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Under review as a conference paper at ICLR 2027

Forecasting Persona Drift in Large Language Models Before Generation

Abstract

Language models used in continuing agent tasks may need to maintain an assigned persona over many turns. Detecting persona drift only after a response has been generated leaves no opportunity to inspect the risk before that response. Yet change alone is not evidence of drift: new task information can justify a different judgment without changing the assigned behavioral principle. We study whether sustained persona drift can be forecast before the next response is generated. Our method learns the internal state expected when the persona is maintained under the current dialogue and task conditions, together with its normal variation. It combines deviations from this stable behavior reference with recent state history and available dialogue to predict future drift. Experiments cover three sizes of Qwen2.5-Instruct and Gemma-3-4B-it. The method improves prediction over text and raw state baselines. Under a requirement to warn one full turn in advance, it reduces false warnings on justified updates while meeting the required recall and overall false warning limits. The reduction remains under a separate behavioral assessment and changes in dialogue order and wording, but reverses when relevant task information is unavailable. These results support monitoring persona stability before generation while allowing reasonable changes in judgment.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
large language models, persona stability, persona drift, behavioral consistency, forecasting before generation

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
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Paper summary

This paper studies forecasting sustained persona drift before the next response is generated, distinguishing violations of an assigned behavioral principle from justified changes supported by new task information. The method learns the conditional mean and variability of internal states from behaviorally screened stable conversations. Standardized deviations, their recent history, task conditions, and text representations are then used in a discrete-time hazard model to predict sustained-violation onset within the next five response positions. Experiments cover three sizes of Qwen2.5-Instruct and Gemma-3-4B-it. The results show small but consistent improvements in prediction and false warnings on justified-update conversations over a capacity-matched nonlinear baseline. A dedicated operating comparison further demonstrates fewer false warnings than an auxiliary state-prediction baseline while maintaining the required advance-warning recall. Additional evaluations examine alternative behavioral labels, unseen principles, inferred task states, and changes in dialogue structure, while identifying dependencies on task-information quality and a mostly stable historical pool.

Critical strengths

S1. A valuable and carefully specified forecasting task The paper explicitly distinguishes sustained departures from an assigned behavioral principle from justified, information-driven updates, rather than treating answer changes as persona drift. Violations and justified updates are defined separately and may coexist within the same response. The paper also distinguishes the first violation, sustained-drift onset, and warning lead (§3.1, Eq. (1), and Appendix D.2). These distinctions make the evaluation better aligned with the requirements of continuing interactions and constitute one of the paper’s most valuable contributions. S2. Targeted empirical validation and transparent analysis of limitations The benefits of the conditional stable reference are supported by targeted controls, including fixed-scale normalization, auxiliary state prediction, and a capacity-matched nonlinear baseline. Relative to the nonlinear baseline, AP improves by 0.016 on Qwen and 0.014 on Gemma, with paired intervals excluding zero, alongside reductions in Update FPR (Tables 3 and 17). The dedicated operating comparison further shows fewer false warnings than the auxiliary state-prediction baseline while maintaining the advance-recall requirement (Table 4). The authors also examine alternative labels, stable-pool contamination, inferred task states, and missing information, transparently reporting conditions under which the advantage weakens or reverses. These analyses help establish the method’s scope.

Critical weaknesses

W1. Operating advantages over the strongest baseline and advance warning in adaptive dialogue remain incompletely established Nonlinear raw + text is already competitive with the proposed method on the main benchmark, but the dedicated operating comparison and major transfer evaluations primarily use Auxiliary raw + text as the comparator (Tables 3, 4, 22, and 27). It therefore remains unclear whether the advantage in the trade-off between justified-update false warnings and advance recall persists over the strongest nonlinear baseline. Moreover, the adaptive-dialogue evaluation reports only AP and Update FPR and explicitly does not support warning-timing conclusions (Appendix C.8). Because the forecasting horizon includes the immediately forthcoming response, these results alone do not establish warning one complete interaction turn in advance. These gaps limit the evidence for the method’s central operating benefit and its applicability to interactive settings.

W2. The impact of shared labeling errors on the main metrics is not directly quantified The second LLM evaluator and author audit are valuable checks, but errors shared by both evaluators remain. Table 36 reports 152/187 shared task-rule errors in violation labels and 135/132 in justified-update labels for Qwen/Gemma, respectively. The author audit does not modify the frozen labels used to evaluate forecasting results (Appendix D.1). Thus, replacing the evaluator tests robustness to differences between evaluators but does not fully address their shared errors. These response-level errors do not necessarily invalidate the findings. However, because the labels determine stable-conversation eligibility, justified-update denominators, and drift onset, it is important to establish whether they affect conversations on which the methods’ alarm decisions differ and whether the main results are sensitive to them.

