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Under review as a conference paper at ICLR 2027

State-Grounded Credit Assignment for Dual-Control Tool Agents: Separating Progress from Attribution

Abstract

Multi-turn tool agents in dual-control environments complete tasks jointly with users who can also act on a shared world. Standard GRPO with terminal rewards evaluates the resulting joint trajectory but does not distinguish progress produced directly by the agent from progress made through user-side operations. We introduce state-grounded process rewards that measure progress toward target states constructed from reference actions, assigning direct credit to assistant-side changes and factual delegated credit to user-side changes. We further introduce delegated credit estimation (DCE), which adjusts user-side credit by replaying user turns after replacing the assistant’s current message with a neutral acknowledgement. Across three -bench-Verified domains, Qwen3.5-9B jointly trained with direct and factual delegated supervision achieves higher mean scores than Terminal GRPO and an adapted tool-call-matching baseline across all reported metrics. On Telecom, the online variant of DCE reaches 84.8% Pass (success in all five trials), exceeding Terminal GRPO by 9.1 percentage points and factual delegated supervision by 2.1 points, with comparable single-trial success to the latter. Validation with separate replays shows that online DCE selectively reduces credit for user-side progress that recurs under the neutral message. These results support user-side state supervision and contextual refinement of delegated credit.

Primary area:
reinforcement learning
Keywords:
Multi-Turn Tool Agents, State-Grounded Process Rewards, Credit Assignment, User-Agent Collaboration, Reinforcement Learning

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_yTcxOpenReview ↗
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1
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3
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2
Presentation
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Paper summary

The paper studies credit assignment for tool agents when both the assistant and the user can act on the environment. It measures progress through state-field matches against targets obtained from reference actions, separating assistant-side and user-side progress. Delegated Credit Estimation (DCE) further discounts user-side credit when the same progress recurs after replacing the assistant's message with a neutral acknowledgement. These signals supplement terminal GRPO rewards. Experiments across multiple domains evaluate policy performance, with additional replay analyses of the credit correction.

Critical strengths
  1. User-side execution is a practical aspect of tool use. Crediting useful user actions and asking whether they depend on the current assistant instruction is a sensible problem to study. The neutral-message replay design is intuitive.

  2. The paper includes useful controls for user-side supervision and validates its recurrence estimates using separate replays. These analyses provide evidence that contextual DCE identifies progress that also occurs under a neutral message.

Critical weaknesses
  1. The empirical contribution is limited to in-domain benchmark optimization. The training data come from the same benchmark task framework, with part of the Retail data synthesized from failed AReaL training trajectories. For Telecom, the authors generate new customer profiles but instantiate tasks from the official non-test collection. It is unclear how much training and evaluation overlap in problem types, failure patterns, and their combinations. This leaves a concern that the gains largely reflect adaptation to familiar task patterns. The baseline already has high single-trial success, while DCE's additional gains over factual delegated supervision are modest and confined to repeated-trial success. I do not find these results sufficient to establish a significant contribution.

  2. The process reward is narrowly suited to tasks with explicit reference target states. Exact field matching fits Telecom configuration tasks, but it is unclear how it would provide meaningful progress signals for numerical goals where partial progress matters, tasks with multiple valid end states, or artifact creation. The central user-side credit mechanism is also tested only in Telecom; the other domains do not provide user-side state rewards. The problem is practical, but the design and evidence do not establish applicability to user-side execution more generally.

  3. Online Contextual DCE adds substantial extra user-turn simulation, but its benefit under a matched compute budget is not established. The comparisons use the same training steps rather than the same total computation, and replay counts are not translated into token or runtime costs. It is unclear whether spending that budget on more ordinary rollouts or longer training would perform as well or better. Given the modest additional policy gain, this comparison matters for judging whether DCE is worthwhile.

Questions for authors
  1. How much do Telecom training and evaluation tasks overlap in problem types and failure-pattern combinations? Is there evidence of transfer to held-out task patterns beyond changing customer profiles?

  2. What evidence supports the reward design beyond tasks with an explicit reference target state, such as tasks with multiple valid outcomes or artifact outputs?

  3. What is the additional token or runtime cost of Online Contextual DCE, and how does it compare with spending the same budget on more ordinary rollouts or longer training?

