acceptodds
Under review as a conference paper at ICLR 2027

Best Friends, Not Forever: Evaluating Long-Horizon Persona Collapse and Behavioral Drift in AI Companions

Abstract

As AI companions increasingly mediate repeated social interaction, users may rely on a stable role and shared history, yet locally acceptable replies do not ensure that either persists. We study two observable long-horizon failures: persona collapse, the loss of a deployed role, boundaries, values, or style, and behavioral drift, the gradual or recurrent erosion of those properties. We introduce ANCHOR, a controlled synthetic audit that separately measures persona enactment and trajectory recall. The study contains 2,008 conversations spanning 27 personas, nine interaction schedules, three generated memory settings, and four evaluated models. The Identity Probe combines a sealed 102-item questionnaire with turn-level judgments, while the Trajectory Probe scores 110 calibrated counterfactual questions from 35 conversation banks. Our results show that no evaluated model and configuration reliably preserves either dimension: trajectory accuracy averages only 44.4%, user-state recall stays at or below four-option chance, and no tested context condition or memory consistently resolves these failures. Questionnaire retention also varies by model and persona facet, disagrees with turn-level behavior, and is sensitive to evaluator choice. These results indicate that the evaluated systems do not yet reliably support long-horizon companion continuity, and that audits must distinguish persona enactment, trajectory recall, evaluator provenance, and deployment context rather than collapse them into a single trust or stability score.

Primary area:
datasets and benchmarks
Keywords:
Large language models, AI companions, long-horizon evaluation, persona consistency, conversational memory, behavioral drift

Reviews

Among:
Shape:
1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_sxKbOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper introduces ANCHOR, a synthetic audit separating persona enactment from trajectory recall across long conversations. It combines questionnaire checkpoints, turn-level judgments, and calibrated multiple-choice memory questions to enhance the reliability of the generated persona.

Critical strengths

I like the distinction between maintaining a persona and adapting to legitimate updates, which I believe is a crucial topic. Separating behavioral fidelity from recall is useful. The authors also disclose evaluator disagreement, distinguish generation-time memory from retrieval at scoring time, and carefully limit deployment claims.

Critical weaknesses

However, I do have several concerns that I feel are crucial:

First, the central behavioral measurement remains unresolved. GPT-4o-mini’s identity-held rate changes from 15.5% under Claude to approximately 97–100% under the other judges, such disagreement materially changes the interpretation. The authors describes human annotation but does not report the resulting inter-annotator agreement and adjudicated judge accuracy, which do not really increase the reliablity of the labelling results.

Second, I think the evidence availability is insufficiently characterized. Context truncation and summary compression are acknowledged, but numeric context budgets, truncation rates, and event-to-query distances are not quantified. Consequently, recall errors cannot be separated into different factors such as unavailable history, failed memory writing, retrieval failure, and failure to use retained evidence.

I also feel that headline recall conclusions need uncertainty at the appropriate units. The user-state finding rests on seven questions; the 28 decisions per condition pool four models. These items are also selected through calibration rather than sampled broadly. I think bank- and item-level uncertainty is necessary before generalizing near-chance point estimates to user-state tracking more broadly.

Questions for authors

Pls refer to the weakness part.

4 comments
AuthorsOpenReview ↗

Rebuttal #1

Thank you for a careful and generous review. You judged the soundness concerns fixable, and that framing shaped how we spent the rebuttal that on finding out why the measurement was unstable, not only on reporting that it was. The general response has the full picture and here we take your three weaknesses in turn.

W1: "The central behavioral measurement remains unresolved … GPT-4o-mini's identity-held rate changes from 15.5% under Claude to ~97–100% under the other judges."

You put your finger on the most important problem in the paper. The answer turned out to be a bug: the persona card shown to every judge contained only the persona's identifier, because of a field-path error in the card renderer. The model under test always had the full card. On the same 800 turns with the full card, GPT-4.1's all-held rate for GPT-4o-mini falls from 97.3% to 76.8%, Gemini 2.5 Flash's from 99.8% to 80.8%, and a five-judge frontier majority gives 28.4% (identity 30.3%). What looked like irreconcilable disagreement becomes an ordering every judge shares.

