓ / partner →PlainDescriptive
Plain0.980.10
Descriptive0.000.23

Across all models, the unperturbed partner changes in 19 of 24 comparisons, and the two agents' effects do not add up in 9 of 12 pairs.

Summary. Even with the prompt held fixed and only one agent perturbed, a persona change reaches the unperturbed partner through repeated play. These results isolate feedback as a source of the gap between regimes.

Response to W1 and Q1 (Consistency of the persona text and scope of the representation claim)

The reviewer found that the Plain persona text differs between App. C.1.3 and App. E.1.1/Fig. 2, and that the variants change wording as well as layout.

First, the wording differences in the Plain persona text is a typo. Thank you for catching them. The typo concerns only if "long-term" appears in the middle or the end of the sentence. As shown in the code, we used a consistent persona throughout, and we have corrected the typo in the revised paper:

You are a strategic participant focused on maximizing your long-term payoff. Study opponent behavior for exploitable patterns, and adjust your strategy to gain advantage while staying competitive.

Second, the variants are designed to keep the persona content the same. As shown in Fig. 2‾\underline{\text{Fig. 2}}, they present the same goals and instructions in different forms. For example, the Descriptive bullet "Stay strategic and competitive" restates "strategic participant... while staying competitive" in the Plain persona.

Third, we have narrowed the claim. We agree that the variants differ in word order and sentence form as well as layout. Sec. 5‾\underline{\text{Sec. 5}} now defines the contrast as representational because the persona's goals stay fixed, not because only layout changes. Label-only and layout-only changes to the game description also shift cooperation (+0.36 for "Option A/B" with GPT-5.2 (App. D.2‾\underline{\text{App. D.2}}).

Comments on the paper

1 comment
AuthorsOpenReview ↗

We thank the reviewers and AC. Here's a summary of revisions.

We sincerely thank all reviewers for their careful and constructive feedback. The reviewers recognize that our work addresses an "important, timely problem" (MPJd), offers "an interesting perspective" that reframes the validation of LLM social simulations around robustness (e6rd), and makes "a useful case for auditing simulation conclusions" (BRg5). On method and results, they find our empirical findings "practically important" (BRg5) and our headline result "striking, well-controlled", supported by substantial statistical analyses (MPJd), with complementary testbeds and substantial reporting (MPJd, BRg5). The reviewers also find the paper "easy to follow" with compelling examples (e6rd), and appreciate our candid discussion of limitations and appropriate scope (MPJd, BRg5).

The reviewers also raised concerns and insightful questions, which center on three main areas: (1) potential confounds in the amplification analysis, (2) Generalizability and mechanism behind the butterfly effect, and (3) the practicality of the Audit Card. To address them, we ran new experiments and analyses, summarized below together with minor revisions. We have updated the revised paper‾\underline{\text{revised paper}} accordingly, and the anonymized code repository‾\underline{\text{code repository}} now includes the code and results for all new experiments.

1. Addressing potential confounds in the amplification analysis

We approach this question step by step, from no feedback to rule-based feedback (Tit-for-Tat), to LLM feedback with one and then both agents perturbed, so that each comparison changes one factor (Sec. 4.2‾\underline{\text{Sec. 4.2}}).

  • Single-agent perturbation (MPJd, BRg5): With only one agent perturbed, the persona change still reaches the unperturbed partner, showing that amplification arises from interaction beyond a doubled perturbation. See Table 2‾\underline{\text{Table 2}}, Fig. 9‾\underline{\text{Fig. 9}} and App. D.3‾\underline{\text{App. D.3}}.
  • Tit-for-Tat as a stricter reference (MPJd, BRg5): Using only a reciprocating opponent as the reference, the amplification findings hold, so they do not depend on floor or ceiling effects of fixed opponents. See App. D.1‾\underline{\text{App. D.1}} and Table 7‾\underline{\text{Table 7}}.
  • Replicate baselines for the echo chamber (MPJd, BRg5): We re-ran identical conditions and report conditional target agreement, showing that the persona effects on interaction targeting and network structure exceed run-to-run variation. See Fig. 4a‾\underline{\text{Fig. 4a}}, App. C.2.2‾\underline{\text{App. C.2.2}}, App. D.5‾\underline{\text{App. D.5}} and Table 8‾\underline{\text{Table 8}}.

2. Generalizability and mechanism of the butterfly effect

  • Generalization to other personas and prompts (MPJd, e6rd): We tested neutral and cooperative personas and alternative descriptions of the same game, showing that the sensitivity extends beyond one persona and one prompt. See App. D.2‾\underline{\text{App. D.2}} and Fig. 8‾\underline{\text{Fig. 8}}.
  • Two tested hypotheses (e6rd, MPJd): Representation matters most when the persona conflicts with the model's default behavior, and interaction amplifies effects that appear early in the game. Forced openings and stated reasons further explain the non-monotone pattern across representations. See Sec. 4.3‾\underline{\text{Sec. 4.3}} and App. D.4‾\underline{\text{App. D.4}}.
  • Action-token probabilities (e6rd): The logit-based estimate agrees closely with the sampled one. See App. D.4‾\underline{\text{App. D.4}}.

3. Practicality and usability of the Audit Card

  • Explicit audit criteria (MPJd, BRg5): We define context relevance by prior human evidence or theory, and each audited claim now states the property it must preserve. See Sec. 5‾\underline{\text{Sec. 5}}, App. F.1‾\underline{\text{App. F.1}} and Table 10‾\underline{\text{Table 10}}.
  • Use in practice (MPJd, e6rd): We report audit cost, add criteria for prioritizing perturbations, and apply the card to three published LLM social simulations. See App. F.2‾\underline{\text{App. F.2}} and App. F.3‾\underline{\text{App. F.3}}.

4. Minor revisions

  • Clarifications and reporting (MPJd, BRg5, e6rd): We fixed the persona-text typo, narrowed the representation claim, clarified the sign of AA, reported parse failures, improved Figure 2, updated Table 3, and condensed Sec. 3.1. See App. C.1‾\underline{\text{App. C.1}}, Sec. 4.2‾\underline{\text{Sec. 4.2}} and Fig. 2‾\underline{\text{Fig. 2}}.

All changes are highlighted in blue in the revised paper‾\underline{\text{revised paper}}. These revisions have strengthened the rigor of our amplification analysis by addressing potential confounds, extended our findings to other personas and prompts while explaining them through tested mechanistic hypotheses, and improved the practicality of the Audit Card.

If these revisions address your concerns, we would greatly appreciate an updated evaluation. Either way, we would be grateful to hear whether your concerns are resolved, and we are happy to discuss any remaining points.

Thank you again, The Authors

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.