1 comment
AuthorsOpenReview ↗

Author Response: Task Transfer, Method Scope, and Computational Cost

We thank the reviewer for recognizing the importance of user-side execution and for the questions on transfer, scope, and computational cost. Factual denotes Direct + Delegated. Page references are to the revised manuscript.

Q1: Training–evaluation overlap and transfer to unseen patterns

We audited all 1,300 Telecom training instances against the 114 evaluation tasks. Each task pattern pairs a problem type with its fault set, excluding customer identity and persona.

Training-pool coverageEvaluation tasks
Problem type seen85/114
All individual faults seen86/114
Complete fault set seen, ignoring type4/114
Joint (problem type, fault set) seen0/114

110/114 tasks (96.5%) have unseen fault combinations. The four shared fault sets occur under different problem types. Training excludes the official base evaluation split and uses new customer profiles; the audit establishes separation beyond profile changes.

G2 contains 81 tasks with unseen combinations of familiar faults within known problem types. G4 contains 29 service_issue tasks, a problem type absent from training. Scores are means over three evaluations of each checkpoint (%):

GroupPolicyPass¹Pass³Pass⁵
G2Terminal GRPO93.983.876.1
G2Factual96.590.384.8
G2Online Contextual DCE95.388.383.5
G4Terminal GRPO94.082.872.4
G4Factual94.784.574.7
G4Online Contextual DCE97.291.786.2

Factual and Online improve Pass⁵ over Terminal by 8.7 and 7.4 points on unseen combinations. The overall +2.1-point DCE gain combines different group effects: Factual leads on G2, while DCE gains +2.5 Pass¹ and +11.5 Pass⁵ points over Factual on the unseen G4 problem type. These results show transfer to unseen structures within the same tool environment (§5.4, pp. 9–10; Appendix G, pp. 28–30).

Q2: Scope of progress measurement and user-side credit

Our method separates role-specific progress measurement from recurrence-adjusted user-side credit. Reference-field matching supplies the progress score in our implementation, allowing different action sequences to reach the same target. DCE tests whether an observed user-side progress event recurs after replacing the current assistant message, using restorable context and a common event criterion across branches.

Telecom provides the benchmark's user-side tools that modify environment state. Airline and Retail have no mutable user-side component (§3.1, pp. 3–4). This determines where delegated credit can be evaluated in tau2-bench. On Telecom, adding delegated supervision raises Pass⁵ from 80.7 to 82.7 with direct-progress and risk settings fixed.

Task-specific scoring extensions include:

TaskPossible progress measure
Numerical goalsBounded score based on distance to a valid target region
Multiple valid outcomesSatisfaction of task constraints
Artifact creationFunctional tests or validated semantic criteria

Extending DCE also requires defining observable user-side progress events. For artifacts, an event could be satisfaction of a functional requirement across different valid outputs.

ProCredit demonstrates acceptance-check progress rewards on AppWorld and ToolSandbox; FACA learns from user reactions and transfers to shared-workspace tasks. These provide examples of progress and user-feedback supervision (§2, pp. 2–3; Appendix F.5, p. 28).

The trained DCE policy also transfers to a second user simulator: +5.0 Pass⁵ points over Factual with Qwen3.8-27B, without retraining (Table 20, p. 32).

Q3: Replay cost and additional-training control

With the same ten actor/rollout GPUs, the aligned rollout-0–119 window takes 56.60 h for Online versus 46.84/46.01 h for Terminal Partial-State/Matched Global-Discount (119 intervals each): +9.76–10.59 h (+20.8–23.0%). These no-replay runs calibrate the budget because the historical Factual run shared its simulator endpoint with other workloads.

We continued Factual for 30 updates (120→150) under its original training setup. This took 11.38 h, exceeding the calibrated overhead. Evaluation uses the original Telecom protocol. Mean ± evaluation SD (%):

PolicyUpdatesPass¹Pass³Pass⁵
Factual12096.2 ± 0.489.2 ± 0.882.7 ± 1.0
Factual, continued15095.5 ± 0.588.2 ± 0.682.2 ± 0.5
Online Contextual DCE12096.0 ± 0.789.5 ± 0.884.8 ± 0.5

Online DCE exceeds continued Factual on all five metrics (Pass⁵ 84.8 vs 82.2). Thus, 30 additional updates did not recover its gain at the calibrated runtime budget (Appendix I, pp. 33–34; Table 23, p. 34).

