acceptodds
Under review as a conference paper at ICLR 2027

REVEAL: Reverse Engineering Agentic Latents from Frontier-Model Traces

Abstract

Frontier LLM agents perform complex interactive tasks, but their inference costs motivate transferring their experience to smaller open-source agents. Distillation and latent communication typically require target-model training or access to source-model internals. We study how textual frontier-model trajectories can provide reusable local controls for a frozen agent. Inspired by protocol reverse engineering, we introduce , comprising anchored states and dynamic profiles of feedback–response cycles elicited by replay in the target model. Our training-free framework, (erse ngineering gentic atents), uses these profiles and trajectory outcomes to match and select local events from successful and failed rollouts of the same task and source model. Their response-transition contrasts yield a target-specific steering direction, applied before each response. Within-benchmark evaluations on Terminal-Bench 2.1 and Humanity's Last Exam with tools report higher accuracy than unmodified agents across three targets. Representation analyses and behavioral case studies support reusing frontier-model experience as local activation control.

Primary area:
interpretability and explainable AI
Keywords:
LLM Agents, Representation Engineering, Activation Steering, Long-Horizon Decision-Making, Tool Use

Reviews

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1234this paper, Top 32%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.50 over 4 reviews, above 68% of the others.
Reviewer_5xJ8OpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
3
Soundness
1
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Paper summary

The paper studies how text-only interaction traces from a stronger closed-source model can be used to construct activation steering for a frozen open-source student. The student replays teacher trajectories offline, extracts states before and after feedback and at the beginning and end of responses, and computes U (update magnitude), C (direction retention), V (a J-lens-based ranking of content tokens), and S (cross-turn consistency). The method matches local events from successful and failed trajectories of the same task using U/V, filters them by differences in C/S, and averages the success-minus-failure differences in the student's original response-state transitions separately by layer to obtain steering directions. Online, the corresponding direction is added at a fixed layer before each response. The authors report aggregate improvements for three student models on Terminal-Bench 2.1 and a tool-enabled HLE subset, and compare against SFT on the same trajectory data in the Qwen/Terminal-Bench experiment. The evaluation is explicitly described as within-benchmark adaptation, without a task-level held-out split.

Critical strengths
  1. The method requires teacher text traces rather than access to the closed-source model's internal states, and does not update student parameters online. Turning offline state analysis into reusable activation directions is practically appealing. The paper also clearly distinguishes offline construction from online deployment.

  2. The aggregate scores in all six model-benchmark settings in Table 1 improve over the listed controls. Table 2 additionally provides a Qwen SFT comparison using the same 124 trajectories and reports fewer online tokens and interactions. These results provide initial empirical support. The paper also discloses task overlap, the rank-based interpretation of V, and the scope of its online cost accounting.

Critical weaknesses
  1. The evaluation design and incremental results do not sufficiently establish the method's reusable value. Section 3.3 explicitly uses outcome-labeled teacher trajectories from the evaluation task collection, without a task-level held-out split. For Terminal-Bench, construction uses 124 trajectories from 33 evaluation tasks, while the final scores are reported over 89 tasks. This setting is disclosed and should not be characterized as undisclosed data leakage. Nevertheless, the aggregate scores do not separate adaptation gains on construction tasks from gains on the remaining tasks. Relative to the most relevant REVEAL-Base control, the full method yields net gains of only 3, 1, and 3 tasks for Qwen, Gemma, and GPT-OSS, respectively, and the main performance table does not report uncertainty across repeated runs. Qwen's Hard score also falls from 6/30 (20%) for Base to 5/30 (16.67%). This is a Qwen-specific regression relative to Base, not a claim that every model regresses relative to its original version. It makes the stability of the complex event-selection procedure on difficult tasks particularly unclear. Table 2 does include a same-data SFT comparison, but only for Qwen/Terminal-Bench; training details, handling of failed trajectories, and the adequacy of baseline tuning still need clarification. The reported cost advantage covers only online execution after adaptation, excluding teacher sampling, offline replay, and metric computation, and therefore does not establish end-to-end cost savings.

  2. The measurement validity, selection rationale, and necessity of J-lens/V lack direct experimental support. V is a vocabulary-ranking score obtained by applying a fixed readout to the pre-response state, not an actual generation probability, content-recovery rate, or correctness measure. That distinction alone does not invalidate the method. Appendices A.4, B.3, and D.4 provide ranking-property and content-coverage diagnostics and acknowledge systematic preferences for frequent tokens and task vocabulary; these diagnostics do not establish superiority over alternative readouts. The substantive questions are whether V remains a reliable, task-relevant matching signal after controlling for lexical preferences, and whether final performance depends on the particular fitted lens, supported layers, and tokenization. V directly affects event pairing and thus the samples used to compute directions; it is not merely a visualization metric. I did not find controlled online performance comparisons that remove V and match using U alone, or replace J-lens with a direct or alternative readout. The aggregate gains cannot be attributed specifically to this measurement and filtering design.

Questions for authors

The following questions could materially affect my assessment:

  1. Please report per-task results and aggregate gains separately for the 33 Terminal-Bench tasks used for direction construction and the remaining 56 tasks, and identify which tasks were used to select metric statistics, intervention layers, strengths, and filtering thresholds. The remaining 56 tasks should not automatically be treated as a strictly held-out set. Can you provide an independent task-level split with configurations selected only on construction/development tasks?

  2. Are the net gains of 3, 1, and 3 tasks over Base stable across repeated runs? Please provide paired per-task success/failure outcomes and repeated-run intervals, and explain which task outcomes account for the Qwen Hard decrease from 6/30 to 5/30.

  3. Please compare online performance after removing V and matching only on U, and after replacing the J-lens readout. Control the number of selected events, intervention layer, strength, and tuning budget. Do controls for frequent tokens, task vocabulary, and tokenization differences change V-based matching or final gains?

  4. For the SFT baseline in Table 2, please provide training configurations, supervision/loss masks, failed-trajectory handling, and the tuning procedure, as well as a successful-trajectories-only result. Does the comparison hold for other students or HLE? If practical cost savings are claimed, please also report teacher-trajectory sampling, offline state replay, and metric-computation costs and explain their amortization.

9 comments
AuthorsOpenReview ↗

Response to Reviewer 5xJ8 (Part 1 of 5)

Thank you for the careful and detailed review, and for recognizing the practical appeal of converting teacher text into reusable activation controls without access to teacher internals, as well as the gains across all six model–benchmark settings and over same-data SFT. Your questions pinpoint the evidence needed to assess REVEAL's reusable value, and we have run the corresponding experiments. We address each point below.

