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Under review as a conference paper at ICLR 2027

A Theoretical Perspective on Why LLMs Get Lost in Multi-Turn Conversations

Abstract

Recent empirical studies show that LLM task performance can degrade when the same user information is distributed across multiple turns rather than presented at once (Laban et al., 2026). We study this phenomenon theoretically by modeling multi-turn conversation as closed-loop inference over a fixed user intent: the model repeatedly updates its interpretation, generates a response, and may reuse that response as evidence later. This feedback loop creates a fundamental asymmetry between the two sources of conversational evidence: user messages provide exogenous information about the true intent, whereas model responses are generated from the model’s current interpretation and therefore tend to reinforce it. We show that user evidence alone matches the corresponding single-turn error probability and becomes exponentially reliable as additional information arrives. Although model-generated evidence is Bayes-correct in a reference setting where user and model messages are generated from the same latent intent, in the closed loop it instead reinforces the current estimate, whether correct or incorrect. This competition creates distinct recovery and lock-in regimes: sufficiently strong feedback can make errors persist indefinitely, producing a non-vanishing multi-turn performance gap and coexistence of persistently correct and incorrect conversations. We further characterize how pruning or delaying model-history reuse and increasing the relative influence of user evidence mitigate these effects.

Primary area:
learning theory
Keywords:
Multi-turn conversation, Intent inference, Closed-loop feedback, Theoretical analysis, Stochastic dynamics

Reviews

Among:
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1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_2titOpenReview ↗
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3(+1)
Confidence
3
Informativeness
2
Presentation
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2
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Paper summary

This paper develops a theoretical framework to explain the performance degradation observed when task information is distributed across multiple conversational turns. The authors formulate conversational interaction as closed-loop inference over a fixed latent user intent, where user messages provide independent evidence regarding the true intent and model-generated responses reinforce the model's current interpretation.

Critical strengths
  1. The formalization of feedback in multi-turn interaction is clear. The paper separates user-provided evidence from model-generated history and makes explicit how a model’s current estimate can influence what it later treats as evidence. This is a useful abstraction for studying self-reinforcing conversational errors.

  2. The recovery, lock-in, persistent degradation, and intervention analyses fit together into a clear theoretical picture. The paper also distinguishes finite-horizon guarantees from asymptotic claims, particularly in its discussion of snowballing.

Critical weaknesses
  1. The real-LLM validation is limited relative to the scope of the theoretical explanation. The experiments use 54 binary-intent instances and two 7B models to measure one-step preference shifts under controlled intent instructions. They do not test whether early errors persist during actual multi-turn rollouts or whether pruning reduces the gap to a matched single-turn baseline. The authors acknowledge this scope in Appendix B, but the central trajectory-level predictions remain unverified on real LLMs (Sec. 7; Appx. H).

  2. The mapping from the formal model to actual LLM behavior remains underdeveloped. The analysis assumes specified likelihood families and additive scores with a fixed model-evidence weight, whereas real LLMs' use of history can depend on the context. The empirical probe measures changes in the log-likelihood of candidate intent descriptions; these changes are not calibrated to the theoretical drift quantities. This limits the practical interpretation of the recovery and lock-in thresholds (Secs. 2, 4, and 7).

  3. The connection to fixed-information sharding needs clarification. Assumption 2.2 requires uniformly informative user shards after the first turn, so increasing the horizon also supplies continuing evidence. This differs from holding a complete task specification fixed and dividing it across more turns. Appendix B discusses a cumulative-information extension, but the implications of the asymptotic results for this fixed-budget setting remain unclear (Sec. 2; Appx. B).

  4. The interpretation of unreliability is narrower than repeated-run consistency on the same instance. Theorem 5.2 concerns the variance of a binary terminal-error indicator over randomness that includes user shards and model responses. It establishes coexistence of persistently correct and incorrect trajectories, but does not directly establish persistent variability across repeated model runs with an identical user-shard sequence. This distinction should be clearer (Secs. 2 and 5).

  5. Positioning relative to prior self-delusion analyses is incomplete. Ortega et al. (2021) (https://arxiv.org/abs/2110.10819) already explain how treating a model's own actions as evidence can distort inference about a latent task. A direct comparison would help identify the additional contribution of the present recovery and persistence guarantees and mitigation analysis (Appx. A).