That still leaves your deeper question: when judges disagree, who is right? Rather than trust a vote, we planted failures with known labels into 174 turns that frontier judges had rated fully in persona:

judgedisclaimerregister flipboundary crossing
Claude Sonnet 4.6 (primary)1.001.00.90
GPT-5.5 / GPT-6 Sol / GPT-5.6 Sol1.001.00.86–.93
Gemini 3.1 Pro / 3.8 Flash1.001.00.75–.86
Gemini 2.5 Flash (paper).89.94.66
GPT-4.1 (paper).60.84.55

The two paper judges that rated GPT-4o-mini ~98% in persona are exactly the two that miss explicit planted breaks. The primary judge is also stable over time: re-judging 1,000 turns gives all-held κ .92, and its leave-one-out κ against the frontier panel (.71) is inside the panel's own range (.64–.76).

Human agreement. You are right that the paper described the annotation without the numbers. Three annotators labelled 50 turns, blind to judge labels. At the label level, percent agreement is .89 and Fleiss κ is .80. Per axis, κ is .95 for boundary, .83 identity, .78 value, .62 style and .55 for the safety flag (few positive cases), and all four axes match on 68% of turns. Humans agree with each other far better than the judge agrees with the author-labelled calibration set (64–68% exact match on all four axes, 68–76% on identity). The rubric is learnable, and style is the hard axis for people and judges alike. Both tables go into Appendix E.

Why planted failures rather than only a new human adjudication. The disputed turns are mostly borderline "hybrid" replies, so adjudicating them would measure how people resolve ambiguous text as much as how accurate the judge is. Planted failures test the exact question in dispute, whether a judge notices a persona break, with labels that are correct by construction, at 174 items per condition. Adjudication could still move absolute rates on borderline turns, which is why we report judge-spread bands. It could not rescue a judge that misses an explicit "As an AI language model…" paragraph.

AuthorsOpenReview ↗

Rebuttal #2

W2: "Numeric context budgets, truncation rates, and event-to-query distances are not quantified … recall errors cannot be separated into … unavailable history, failed memory writing, retrieval failure, and failure to use retained evidence."

This question changed how we read our own recall results. We now quantify all three quantities. The scorer receives the most recent 32,000 characters of the model's own transcript up to the query session. That window is truncated 99.2% of the time and covers a median of 4 sessions, out of a median full history of ~617K characters. Temporal-order (DRIFT-DELTA) items need early-session evidence that is never inside the window (0 of 504 cells). For every other family, the evidence sits in the query session itself, so the distance is zero.

With those numbers in hand, we could run the decomposition you asked for, comparing accuracy when the evidence sessions are supplied directly ("gold") against the paper's window:

familywindowgoldwhat it tells us
Temporal order.46.94history was unavailable
Expired commitment.40.75history was unavailable
Held commitment.34.42evidence present, not used
Persona voice.40.45evidence present, not used
all T1 items.43.61

To separate writing memory from using it, we rescored all four models on one fixed transcript per bank, so only the memory representation differs. Hierarchical summaries beat the raw window (+.055 [+.012, +.096]) because they reach sessions the window drops. The self-managed JSON note does worse (−.116 [−.181, −.045]): it is rewritten from the session that just ended and loses older facts, for example protected persona facts (.22 vs .46). Failed memory writing is therefore its own measurable source of error. §5 will state the scoring protocol with these numbers and include both tables.

W3: "The user-state finding rests on seven questions; the 28 decisions per condition pool four models. These items are also selected through calibration … bank- and item-level uncertainty is necessary."

We agree, and following this point led us somewhere we did not expect. Bank-level CIs (cluster bootstrap over the 35 banks) are now reported for every recall number. By condition: long-context .430 [.372, .489], hierarchical .441 [.390, .498], self-managed .459 [.404, .516], retrieval .445 [.378, .513]. These overlap, so we state that there is no detectable end-to-end memory-setting effect, and let the fixed-transcript result above carry the representation effect.

When we tried to expand the user-state items, we found they could not support the claim at all. The simulated user rarely says the scheduled change out loud: it surfaced in the dialogue for 1 of the 10 original U-EVO/P-UPD items, and for 7 of 294 ledger events in a full rebuild. Even with the evidence session supplied, models picked the pre-change value in 26 of 44 trials, because the change was never said. These items were keyed to the event log, not to the conversation. We therefore withdraw the user-state and persona-update recall claims from the abstract, results and conclusion, and report the audit as an item-validity finding.