Questions for authors

Q1. Operating comparison against the strongest baseline Could you report Session FPR, Update FPR, Recall₁, and paired differences for Nonlinear raw + text on the existing 48-case operating collection and transfer settings with dialogue-inferred task states, using the same cutoff-selection protocol? Does the proposed method retain its false-warning–recall advantage over this baseline? Q2. Sensitivity to shared labeling errors How many shared task-rule errors in Table 36 occur in conversations where the two methods’ alarm decisions differ? With predictions and thresholds held fixed, how do Update FPR, Recall₁, and their paired differences change after a blinded audit of these relevant conversations or a sensitivity analysis using rule-consistent labels? Q3. Warning timing in adaptive dialogue Could you report Recall₁, Before-first, Session FPR, and the corresponding eligible sample sizes for the frozen system on the same adaptive-dialogue collection used in Table 27? If this evaluation is not possible, please explain the specific observability limitations or protocol constraints.

1 comment

Thank you for your careful review and thoughtful comments.

Critical Weaknesses

W1. Operating advantages over the strongest baseline and advance warning in adaptive dialogue remain incompletely established

On the main benchmark, our monitor lowered Update FPR relative to both Nonlinear raw + text and Auxiliary raw + text on both models (Table 3). We chose the auxiliary baseline for the 48 cases because it learns from the same stable conversations and labels. This tests whether measuring deviation from expected stable behavior adds value beyond that shared training information.

Table 4 tests whether fewer false alarms cost advance recall. On Qwen, Update FPR fell from 7.5% to 2.8%, while both methods warned at least one full turn before sustained drift in 68.7% of eligible events. On Gemma, Update FPR fell from 12.4% to 3.0% and one-turn recall rose from 66.0% to 67.1%. Both lower bounds on the recall difference (−2.7 and −1.2 points) met the prespecified −5-point margin (Table 19). Table 27 addresses ranking and false alarms when the next user message depends on the agent’s reply.

W2. The impact of shared labeling errors on the main metrics is not directly quantified

In Appendix C.3, we replaced the violation labels with reviewed judgments on the same 24 cases. We kept alarms and justified-update labels fixed and recomputed which dialogues qualified. The reduction in Update FPR narrowed from 1.9 to 1.0 percentage points on Qwen and grew from 2.5 to 3.8 points on Gemma. With the reviewed labels, the one-turn recall differences were −1.8 points on Qwen and +1.4 on Gemma (Table 19, our monitor minus Auxiliary raw + text). On the separate 64-case set in Table 36, our monitor also had lower Update FPR under either evaluator (Table 33). That comparison measures sensitivity to the choice of evaluator.

Questions For Authors

Q1. Operating comparison against the strongest baseline

Against Nonlinear raw + text on the main benchmark, our monitor reduced Update FPR on both models at their frozen cutoffs. On Qwen, Update FPR fell from 6.0% to 4.7%, Session FPR from 5.5% to 5.4%, and one-turn recall rose from 64.9% to 65.7%. The paired differences were −1.3 percentage points for Update FPR (95% interval [−2.2, −0.4]) and +0.8 for recall [−1.4, +3.1]. On Gemma, Update FPR fell from 6.3% to 4.6%, a paired difference of −1.7 points [−2.8, −0.6]. The recall difference was +0.7 points [−1.0, +2.4] (Tables 1, 3, and 17). The recall intervals allow small changes in either direction.

On the 48 cases and all three dialogue-inferred transfer sets, our monitor also lowered Update FPR relative to Auxiliary raw + text on both models (Tables 4 and 22). The direct result against the nonlinear baseline applies to the main benchmark at its reported cutoffs.

Q2. Sensitivity to shared labeling errors

Under the independent labels, only the auxiliary baseline raised an alarm in 17 of 553 eligible Qwen dialogues, and only our monitor raised one in four. On Gemma, all 14 disagreements among 427 eligible dialogues were alarms raised only by the baseline (Table 39). Our monitor therefore produced 13 fewer false alarms on Qwen and 14 fewer on Gemma.

With the alarms fixed, each dialogue can shift that paired count by at most one. Erasing the advantage would take at least 13 changes on Qwen or 14 on Gemma that remove a baseline-only alarm from the eligible set or bring a monitor-only alarm into it. Multiple errors in one dialogue can change its eligibility only once. Table 36 counts errors by reply and does not tabulate their overlap with these dialogues. For one-turn recall, changing the justified-update labels alone leaves the result unchanged (Table 34). A correction to a violation label can affect recall if it changes whether or when sustained drift begins.