Questions for authors
  1. Which aspects of the formulation, recovery and lock-in guarantees, and mitigation analysis are new relative to Ortega et al.'s (2021) self-delusion account of treating model-generated actions as evidence?
  2. Could a small real-LLM multi-turn evaluation test whether early intent errors persist and whether pruning assistant history narrows the gap to a matched single-turn baseline?
  3. Can the measured user and model preference shifts be related to the drift quantities in Section 4 in a way that supports identifying a recovery or lock-in regime in an actual LLM?
  4. How should the degradation guarantees be interpreted when a fixed total amount of task information is split across different numbers of turns, given Assumption 2.2's requirement of uniformly informative new shards?
  5. What supports treating each repetition of a user shard as an equal additive score contribution in the recap/snowball model, and which conclusions would change if the effect of repetition saturates?
  6. How does Theorem 5.2's variability over the stochastic conversation process relate to variability across repeated model runs with exactly the same user-shard sequence?
4 comments

We thank the reviewer for the detailed assessment and for recognizing the explicit separation between user evidence and model-generated history and the connection among recovery, persistence, and intervention results. If further clarification on any point would help your evaluation, please let us know.

W5 / Q1: Relation to Ortega et al. (2021)

We thank the reviewer for this reference, which we now discuss in the related work (Appx. A). Ortega et al. provide a closely related causal account of self-generated evidence. They distinguish an expert's actions, which reveal information about a latent task, from an agent's own actions, which must be treated as interventions. Under this treatment, the action likelihood drops out of the belief update, so P(θ∣do(a))=P(θ)P(\theta\mid do(a))=P(\theta). They discuss interactive language models explicitly and propose training with factual and counterfactual teaching signals.

Both works build on the Bayesian view of in-context learning, which explains the shared structure. Our model follows statistical accounts of in-context learning as inference of a latent task from context (Xie et al., 2022; Zhang et al., 2024), and Ortega et al. adopt the same view of language models. Within this common view, the two treatments of self-generated evidence that they contrast become the endpoints of our family:

  • Treating one's own responses as interventions is λ=0\lambda=0, our pruning and user-only estimator (Thm. 3.1).
  • Conditioning on them as if they were observations, the source of self-delusion, is the closed loop with full weight λ=1\lambda=1.
  • Passive prediction of expert trajectories is our self-consistent reference, where λ=1\lambda=1 gives the exact posterior (Props. 3.1–3.2).

Our analysis covers the whole range 0<λ≤10 < \lambda \le 1 between these endpoints.

What we add. Ortega et al. explain why conditioning on one's own actions is wrong and how to avoid it; their opening example is a dialogue in which user corrections fail to remove such an error. We ask what happens when a model nonetheless reuses its responses with λ>0\lambda>0 while informative user evidence keeps arriving. To our reading, they do not give conditions or rates for this case. Our contributions are:

  1. Recovery and persistence conditions. A lower bound on the probability of never recovering from a negative leader gap, including competition among multiple wrong intents (Thm. 4.1). We also show recovery under uniformly corrective drift and bound the probability of leaving a correct state (Thms. 4.2–4.3).
  2. A comparison under matched user information. A persistent gap from user-only inference, and variability over the conversation process (Sec. 5).
  3. Guarantees for interventions that reduce feedback without removing it. Deferral, recap, and snowballing (Sec. 6). Pruning recovers the prescription of Ortega et al. as the special case λ=0\lambda=0.

W1 / Q2: Actual multi-turn evaluation and matched pruning baseline

The new task evaluation shows that clearing assistant history narrows the gap to a single-turn baseline with the same user information. On 50 Actions and 50 Math problems from Laban et al. (2026), with five runs per problem and model, CONCAT, two-turn KEEP, and four-turn KEEP use the same ordered user shards. Before the fourth answer, PRUNE shares KEEP's first three answers but clears their bodies, keeping user messages and role slots.

ModelCONCAT errorTwo-turn KEEP errorFour-turn KEEP errorFour-turn PRUNE error
Qwen2.5-7B11.2%16.8%37.0%13.6%
Mistral-7B-v0.365.4%65.4%91.8%76.2%

Pruning reduces four-turn error by 23.4 pp [15.8, 30.8] for Qwen and 15.6 pp [9.6, 22.0] for Mistral. The remaining PRUNE−CONCAT gap is 2.4 pp [−2.2, 7.4] for Qwen, which is not distinguishable from zero, and 10.8 pp [3.2, 18.4] for Mistral. Because clearing text also changes context length, this contrast does not measure λ\lambda itself.

Early errors persist when history is retained. On a predefined panel of 20 problems per task with three runs each, we fork every run after the fourth answer into two branches: one retains A1A_1–A4A_4, and the other clears their bodies. Both receive the same two neutral retry prompts, without new facts or error notification. Among runs whose fourth answer fails (38 for Qwen; 106 for Mistral):

  • With history retained, failures persist through both retries at task-balanced rates of 80.0% (Qwen) and 87.7% (Mistral).
  • After clearing, these figures drop to 29.4% and 75.3%, i.e., reductions of 50.6 pp [23.3, 76.1] and 12.4 pp [2.7, 22.6].