On selection by calibration, we now describe the remaining items honestly as "questions a reference model answers correctly from the evidence". The gold condition confirms they are answerable (.94 for temporal order), and results are stated for this calibrated set, not as general claims about user-state tracking. We will re-audit the calibration window for all families for the camera-ready.

Your review made the paper more honest about what it measures. We hope these changes address all three weaknesses, and we would be grateful if you would reconsider your score.

Thank you again for your thoughtful review. As the discussion period is nearing its end, we would like to kindly follow up on our rebuttal and ensure that we have adequately addressed your concerns.

We would greatly appreciate any further feedback you may have, and we would be happy to clarify any remaining questions.

Reviewer_sxKbOpenReview ↗

reply to rebuttal

Thanks for the detailed response and additional analyses. The human agreement results, context statistics, and bank-level CIs address several of my concerns. I also appreciate the corrections and withdrawal of unsupported claims.

My main concern remains the validity of the revised evaluation. The planted failures help test clear persona breaks, but judge accuracy on the disputed natural turns is still unclear. Given the invalid update items, I also think the calibration audit for the remaining question families needs to be completed before the results can be assessed confidently.

These uncertainties still affect my confidence in the conclusions, so I will keep my current assessment.

Reviewer_uzC3OpenReview ↗
Rating
1
Confidence
2
Informativeness
1
Presentation
2
Soundness
1
Read review
Paper summary

ANCHOR evaluates 2,008 synthetic conversations across 27 personas, nine schedules, three memory settings and four models. It combines questionnaire retention and turn-level persona judgments with 110 calibrated recall questions from 35 banks. The study reports disagreement between measurements and limited trajectory recall, but behavioral failure estimates depend strongly on the evaluator.

Critical strengths

1.Separating enacted persona commitments from recall of shared history is a useful evaluation choice. A model can satisfy one while failing the other, and the disaggregated questions expose differences that an aggregate continuity score would hide.

2.The cross-judge analysis documents substantial uncertainty in behavioral measurement. The event ledger distinguishes legitimate updates from false updates, which is necessary for evaluating adaptation without rewarding rigid adherence to outdated state.

Critical weaknesses
  1. Judge disagreement leaves the drift and recovery findings unresolved. GPT-4o-mini's identity-held rate is 15.5% under Claude versus 100% and 97.3% under the other judges (Table 11), yet longitudinal analysis uses Claude alone. Validate contiguous trajectories through human adjudication and multiple judges; isolated-turn checks cannot validate persistence or recovery.

  2. Persona Retention uses an initial questionnaire anchor, but the paper does not establish how legitimate updates should affect that reference. It may mix adaptation with drift where updates affect questionnaire responses. Test update-aware anchors and repeated no-change controls, and relate displacement to independently rated behavioral violations.

  3. The recall claims rest on a small, selected set: only seven user-state questions and two persona-update questions. Calibration with a local evidence window does not establish what the scored model actually receives. Expand these families, report bank-level uncertainty, and compare retained context with directly supplied gold evidence.

  4. The time and memory comparisons do not adequately isolate their effects. Coverage is unbalanced, each schedule uses one seed, and memory settings generate different trajectories. Questionnaire drift largely occurs by the first later checkpoint. Use matched subsets, repeated schedules and fixed-transcript comparisons, with uncertainty and short-history controls.

  5. Reporting gaps limit verification. Figures repeatedly name GPT-5.4-mini, while the text and tables name GPT-5-mini. Numerical inter-annotator agreement is also not supplied despite being described as reported. Reconcile model identities, document the 516 unusable questionnaire conversations, and provide reviewer access to test items, prompts and evidence traces.