W1 (part 1). The evaluation design and incremental results do not sufficiently establish the method's reusable value. Section 3.3 explicitly uses outcome-labeled teacher trajectories from the evaluation task collection, without a task-level held-out split. For Terminal-Bench, construction uses 124 trajectories from 33 evaluation tasks, while the final scores are reported over 89 tasks. This setting is disclosed and should not be characterized as undisclosed data leakage. Nevertheless, the aggregate scores do not separate adaptation gains on construction tasks from gains on the remaining tasks.

Q1. Please report per-task results and aggregate gains separately for the 33 Terminal-Bench tasks used for direction construction and the remaining 56 tasks, and identify which tasks were used to select metric statistics, intervention layers, strengths, and filtering thresholds. The remaining 56 tasks should not automatically be treated as a strictly held-out set. Can you provide an independent task-level split with configurations selected only on construction/development tasks?

Response to W1 (part 1) and Q1: We answer both parts of the question: which tasks enter each stage of construction, and how the configuration is chosen.

Which tasks are used. Table H at the end of this response (App. E.1, Table 12 in the revision) lists, for each of the 89 tasks, whether it contributes to the steering vector, whether it enters the U, V, C, and S statistics, and the outcome of each method. The tasks fall into three groups. 33 tasks (37.1%) contribute to both the statistics and the vector; 2 tasks (2.2%; cancel-async-tasks, git-multibranch) enter only the statistics; and 54 tasks (60.7%) are never used by REVEAL. No task enters the vector without also entering the statistics. In trajectory terms, REVEAL computes its statistics on 131 trajectories from 35 tasks and builds its vector from 124 trajectories of 33 tasks (424 matched event pairs), whereas Base averages over 338 trajectories covering all 89 tasks, drawn from the same sampled pool. The per-task counts are similar (3.76 vs. 3.80), so REVEAL uses less than 40% of Base's trajectories because it keeps only tasks with both successful and failed rollouts. Base has therefore seen every evaluation task during construction, while REVEAL has never seen 54 of them. Table A summarizes the outcomes by group. On these 54 tasks, REVEAL solves 22, versus 21 for Vanilla and 16 for Base, gaining six tasks over Base and losing none, even though Base's direction was built partly from these same tasks. On the 33 contributing tasks, Base solves 14 and REVEAL 12, so REVEAL's overall gain over Base comes entirely from tasks it never used.

How the configuration is chosen. No task is used to select the intervention layer, strength, or selection threshold. Steering performance depends jointly on layer and strength and is sensitive to the target model, so searching this space per task or per benchmark would both require held-out data and risk overfitting. We therefore fix one setting per target before evaluation, following common activation-steering practice: an intermediate layer at roughly half to two-thirds of the network depth (layers 40, 30, and 15 for Qwen3.6-27B, Gemma-4-31B-IT, and GPT-OSS-20B) and a single strength of α = 0.5 for all three targets. The selection rule has no threshold to tune: matching is one-to-one within each rollout pair, and the top half of matched pairs is kept.

This fixed configuration also makes the comparisons controlled. REVEAL and Base share the same layer and strength for each target, so they differ only in which success–failure contrasts enter the vector, and the gain over Base isolates the contribution of event selection. Because the setting is shared and not tuned for either method, the reported gains are a conservative estimate.

For an independent split, we rebuild the vector solely from the teacher trajectories of the 56 tasks outside the vector's construction set, recomputing all standardization statistics on these tasks and reusing the original layer, strength, and selection rule without any retuning (Table B). The rebuilt vector reaches 38.20% on all 89 tasks, 2.25 pp above Base and within 1.12 pp of the original vector. The gain thus holds with a different construction set and fixed configurations.

AuthorsOpenReview ↗

Response to Reviewer 5xJ8 (Part 2 of 5)

Table A. Qwen3.6-27B on Terminal-Bench 2.1, by role of each task in REVEAL's construction. Base uses trajectories from all 89 tasks.

Task groupNVanillaBase (Outcome-CAA)REVEALREVEAL − Base
Vector + statistics339/33 (27.27%)14/33 (42.42%)12/33 (36.36%)−6.06 pp
Statistics only20/2 (0.00%)2/2 (100.00%)1/2 (50.00%)−50.00 pp
Not used by REVEAL5421/54 (38.89%)16/54 (29.63%)22/54 (40.74%)+11.11 pp
All8930/89 (33.71%)32/89 (35.96%)35/89 (39.33%)+3.37 pp

Table B. Vector rebuilt from the 56 non-contributing tasks (Terminal-Bench 2.1, Qwen3.6-27B, accuracy %).

MethodEasyMediumHardAll
REVEAL-Base75.0041.8220.0035.96
REVEAL (rebuilt from 56 tasks)75.0049.0913.3338.20
REVEAL (original vector)100.0047.2716.6739.33

W1 (part 2). Relative to the most relevant REVEAL-Base control, the full method yields net gains of only 3, 1, and 3 tasks for Qwen, Gemma, and GPT-OSS, respectively, and the main performance table does not report uncertainty across repeated runs. Qwen's Hard score also falls from 6/30 (20%) for Base to 5/30 (16.67%). This is a Qwen-specific regression relative to Base, not a claim that every model regresses relative to its original version. It makes the stability of the complex event-selection procedure on difficult tasks particularly unclear.

Q2. Are the net gains of 3, 1, and 3 tasks over Base stable across repeated runs? Please provide paired per-task success/failure outcomes and repeated-run intervals, and explain which task outcomes account for the Qwen Hard decrease from 6/30 to 5/30.

Response to W1 (part 2) and Q2: We repeat the Qwen3.6-27B evaluation on Terminal-Bench 2.1 four times at temperature 1.0 for both REVEAL-Base and REVEAL, with the same vectors and protocol (Table C). REVEAL reaches 38.20% ± 0.92 pp (mean ± SD; 95% CI 36.74%–39.66%), versus 33.43% ± 0.56 pp for Base. The gain of 4.77 pp has a 95% CI of [3.38, 6.16] and is significant (Welch's t-test across runs, p < 0.001).

The Hard decrease does not recur across repeated runs: REVEAL averages 15.83% on Hard tasks, versus 8.33% for Base. In the original run, REVEAL and Base differ by a net of one Hard task (5/30 vs. 6/30), and Table H lists the per-task outcomes. A one-task net difference on 30 Hard tasks falls within run-to-run variation, as the repeated runs confirm.