W2 / Q3: What the model captures and how probes relate to drift

The model captures feedback from the current intent estimate into later inference. User messages arise from the true intent; model responses arise from the current estimate. Reusing those responses lets the current estimate shape subsequent evidence. A fixed λ\lambda still permits different feedback contributions: λlog⁡pA(At∣z)pA(At∣z′)\lambda\log\frac{p_A(A_t\mid z)}{p_A(A_t\mid z')} varies with the response and candidate intents, and the current estimate changes which responses are generated. Appx. B discusses context-dependent weights and response families. The practical insight is to distinguish changes to history weight, feedback timing, and user-evidence accumulation. The intervention analysis and the pruning results above connect this abstraction to actual history handling. Text deletion remains a concrete context intervention, rather than a measurement of λ\lambda.

What the new probes and continuations show. On the original 54 tasks, we follow each of ten wrong-seeded responses with a Weak, Medium, or Strong clarification. Here H0H_0 is the ambiguous initial request, A1A_1 a stored response generated under the wrong intent, UsU_s the clarification at strength ss, and gg the probe margin. The joint margin g11(s)=g(H0+A1+Us)g_{11}(s)=g(H_0+A_1+U_s) and residual RA(s)=g11(s)−g(H0+Us)R_A(s)=g_{11}(s)-g(H_0+U_s) are:

ModelClarificationJoint margin g11g_{11}Residual comparison RAR_A
Qwen2.5-7BWeak1.8050.395
Qwen2.5-7BMedium2.0390.349
Qwen2.5-7BStrong1.962−0.105
Mistral-7B-v0.3Weak1.248−0.141
Mistral-7B-v0.3Medium1.581−0.050
Mistral-7B-v0.3Strong1.195−0.358

Wrong-seeded histories alone shift the margin toward the alternative intent (mean −1.154 / −0.929), yet after clarification every joint margin is positive and RAR_A is small and not consistently signed. In generated continuations, keeping the wrong-seeded answer does not detectably change error after the same clarification (Appx. H.4; details in our response to Reviewer Aomi, W1).

The drift quantities are hard to measure in an LLM, but the theory locates the boundary and explains the observed regimes. Our probe reads out which intent the model prefers; the theorems depend instead on how strongly each message separates the intents (κ\kappa for user messages, αerr\alpha_{\rm err} and β\beta for model responses), which would require estimating divergences between intent-conditioned message distributions. We therefore do not place a deployed LLM in a regime numerically. What the theory provides is the boundary itself: both regimes exist, they are separated by λαerr\lambda\alpha_{\rm err} versus κ\kappa (exactly at λαerr=κ\lambda\alpha_{\rm err}=\kappa in the binary case), and the outcome moves with the history weight and with how informative each user turn is. This explains the contrast in our new experiments: a single rule-stating clarification is highly informative and the model recovers, whereas sharded tasks deliver partial evidence per turn while responses accumulate, and errors persist (W1/Q2).

Where these quantities are known, simulations confirm the boundary. In the formal model, wrong states persist when λαerr>κ\lambda\alpha_{\rm err} > \kappa and errors vanish when λβ<κ\lambda\beta < \kappa (Appx. G.2). Moving only the snowball cap cc across λβ=cκ\lambda\beta = c\kappa cuts wrong final intents from 1,833 to 8 of 5,000 (Appx. G.6).

W4 / Q6: Conversation-level variability versus fixed-script repetitions

Thm. 5.2 links the coexistence of persistently correct and persistently incorrect trajectories, each with positive probability, to non-vanishing terminal-error variance over the conversation process, which includes randomness in both user messages and model responses. For terminal error ETE_T and the realized user script UU, Var⁡(ET)=EU[Var⁡(ET∣U)]+Var⁡U(E[ET∣U])\operatorname{Var}(E_T)=\mathbb E_U[\operatorname{Var}(E_T\mid U)]+\operatorname{Var}_U(\mathbb E[E_T\mid U]). A total-variance bound therefore does not imply a conditional bound for every script. Thm. 5.2 concerns variability across conversations, and Sec. 7.2 and Appx. I.3 keep the two notions separate.