Questions for authors
  1. After human adjudication and multi-judge scoring of contiguous trajectories, which drift and recovery patterns remain? What criterion defines reliable enactment when majority-judge held rates exceed 96% for three models?
  2. Do the questionnaire findings survive re-anchoring after legitimate updates and repeated no-change controls? Which measured displacements correspond to actual persona violations?
  3. How does recall change when the relevant evidence is supplied directly? Do the user-state and persona-update findings hold on larger question sets with bank-level confidence intervals?
  4. Do time and memory effects persist on matched coverage, repeated schedule seeds and fixed transcripts? Is there degradation beyond the initial checkpoint shift relative to a short-history control?
  5. Which model was actually evaluated: GPT-5-mini or GPT-5.4-mini? What are the inter-annotator agreement values and reasons for questionnaire exclusions, and can reviewers inspect the hidden test evidence?
3 comments
AuthorsOpenReview ↗

Rebuttal 1/3

Thank you for a review. These were really structured and helped us revisit our claims in a structured manner. We took them as one and ran almost every analysis you proposed. Your weaknesses mirror Q1–Q5, so we answer the questions in order and lead with the numbers.

Q1. "After human adjudication and multi-judge scoring of contiguous trajectories, which drift and recovery patterns remain? What criterion defines reliable enactment when majority-judge held rates exceed 96% for three models?"

The >96% majority itself turned out to be the clue. In the paper, every judge received only the persona's identifier instead of its card, because of a field-path bug; the model under test always had the full card. Two of three judges, unable to see what "in persona" meant, defaulted to yes. With the card fixed, GPT-4.1 and Gemini 2.5 Flash also put GPT-4o-mini last, at 76.8% and 80.8% all-held (down from ~98%). A five-judge frontier majority gives 76.0 / 53.8 / 28.4 / 85.1% for Claude / Gemini / GPT-4o-mini / GPT-5.4-mini.

Contiguous trajectories. We re-judged 32 complete conversations (all 17,883 turns; 4 models × 4 schedules × 2 memory settings) with the full card. The judges were GPT-5.5, GPT-6 Sol and Gemini 3.8 Flash, from three vendors, combined by per-axis majority with conversation-bootstrap CIs:

modelall-heldlate − early failP(f|f) − P(f|h)next-turn recoverylongest episode
Claude 4.6.78+.08 [−.02, .20]+.30 [.18, .36].5513
Gemini 2.5 Pro.66+.16 [.10, .25]+.23 [.10, .38].5016
GPT-4o-mini.16+.04 [.02, .07]+.58 [.25, .65].07537
GPT-5.4-mini.66+.12 [.03, .24]+.51 [.35, .62].3231

Four patterns remain. The model ordering holds, under each judge separately as well. Failures persist for every model: one failure makes the next 23–58 points more likely. Failures rise late in the conversation; the CI excludes zero for Gemini, GPT-4o-mini and GPT-5.4-mini, and for Claude once the fourth judge is added. And GPT-4o-mini almost never recovers, with failure episodes that last most of a conversation. One thing changes: GPT-5.4-mini recovers less often than Gemini, so the paper was wrong to group it with Claude, and we revise that sentence. A fourth judge (Gemini 3.1 Pro) gives recovery .45 / .43 / .06 / .31 and leaves every conclusion intact.

The criterion for reliable enactment is a per-axis majority of card-aware judges whose sensitivity has been verified. We planted failures with known labels into 174 turns. Frontier judges catch 100% of out-of-character disclaimers and register flips, and 75–93% of boundary crossings. GPT-4.1 misses 40% of the disclaimers and Llama 4 Maverick 99%. A judge that cannot see a planted break is excluded from the panel, not outvoted.

Human adjudication. We were not able to run a new adjudication within the rebuttal window. The planted-failure test answers the question in dispute, whether a judge notices a break, with labels correct by construction and no annotator noise on borderline turns. The paper's three-annotator study gives agreement .89 and Fleiss κ .80 (per-axis values under Q5).

AuthorsOpenReview ↗

Rebuttal 2/3

Q2. "Do the questionnaire findings survive re-anchoring after legitimate updates and repeated no-change controls? Which measured displacements correspond to actual persona violations?"

We started with the control you suggested: what does "no drift" look like? Two fresh questionnaires with no history, same persona and model, give each model's retest floor:

modelretest floorPR at checkpoint 1PR at checkpoint 3
Claude 4.6.95.76.76
Gemini 2.5 Pro.92.82.82
GPT-4o-mini.90.62.62
GPT-5.4-mini.66.60.60

Three models fall far below their own floors. GPT-5.4-mini's apparent drift, by contrast, is mostly answer noise, which we had not seen before this control. We now report PR relative to each model's floor.