Reviewer_yB2uOpenReview ↗
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2
Confidence
3
Informativeness
2
Presentation
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2
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Paper summary

Addressing the problem that standard GRPO with terminal rewards cannot distinguish progress made directly by the agent from progress made through user-side operations, the paper proposes role-decomposed state-grounded process rewards that measure progress toward target states constructed from reference actions, and introduces delegated credit estimation (DCE), which replays user turns after replacing the assistant’s current message with a neutral acknowledgement and reduces credit for user-side progress that also recurs under the neutral message. On Qwen3.5-9B trained jointly across three τ²-bench-Verified domains, the Direct + Delegated configuration outperforms Terminal GRPO and an adapted ToolRL baseline on all reported metrics, and on Telecom, Online Contextual DCE reaches 84.8% Pass5, 9.1 percentage points above Terminal GRPO and 2.1 points above factual delegated supervision.

Critical strengths
  1. A meaningful problem setting that is genuinely under-addressed. Distinguishing "who caused progress" in scenarios where users can manipulate a shared environment is a real problem in agentic RL, and the attribution of user-side state changes is indeed worth investigating;
  2. Detailed and transparent diagnostic analysis of the replay procedure. The appendix gives replay coverage, failure rate, regression audit, closed-loop residual credit, etc., and works fine and transparent.
Critical weaknesses
  1. The core empirical conclusions lack statistical power and cannot be attributed to the proposed method. The paper’s own results suggest that training variance is large. Retail and Airline have no user-side state rewards, so Direct-only and Direct + Delegated receive identical rewards in both domains. Yet in Retail they differ by 3.6 Pass1 and 3.5 Pass5 (76.7 → 80.3; 47.7 → 51.2). The authors attribute this to changes in the shared, jointly trained policy, but it shows that, under identical rewards, differences comparable to the claimed method gains can arise between separately trained checkpoints. Since each method is trained only once and the reported standard deviations reflect repeated evaluation of the same checkpoint, the claimed gains cannot be separated from training variance.
  2. The “validation” of DCE is partly circular, so it does not establish that DCE allocates credit correctly. In the matched-budget comparison (Table 8), the evaluation metric S is the removed credit weighted by held-out recurrence q(2), and the contextual rule allocates removal according to q(1), whereas the global-constant and field-stage-constant controls do not use recurrence information. As long as q(1) and q(2) are correlated, the contextual rule must win by a large margin, so the gap between 0.409 and 0.063 is a direct consequence of how the metric is defined.
Questions for authors
  1. Could you report training results for two additional baselines: (a) a terminal partial-state reward that assigns F(x_T) only at the end of the trajectory, without the current-state term, and (b) a delegated credit discounted by a simple global constant or a random discount at a matched removal budget?
  2. Are the recurrence estimates stable under different neutral messages (e.g., a longer neutral statement, a version that removes only the executable requests while keeping the rest of the message, or a generic “please continue”) and under different user simulators?
  3. Does the gain from DCE persist in these settings?Is there qualitative evidence (e.g., trajectory examples) showing that the discounted transitions are ones the user would indeed have performed anyway, rather than anomalous simulator behavior triggered by the neutral message?
1 comment
AuthorsOpenReview ↗

Author Response: Training Controls and Replay Robustness

We thank the reviewer for the concrete suggestions, which motivated the new training controls and replay analyses. Factual denotes Direct + Delegated; scores are mean ± evaluation SD (%). Page references are to the revised manuscript.

W1: Training variance. Direct-only and Factual share Airline/Retail reward rules, but Telecom supervision changes their joint objective; the Retail gap alone therefore does not estimate seed variance. The trained controls support the reward design (Q1), and the DCE policy gain persists with a second simulator (Q2). Extending Factual by 30 updates (11.38 h, exceeding the calibrated overhead) yields Pass⁵ 82.2 versus Online's 84.8 (Appendix I, Table 23, p. 34). Each policy has one training run; training-seed variability remains a limitation (Sections 5.1 and 6, pp. 7, 10).