We measure fixed-script variability separately as the fraction of run pairs that disagree in correctness, using the five runs per problem:

ModelCONCATFour-turn KEEPFour-turn PRUNE
Qwen2.5-7B0.0800.1600.074
Mistral-7B-v0.30.1840.1040.128

Qwen's disagreement is higher under four-turn KEEP (0.160) than under CONCAT (0.080) or PRUNE (0.074). Mistral's lower KEEP disagreement accompanies a 91.8% error rate: repeated runs can agree because they repeatedly fail.

W3 / Q4: Continuing information versus a fixed budget

Assumption 2.2 deliberately isolates feedback-induced failure when user information is sufficient for consistent inference. At each horizon, both protocols receive the same realized user messages, and the theory identifies when feedback can still sustain an error. Splitting a fixed amount of user information across more turns supplies no growing budget. In the additive model, regrouping also preserves the terminal user-only score, so Thm. 5.1 does not transfer directly.

Theoretical extension: the lock-in bound of Thm. 4.1 carries over to a fixed budget. Splitting NN conditionally i.i.d. evidence atoms into nn equal groups weakens each user turn to κˉn=Nnκˉatom\bar\kappa_n=\frac{N}{n}\bar\kappa_{\rm atom}, while each retained response still reinforces a wrong estimate by at least λαerr\lambda\alpha_{\rm err}. Because the nn-group conversation matches the first n+1n+1 turns of an infinite-horizon one, Thm. 4.1's bound lower-bounds terminal error whenever n>Nκˉatom/(λαerr)n > N\bar\kappa_{\rm atom}/(\lambda\alpha_{\rm err}), while user-only error does not depend on nn. This is a sufficient condition, not a monotonicity result (Cor. E.1, Appx. E.3).

Evidence. In the matched-task evaluation (W1/Q2), four-turn KEEP error exceeds two-turn KEEP by 20.2 pp for Qwen and 26.4 pp for Mistral; grouping changes disclosure timing and the number of intermediate answers together. In the formal model, we fix 32 realized evidence atoms in each of 5,000 trajectories and regroup them into nn informative turns (T=n+1T=n+1):

Number of informative groups12481632
User-only error0.1990.1990.1990.1990.1990.199
SHARDED error0.2430.3000.4360.6540.7720.799

User-only error is constant across groupings, while closed-loop error rises (Appx. G.5).

Q5: Why count repetitions equally, and what happens if their effect weakens?

Equal additive contributions follow from how the score treats context, and the reported gains of these protocols support them. Let ℓs=log⁡p(us∣z⋆)p(us∣z′)\ell_s=\log\frac{p(u_s\mid z^\star)}{p(u_s\mid z')} and let msm_s be the model-evidence term of response ss. Our score adds one log-likelihood term for every user message present in the context. Recap and snowball add no new facts; they put copies of earlier messages back into the context, and the same rule counts each copy as one more term. Under snowball, usu_s is present in every later turn, so the margin at turn tt is Δt=∑s≤tws,t ℓs+λ∑s<tms\Delta_t=\sum_{s\le t} w_{s,t}\,\ell_s+\lambda\sum_{s<t}m_s with ws,t=t−s+1w_{s,t}=t-s+1; a recap adds one copy of each earlier message at a single turn. Laban et al. (2026) report that both protocols reduce multi-turn degradation, which a model in which repetition carries no weight could not explain. Equal weights are the simplest such choice. The analysis depends only on how fast the total user weight grows, so unequal weights enter through ws,tw_{s,t} in the same way.

Saturation can be modeled by a counting window (Appx. B). If each message counts at most cc times, the weight becomes ws,t=min⁡(t−s+1, c)w_{s,t}=\min(t-s+1,\,c). Only recap and snowball are affected; the original protocol, pruning, and deferral involve no repetition.

  • Recap: it still adds one copy unless c=1c=1, in which case it has no effect.
  • Snowball: the user part of the margin now grows linearly, by about cκc\kappa per turn, rather than quadratically, so the every-λ\lambda guarantee becomes a threshold. The argument of Thm. F.2 (snowballing) extends directly: the user part is still a sum of independent terms, now with weights at most cc, and the model part is the same martingale. The same concentration steps then apply with κ\kappa replaced by cκc\kappa, which points to recovery when λβ<cκ\lambda\beta < c\kappa. Unlimited repetition is the limit c→∞c\to\infty.

We simulated capped snowball in the formal model. The cap includes each message's first appearance, and results are reported after 1,000 turns:

ProtocolMaximum times each user message countsWrong final intents
No repetition (baseline)11,833 / 5,000
Capped snowball28 / 5,000
Capped snowball40 / 5,000
Original snowballNo limit0 / 5,000

Thank the author for the detailed response, they have resolved some of my concerns. I will raise my rating.