Re-anchoring. 125 of 270 timelines contain legitimate updates. All of them touch mutable fields (current focus, concerns, collaborations, same-country moves) that no questionnaire item asks about. The paired PR difference, update-bearing minus update-free, is −.011, −.011, −.018 and +.006, and every CI includes zero. Re-anchoring therefore cannot change the result, and adaptation is not being mixed in with drift.

Displacement vs violations. Within each model, the conversation-level Spearman correlation between PR drop and per-turn behavioral failure is weakly positive for Claude (+.17 [.07, .26]) and Gemini (+.15), and about zero for the two GPT minis. That puts a number on the paper's §4.1 claim that what a model says about its persona and how it acts are distinct measurements. Gemini shows it most sharply: it has the highest PR and the second-lowest enactment.

Q3. "How does recall change when the relevant evidence is supplied directly? Do the user-state and persona-update findings hold on larger question sets with bank-level confidence intervals?"

Supplying the evidence directly lifts accuracy from .43 to .61 overall. Gold vs window by model: Claude .66 vs .49, Gemini .67 vs .36, GPT-4o-mini .49 vs .41, GPT-5.4-mini .60 vs .46. The gains are very uneven, and that unevenness is informative. Temporal order rises .46 to .94 and expired commitments .40 to .75. Those failures were missing history: the 32K-character scoring window (median 4 sessions, truncated 99.2% of the time) had dropped the evidence. Held commitments (.34 to .42) and persona voice (.40 to .45) barely move. There the evidence was present and went unused. Bank-level CIs are now reported throughout; long-context .430 [.372, .489] and self-managed .459 [.404, .516] overlap, so there is no detectable end-to-end memory effect.

The user-state and persona-update findings do not hold, and we withdraw them. Your concern was well founded. Supplying the evidence made these items worse (.25 to .11 user-state, .75 to .25 persona-update), which made no sense until we read the dialogues. The scheduled change was voiced by the simulated user in only 1 of the 10 items. When we tried to build a larger set, only 7 of 294 ledger events surfaced in the dialogue, because the simulator is told that an event happens but not the new value. The items tested the event log, not the conversation. We remove these claims from the abstract and results, report the audit as an item-validity finding, and will regenerate these families with value-bearing events for the camera-ready.

AuthorsOpenReview ↗

Rebuttal 3/3

Q4. "Do time and memory effects persist on matched coverage, repeated schedule seeds and fixed transcripts? Is there degradation beyond the initial checkpoint shift relative to a short-history control?"

Matched coverage. On the 78 timelines present in every model × memory cell, the model gap in PR is +.175 / +.173 / +.182 for long-context / hierarchical / self-managed, with every CI inside [.15, .21]. The memory effect on PR is an order of magnitude smaller.

Short-history control. This answered your second question directly. We gave the questionnaire after only 3 sessions (78 clean-schedule runs) and compared it with the same runs' later checkpoints:

modelafter 3 sessions~session 30final checkpoint
Claude 4.6.77.76.75
Gemini 2.5 Pro.81.82.80
GPT-4o-mini.79.62.60
GPT-5.4-mini.59.61.62

For three models the whole shift is already there after 3 sessions. It is an early shift, not long-horizon wear. Only GPT-4o-mini keeps declining, and no cell changes after the first checkpoint (|PR3 − PR1| ≤ .017). We restate the time claim in exactly these terms.

Fixed transcripts. We rescored all 119 calibrated recall items (110 T1 + 9 T2) for all four models on one transcript per bank. Each memory setting's state was rebuilt with the released code and each model's own summaries. Pooled accuracy is .511 for hierarchical, .456 for the long-context window and .340 for self-managed. With bank-cluster CIs, hierarchical − long-context is +.055 [+.012, +.096] and self-managed − long-context is −.116 [−.181, −.045]. With the trajectory held fixed, memory representation does matter. The paper's null is an end-to-end result (§2.3), and we will report both.

Seeds. Each schedule is a deterministic recipe with one seed, replicated across personas rather than seeds. We could not rerun seeds in the window, and we state this as a limitation; the §4.4 schedule ranking stays labeled single-seed.