Table C. Repeated evaluation of Qwen3.6-27B on Terminal-Bench 2.1 (accuracy %, mean ± SD over four runs, temperature 1.0).

MethodEasyMediumHardAll
REVEAL-Base56.25 ± 12.5045.45 ± 1.488.33 ± 1.9233.43 ± 0.56
REVEAL87.50 ± 14.4346.82 ± 2.2915.83 ± 3.1938.20 ± 0.92
AuthorsOpenReview ↗

Response to Reviewer 5xJ8 (Part 3 of 5)

W2. The measurement validity, selection rationale, and necessity of J-lens/V lack direct experimental support. V is a vocabulary-ranking score obtained by applying a fixed readout to the pre-response state, not an actual generation probability, content-recovery rate, or correctness measure. That distinction alone does not invalidate the method. Appendices A.4, B.3, and D.4 provide ranking-property and content-coverage diagnostics and acknowledge systematic preferences for frequent tokens and task vocabulary; these diagnostics do not establish superiority over alternative readouts. The substantive questions are whether V remains a reliable, task-relevant matching signal after controlling for lexical preferences, and whether final performance depends on the particular fitted lens, supported layers, and tokenization. V directly affects event pairing and thus the samples used to compute directions; it is not merely a visualization metric. I did not find controlled online performance comparisons that remove V and match using U alone, or replace J-lens with a direct or alternative readout. The aggregate gains cannot be attributed specifically to this measurement and filtering design.

Q3. Please compare online performance after removing V and matching only on U, and after replacing the J-lens readout. Control the number of selected events, intervention layer, strength, and tuning budget. Do controls for frequent tokens, task vocabulary, and tokenization differences change V-based matching or final gains?

Response to W2 and Q3: Table D reports both requested controls under the same candidate pool, intervention layer (40), strength (α = 0.5), and selection rule, with no variant retuned. w/o V matches events on U alone, and V (logit lens) replaces J-lens transport with the identity map while keeping everything else. The number of selected events is also identical across variants, since each rollout pair yields min(#success events, #failure events) matched pairs and the top half is kept regardless of the matching features. Removing V lowers accuracy from 39.33% to 38.20%, and the logit lens lowers it further to 37.08%, below not using V at all, with the entire loss on Hard tasks (10.00% vs. 16.67%). V's contribution therefore comes from the J-lens readout itself: an unsuitable readout misguides event pairing rather than merely failing to help.

The reason lies in how V is used. V is a rank statistic, not a generation probability (Proposition 2, App. B.3), and REVEAL uses it only to decide which events are comparable; the direction itself is computed from the target's raw response-state transitions (App. A.3, B.4). V must therefore measure how accessible the content of the whole upcoming response is from the boundary state. A logit lens reads an intermediate state as if it were already the final state, skipping the transformation applied by later layers, and a tuned lens is fitted for next-token fidelity. The J-lens averages the Jacobian transport from the source layer to the output layer (App. A.1), and thus reads what the boundary state contributes to the downstream response, which is exactly the quantity matching requires.

The lexical factors you raise are controlled by the pairing itself. Both events in a matched pair come from the same task and teacher, and are measured with the same observer, tokenizer, layer, and lens. Task vocabulary, tokenization, and the lens's preference for frequent tokens are therefore shared within each comparison and largely cancel in the matching distance. In addition, V counts each unique content token once, so repeated tokens add no weight, and as a rank statistic it is invariant to any strictly increasing transformation of the scores.

Table D. V and readout controls (Terminal-Bench 2.1, Qwen3.6-27B, accuracy %).

MethodEasyMediumHardAll
Vanilla75.0043.6410.0033.71
REVEAL-Base75.0041.8220.0035.96
w/o V (U-only matching)75.0049.0913.3338.20
V (logit lens)100.0047.2710.0037.08
REVEAL (J-lens)100.0047.2716.6739.33
Reviewer_1mqQOpenReview ↗
Rating
3(+1)
Confidence
2
Informativeness
2
Presentation
1
Soundness
2
Read review
Paper summary
  • The paper proposes a method for constructing turn-level anchor states from trajectories generated by a teacher agent and extracting agentic latents consisting of four features from these states.
  • The authors present experimental results suggesting that the analysis of these agentic latents alone can guide a target agent toward desirable behavioral patterns.
Critical strengths
  • The authors provide empirical evidence that analyzing agentic latents can help guide a target agent toward desirable behavioral patterns.
  • The paper proposes a novel knowledge transfer approach that differs from conventional fine-tuning and distillation methods.
Critical weaknesses
  • The analysis is conducted using a relatively small training dataset, and the extracted information is evaluated on the same evaluation dataset used in the analysis process. As a result, it is unclear whether the observed performance gains reflect generalizable improvements in the reasoning approach or are limited to the specific domain from which the analysis information was extracted.
  • The proposed method is evaluated on a limited set of benchmarks where the baseline performance is relatively low, and the reported improvements are modest. Therefore, it remains unclear whether the method provides broadly generalizable performance gains.
  • An ablation study is also needed to evaluate whether each feature fulfills its intended role and to assess its individual contribution to the overall performance of the proposed method.
Questions for authors
  • Evaluating the proposed method on a broader range of larger and more general-purpose benchmarks would provide a more convincing assessment of its effectiveness and generalizability.
  • The paper provides insufficient justification for the choice of the four features comprising the agentic latents: Update Magnitude, Directional Retention, Verbal Accessibility, and Cross-Cycle Consistency. This makes the proposed representation difficult to interpret. A concrete example illustrating these features in a specific anchor state could help readers better understand their definitions, rationale, and roles.
5 comments
AuthorsOpenReview ↗

Response to Reviewer 1mqQ (Part 1 of 3)

Thank you for recognizing REVEAL's distinct approach to knowledge transfer and the evidence that agentic latents can guide target behavior. We address your concerns below.

W1. The analysis is conducted using a relatively small training dataset, and the extracted information is evaluated on the same evaluation dataset used in the analysis process. As a result, it is unclear whether the observed performance gains reflect generalizable improvements in the reasoning approach or are limited to the specific domain from which the analysis information was extracted.

Response to W1: The question is whether a direction extracted from one set of tasks also helps tasks outside it. We test this directly by extracting the vector from one part of Terminal-Bench 2.1 and evaluating it on another part, without retuning any setting. Terminal-Bench covers heterogeneous task domains, including software builds, system configuration, security, data processing, scientific computing, and model training, so these splits also separate task domains rather than near-duplicate tasks. Both directions of transfer hold (Table A).