Reviewer_phYsOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper introduces theoretical arguments on why large language models face performance degradation in multi-turn conversations. Multi-turn conversations condition on past assistant responses, resulting in error propagation, leading to a decrease in performance compared to single-turn prompting. The authors provide a theoretical account of how error propagates in a multi-turn conversation and provides an account of how various context engineering strategies---like history pruning, deferral, recaps, and snowballing---alleviate these errors.

Critical strengths
  1. The paper offers a unique theoretical analysis on the failure modes of multi-turn conversations, context pollution, and on recovery from context pollution.

  2. The study also analyzes various practical intervention strategies (e.g., omitting assistant responses, recapping, snowballing). The paper makes asymptotic arguments that are potentially helpful in giving the community a better sense of the effects of conditioning on the past in multi-turn conversations.

Critical weaknesses
  1. It is unclear how useful or realistic this work is. The rate at which an assistant response carries over from one turn to another seems, likely, very dependent on qualitative factors that cannot be theorized about. The empirical evidence in section 7 also does not provide a conclusive answer to this question.

  2. The writing is rather difficult to follow; make sure to define technical terms before their first usage. On page 2, the term “Bayes-correct” and “assigning it a full likelihood weight” are used before any setup is given, making the meaning difficult to understand. Also, there are multiple places in the work where modeling choices are made without sufficient justification (see section on Randomness and initial ambiguity); one thing that would help justify the many modeling choices is a brief detailing of contrasting alternative choices that could have been made.

Questions for authors

alongside each assumption made in the paper, could you provide an explanation as to how each assumption you've chosen may or may not be reflective of how multi-turn conversations are structured in the real world?

2 comments

We thank the reviewer for recognizing our analysis of context pollution, recovery, and practical interventions, and would be happy to answer any further question that may influence your assessment.

W1: Realism and practical usefulness of the theoretical framework

The model explains how informative user evidence and generated history compete. Our aim is to complement empirical studies with a formal analysis of evidence accumulation in multi-turn inference. We distinguish user messages generated under the ground-truth intent from model responses generated under the model’s current intent estimate. Reusing the latter creates a feedback loop in which a provisional estimate shapes the evidence subsequently used to revise it. We derive when this closed loop recovers (Thm. 4.2), when it locks into an error with positive probability (Thm. 4.1), and the resulting error floor (Thm. 5.1). These results are stated as conditions on the weight λ\lambda placed on model-generated history, so they can guide how history is handled.

The carry-over rate λ\lambda is an explicit parameter, and its effect is state-dependent. Response AtA_t contributes λlog⁡pA(At∣z)pA(At∣z′)\lambda\log\frac{p_A(A_t\mid z)}{p_A(A_t\mid z')} to the comparison between candidates zz and z′z', so λ\lambda is the rate at which a response carries over. Even with λ\lambda fixed, this contribution varies with the content of AtA_t, the candidate pair, and the estimate that generated it. Qualitative factors such as content and wording act through this term.

Existing interventions either delete history or strengthen user evidence. Pruning removes all earlier responses (λ=0\lambda=0) and deferral removes the early ones; a recap raises the current margin and snowballing makes user evidence accumulate faster (Sec. 6). None of them adjusts how strongly the retained history counts.

Our theory identifies this weight, λ\lambda, as a direct lever for closing the multi-turn gap. Thm. 4.1 and Thm. 4.2 show that λ\lambda sets the regime: lock-in occurs with positive probability when λαerr>κˉ\lambda\alpha_{\rm err} > \bar\kappa, and recovery is guaranteed when λβ<κ\lambda\beta < \kappa. History therefore need not be deleted; it only needs to be down-weighted. Our analysis makes history weighting an explicit design dimension and motivates investigating when and how strongly generated history should influence later inference when designing models. A natural next step is a context-dependent weight λt=λ(Ht)\lambda_t=\lambda(H_t) that drops after a clarification or when the estimate is uncertain; our probes already suggest such a drop after an explicit clarification, and Appx. B gives the corresponding local conditions.

On the empirical evidence in Sec. 7. Beyond the original one-step probes, we added trajectory-level tests on the sharded tasks of Laban et al. (2026) (Appx. I), and each prediction holds in direction: with fixed user information, four turns of retained history raise error over two (+20.2 / +26.4 pp for Qwen / Mistral), clearing history narrows the gap to the single-turn baseline (−23.4 / −15.6 pp), and clearing it after a failure raises recovery within two retries (20.0→70.6% / 12.3→24.7%).