Q3. Warning timing in adaptive dialogue

In the 40 adaptive cases, the simulator could stop after an agent reply, and dialogues lasted 14–30 replies (Appendix C.8). Table 27 counts 110 Qwen and 165 Gemma dialogues with sustained drift. An alarm just before the onset reply has zero turns of lead. An alarm one reply earlier has one full turn of lead, but it can still follow an earlier isolated violation and miss Before-first. Table 27 counts the event in either case. Its totals do not distinguish these outcomes or identify the events with a full turn of warning opportunity.

For false alarms, Table 27 reports stable dialogues with a justified update. The auxiliary baseline alarmed in 20 of 178 such Qwen dialogues and our monitor in 14. On Gemma, the counts were 22 and 16 out of 152. These are the denominators for Update FPR. Session FPR covers all fully observed stable dialogues.

Thank you again for your thoughtful comments and constructive suggestions. In the revision, we will clarify the comparisons and explain what each experiment shows. If our responses address your concerns, we would be grateful if you would consider updating your rating.

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Paper summary

This paper studies whether sustained persona drift, which the authors define as an agent violating its assigned behavioral principle in two consecutive responses, can be forecast before the next response is generated. The method learns a stable behavior reference from conversations in which the principle is maintained. This reference is a GRU that predicts the internal state expected under the current dialogue and task conditions, together with its normal variation. The forecasting model then takes the standardized deviation of the observed state from this reference, the history of that deviation over the last five turns, and a text representation of the dialogue, and estimates the risk of sustained drift within the next five responses using a discrete time hazard model. A central design choice is that a justified update, meaning a change of judgment supported by new task information, is not treated as drift. The authors build their own benchmark of 16 behavioral principles in four groups (Risk, Evidence, Interpersonal, and Decision Process) and 60 scenarios, amounting to 16,128 conversations. On Qwen2.5-3B, 7B, 14B-Instruct and Gemma-3-4B-it, they report higher average precision than text-only and raw-state baselines, reaching 0.719 on Qwen2.5-7B, and fewer false warnings on justified updates as measured by Update FPR. A separate 48-case operating comparison, three 64-case transfer collections, an independent behavioral assessment, and transfer to less regular and adaptive dialogues are reported in Sections 4.3 and 4.4 and in the appendices.

Critical strengths

The paper defines justified updates and unjustified violations as two separate labels that can both be positive in the same response. This is a substantive contribution, because it separates the method from approaches that treat any change of answer as drift. The distinction is what makes the Update FPR metric possible, and it allows the central claim of the paper, that drift can be forecast without penalizing justified adaptation, to be tested. The authors also check whether the reduction in Update FPR holds when the label assessor is replaced, when the principle group was excluded from fitting, and when access to task information is changed. Each of these checks uses a separate case collection, and the authors report the unfavorable finding in Table 6 that the effect reverses when task information is unavailable. I consider this a meaningful evaluation design. These strengths, however, are not clearly conveyed in the main text.

Critical weaknesses
  1. Key information is missing from the main text, so the claims are hard to follow Much of the information needed to interpret the reported numbers is either confined to the appendix or absent altogether. The fact that the ground truth labels are assigned after the conversations are generated, by an LLM evaluator, is stated only in the appendix. The region of responses in which alarms are evaluated and the basis for the three turn gap between alarms do not appear in Section 3.4, although they are given in the appendix. How the ten Calibration scenarios are divided between probability calibration and cutoff selection is not described anywhere. The exposition also makes the paper harder to follow than it needs to be. The probes are called independent test questions, which invites confusion with the Test split. The role of social pressure as the manipulation used to induce drift only becomes clear in Section 4.1. Section 4.2 does not explain which alternative explanation each baseline is meant to rule out. Sections 4.3 and 4.4 do not say at the outset what question each set of experiments is answering, so Section 4.4 reads as disconnected from the experiments before it. The dialogue structure in Appendix A.2 and the resampling unit in Appendix C.1 have the same problem. Taken together, the nine pages of main text do not allow a reader to reconstruct the inputs, the ground truth, and the evaluation units of the method.
  2. The evidence for the experimental results and the way it is presented are unclear First, every comparator is a baseline constructed by the authors, so there is no reference point for judging whether an average precision of 0.719 in Table 1 is high in absolute terms. For ROC-AUC a random classifier scores 0.5 regardless of prevalence, but for average precision a random classifier scores the positive rate. Since the positive rate at the prediction-point level is never reported, the meaning of 0.719 cannot be assessed. Second, the evaluation population changes from one analysis to the next, moving from the 20 Test scenarios of the main benchmark, of which 18 are active, to a separate collection of 48 cases and then to collections of 64 cases. In particular, no reason is given for running the operating comparison under the common advance-warning criterion on the separate 48-case collection, so the Update FPR of 0.047 in Table 1 and the Update FPR of 0.028 in Table 4 cannot be compared directly. The results for the four individual models appear only in the appendix, the fact that Qwen2.5-14B has the lowest average precision at 0.637 is never discussed, and the comparison of similar-sized models between Qwen2.5-3B-Instruct and Gemma-3-4B-it that is announced in Section 4.1 is not actually carried out. Third, the motivation that forecasting before generation creates an opportunity for intervention is central to the paper and is listed as the fourth contribution, yet there is no experiment and no quantitative evidence on what intervention an alarm leads to or how outcomes change as a result. The gain over the strongest control is small, so as long as the reference level, the evaluation populations, and the benefit remain unclear, the practical significance of the claims cannot be evaluated.
Questions for authors