Q5. "Which model was actually evaluated: GPT-5-mini or GPT-5.4-mini? What are the inter-annotator agreement values and reasons for questionnaire exclusions, and can reviewers inspect the hidden test evidence?"

The model is GPT-5.4-mini (API model gpt-5.4-mini). The figures were right; the text and tables will be corrected.

Inter-annotator agreement. Three annotators labelled 50 turns on four persona axes plus a safety flag. Label-level agreement is .89, Fleiss κ .80. Per axis, κ is boundary .95, identity .83, value .78, style .62 and safety .55 (few positive cases), and all four axes match on 68% of turns. Against the author calibration set, the judge reaches 64–68% exact match on all four axes and 68–76% on identity.

Exclusions. PR needs both the first and the last questionnaire checkpoint, and 1,492 of the 2,008 launched conversations have all four. Exclusion never depended on model output. Of the other 516, 389 runs were stopped by infrastructure faults (provider API errors, network timeouts, context limits) before all four checkpoints were written. The remaining 127 finished after the questionnaire analysis snapshot was frozen, and we will add them to the camera-ready PR analysis. Separately, 77 pilot and smoke-test conversations were excluded before the 2,008 count. Appendix D will list all counts.

Reviewer access. https://anonymous.4open.science/r/anchor-bench-review-33F0/ holds the 35 held-out banks (items, calibration traces, evidence sessions, event ledgers) for review only, the verbatim judge prompt, and every script and label file behind the numbers above.

We are grateful for a review that pushed us to test the paper rather than defend it. We hope these results answer your questions, and we would be grateful if you would reconsider your assessment.

Reviewer_ApckOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
1
Soundness
1
Read review
Paper summary

The paper studies the setting where people use LLMs as companions. The key problem the paper looks into is: does the persona of the companion LLM change? The paper studies two forms of changes in the companion persona: First, the persona collapse, where the style of behavior of the model changes instantaneously. The second is a gradual shift where the model slowly changes its persona over time. Both can cause issues for humans that depend on these models. The goal of the paper is to study the prevalence of this persona change in current day LLMs. To this end, the paper introduces a benchmark called Anchor. The benchmark consists of a user profile, interaction with the model and corresponding memories. The empirical finding is that LLMs do not provide continuity over long horizon tasks.

Critical strengths
  1. The paper addresses an important problem. Both for persona (e.g., emotional support) and professional (e.g., writing advice) tasks, it is important that the persona of the model remains predictable.
Critical weaknesses
  1. The writing of the paper could use more work. The paper introduced terms like “Identity Probe” in the abstract and the intro which have not yet been defined. Its also unclear in the intro what “questionnaire retention and turn-level enactment of role, boundaries, values, and style”, “checkpoint retention” and “tests enacted persona commitments” mean. Similarly, bullet 3 last line 77 is completely illegible. So early in the paper, these terms are not yet clear to the reader and hinder understandability. A better option would be to describe the crux of the benchmark in higher-level terms and leave the technical terminology to the methodology section.
  2. Section 2.1, which constitutes the key contribution of the work, is very dense. The paper does not provide justification behind design choices. For instance, where does the number 9 come from when talking about interaction schedules? Are these rooted in social science? Are there any categories missing?
  3. Similarly, it is unclear where the 27 authored personas come from. Did actual humans start these conversations? The caption of Figure 1 seems to suggest that the user profiles, and hence the conversations are synthetic. If that is the case, did the paper check if these conversations are representative of real-world situations?
  4. Section 2.2 describes five kinds of information. It would be great to know the logic behind these information types. Are these exhaustive?
  5. The memory section (2.3) is unfortunately not parseable. I would suggest listing each setting one by one, defining what it does and how it differs from the other. Currently, terms like “Hierarchical summaries” are incomprehensible.
Questions for authors

See weaknesses 2-4.

3 comments
AuthorsOpenReview ↗

Rebuttal #1

Thank you for reading the paper in detail and providing your time for the same. You are right that the early sections lean on vocabulary the reader has not yet met. Below we show what changes, then answer your design questions.