W2 and Q: Define technical terms and explain each modeling choice

We now define the reference inference problem before using "Bayes-correct." The revised introduction first explains that if both user messages and responses are generated from the same latent intent, multiplying their ordinary likelihoods produces that reference model’s posterior. We thank the reviewer for pointing this out.

The conversational meaning and scope of each assumption and modeling choice. For each, the table states what it captures, the idealization involved, and an alternative.

Assumption or modeling choiceConnection to real conversationsScope and alternatives
2.1 Initial ambiguityAn unclear first request leaves several intents plausible, giving a controlled starting point for studying early estimates.Exact ties are an idealization; real models may favor some intents. A distribution of initial score gaps would change the initial error probabilities and population bounds.
2.2 User informativenessLater messages keep adding clues about the true intent, so we can ask whether the model stays wrong even when the user supplies enough information.Some messages only repeat details or separate a few intents. Splitting a fixed amount of user information across more turns adds no new information; Cor. E.1 covers this case.
2.3 Response separationDifferent intent estimates lead to different answers, so a reused answer supports the estimate that produced it.Fails if replies are generic regardless of the estimate. Intents may share answers as long as their reply patterns differ.
2.4 Bounded log-likelihood ratiosNo single message favors one intent arbitrarily strongly.A message that rules out an intent completely requires an analysis that allows decisive evidence.
Fixed intentOne intended task throughout, as in sharded benchmarks where the full instruction exists in advance.Goals may change; tracking a time-varying intent zt⋆z_t^\star is discussed in Appx. B.
Pre-planned, non-reactive user messagesA fixed user script, as in Laban et al. (2026) and our evaluation. This isolates feedback from the model's own history.Real users react to mistakes. Corrections would raise user informativeness after an error, whereas accommodation would lower it (Appx. B).
MAP estimate with uniform tie-breakingThe assistant commits to one reading when it answers. If the request does not distinguish readings, the choice carries no task information.The model could sample a reading or hedge between readings. Sampling adds randomness at every turn; hedging weakens response separation.
Responses depend on history only through the current estimateThe answer follows the reading currently adopted.Responses also depend on wording and earlier answers; history-dependent response families are discussed in Appx. B.
Additive score with fixed λ\lambdaA transparent way to vary how much past answers count, from ignored (λ=0\lambda=0) to full weight (λ=1\lambda=1).Weights λt=λ(Ht)\lambda_t=\lambda(H_t) give local conditions that compare κt+1\kappa_{t+1} with λtαerr,t\lambda_t\alpha_{{\rm err},t} (Appx. B).

In the revised manuscript, Sec. 2 relates the assumptions to conversational behavior and points to Appx. B, which now contains a compact version of this table alongside the discussion of each relaxation: a distribution over initial score gaps, cumulative informativeness, history-dependent response separation, source-specific likelihood bounds, history-dependent weights λt\lambda_t, and reactive users or time-varying intent.

Reviewer_AomiOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The authors investigate why revealing task requirements across multiple turns can reduce LLM performance even when the corresponding single turn interaction contains the same user information. They model task understanding as inference over a fixed set of user intents and user messages provide conditionally independent evidence about the true intent, while assistant responses are generated from the model's estimate. Under bounded likelihood ratios, the authors establish that user only inference matches the corresponding single turn estimator and achieves exponentially decreasing error. they also analyze pruning, exclusion of early assistant responses, single recap and repeated recapping. The authors provide synthetic experiments with a formal model and compare its regimes and interventions, and provide resutls on Qwen and mistral 7B models on constructed intent instances across task families.

Critical strengths
  1. The setup on SINGLE and SHARDED protocols in section 2 makes the setup interpretable, and they separate information supplied by the user from material generated by the current interpretation
  2. The persistence analysis in Theorem 4.1 handles multiple competing interpretations
  3. The experimental validation of the method with synthetic results strengthens their contribution.
Critical weaknesses
  1. The authors measure �0��0� and �1��1� separately, and they do not test a wrong assistant response followed by a corrective user evidence and further assistant generations. So it does not establish the competition between the two evidence sources and recovery vs persistence.
  2. Assumption 2.2 requires every post initial user shard to be uniformly informative against every competing intent, and hence increasing �2��2� therefore gives indefinitely accumulating informative observations. This is different from taking one fixed instruction and dividing its finite information across increasingly many turns, where per turn informativeness can decrease.
Questions for authors

See weaknesses section above

3 comments

We thank the reviewer for the careful reading and for recognizing the interpretable setup and the synthetic validation. We address the concerns below. We look forward to discussing any point that remains unclear.