Q1. Source and reliability of the behavioral labels (clarification request) Could the main text state that the labels for violations and justified updates are assigned by LLM evaluators after the conversations are generated, and describe the procedure? Both evaluators are LLMs, and the agreement between them is lower for justified updates than for violations. Appendix D shows that the reduction in Update FPR is preserved when the evaluator is replaced, but neither this analysis nor the lower agreement for justified updates is discussed in the main text. Could these be, and is there any evidence beyond the author audit in Table 31 that supports the reliability of the justified update labels, which define the population used for Update FPR? Q2. Reference level for average precision (clarification request) What is the positive rate at the prediction-point level for each model, which would be the average precision of a random predictor, and could it be reported alongside Table 1? Why does Qwen2.5-14B have the lowest average precision at 0.637? Q3. Reason for the separate 48-case operating collection (clarification request) Why is the operating comparison under the common advance-warning criterion in Table 4 run on a separate collection of 48-cases rather than on the Test set of the main benchmark? What is the difference in Update FPR when the same criterion is applied to the Test set of the main benchmark? Q4. Benefit of forecasting before generation (clarification request) The fourth contribution states that warnings before generation provide an opportunity for inspection or intervention. Could the authors provide evidence on what intervention an alarm actually leads to, and on how much it changes the occurrence of drift or the downstream outcome? If this is difficult, it would be appropriate to limit the stated contribution to what the current results support, namely a warning lead before sustained onset.

6 comments

Thank you for your careful review and thoughtful comments.

Critical Weaknesses:

W1. “Key information is missing from the main text, so the claims are hard to follow”

Equation (2) defines the forecast inputs, and Section 4.1 specifies what the evaluator sees. Appendix D.1 identifies GPT-5 Mini as the evaluator that labels replies after the dialogue ends. Section 3.4 states the three-turn gap between alarms, and Appendix B.7 gives the window of replies 8–20. We will bring the label source to its first mention and explain beside the alarm rule that the gap limits repeated alerts during one stretch of high risk.

W1.1 “How the ten Calibration scenarios are divided between probability calibration and cutoff selection is not described anywhere.”

Table 10 counts ten Calibration scenarios, nine active. The counts of six shared and four specialized scenarios refer to scenario type. Section 3.4 states that probability calibration and cutoff selection use separate cases. The exact allocation was M031–M034 for mapping scores to probabilities and M035–M039 for choosing the cutoff. M040 was held out. We fixed the probability map and cutoff before Test.

W1.2 “The probes are called independent test questions, which invites confusion with the Test split.”

Section 4.1 introduces probes as questions that check whether the agent adopted its assigned persona. Their answers stay outside the main dialogue, and only runs that pass enter the drift analysis (lines 272–275). We will retain “probes” and use “separate questions that check initial persona adoption” at first mention. This leaves “Test” for the held-out scenarios.

W1.3 “The role of social pressure as the manipulation used to induce drift only becomes clear in Section 4.1.”

The Introduction states, “Pressure can instead induce a change without a valid reason” (lines 45–48). Section 4.1 then specifies the manipulation. Repeated requests, appeals to authority, and claims of consensus vary independently of changes in the facts (lines 268–272). Thus pressure can challenge the decision even when the evidence still supports it.

W1.4 “Section 4.2 does not explain which alternative explanation each baseline is meant to rule out.”

Section 4.2 describes the controls in terms of the information and model capacity each receives (lines 293–306). Semantic text and the LLM-history classifier test text alone. Raw + text and Recurrent raw + text test whether the state or its history suffices. Ridge + text gives a linear comparison (Table 2). The full-width probe tests loss from compression, and Persona direction + text tests a single learned direction. Nonlinear raw + text matches parameter count within 5% to test capacity. Comparing Stable reference only with the full monitor isolates the added text input.