W2: Recurrence validation. We shuffled estimation-half weights within field × training-stage strata, preserving the metric, weight distributions and removal budgets while changing event assignments. Across 10,000 permutations, the mean was 0.0808 and maximum 0.089, versus contextual 0.4106. The metric does not impose cross-replay correlation: the gap identifies held-out predictive information within strata (Appendix H.3, Table 21, p. 32). Q1 separately tests policy learning.

Q1: Trained terminal partial-state and constant-discount controls

Terminal Partial-State broadcasts final potential to preceding turns, omitting the current-state term with other reward settings fixed. Matched Global-Discount trains without replay, retaining positive/absolute negative credit at 0.9376/0.9050, calibrated on recorded Online DCE rollouts.

DomainPolicyPass¹Pass³Pass⁵
AirlineTerminal Partial-State73.6 ± 1.161.7 ± 2.256.0 ± 4.0
AirlineFactual76.3 ± 0.663.8 ± 1.858.0 ± 3.5
RetailTerminal Partial-State77.0 ± 1.357.0 ± 2.846.8 ± 3.7
RetailFactual80.3 ± 0.961.6 ± 1.451.2 ± 1.0
TelecomTerminal Partial-State93.7 ± 1.283.0 ± 2.974.6 ± 3.8
TelecomMatched Global-Discount93.2 ± 1.482.7 ± 2.575.2 ± 2.7
TelecomFactual96.2 ± 0.489.2 ± 0.882.7 ± 1.0
TelecomOnline Contextual DCE96.0 ± 0.789.5 ± 0.884.8 ± 0.5

Factual exceeds Terminal Partial-State across all domains and reported metrics; Online Contextual DCE exceeds Matched Global-Discount. See §§5.2–5.3 (pp. 8–9), Appendix F.1–F.3 (pp. 27–28), Table 13 (p. 26).

Q2: Message sensitivity, simulators and policy gains

Eight replays per context and intervention use each simulator's own trajectories: default Qwen3.6-35B-A3B and second simulator Qwen3.8-27B. Mean recurrence:

Message35B27B
Original acknowledgement0.1230.039
"Acknowledged."0.2160.077
"I see. Thank you for sharing that information."0.1090.037
"Please continue."0.4620.342
Selective deletion (edited subset)0.5640.366

Selective deletion approximately removes executable requests, preserving other text verbatim. Retained diagnostic facts can guide action and are part of the assistant's contribution: whole-message replacement tests dependence on the current message; deletion tests dependence on requests conditional on retained content. The alternative sentence acknowledgement stays close to the original on both simulators. The reviewer-suggested "Please continue." explicitly invites further interaction; the terse acknowledgement also raises recurrence.

Contextual targeting exceeds global and field–position matched-budget controls in all ten message–simulator settings. Using four estimation and four validation replays, selective deletion gives contextual/field–position scores of 0.822/0.615 (35B) and 0.725/0.481 (27B). See Appendix H.1, Table 19 (pp. 30–31).

Matched 27B evaluation of existing checkpoints:

Policy (27B)Pass¹Pass³Pass⁵
Factual97.3 ± 0.592.0 ± 1.587.1 ± 2.2
Online Contextual DCE98.2 ± 0.595.0 ± 1.192.1 ± 1.5

The policy gain persists: +5.0 points in Pass⁵, without retraining (Appendix H.2, Table 20, pp. 31–32).

Q3: Qualitative evidence

Appendix H.4, Table 22 (pp. 32–33) summarizes four cases linking dialogue, factual actions, replay calls and state changes. Prior dialogue identifies a poorly performing VPN. Replacing the entire assistant message requesting disconnection still yields disconnect_vpn in 7/8 branches under each of the original and alternative sentence acknowledgements. Credit falls from 0.0833 to 0.0104. In the network-setting case, the factual instruction is followed, but 0/8 branches reproduce the transition under either acknowledgement, retaining full credit. These traces connect discounting to context-supported actions across wordings.

Reviewer_Db8ROpenReview ↗
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Confidence
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Informativeness
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Presentation
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Paper summary

Summary

This paper studies process supervision for tool agents that share control of an environment with a user. It constructs target states from reference actions and measures assistant-side and user-side progress separately. These signals augment terminal GRPO, with auxiliary credit restricted to tool-call and communication tokens. Delegated credit estimation (DCE) further discounts user-side changes that recur when the preceding assistant message is replaced by a neutral acknowledgement. Experiments use a jointly trained Qwen3.5-9B policy on three domains of tau2-bench-Verified, with DCE evaluated on Telecom.