W1: Test a wrong assistant response followed by corrective user evidence and further assistant generations

Our separate-source probes establish two complementary directional effects. Across both models, model responses generated under a given intent tend to shift the probe margin toward that intent, while user clarifications shift it toward the ground-truth intent. These findings provide empirical support for the distinct contributions of model-generated history and corrective user evidence highlighted by our analysis. Here, we extend the evaluation to their combined effects and subsequent task behavior through three complementary studies: joint clarification probes on the original tasks, generated continuations on controlled executable tasks, and a matched history-clearing retry evaluation on real tasks.

1. Joint probes now include the same wrong-seeded history followed by each clarification. On the original 54 binary-intent tasks (9 semantic families), we follow each of the ten existing wrong-seeded responses per task and model with the Weak, Medium, or Strong clarification. This follow-up was added during revision (designed after the first Medium-clarification joint probes; Appx. H.3) and generates no new answers. Here H0H_0 is the ambiguous initial request, A1A_1 a stored response generated under the wrong intent, UsU_s the clarification at strength ss, and gg the difference between the mean token log-likelihoods of the true and alternative intent descriptions. We report the joint margin g11(s)=g(H0+A1+Us)g_{11}(s)=g(H_0+A_1+U_s).

ModelWeakMediumStrong
Qwen2.5-7B1.8052.0391.962
Mistral-7B-v0.31.2481.5811.195

Without clarification, these histories shift the margin toward the alternative intent (mean shift of −1.154 for Qwen and −0.929 for Mistral). After clarification, all six joint margins are positive. Among histories whose margin is negative before clarification, the numbers that become positive under Weak/Medium/Strong clarification are 432/464, 464/464, and 464/464 for Qwen, and 506/517, 516/517, and 499/517 for Mistral (Appx. H.3).

2. Controlled continuations test actual answers after history and clarification. We build executable variants of the nine families (two intent directions, BASIC and COMPOSITE versions, three repetitions). Each root generates A1A_1 under a true- or wrong-intent seed, followed by the same clarification and an A2A_2 answer. KEEP retains A1A_1, and DROP clears its body; the seeding instruction is used only to generate A1A_1. The wrong-intent-seeded KEEP−DROP differences in error (the fraction of rule-dependent output components that miss the true-rule reference) are +0.093 [−0.074, 0.259] and −0.039 [−0.094, 0.011] for Qwen BASIC and COMPOSITE, and −0.031 [−0.204, 0.130] and −0.008 [−0.120, 0.099] for Mistral. All four intervals include zero, so retaining the wrong-seeded answer does not detectably change task error after the clarification. The true-intent-seeded Mistral BASIC condition has a positive KEEP−DROP error difference of 0.222 [0.074, 0.407]; seed labels specify generation instructions, not verified correctness, so a true-seeded first answer can itself be wrong. In all 432 KEEP contexts, the joint-probe margin favors the true intent; task error additionally counts computation and output-format failures, which the probe does not measure (Appx. H.4).

3. Clearing earlier model responses improves task recovery within two retries. We use the sharded Actions and Math tasks of Laban et al. (2026), with fixed four-turn user scripts and deterministic evaluators. For a predefined panel of 20 problems per task with three runs each, we fork every conversation after the fourth answer. One branch retains the assistant bodies; the other clears them while keeping user messages and role slots. Both branches receive the same two neutral retry prompts, with no new facts or error notification.

Among runs whose shared fourth answer fails (38 runs from 16 problems for Qwen; 106 runs from 39 problems for Mistral), success within two retries rises from 20.0% to 70.6% for Qwen and from 12.3% to 24.7% for Mistral (Actions and Math weighted equally). Equivalently, with history retained, 80.0% and 87.7% of the failures persist through both retries, compared with 29.4% and 75.3% after clearing.

Relation to the theory. When the current estimate is a wrong intent ww, the expected margin increment combines a positive user-divergence term and a negative model-divergence term. Thm. 4.1 and Thm. 4.2 give sufficient conditions on either side of this balance.

  • In the controlled tasks, one decisive clarification follows one seeded response, and we observe recovery.
  • In the sharded tasks, partial information arrives while answers accumulate. Retaining history raises error relative to the information-matched CONCAT baseline (37.0% vs. 11.2% for Qwen; 91.8% vs. 65.4% for Mistral) and makes recovery after a failure less likely, which is the direction the persistence analysis predicts.

These are directional comparisons. We have added this discussion to Sec. 7 and Appx. H–I.