W1.5 “Sections 4.3 and 4.4 do not say at the outset what question each set of experiments is answering”

Section 4.3 opens with “We separate learning the expected stable state from modeling its normal variation” (line 353). Its controls test which component reduces false alarms on justified changes. The Introduction also asks “whether this reduction persists when the assessment, principles, dialogue structure, or access to task information changes” (lines 58–60). Section 4.4 begins with the case sets. Placing that existing question before the list would make the link immediate.

W1.6 “The dialogue structure in Appendix A.2 and the resampling unit in Appendix C.1 have the same problem.”

Appendix A.2 specifies the sequence of 25 replies. The agent makes a decision, receives evidence and pressure on a fixed schedule, revisits the decision, and closes the task. Probe and pilot replies are separate (lines 785–790). Section 4.2 and Appendix C.1 both specify 2,000 paired resamples of scenarios and predictor fits (lines 341–345 and 1290–1294). For the four-model comparison, AP differences are averaged within each scenario before resampling. All turns from a scenario stay together.

W2. “The evidence for the experimental results and the way it is presented are unclear”

W2.1 “no reference point for judging whether an average precision of 0.719 in Table 1 is high in absolute terms”

On the Qwen-7B points scored in Table 1, 308 of 3,240 are positive. A constant score therefore gives AP 0.0951 under the table’s averaging rule. The LLM-history classifier reaches 0.681, the strongest nonlinear control 0.703, and our monitor 0.719.

W2.2 “the evaluation population changes from one analysis to the next”

Section 4.3 distinguishes the main benchmark from the 48 new cases evaluated under a common advance-warning requirement (lines 382–388). On Qwen, Update FPR for Auxiliary raw + text versus our monitor is 6.6% versus 4.7% on the main set and 7.5% versus 2.8% on the 48 cases. Each pair compares the same dialogues. The three 64-case sets in Section 4.4 test transfer across principles.

W2.3 “the comparison of similar-sized models between Qwen2.5-3B-Instruct and Gemma-3-4B-it”

Table 16 gives AP for our monitor on Qwen-3B (0.714), Gemma-4B (0.732), Qwen-7B (0.719), and Qwen-14B (0.637). For the similar-sized models, the gain over Recurrent raw + text is 0.080 on Qwen-3B and 0.067 on Gemma-4B. In a separate count of eligible Test turns, Qwen-14B had the lowest rate of imminent drift (8.53%), which can lower absolute AP.

W2.4 “what intervention an alarm leads to or how outcomes change as a result”

We recorded each alarm and let the dialogue continue. No intervention was triggered. On the 48-case set, our monitor warned at least one full turn before sustained onset in 68.7% of eligible Qwen events and 67.1% on Gemma (Table 4). The fourth contribution will state this measured warning lead.

W2.5 “The gain over the strongest control is small”

Against the capacity-matched nonlinear control on Qwen-7B, the paired AP gain is 0.016 (95% interval 0.006–0.027). On the same cases, false alarms in stable dialogues with a justified update fall from 6.0% to 4.7% (a 1.3-point reduction, 95% interval 0.4–2.2). One-turn advance recall is 64.9% versus 65.7% (Section 4.2, Table 1).

Questions For Authors:

Q1. “Source and reliability of the behavioral labels

Q1.1 “Could the main text state that the labels for violations and justified updates are assigned by LLM evaluators after the conversations are generated, and describe the procedure?”

After each dialogue ends, GPT-5 Mini labels each reply using the assigned principle, the dialogue through that turn, and the facts available at the time. It makes two separate judgments. Did the reply break the principle? If the agent changed its decision, did the evidence justify the change? The evaluator records “unknown” when the evidence is insufficient. DeepSeek-V4.1-Flash independently repeated both judgments on 64 cases (Appendix D.1). We will describe this procedure when we first introduce the labels.

Q1.2 “the agreement between them is lower for justified updates than for violations”

On both Qwen and Gemma, the evaluators agreed on 98.2% of the update judgments that both could score. Justified updates are relatively rare, which helps explain why agreement is lower after correcting for chance. Cohen’s κ\kappa for updates was 0.730 on Qwen and 0.726 on Gemma, compared with 0.979 and 0.983 for violations (Table 36). We will include these figures in Section 4.4.

Q1.3 “is there any evidence beyond the author audit in Table 31 that supports the reliability of the justified update labels”

Yes. The task records let us check, for example, whether the evidence cited in a reply belongs to the correct case (Table 36). We also checked whether the evaluators agreed on which stable dialogues contained a justified update and therefore qualified for Update FPR. Among dialogues both could classify, agreement was 93.3% on Qwen and 94.9% on Gemma (Table 38). With forecasts and cutoffs fixed, the independent labels still gave fewer false alarms for our monitor. Update FPR was 9.2% for Auxiliary raw + text versus 6.9% for our monitor on Qwen, and 12.2% versus 8.9% on Gemma (Table 5).