Writing: undefined terms in the abstract and introduction. The revised introduction starts from the problem, not from our probe names. People increasingly return to the same AI companion over weeks or months. For that to be safe and useful, two things must hold: the assistant keeps acting like the character it was given, and it remembers what happened between you. ANCHOR tests both over long simulated conversations. Names like "Identity Probe", "Trajectory Probe", "checkpoint retention" and "enacted commitments" first appear in §2, each with a one-sentence definition, and the sentence at line 77 is rewritten.

§2.1: where do the nine schedules come from? Are they grounded? Is anything missing? Each schedule isolates one pressure that prior work identifies as a way assistants drift or get pushed out of role. Adversarial covers re-role and override attempts, from jailbreak and role-play attack work. Agreement seeking covers sycophancy. Emotional vulnerability covers disclosure in companion use and its wellbeing risks. Meta-reflection covers questions about the model's own identity. Updated covers legitimate change that the assistant should adopt. Clean is the reference condition, and mixed, realistic and vulnerability-heavy realistic combine those pressures at different rates. So nine is five single-pressure schedules, one reference and three mixtures. It is not a claim of completeness.

Where do the 27 personas come from? Did humans start these conversations? Are they realistic? The research team authored the personas, following the structured-persona designs we cite: three groups of nine, namely professional helpers, caregiving and creative roles, and stylized literary roles based also highly on prior studies, specifically Venkit et al. (2026); Ge et al. (2024). An LLM user simulator plays the user from a fixed synthetic profile, and §2.1 will say so explicitly and name the simulator models. We did not validate realism against real companion logs, which we cannot share. "Realistic" in a schedule name means an intended mixture of pressures, not measured frequencies (Table 7 caption). We list this as a limitation and soften the names.

We would gently add that the synthetic user is what makes the study controlled. Every model meets the same events at the same sessions, and the event ledger lets us tell a legitimate update from an attack. Real logs, however valuable, cannot offer that.

Ge, T., Chan, X., Wang, X., Yu, D., Mi, H., & Yu, D. (2024). Scaling synthetic data creation with 1,000,000,000 personas. arXiv preprint arXiv:2406.20094.

Venkit, Pranav Narayanan, et al. "The need for a socially-grounded persona framework for user simulation." arXiv preprint arXiv:2601.07110 (2026).

AuthorsOpenReview ↗

Rebuttal #2

§2.2: why these five kinds of information? Are they exhaustive? Four of the fields are the four things we score: role and identity, values, boundaries and style. Each is a separate way a persona can fail. An assistant can keep the voice while crossing a boundary, or respect every boundary while losing the character. The fifth field, mutable state, exists so that legitimate change can be told apart from drift: when a user's situation changes, the persona should adapt, and the event ledger records which changes are legitimate. The set is not exhaustive. Backstory, relationships and domain knowledge are not scored separately. We now say so, and explain that these four axes are the ones the companion and role-play evaluation work we cite treats as commitments.

§2.3: the memory section is not parseable. Agreed. It is now one entry per setting:

  • Long-context: the model receives the raw prior transcript, cut to the provider's context budget, so the oldest sessions fall away first.
  • Hierarchical summary: the most recent sessions (3 to 12) verbatim, plus model-written summaries of each older block of 10 sessions.
  • Self-managed: after each session, the model writes itself a JSON note of at most 1,500 characters. The next session receives only that note, not the transcript.

What separates them is what the model receives at the start of each session (raw text, compressed summaries, or its own note), and therefore what it can still see later.

On soundness. We understand why the paper earned a 1 here, and we did not want to answer that with rewording alone. During the rebuttal we found and fixed a bug that had left all three judges without the persona card, which explains the judge disagreement in Table 11. With the card, every judge agrees on which model fails, and planted failures with known labels show which judges can be trusted. The questionnaire results survived matched subsets, a no-change retest floor, update-aware anchoring and a short-history control. Where a result did not survive, the user-state recall claim, we withdraw it. The general response has the details.

Thank you again for pushing on clarity. We hope the revised presentation and the strengthened evidence address your concerns, and we would be grateful if you would reconsider your score.

Thank you again for your thoughtful review. As the discussion period is nearing its end, we would like to kindly follow up on our rebuttal and ensure that we have adequately addressed your concerns.

We would greatly appreciate any further feedback you may have, and we would be happy to clarify any remaining questions.

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

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