W2: Continuing informative evidence versus a fixed information budget

Assumption 2.2 deliberately isolates a failure mode that persists despite a continuing supply of informative user evidence. Under the stated assumptions, the matched user-only estimator is exponentially consistent (Thm. 3.1). Yet the closed-loop estimator can remain wrong indefinitely with positive probability (Thm. 4.1), which yields the persistent gap in Thm. 5.1. At every horizon, both protocols receive the same realized shards u1:Tu_{1:T} and share the same prior; they differ only in that SHARDED reuses its own responses.

Splitting a fixed amount of user information across more turns is a complementary question, because per-turn informativeness then decreases. We address it both theoretically and empirically.

1. Theory. Regrouping fixed likelihood terms leaves the user-only score, and hence its error, unchanged. The closed loop is different. Suppose the budget consists of NN conditionally i.i.d. evidence atoms, split into nn equal groups after the ambiguous first turn. Each informative turn then has user divergence at most κˉn=Nnκˉatom\bar\kappa_n=\frac{N}{n}\bar\kappa_{\rm atom}. Each retained response, however, still reinforces a wrong estimate by at least λαerr\lambda\alpha_{\rm err} in expectation.

The nn-group conversation has the same law as the first n+1n+1 turns of an infinite-horizon conversation, and a trajectory that never recovers is wrong at the final turn. Hence, whenever λαerr>κˉn\lambda\alpha_{\rm err}>\bar\kappa_n, the bound of Thm. 4.1 lower-bounds the terminal error. This condition holds for all n>Nκˉatomλαerrn > \frac{N\bar\kappa_{\rm atom}}{\lambda\alpha_{\rm err}}, a range that is non-empty when a single atom is weaker than the per-response reinforcement. Finer partitions therefore move the closed loop into the lock-in regime, while user-only inference is unchanged. This is a sufficient condition, not a monotonicity result. We have added it as Cor. E.1 in Appx. E.3.

2. Real LLMs with fixed user information. On 50 Actions and 50 Math problems from Laban et al. (2026), with five runs per problem and model, we keep the user shards and their order identical across CONCAT (one prompt), two-turn KEEP, and four-turn KEEP.

ModelCONCAT errorTwo-turn KEEP errorFour-turn KEEP errorFour-turn minus two-turn KEEP (pp)
Qwen2.5-7B11.2%16.8%37.0%20.2 [13.2, 27.6]
Mistral-7B-v0.365.4%65.4%91.8%26.4 [19.2, 33.8]

Four-turn KEEP has higher error than both CONCAT and two-turn KEEP. The two-versus-four comparison also changes disclosure timing, so it is consistent with the mechanism in (1) but does not isolate it.

3. Formal-model simulation. In each of 5,000 trajectories, we fix 32 realized user-evidence atoms and regroup them into nn informative turns after the ambiguous first turn, so the horizon is T=n+1T=n+1.

Number of informative groups12481632
User-only error0.1990.1990.1990.1990.1990.199
SHARDED error0.2430.3000.4360.6540.7720.799

User-only error is unchanged across groupings, while closed-loop error rises, as the corollary anticipates (Appx. G.5).

Comments on the paper

1 comment

We thank all reviewers for their constructive feedback. We have uploaded a revised manuscript with changes marked in blue. The main changes are:

  • Information-matched multi-turn evaluation (Sec. 7.2, Appx. I). We evaluate Qwen2.5-7B and Mistral-7B-v0.3 on the sharded Actions and Math tasks of Laban et al. (2026), comparing CONCAT, two- and four-turn KEEP, and four-turn PRUNE under identical user shards. We also report recovery after task failure with assistant history retained or cleared, and repeated-run variability under fixed user scripts.
  • Wrong history followed by correction (Sec. 7.1, Appx. H.3–H.4). Joint probes and generated continuations after a wrong-seeded response and a clarification.
  • Fixed information budget (Sec. 5, Appx. E.3, G.5). A corollary showing that, when a fixed amount of user information is split into more turns, the closed loop enters the lock-in regime of Thm. 4.1 while user-only inference is unchanged, together with a simulation.
  • Capped repetition (Sec. 6, Appx. B, G.6). A recovery threshold for snowballing when each user message can be counted at most cc times, together with a simulation.
  • Positioning and presentation (Sec. 1–2, Appx. A). A comparison with Ortega et al. (2021) in Appx. A, and definitions before first use.
  • Assumptions, scope, and future directions (Sec. 8, Appx. B). A table giving, for each assumption and modeling choice, its conversational meaning and the alternative that relaxes it, linked to the discussion of how each assumption can be relaxed; the conclusion points to the history weight λ\lambda as a direction for closing the multi-turn gap.

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

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