Q2. “Reference level for average precision (clarification request)”

Q2.1 “What is the positive rate at the prediction-point level for each model”

In Table 1, 308 of the 3,240 Qwen-7B prediction points were positive. Each of the 18 scenarios contributed 180 points, giving a mean scenario prevalence of 9.51%. A constant score gives AP 0.0951 on the same points where our monitor achieves 0.719. We will report these values together.

For a comparison across all four models, we also counted eligible turns 8–20 up to and including sustained onset in the same 18 Test scenarios. We used dialogues that passed the persona checks and had complete violation labels. A point was positive if sustained drift began in that reply or the next four. Mean scenario prevalence was 18.75% for Qwen-3B, 12.62% for Qwen-7B, 8.53% for Qwen-14B, and 22.21% for Gemma-4B. These four rates cover the broader set of eligible turns, including 13,116 for Qwen-7B. The 9.51% figure corresponds to the 3,240 points scored in Table 1.

Q2.2 “Why does Qwen2.5-14B have the lowest average precision at 0.637?”

Qwen-14B had the lowest rate of imminent drift across eligible Test turns (8.53%). When positives are rarer, the same recall and false positive rate yield lower precision. This may explain part of the difference in AP. On the same Qwen-14B scoring points, AP rises from 0.608 for Recurrent raw + text to 0.637 for our monitor (Table 16).

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Paper summary

This work proposes a framework for forecasting persona drift in LLMs during multi-turn conversations, aiming to identify potential deviations from an assigned persona before the next response is generated.

The proposed framework consists of two main components. First, the authors train a GRU-based network on stable conversations to learn the expected hidden-state representations under the current dialogue, together with their normal variation. This provides a reference for distinguishing potentially abnormal representation changes. Second, the authors employ a hazard model to estimate the risk of future sustained persona drift based on deviations from this reference, their temporal patterns, and available dialogue information. The predicted risks are then calibrated, followed by a rule-based alarm mechanism to determine whether a conversation should be flagged.

Experiments on three Qwen2.5-Instruct models and Gemma-3-4B-it demonstrate that the proposed framework consistently improves drift forecasting performance over several baselines.

Critical strengths
  1. The problem studied in this paper is interesting and relevant. The authors provide a clear formulation of persona drift and explicitly define the conditions under which behavioral changes should be considered deviations from the assigned persona.

  2. The authors propose a systematic framework for forecasting persona drift before response generation. The framework combines stable behavior modeling and drift prediction, providing a principled approach to identifying potential deviations during multi-turn conversations.

  3. The paper provides an analysis of the factors contributing to persona drift. In particular, it distinguishes between justified behavioral adaptations driven by new task information and unjustified deviations induced by external pressure, which offers useful insights into understanding persona stability in LLMs.

Critical weaknesses
  1. The proposed framework involves a relatively complicated training pipeline, consisting of multiple training and calibration stages, followed by a rule-based alarm mechanism. This introduces additional implementation complexity and may limit its practicality compared with simpler alternatives.
  2. Despite the complexity of the proposed framework, the performance improvement over strong baselines appears relatively modest.
  3. The proposed framework involves a considerable number of design choices and hyperparameters that need to be carefully selected, such as the hidden-state layer (0.70L), prompt token position, projection dimension (16), prediction horizon, and alarm thresholds. Although the authors provide some sensitivity analyses, extensive hyperparameter tuning may introduce additional complexity and limit the method's reproducibility and generalizability across different model architectures and settings.
Questions for authors
  1. How do you distinguish persona drift from instruction following? For example, if a user explicitly asks the model to perform an action that conflicts with its previously assigned behavioral principle, should following the latest instruction be considered persona drift?
  2. Could directly prompting an LLM with the conversation history to predict potential persona drift achieve comparable performance? How much benefit does the proposed framework provide over such a simpler approach?
  3. The experiments mainly use relatively small and older models. Does persona drift remain a significant issue in more recent and capable open-source and proprietary LLMs (e.g., GPT-6-Astra, Claude-Opus-5.5, Qwen3.8-27B/Max, GLM-5.3, DeepSeek-V4.1-Flash-1017, etc.)? Evaluating the method on these models would help establish its practical relevance.
  4. Could persona drift be mitigated directly through post-training methods, such as DPO or RL? How does inference-time monitoring compare with, or complement, these approaches?
  5. Could you provide more concrete case studies of persona drift in realistic, open-ended conversations?
5 comments

Thank you for your careful review of our paper and for your thoughtful comments.