Strengths

S1. The distinction between assistant-side progress and progress made through user tools is useful. The Direct-only versus Direct + Delegated comparison keeps the direct reward and risk settings fixed and provides evidence for including user-side supervision on Telecom: Pass5 increases from 80.7 to 82.7.

S2. The paper carefully defines what its rewards measure. Appendix A distinguishes the state potential from the terminal evaluator, while Appendix D explicitly separates recurrence-adjusted credit from a mean intervention effect. These qualifications make the method easier to assess.

S3. The split-replay analysis and field-stage controls are informative. They show that contextual recurrence estimates generalize to separate replay samples at the same contexts, rather than merely reflecting noise in the samples used to compute the discount. The routing and process-strength ablations also address useful implementation choices.

Weaknesses

W1. The experiments do not establish the benefit of process supervision over the simpler terminal partial-state signal available from the same targets. At the reported gamma = 1, Appendix A.3 gives the factual return as F(x_T) - F(x_t), and explicitly notes that the experiments do not isolate an advantage over terminal partial-state supervision. Table 3 establishes a benefit over Terminal + Risk, whose task reward is binary, but does not resolve this distinction. A comparison that supplies F(x_T) to all preceding turns, with the same role weights, routing, gating, normalization, and risk settings, would clarify whether the temporal construction adds value beyond access to partial completion scores. This matters for the contribution attributed to the process-reward design.

W2. The DCE diagnostics establish selective credit removal, but its advantage for policy learning remains less clear. The matched-budget constant discounts in Appendix D.7 are evaluated on recorded trajectories, not used to train policies. Thus, they do not determine whether the Telecom improvement comes from contextual allocation or simply attenuating delegated supervision. This is relevant because the runtime audit retains 93.8% of positive factual credit. A trained constant-discount control, matching the removed positive and negative credit separately, would test the value of the contextual correction more directly.

W3. The evidence for the incremental DCE gain is limited relative to its additional computation. Each variant is trained once; the three repeats and the standard deviations in Table 12 describe evaluation of that checkpoint. Online DCE raises Telecom Pass5 from 82.7 to 84.8 while Pass1 changes from 96.2 to 96.0. The paper acknowledges reduced throughput, and Appendix D.5 reports 11.08 neutral user-turn replays per recorded trajectory, but no token or wall-clock estimate is available. A focused repeat of the factual-versus-online comparison and a measured replay-cost breakdown would help determine whether this smaller gain is reliable and practically worthwhile. Equal training steps do not provide that comparison when replay workloads differ.

Critical strengths

S1. The distinction between assistant-side progress and progress made through user tools is useful. The Direct-only versus Direct + Delegated comparison keeps the direct reward and risk settings fixed and provides evidence for including user-side supervision on Telecom: Pass5 increases from 80.7 to 82.7.

Critical weaknesses

W1. The experiments do not establish the benefit of process supervision over the simpler terminal partial-state signal available from the same targets. At the reported gamma = 1, Appendix A.3 gives the factual return as F(x_T) - F(x_t), and explicitly notes that the experiments do not isolate an advantage over terminal partial-state supervision. Table 3 establishes a benefit over Terminal + Risk, whose task reward is binary, but does not resolve this distinction. A comparison that supplies F(x_T) to all preceding turns, with the same role weights, routing, gating, normalization, and risk settings, would clarify whether the temporal construction adds value beyond access to partial completion scores. This matters for the contribution attributed to the process-reward design.

Questions for authors

Q1. What results are obtained with the matched terminal partial-state baseline described in W1?

Q2. Does contextual DCE outperform a trained constant-discount control at a comparable delegated-credit scale? The existing targeting diagnostics answer a different question.

Q3. Can the authors provide an independent training repeat for the key DCE comparison and an estimate of simulator-token or wall-clock overhead?

2 comments
AuthorsOpenReview ↗

Author Response: Trained Controls and Computational Cost

We thank the reviewer for the concrete suggestions. We trained both requested controls under the paper's 120-update protocol. Scores below are means ± evaluation SD (%); Factual denotes Direct + Delegated. All page references refer to the revised manuscript.