  • Construction tasks → other tasks. The original vector is built from 124 trajectories of 33 tasks. On the 56 remaining tasks, it solves 23/56 (41.07%), versus 21/56 (37.50%) for Vanilla and 18/56 (32.14%) for Base, and the entire gain over Base comes from these tasks.
  • Other tasks → all tasks. Swapping the construction set entirely, a vector rebuilt only from the 91 trajectories of those 56 tasks reaches 38.20% on all 89 tasks, 2.25 pp above Base and within 1.12 pp of the original vector.

The small construction set is therefore not a limitation but a property of the method: REVEAL turns about a hundred frontier-agent text traces into a control that transfers to tasks it has never seen, without teacher internals or target-model training. Directions re-estimated on different task subsets are also nearly orthogonal to each other (cosine −0.221 to 0.031 across Terminal-Bench difficulty levels, −0.015 across HLE categories; App. E.3), showing that each subset contributes its own feedback–response patterns rather than a benchmark-specific shortcut, and that pooling them yields a direction that transfers.

Table A. Transfer across task sets on Terminal-Bench 2.1 (Qwen3.6-27B, accuracy %).

Construction setEvaluation setVanillaBaseREVEAL
33 tasks (124 trajectories)56 unseen tasks37.5032.1441.07
56 tasks (91 trajectories)All 89 tasks33.7135.9638.20
33 tasks (124 trajectories)All 89 tasks33.7135.9639.33
AuthorsOpenReview ↗

Response to Reviewer 1mqQ (Part 2 of 3)

W2. The proposed method is evaluated on a limited set of benchmarks where the baseline performance is relatively low, and the reported improvements are modest. Therefore, it remains unclear whether the method provides broadly generalizable performance gains.

Q1. Evaluating the proposed method on a broader range of larger and more general-purpose benchmarks would provide a more convincing assessment of its effectiveness and generalizability.

Response to W2 and Q1: The low baselines reflect the difficulty of the benchmarks, not a narrow scope. Terminal-Bench 2.1 and HLE with tools are among the most demanding agent benchmarks, and they test complementary abilities. Terminal-Bench 2.1 consists of long-horizon terminal tasks ranging from software builds and system configuration to data processing and model training. HLE with tools covers 500 expert-level questions across eight subject categories, from mathematics and physics to the humanities and social sciences.

REVEAL improves all three target models on both benchmarks (Table 1). On HLE, overall accuracy rises from 18.0% to 22.0% for Qwen, from 22.4% to 25.8% for Gemma, and from 7.8% to 12.0% for GPT-OSS, i.e., relative gains of 22%, 15%, and 54%. On Terminal-Bench 2.1, Qwen improves from 33.71% to 39.33% (+17% relative). These gains come from a single fixed vector added once before each response, with no change to the target's weights.

To verify that these gains are not run-to-run noise, we repeat the Qwen3.6-27B evaluation on Terminal-Bench 2.1 four times at temperature 1.0 for both REVEAL and REVEAL-Base (Table B). REVEAL reaches 38.20% ± 0.92 pp versus 33.43% ± 0.56 pp for Base, a gain of 4.77 pp (95% CI [3.38, 6.16], Welch's t-test p < 0.001), and it leads at every difficulty level. Following your suggestion, we will extend the evaluation to an additional general-purpose agent benchmark in the final version.

Table B. Repeated evaluation of Qwen3.6-27B on Terminal-Bench 2.1 (accuracy %, mean ± SD over four runs, temperature 1.0).

MethodEasyMediumHardAll
REVEAL-Base56.25 ± 12.5045.45 ± 1.488.33 ± 1.9233.43 ± 0.56
REVEAL87.50 ± 14.4346.82 ± 2.2915.83 ± 3.1938.20 ± 0.92

W3. An ablation study is also needed to evaluate whether each feature fulfills its intended role and to assess its individual contribution to the overall performance of the proposed method.

Response to W3: Table C removes each feature group in turn: w/o U/V keeps only C/S selection, and w/o C/S keeps only U/V matching. Selection carries most of the gain. C/S selection alone reaches 38.20%, recovering two-thirds of REVEAL's improvement over Base (2.25 of 3.37 pp), while U/V matching alone recovers the remaining third (37.08%, +1.12 pp). The two partial gains add up to REVEAL's full gain, indicating that the groups contribute complementary rather than overlapping information: matching alone has no criterion for which comparable pairs matter, and selection without matching may contrast events that differ for unrelated reasons. Combined, they reach 39.33%. The example in Q2 below shows the role of each feature on a single selected pair.

Table C. Component ablations (Terminal-Bench 2.1, Qwen3.6-27B, accuracy %).

MethodEasyMediumHardAll
REVEAL-Base75.0041.8220.0035.96
w/o U/V (C/S only)75.0043.6423.3338.20
w/o C/S (U/V only)75.0043.6420.0037.08
REVEAL100.0047.2716.6739.33
AuthorsOpenReview ↗

Response to Reviewer 1mqQ (Part 3 of 3)

Q2. The paper provides insufficient justification for the choice of the four features comprising the agentic latents: Update Magnitude, Directional Retention, Verbal Accessibility, and Cross-Cycle Consistency. This makes the proposed representation difficult to interpret. A concrete example illustrating these features in a specific anchor state could help readers better understand their definitions, rationale, and roles.

Response to Q2: REVEAL builds its direction from local events, each consisting of a tool feedback and the agent's next response; the following feedback characterizes cross-cycle dynamics (§2.3). A contrast between a successful and a failed rollout is informative when the two events start from comparable conditions but process the feedback differently. This criterion determines the four features: U and V describe the starting conditions and are used for matching; C and S describe how the feedback is processed, within the response and across cycles, and are used for selection.

Table D shows such a pair from caffe-cifar-10. In both rollouts, the agent downloads CIFAR-10 over parallel connections, receives TLS connection errors, and decides to keep waiting. The successful rollout grounds this decision in observed progress: "eight connections remain active … the download should be allowed to continue." The failed rollout relies on an expectation: "the jobs may still recover." The next feedback reports 50% progress in the first rollout and another TLS error in the second, and the second rollout later finds that no segment was written.

Table D. A selected event pair from caffe-cifar-10 (Qwen3.6-27B observer, layer 30).