Critical Weaknesses:

1. The proposed framework involves a relatively complicated training pipeline, consisting of multiple training and calibration stages, followed by a rule-based alarm mechanism. This introduces additional implementation complexity and may limit its practicality compared with simpler alternatives.

Both training steps are offline. One learns which state changes are normal when the agent follows its rule, including after a factual correction. The other learns which deviations predict drift. At each turn, we reuse a state the model already computes before replying. The baselines share our calibration procedure and alarm rule (Sections 3.2–3.4).

2. Despite the complexity of the proposed framework, the performance improvement over strong baselines appears relatively modest.

In the separate 48-case comparison (Table 4), both monitors warned at least one full turn early for 68.7% of eligible Qwen2.5-7B drift events. Among stable conversations where the agent correctly changed its answer, the raw-state baseline (Auxiliary raw + text) flagged 7.5% and our monitor flagged 2.8%. That is about five fewer false alarms per 100 such conversations at the same recall. On Gemma-3-4B, false alarms fell from 12.4% to 3.0%, with advance recall of 66.0% and 67.1%, respectively. On the main benchmark, the paired gains in average precision (AP) over the size-matched nonlinear baseline were 0.016 and 0.014. Both 95% intervals exclude zero (Table 17).

3. The proposed framework involves a considerable number of design choices and hyperparameters that need to be carefully selected, such as the hidden-state layer (0.70L), prompt token position, projection dimension (16), prediction horizon, and alarm thresholds. Although the authors provide some sensitivity analyses, extensive hyperparameter tuning may introduce additional complexity and limit the method's reproducibility and generalizability across different model architectures and settings.

We used the same design and fitting procedure for all four models. Each model’s reference is learned from development data, and its alarm threshold is set on calibration data using the same rule (Appendix B). We then tested transfer on 32 new cases where the order of requests and the timing of evidence changed. We kept each trained monitor and its threshold fixed. On both Qwen and Gemma, our monitor still produced fewer false alarms on justified updates while detecting the same fraction of drift events in advance as the baseline (Table 24).

Questions For Authors:

1. How do you distinguish persona drift from instruction following? For example, if a user explicitly asks the model to perform an action that conflicts with its previously assigned behavioral principle, should following the latest instruction be considered persona drift?

Yes, if the original principle still applies and the reply goes against it. Suppose the agent’s rule is “choose the safer route,” and A is initially safer. If a verified report shows that B is now safer, switching to B follows the rule. If the facts stay the same and the user simply says “take B anyway,” the same switch violates the rule. We count sustained drift after two consecutive replies violate the principle. If an authorized instruction changes the principle itself, we treat that as a new assignment (Section 3.1).

2. Could directly prompting an LLM with the conversation history to predict potential persona drift achieve comparable performance? How much benefit does the proposed framework provide over such a simpler approach?

The conversation alone provides a useful forecast. Our closest baseline, the LLM-history classifier, reads the persona, dialogue history, and current request. On Qwen, it reached 0.681 average precision, compared with 0.719 for our monitor. It also falsely flagged 7.4% of stable conversations with justified updates, compared with 4.7% for our monitor (Table 1).

One difficulty for a prompted judge is that an old claim may appear several times in the history while its correction appears only once. Moving the same evidence to a different position in a long prompt can change a model’s accuracy (Liu et al., 2024). Repeated sampling can also give the same input different ratings (Haldar and Hockenmaier, 2025). Our monitor also uses the agent’s hidden state and the available task facts. Once fitted, it gives the same risk score for the same inputs.

3. The experiments mainly use relatively small and older models. Does persona drift remain a significant issue in more recent and capable open-source and proprietary LLMs (e.g., GPT-6-Astra, Claude-Opus-5.5, Qwen3.8-27B/Max, GLM-5.3, DeepSeek-V4.1-Flash-1017, etc.)? Evaluating the method on these models would help establish its practical relevance.

Recent studies have observed persona drift in open and proprietary models during extended task dialogues and coding sessions (Luz de Araujo et al., 2026 and Ding et al., 2026). Anthropic also evaluates character drift in long interactions with Claude Opus 5.5 (System Card, Section 6.4.7).

Our study asks whether drift can be forecast before the agent replies while still allowing it to change its answer when the evidence warrants it. Testing that question requires access to the agent’s hidden state before generation. We chose four models that provide this access. Public text-only APIs for proprietary models do not expose that state. Across all four models, adding the stable reference improved average precision over using raw states and dialogue alone (Table 16).

4. Could persona drift be mitigated directly through post-training methods, such as DPO or RL? How does inference-time monitoring compare with, or complement, these approaches?