Q1/W1: Does temporal supervision improve over terminal partial-state supervision?

At a return discount of 1, the factual auxiliary return is the final state potential minus the current state potential. Terminal Partial-State assigns the final potential at episode end and broadcasts it to preceding turns. Role weights, terminal GRPO, auxiliary strength, risk penalties, routing, gating and normalization remain unchanged.

DomainPolicyPass¹Pass³Pass⁵
AirlineTerminal Partial-State73.6 ± 1.161.7 ± 2.256.0 ± 4.0
AirlineFactual76.3 ± 0.663.8 ± 1.858.0 ± 3.5
RetailTerminal Partial-State77.0 ± 1.357.0 ± 2.846.8 ± 3.7
RetailFactual80.3 ± 0.961.6 ± 1.451.2 ± 1.0
TelecomTerminal Partial-State93.7 ± 1.283.0 ± 2.974.6 ± 3.8
TelecomFactual96.2 ± 0.489.2 ± 0.882.7 ± 1.0

Factual achieves higher means in all three domains and metrics, with Pass⁵ gains of 2.0, 4.4 and 8.1 points on Airline, Retail and Telecom. The matched comparison supports the contribution of turn-specific current-state information beyond final partial completion. §5.2 (p. 8) explains this result; Appendix F.1 (p. 27) specifies the control, and Table 13 (p. 26) gives all five metrics with SDs.

Q2/W2: Does contextual DCE outperform a trained constant-discount control?

We trained Matched Global-Discount without replay, using retention coefficients of 0.9376 for positive credit and 0.9050 for absolute negative credit. These separately match Online Contextual DCE's retained fractions on its recorded training rollouts. Other reward-processing settings remain unchanged; calibration uses these reference rollouts, while each policy generates its own training trajectories.

Telecom policyPass¹Pass³Pass⁵
Matched Global-Discount93.2 ± 1.482.7 ± 2.575.2 ± 2.7
Factual96.2 ± 0.489.2 ± 0.882.7 ± 1.0
Online Contextual DCE96.0 ± 0.789.5 ± 0.884.8 ± 0.5

Online Contextual DCE achieves higher means at all three metrics, including 84.8 versus 75.2 in Pass⁵. Matched Global-Discount also scores below Factual. All three policies use the same centering and RMS normalization. The fixed coefficients act on delegated transitions before normalization, changing their contribution relative to direct progress. Contextual DCE additionally varies allocation by event, preserving full factual credit when neutral recurrence is zero. The trained comparison supports contextual allocation; Online's Pass⁵ gain over Factual is 2.1 points. See §5.3 (pp. 8–9) and Appendix F.2 (p. 27).

Q3/W3: What is the wall-clock overhead, and is a training repeat available?

All three runs used eight actor GPUs and two rollout GPUs. We measured completion of rollout 0 to completion of rollout 119: 119 intervals, excluding startup and the first rollout.

ConfigurationMean interval (min)Window (h)
Terminal Partial-State23.6246.84
Matched Global-Discount23.2046.01
Online Contextual DCE28.5456.60

Online Contextual DCE required 20.83–23.02% more wall-clock time, or 9.76–10.59 additional hours, than the two no-replay controls under unchanged hardware allocation.

Factual continuation averaged 22.8 min/update, close to the two no-replay controls (23.2–23.6 min). Continuing from 120 to 150 updates under the original setup took 11.38 h, exceeding the calibrated DCE overhead. Online remains higher on all five metrics, with Pass⁵ of 84.8 ± 0.5 versus 82.2 ± 0.5 (Appendix I, pp. 33–34; Table 23).

With the second user simulator (Qwen3.8-27B), Online also leads on all five metrics: Pass⁵ 92.1 ± 1.5 versus Factual's 87.1 ± 2.2 (+5.0 points) (Table 20, p. 32).

Together, the trained controls, additional-training comparison and second-simulator evaluation support contextual allocation across the tested settings. Each configuration has one training run; reported SDs describe repeated evaluation of fixed checkpoints. Training-seed variability remains a limitation (§6, p. 10).

I appreciate the authors' efforts in addressing my concerns through the additional results. After considering the rebuttal, my final rating is 2.

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

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