Trace positionSuccessful rolloutFailed rolloutProfile (success / failure)
Tool feedbackaria2 reports eight TLS handshake failures; 8 of 16 connections remain, 568 KiB/s, 13% downloaded16 parallel curl range jobs; repeated SSL_ERROR_SYSCALL, no completed segments reportedU: 0.641 / 0.629
Next response"eight connections remain active … the download should be allowed to continue""likely because the server limits concurrent connections … the jobs may still recover"V: 0.896 / 0.861; C_end: 0.093 / 0.404
Next feedback50% downloaded, 835 KiB/sAnother SSL_ERROR_SYSCALL; after the jobs are stopped, the segment directory shows total 0S: 0.861 / 0.168

U: how much the feedback changes the state. U is the magnitude of the target-state change across the feedback. Both feedbacks report TLS failures during a parallel download, and their measured updates are nearly equal (0.641 vs. 0.629): the two events receive a comparable shock.

V: how readily the next response is available. V is the mean normalized rank score of the response's unique content tokens in the J-lens readout at the feedback boundary; higher values mean the content ranks higher. Both responses decide to wait, and their content is similarly available right after the feedback (0.896 vs. 0.861).

C: how much of the feedback update persists in the response. C projects the response-start and response-end states, measured relative to the preceding response endpoint, onto the feedback-update direction; Table D reports the endpoint value C_end. The successful response retains little of the update by its end (0.093), as it moves from the failed connections to the surviving ones and a polling plan. The failed response retains more (0.404), consistent with an analysis that stays on the cause of the errors.

S: whether consecutive feedback updates align. S is the cosine between the state updates induced by the current and the next feedback. In the successful rollout, the next feedback continues the progress the response relied on (13% to 50%), and the two updates align (0.861). In the failed rollout, the next feedback brings another error instead of progress, and the updates barely align (0.168).

U and V thus make the two events comparable, while C and S separate them. Outcome labels orient the response-transition differences of such selected pairs, and hierarchical averaging turns these differences into the steering vector (§2.4; Appendices B.4–B.5). In this pair, the contrast entering the vector separates waiting grounded in observed progress from waiting grounded in an untested expectation.

We hope the additional results and the concrete example address your concerns, and would be grateful if you could reconsider your assessment. We welcome further questions.

Reviewer_nAePOpenReview ↗
Rating
4
Confidence
2
Informativeness
3
Presentation
3
Soundness
2
Read review
Paper summary

This paper proposes REVEAL. By replaying successful and failed frontier-model trajectories in a frozen target model, REVEAL extracts anchored states and dynamic profiles. REVEAL uses U and V to match local feedback–response events and C and S to select contrasting event pairs, then aggregates their response-transition contrasts into a steering direction. This direction is then used for activation steering prior to each response generation, all without requiring any updates to the target model's parameters. Experiments conducted on Terminal-Bench 2.1 and HLE with tools demonstrate improvements in overall accuracy across three different target models.

Critical strengths
  1. Reusing trajectories from a frontier model without fine-tuning the target model offers practical value. REVEAL transforms comparisons of local feedback–response events into a target-specific steering direction. Once the offline construction phase is complete, online execution requires no additional observer passes or queries to the frontier model.

  2. Results across multiple target models support the effectiveness of the proposed method. As shown in Table 1, REVEAL achieves higher overall accuracy than both Vanilla and REVEAL-Base across two benchmarks and three target models. Furthermore, the comparison using Qwen3.6-27B in Table 2 demonstrates that REVEAL attains higher accuracy than trajectory SFT while requiring fewer online tokens and interactions.

Critical weaknesses
  1. The benefits for tasks that are not included in the direction construction process remain not sufficiently clear. The authors explicitly employ a "within-benchmark adaptation" approach. In the experiments presented in Table 2, the construction trajectories are derived from 33 tasks within the evaluation collection, yet the reported accuracy is aggregated across all 89 tasks. Providing a separate breakdown of performance gains for tasks that were and were not involved in the direction construction process would offer a much clearer picture of how the steering direction performs on other tasks.

  2. The individual contributions of the various dynamic profiles are also not clear enough. While the REVEAL-Base comparison in Table 1 supports the benefits of the full approach, it does not yet isolate the respective contributions of U/V-based matching and C/S-based selection to the final task accuracy. More granular component ablations would help determine which design elements are the most critical.

Questions for authors

For the Qwen3.6-27B experiment in Table 2, could the authors report the accuracy separately for tasks that were included in the construction of the steering direction versus those that were not, along with the performance gains relative to the Vanilla model?

4 comments
AuthorsOpenReview ↗

Response to Reviewer nAeP

Thank you for your positive assessment and support. We appreciate your recognition that REVEAL turns local feedback–response comparisons into reusable controls without target-model fine-tuning or online teacher queries, and of the results across models and benchmarks, including the comparison with trajectory SFT. We address your questions below.

W1. The benefits for tasks that are not included in the direction construction process remain not sufficiently clear. The authors explicitly employ a "within-benchmark adaptation" approach. In the experiments presented in Table 2, the construction trajectories are derived from 33 tasks within the evaluation collection, yet the reported accuracy is aggregated across all 89 tasks. Providing a separate breakdown of performance gains for tasks that were and were not involved in the direction construction process would offer a much clearer picture of how the steering direction performs on other tasks.

Q1. For the Qwen3.6-27B experiment in Table 2, could the authors report the accuracy separately for tasks that were included in the construction of the steering direction versus those that were not, along with the performance gains relative to the Vanilla model?

Response to W1 and Q1: Table A splits the Qwen3.6-27B results by whether a task contributes trajectories to the vector. REVEAL improves over Vanilla on both groups: +9.09 pp on the 33 contributing tasks and +3.57 pp on the 56 non-contributing tasks. On the non-contributing tasks, it also exceeds Base by 8.93 pp (23/56 vs. 18/56), so the gain over Base comes entirely from tasks the vector was not built on.

To further show that the gain does not depend on which tasks supply the trajectories, we rebuild the vector solely from teacher trajectories of the 56 non-contributing tasks (91 trajectories) and evaluate it on all 89 tasks (Table B). The rebuilt vector reaches 38.20%, 2.25 pp above Base and within 1.12 pp of the original vector, showing that REVEAL does not rely on a particular construction subset.

Table A. Qwen3.6-27B on Terminal-Bench 2.1, split by contribution to the REVEAL vector.

Task groupNVanillaBase (Outcome-CAA)REVEALREVEAL − Vanilla
Contributing tasks339/33 (27.27%)14/33 (42.42%)12/33 (36.36%)+9.09 pp
Non-contributing tasks5621/56 (37.50%)18/56 (32.14%)23/56 (41.07%)+3.57 pp
All8930/89 (33.71%)32/89 (35.96%)35/89 (39.33%)+5.62 pp

Table B. Vector rebuilt from the 56 non-contributing tasks, Qwen3.6-27B on Terminal-Bench 2.1 (accuracy %).