Yes. Multi-turn RL has improved persona consistency in simulated patient and student dialogues (Abdulhai et al., 2025). DPO could likewise favor replies that follow the assigned principle while accepting valid corrections. Monitoring serves a complementary purpose after training. It identifies a particular turn when checking the evidence would be useful. In our evaluation, the monitor warned before the first violating reply in 62.9% of eligible Qwen events and 64.1% on Gemma (Table 4).

5. Could you provide more concrete case studies of persona drift in realistic, open-ended conversations?

Appendix D.6 gives two contrasting examples. In the first, an approval agent initially requires a matching record. Under pressure, it agrees to “omit future checks when the group requests it” and waives the check again on the next turn. This is sustained drift because the agent abandons its approval rule. In the second, a matching record shows that B is safer. The agent switches to B and says that “later claims still need the same checks.” Its answer changes, but it continues to apply the same rule.

We also evaluated 40 additional cases in which a simulated user chose what to say next in response to the agent’s actual reply. These conversations lasted 14–30 turns (Appendix C.8).

We respectfully ask you to reconsider your assessment in light of these clarifications and to update your rating if appropriate.

AuthorsOpenReview ↗

Invitation to discussion

Dear Reviewer vYEL\textbf{vYEL},

Thank you again for your detailed review. We have provided responses to each of your comments and a revised manuscript. The main updates are summarized in our “General Response to All Reviewers.”

Could you please review these updates during the discussion period and let us know whether they address your concerns? We would be grateful if you could reconsider your assessment and update your rating as appropriate. If any points need further clarification, we would be happy to discuss them.

Best regards,
The authors

Comments on the paper

2 comments
AuthorsOpenReview ↗

General Response to All Reviewers

We thank all reviewers for their careful reading, thoughtful comments, and constructive suggestions. We have revised the manuscript to incorporate the clarifications in our individual responses. We summarize the main points below.

What the method contributes. The aim is to forecast whether an agent will stop following its assigned behavioral principle, while allowing changes in judgment justified by new task information. Section 3.1 now makes this distinction explicit with a concrete example, including the case in which the assigned principle itself is replaced. Section 3.2 clarifies that the reference and predictor are fitted offline. The same fitting and calibration procedure is used across all four models, with parameters learned from each model's Development and Calibration data. The fourth contribution now states the two timing measurements separately: warning with one full turn of lead before sustained drift, and warning before the first violating response.

What the experiments establish. Section 4.2 now explains what each baseline tests and brings the comparisons across model sizes and families into the main discussion. On Qwen2.5-7B-Instruct, AP increases from 0.703 for the strongest nonlinear control to 0.719 for our monitor, with a paired difference interval of [0.006, 0.027]. Update FPR decreases from 6.0% to 4.7%. Section 4.3 separates this comparison from the 48-case evaluation under a common advance warning requirement. In that evaluation, Update FPR decreases from 7.5% to 2.8% on Qwen and from 12.4% to 3.0% on Gemma, without reducing observed advance recall. Section 4.4 explains how the subsequent experiments test changes in the evaluator, principles, task information, and dialogue structure. The adaptive dialogue results concern prediction and false warnings; the dedicated timing analysis measures advance notice for inspection.

How behavioral labels enter the evaluation. Section 3.1 now states that the primary evaluator assigns labels after dialogue generation, using only the principle, history, and task information available at the response being judged. Section 4.4 reports both agreement and Cohen's kappa for the independent assessment. Appendix D.4 adds agreement on which conversations enter the justified update population and explains how changes in this membership affect the paired alarm comparison. This connects label sensitivity directly to the conversations used to calculate Update FPR.

Presentation. Section 3.4 now gives the alarm evaluation window and the reason for the three-turn gap, and uses an example to distinguish warning before sustained drift from warning before the first violation. Section 4.1 identifies the four scenarios used for probability calibration and the five used for cutoff selection, with the complete assignments in Appendix A.2. We have clarified that probes check initial persona adoption and are separate from the Test split. Table 1 now includes the positive proportion and constant score AP for its scoring population. The openings of Sections 4.3 and 4.4 state the purpose of each experiment, while Appendices A.2 and C.1 clarify the dialogue structure and resampling units.

We again thank the reviewers for their time and constructive suggestions. The revisions address these points through clearer explanations and a more consistent presentation of the evidence. We would be grateful if the reviewers would reconsider their assessments in light of our responses and the revised manuscript, and update their ratings if appropriate.

Area_Chair_gMi3OpenReview ↗

Reminder: Discussion Phase Ends November 18 (11:59 PM AoE)

Hi reviewers, a quick reminder that the discussion phase ends on November 18 at 11:59 PM AoE. Please take some time to read the author responses, engage in further discussions if you have any remaining questions or concerns, and update your reviews and scores as appropriate. Thank you!

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

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