MethodEasyMediumHardAll
REVEAL-Base75.0041.8220.0035.96
REVEAL (rebuilt from 56 tasks)75.0049.0913.3338.20
REVEAL (original vector)100.0047.2716.6739.33

W2. The individual contributions of the various dynamic profiles are also not clear enough. While the REVEAL-Base comparison in Table 1 supports the benefits of the full approach, it does not yet isolate the respective contributions of U/V-based matching and C/S-based selection to the final task accuracy. More granular component ablations would help determine which design elements are the most critical.

Response to W2: Table C separates matching from selection: w/o U/V keeps only C/S selection, and w/o C/S keeps only U/V matching. U/V matching pairs events with similar feedback-update magnitude and response-content accessibility; C/S selection then keeps pairs that contrast in within-response retention and cross-cycle consistency. The direction is computed from the selected response-state transitions, so the two groups determine which local comparisons enter the vector.

C/S selection is the most critical component. With C/S selection alone, accuracy reaches 38.20%, 2.25 pp above Base, whereas U/V matching alone reaches 37.08%, 1.12 pp above Base. Each group improves over Base on its own, and combining them gives the best result (39.33%): matching makes the selected contrasts comparable, and selection then picks the contrasts that carry the outcome-relevant difference. Our response to Reviewer 1mqQ (Q2) illustrates both roles on a concrete feedback–response pair.

Table C. Component ablations, Qwen3.6-27B on Terminal-Bench 2.1 (accuracy %).

MethodEasyMediumHardAll
REVEAL-Base75.0041.8220.0035.96
w/o U/V (C/S only)75.0043.6423.3338.20
w/o C/S (U/V only)75.0043.6420.0037.08
REVEAL100.0047.2716.6739.33

Thank you again for your support. We hope the additional results address your questions on task transfer and component contributions, and we welcome further discussion.

AuthorsOpenReview ↗

Looking Forward to Your Feedback and Further Discussion

Dear Reviewer nAeP,

We sincerely appreciate your positive assessment, strong support, and constructive feedback on our work.

As the discussion deadline approaches, we would be grateful if you could review our responses when you have a chance and let us know if any questions or concerns remain. We would be happy to provide further clarification or additional information if needed.

Thank you again for your time, thoughtful feedback, and continued support.

Sincerely, Authors of Paper 29213

AuthorsOpenReview ↗

Kind Reminder Before the Discussion Deadline

Dear Reviewer nAeP,

Thank you again for your positive assessment and constructive suggestions. As fewer than 24 hours remain in the author–reviewer discussion phase, we would be grateful if you could take a brief look at our responses, which report the requested breakdown by construction and non-contributing tasks and the component ablations, and let us know whether any questions remain.

We sincerely appreciate your support of this work.

Best regards, Authors of Paper 29213

Thank you for the detailed response and additional experiments, which help address my concerns. I maintain my positive assessment and original rating.

Reviewer_WmwiOpenReview ↗
Rating
2
Confidence
4
Informativeness
1
Presentation
2
Soundness
1
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Paper summary

REVEAL uses textual trajectories from a frontier model to construct activation-steering directions for frozen target agents. It replays the trajectories in each target, profiles local feedback–response events, and selects contrasts between successful and failed rollouts of the same task. These contrasts are averaged into a target- and benchmark-specific direction, injected once before each response. The paper reports accuracy gains across three targets on Terminal-Bench 2.1 and tool-assisted HLE, together with lower online interaction costs than trajectory SFT for Qwen.

Critical strengths
  1. The method turns accessible teacher text and rollout outcomes into a compact control for a frozen target. It requires neither teacher hidden states nor an online teacher call. This is a practical way to reuse expensive agent experience, and the positive accuracy differences across all six target–benchmark combinations make the approach worth investigating.
  2. The endpoint and representation analyses provide a concrete framework for examining long agent traces. The paper also distinguishes target replay representations from teacher internals and acknowledges that descriptive correlations do not establish the causal value of event selection. These limits help make the analyses interpretable, even though the behavioral evidence remains incomplete.
Critical weaknesses
  1. Extracting a shared direction from successful and failed experiences conceptually resembles meta-learning, but the paper does not directly test its stability across independently sampled teacher trajectories or different task subsets. Cross-model correlations of scalar descriptors do not establish the stability or transferability of the actual steering vector.
  2. The vector is extracted by replaying teacher text through the target, whose autonomous history may progressively diverge from the teacher’s path. Table 1 shows aggregate gains, but does not examine how intervention effects vary with prefix source, interaction length, or divergence. Its sustained effectiveness over long trajectories therefore remains unclear.
  3. Statistical significance over REVEAL-Base is not established on TerminalBench. The net gains are only 3, 1, and 3 solved tasks out of 89. Assuming one binary outcome per task and method, the minimum possible two-sided exact McNemar p-values are 0.25, 1.00, and 0.25. Variability across repeated evaluations at temperature = 1.0 is also unreported, leaving the gains’ stability unclear. Although I have given the paper a score of 2, I remain unconvinced by its core idea and do not intend to raise my score.
Questions for authors
  1. Could you re-estimate the vectors using independently sampled teacher trajectories and different task subsets, report their directional consistency, and test whether they consistently improve performance on tasks excluded from vector construction? How do these results compare with shuffled success/failure labels?
  2. Could you compare subsequent performance with and without intervention while holding each prefix fixed, separately for teacher-provided and target-generated prefixes, and report gains by interaction round or trajectory length? Does the direction remain effective after the target’s history has substantially diverged from the teacher’s path?
  3. Could you provide paired task-level outcomes, repeat evaluation at temperature = 1.0, and report confidence intervals and paired significance tests for gains over REVEAL-Base? Please also evaluate at temperature = 0 or 0.1 to assess sensitivity to sampling randomness.
4 comments
AuthorsOpenReview ↗

Response to Reviewer Wmwi (Part 1 of 2)

Thank you for recognizing that REVEAL reuses frontier-model experience without teacher internals or online teacher calls, and that it improves all six model–benchmark settings. We address your concerns below.

W1. Extracting a shared direction from successful and failed experiences conceptually resembles meta-learning, but the paper does not directly test its stability across independently sampled teacher trajectories or different task subsets. Cross-model correlations of scalar descriptors do not establish the stability or transferability of the actual steering vector.

Q1. Could you re-estimate the vectors using independently sampled teacher trajectories and different task subsets, report their directional consistency, and test whether they consistently improve performance on tasks excluded from vector construction? How do these results compare with shuffled success/failure labels?

Response to W1 and Q1: To test whether the direction depends on the particular trajectories used to build it, we rebuild the vector from entirely different teacher trajectories: those of the 56 Terminal-Bench tasks outside the original 33-task construction set. The rebuilt vector reaches 38.20% on all 89 tasks, close to the original vector (39.33%) and above Base (35.96%) (Table A). REVEAL's gain therefore does not depend on which tasks supply the trajectories. The original vector likewise improves tasks excluded from its construction: on the 56 tasks that contribute no trajectories, it solves 23/56 (41.07%), versus 21/56 (37.50%) for Vanilla and 18/56 (32.14%) for Base.

To compare directions, we re-estimate vectors on task subsets of Terminal-Bench 2.1 (three difficulty levels) and HLE with tools (eight subject categories), and compute the signed cosine between the actual steering vectors, averaged over layers 0–62 (Tables B and C). Base, which averages all success–failure differences, yields largely the same direction across subsets (0.821 for Medium–Hard; 0.432 across the 28 HLE category pairs). REVEAL's event-selected contrasts are nearly orthogonal across subsets (−0.221 to 0.031 across difficulty pairs; −0.015 across HLE categories). Rather than recovering one generic success direction, each task group contributes the feedback–response patterns specific to it, and pooling these patterns over a sufficiently broad task set yields a vector that generalizes, as the rebuilt vector shows.

Regarding shuffled labels: outcome labels in REVEAL only set the sign of each selected contrast. Event matching and selection use U, V, C, and S, which are computed without labels. Shuffling the labels makes each contrast's sign random, so the averaged vector cancels toward zero and reduces to the unsteered model. Base serves as the informative control here: it uses the same labels and trajectories without event selection, and REVEAL outperforms it in all six model–benchmark settings.

Table A. Vector rebuilt from the other 56 tasks (Terminal-Bench 2.1, Qwen3.6-27B, accuracy %).

MethodEasyMediumHardAll
REVEAL-Base75.0041.8220.0035.96
REVEAL (rebuilt from 56 tasks)75.0049.0913.3338.20
REVEAL (original vector)100.0047.2716.6739.33

Table B. Cross-difficulty signed cosine between subset vectors (Terminal-Bench 2.1, Qwen3.6-27B).

MethodEasy–MediumEasy–HardMedium–Hard
Base (Outcome-CAA)0.3230.4380.821
REVEAL0.0110.031−0.221

Table C. Mean signed cosine of each category vector with the other seven (HLE with tools, Qwen3.6-27B).

MethodBio/MedChemCS/AIEngHum/SocMathOtherPhysAll 28 pairs
Base (Outcome-CAA)0.4150.4840.3870.1310.5800.5260.5030.4320.432
REVEAL−0.0480.024−0.0080.018−0.014−0.028−0.000−0.061−0.015
AuthorsOpenReview ↗

Response to Reviewer Wmwi (Part 2 of 2)

W2. The vector is extracted by replaying teacher text through the target, whose autonomous history may progressively diverge from the teacher's path. Table 1 shows aggregate gains, but does not examine how intervention effects vary with prefix source, interaction length, or divergence. Its sustained effectiveness over long trajectories therefore remains unclear.

Q2. Could you compare subsequent performance with and without intervention while holding each prefix fixed, separately for teacher-provided and target-generated prefixes, and report gains by interaction round or trajectory length? Does the direction remain effective after the target's history has substantially diverged from the teacher's path?

Response to W2 and Q2: REVEAL never requires the target to follow the teacher's path. The teacher text is used only offline: during construction (§§2.2–2.4), the frozen target reads recorded teacher trajectories through teacher-forced forward passes, and U/V matching and C/S selection turn local event contrasts into a steering direction. Online, this fixed direction is added to the target's current prefix-boundary state before each response (§2.4, Eq. 11). Every online prefix is therefore target-generated: it consists of the target's own previous actions and the latest environment feedback, with no teacher prefix, teacher query, or alignment with the teacher's actions. Teacher-provided prefixes never occur at deployment, so the setting the reviewer asks about, a history that has diverged from the teacher's path, is the only one in which REVEAL operates. Figure 6 illustrates this on count-dataset-tokens: REVEAL writes a different counting script from the teacher, checks competing counting conventions, and reaches the correct answer, 79,586, reusing the teacher's verification pattern while following its own action sequence.

To assess whether the effect persists as the target's history grows, we group tasks by the number of rounds Vanilla needs (Table D). The gains grow with interaction length: REVEAL improves over Vanilla by +5.56 pp on tasks with 21–40 rounds and +9.09 pp on tasks with more than 40 rounds, where the target's own history extends furthest. On the five long tasks that REVEAL solves, it also needs fewer rounds than Vanilla (e.g., 106 → 28).

Table D. Qwen3.6-27B on Terminal-Bench 2.1 by Vanilla interaction rounds (77 tasks with recorded lengths).

Vanilla roundsTasksVanillaREVEALREVEAL − Vanilla
0–102815/28 (53.57%)16/28 (57.14%)+3.57 pp
11–202011/20 (55.00%)10/20 (50.00%)−5.00 pp
21–40182/18 (11.11%)3/18 (16.67%)+5.56 pp
> 40111/11 (9.09%)2/11 (18.18%)+9.09 pp
All7729/77 (37.66%)31/77 (40.26%)+2.60 pp

W3. Statistical significance over REVEAL-Base is not established on TerminalBench. The net gains are only 3, 1, and 3 solved tasks out of 89. Assuming one binary outcome per task and method, the minimum possible two-sided exact McNemar p-values are 0.25, 1.00, and 0.25. Variability across repeated evaluations at temperature = 1.0 is also unreported, leaving the gains' stability unclear.

Q3. Could you provide paired task-level outcomes, repeat evaluation at temperature = 1.0, and report confidence intervals and paired significance tests for gains over REVEAL-Base? Please also evaluate at temperature = 0 or 0.1 to assess sensitivity to sampling randomness.

Response to W3 and Q3: We repeat the Qwen3.6-27B evaluation on Terminal-Bench 2.1 four times at temperature 1.0 for both REVEAL and REVEAL-Base, with the same vectors and protocol (Table E). REVEAL reaches 38.20% ± 0.92 pp (mean ± SD; 95% CI 36.74%–39.66%), versus 33.43% ± 0.56 pp for Base. The gain of 4.77 pp has a 95% CI of [3.38, 6.16] and is significant (Welch's t-test, p < 0.001), and REVEAL leads at every difficulty level. At temperature 0, REVEAL reaches 37.08%, within 1.2 pp of its temperature-1.0 mean, so the gain does not depend on sampling randomness. Paired task-level outcomes of the original runs, split by contribution to the vector, are reported in our response to Reviewer 5xJ8 (W1/Q1).

Table E. Terminal-Bench 2.1 accuracy (%) of Qwen3.6-27B. Temperature-1.0 rows report mean ± SD over four runs.

MethodEasyMediumHardAll
REVEAL-Base (T = 1.0)56.25 ± 12.5045.45 ± 1.488.33 ± 1.9233.43 ± 0.56
REVEAL (T = 1.0)87.50 ± 14.4346.82 ± 2.2915.83 ± 3.1938.20 ± 0.92
REVEAL (T = 0.0)75.0047.2713.3337.08

We hope these additional results clarify the stability and scope of REVEAL, and we welcome further discussion.

AuthorsOpenReview ↗

Looking Forward to Your Feedback and Further Discussion

Dear Reviewer Wmwi,

We hope you are doing well. We sincerely appreciate the thoughtful feedback and constructive suggestions you have provided.

As the discussion deadline approaches, we would be grateful if you could review our responses when you have a chance and let us know whether any concerns remain. Your feedback would allow us sufficient time to address additional questions and provide any further information that would support the discussion.

If our rebuttal and manuscript revisions have resolved your concerns, we would sincerely appreciate your consideration of raising your rating.

Thank you again for your time and consideration. We look forward to continuing the discussion with you.

Sincerely, Authors of Paper 29213

AuthorsOpenReview ↗

Kind Reminder Before the Discussion Deadline

Dear Reviewer Wmwi,

Thank you again for your time and thoughtful review. As fewer than 24 hours remain in the author–reviewer discussion phase, we would be grateful if you could take a brief look at our responses and revisions, and let us know whether any concerns remain so that we can still address them.

If our responses have resolved your concerns, we would sincerely appreciate your consideration in updating your assessment.

Best regards, Authors of Paper 29213

Comments on the paper

1 comment
AuthorsOpenReview ↗

Revision Summary

We sincerely thank all reviewers for their detailed and constructive feedback. We have uploaded a revised manuscript, with the main additions marked in blue. Below we summarize the revisions, grouped by the reviewer whose comments prompted them. All section, figure, and table numbers refer to the revised manuscript.

Reviewer Wmwi

  • App. E.2 (Table 4, new). A direction rebuilt solely from the 91 trajectories of the 56 non-contributing Terminal-Bench tasks, reusing the original layer, strength, and selection rule without retuning, and evaluated on all 89 tasks (W1, Q1).
  • App. E.3 (Table 5, new). Directional consistency of directions re-estimated on task subsets, covering the three Terminal-Bench difficulty levels and the eight HLE categories, compared with REVEAL-Base. We also explain why shuffled outcome labels reduce REVEAL to the unsteered model, and why REVEAL-Base serves as the label-preserving control (W1, Q1).
  • App. E.4 (Table 6, new). Gains stratified by interaction length, with a clarification that every online prefix is generated by the target rather than the frontier model (W2, Q2).
  • App. E.5 (Table 7, new). Four repeated runs at temperature 1.0 for REVEAL and REVEAL-Base, with confidence intervals and a significance test, and an evaluation at temperature 0 (W3, Q3).

Reviewer nAeP

  • App. E.1 (Table 3, new). Accuracy and gains over Vanilla and REVEAL-Base, split by each task's role in constructing the direction (W1, Q1).
  • App. E.2 (Table 4, new). The direction rebuilt from the 56 non-contributing tasks (W1).
  • App. E.6 (Table 8, new). Component ablations isolating UU/VV matching (w/o CC/SS) and CC/SS selection (w/o UU/VV) (W2).

Reviewer 1mqQ

  • App. E.1 and E.2 (Tables 3 and 4, new). Gains on non-contributing tasks and with a fully replaced construction set (W1).
  • App. E.5 (Table 7, new). Repeated runs and significance, supporting the reliability of the gains (W2).
  • App. E.6 (Table 8, new). Component ablations showing the contribution of each feature group (W3).
  • App. E.7 (Table 9, new). A worked example from caffe-cifar-10 that aligns the frontier model's actual text with the measured UU, VV, CC, and SS, illustrating the definition, rationale, and role of each feature (Q2).

Reviewer 5xJ8

  • App. E.1 (Tables 3 and 12, new). Per-task outcomes of all 89 tasks with each task's role in construction (direction and statistics, statistics only, or unused), group-level results, and the trajectories used by REVEAL and REVEAL-Base. REVEAL never uses 54 tasks, all of which REVEAL-Base uses (W1, Q1).
  • Sec. 3.3, App. E.1, and App. E.2 (Table 4, new). We state that the intervention layer and strength are fixed per target rather than selected on any task, are shared by REVEAL and REVEAL-Base, and are reused without retuning for a direction rebuilt from non-contributing tasks (W1, Q1).
  • App. E.5 (Table 7, new). Repeated-run intervals and significance over REVEAL-Base, and the net one-task Hard difference (6/30 vs. 5/30) in the original runs, which does not recur across repeated runs (W1, Q2).
  • App. E.6 (Table 8, new). Online performance with UU-only matching (w/o VV) and with a logit-lens readout, under the same candidate pool, layer, strength, and number of selected events (W2, Q3).
  • App. A.3. We explain how sharing the task, source model, observer, tokenizer, and lens within each matched pair limits the effect of frequent tokens, task vocabulary, and tokenization on VV-based matching (W2, Q3).
  • App. E.8 (Tables 10 and 11, new). The SFT configuration, SFT on successful trajectories only, SFT on Gemma-4-31B-IT, and an end-to-end cost comparison covering trajectory collection, offline adaptation, and online inference (W1, Q4).
  • Sec. 3.4 (Finding 2). We state that REVEAL's offline adaptation is a single gradient-free replay, so its end-to-end cost is also lower than that of SFT (Q4).

Other changes

  • App. E (Additional Experiments, Tables 3–12) is new. Existing sections, appendices, figures, and Tables 1–2 keep their original numbers, and the main text keeps its original length.
  • We also made minor wording edits for clarity, which do not change any claim or result.

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

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