acceptodds
Under review as a conference paper at ICLR 2027

SkillGRACE: Group-Relative Advantage-Guided Contrastive Editing of Agent Skills

Abstract

Large language models (LLMs) have evolved from text generators into agents that reason, use tools, and interact with environments, while skills improve their behavior through reusable instructions without updating model parameters. In this paper, we argue that existing skill optimizers do not fully exploit the information in task trajectories: each execution of a validation task provides only a single reward signal to guide patch selection, and their computational cost increases substantially as task execution becomes more complex. Moreover, aggregating evidence across diverse tasks can obscure the behaviors responsible for success or failure, making the proposal of effective candidate edits challenging and thereby highly dependent on strong external LLM editors. To address these limitations, we introduce SkillGRACE, which formulates skill editing as group-relative policy optimization over an external language policy. To enable discrete skill optimization, SkillGRACE samples multiple rollouts for each task and leverages group-relative advantages to construct same-task contrastive evidence for patch generation. The proposed patches are then selected by replaying these trajectories under candidate skills, eliminating the need for a separate validation set and substantially reducing optimization cost. Notably, since each skill patch is informed by contrastive evidence from same-task rollouts, SkillGRACE enables the executor itself to generate effective edits without requiring a powerful external LLM editor. Across three benchmarks, SkillGRACE consistently outperforms the strongest baseline in each setting. Across three benchmarks, SkillGrace outperforms SkillOpt by 2.8 percentage points on average and by up to 6.8 points, while using 77.6% fewer optimization rollouts overall. An ALFWorld ablation further shows that same-task contrastive evidence improves success by 13.4 points over cross-task collections, highlighting its importance for effective self-evolution.

Primary area:
foundation or frontier models, including LLMs
Keywords:
prompt optimization, agent skills, agents, evolutionary algorithm, non-parametric optimization, self-improving AI

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_SiRGOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper proposes SkillGrace, a skill optimization method that leverages same-task contrastive evidence from grouped rollouts to generate and evaluate local skill patches via trajectory replay. By employing advantage-weighted scoring, gain checks, and KL constraints, it updates skills without modifying model parameters or requiring additional environment interactions. Experiments on SearchQA, SpreadsheetBench, and ALFWorld show a 2.8% average improvement over SkillOpt with 77.6% fewer rollouts, validating the effectiveness of same-task contrastive learning and replay-based optimization.

Critical strengths
  1. The motivation is clear, and the optimization framework is coherently designed. To address the limited use of trajectory information and costly candidate patch evaluation, this paper proposes a targeted overall optimization framework.

  2. The replay-based candidate patch screening mechanism improves interaction efficiency. By reusing existing trajectories for patch evaluation, it reduces total optimization rollouts by 77.6%.

  3. The method achieves positive results on multiple-agent tasks. Across three benchmarks, the average score improves by 2.8 percentage points over SkillOpt, and the ablation preliminarily supports the same-task contrast mechanism.

Critical weaknesses
  1. The relationship between the replay objective and task performance is unclear. The paper uses an advantage-weighted token-likelihood objective to select patches, but its relationship to actual task rewards remains unclear.

  2. The efficiency evaluation is incomplete. The paper mainly measures optimization rollout counts, excluding the inference costs of patch generation and trajectory replay. Thus, it does not capture end-to-end computational cost.

  3. The ablation study is limited. It compares same-task and cross-task contrastive evidence but does not isolate the contributions of replay screening and other constraints (such as the KL constraint and ESS checks).

  4. The experimental scope is limited. The evaluation uses one executor across three benchmarks, leaving cross-model generalization unclear. The initial skill's construction is also insufficiently specified, limiting reproducibility.

Questions for authors

See weaknesses. I am open to raising my score if the authors provide convincing responses to the concerns raised.

3 comments

Thank you for the constructive feedback. We address each concern below.

W1. The relationship between the replay objective and task performance is unclear. The paper uses an advantage-weighted token-likelihood objective to select patches, but its relationship to actual task rewards remains unclear.

Higher replay objective were positively correlated with better task performance. To investigate the relationship between replay objective and task performance, we added Table 5 (line 444) to report how gains in the replay objective and validation reward correlate with reward gains on test set. Appendix D (line 1332) defines these gains and details the scoring protocol.

Pearson rr with fresh test reward gainIter. 5Iter. 15Iter.25Mean
Replay objective gain0.2970.4400.5130.417
Validation reward gain0.3080.2150.3220.282

Replay had a higher mean correlation than validation across these iterations, although validation was slightly better at iteration 5. This supports replay as a useful selection signal without interactions with environment.

W2. The efficiency evaluation is incomplete. The paper mainly measures optimization rollout counts, excluding the inference costs of patch generation and trajectory replay. Thus, it does not capture end-to-end computational cost.

We added Appendix F (line 1404) to account for total usage beyond rollouts. The token totals include patch generation and trajectory replay. Across the three benchmarks, SkillGrace uses 77.8% fewer optimization rollouts and processes 32.3% fewer optimization tokens overall than SkillOpt.

BenchmarkSkillOpt rolloutsSkillGrace rolloutsSkillOpt tokensSkillGrace tokens
SearchQA10,52096043.7M9.5M
SpreadsheetBench92096061.2M52.3M
ALFWorld1,39693653.1M45.1M
Avg.4,27995252.7M35.6M

We report both measures because teacher-forced replay still uses model inference, but scores stored trajectories without generating new actions, rerunning tools, or recomputing rewards. These measurements quantify token use and environment interactions separately.

W3. The ablation study is limited. It compares same-task and cross-task contrastive evidence but does not isolate the contributions of replay screening and other constraints (such as the KL constraint and ESS checks).

In light of your suggestion, we have conducted an additional replay-selection ablation study to test whether replay improves final task performance beyond what the patch generation procedure achieves on its own. We held the initial skill and patch generation procedure fixed and compared random, validation-gated, and replay-based patch selection. The results are shown in Table 4 (line 433) of the revised manuscript and detail the experimental protocol in Appendix D (line 1332). It can be observed that replay improves test success on SpreadsheetBench by 7.5 percentage points over random selection and 4.6 points over validation-gated selection. Replay thus outperforms both alternatives on SpreadsheetBench, showing that stored trajectories provide a useful signal for patch selection without requiring fresh rollouts.

Patch selectionSpreadsheetBench · Qwen3.6–27BALFWorld · Qwen3.6–35B-A3B
No skill38.6%70.1%
Random51.4%92.5%
Validation-gated54.3%91.0%
Replay58.9%92.5%

W4. The experimental scope is limited. The evaluation uses one executor across three benchmarks, leaving cross-model generalization unclear. The initial skill's construction is also insufficiently specified, limiting reproducibility.

To address your concern, we evaluated another model Qwen3.6-27B, updated Table 1 (line 325)

Skill sourceEditorSearchQASpreadsheetBenchALFWorldAvg.
No skill—76.538.676.163.7
LLM skillGPT-5.579.541.781.367.5
Trace2SkillSelf81.153.293.375.9
SkillOptGPT-5.582.055.495.577.6
SkillGraceSelf82.758.997.879.8

With Qwen3.6–27B, SkillGrace uses the executor itself as the editor and achieves the highest observed score on all three benchmarks. It also outperforms SkillOpt, the strongest baseline, by 0.7, 3.5, and 2.3 points on SearchQA, SpreadsheetBench, and ALFWorld, respectively, while using Qwen3.6–27B itself as the editor rather than GPT‑5.5. Together with the original results, these findings show that SkillGrace’s skill optimization procedure is effective across models without requiring a separate stronger editor.

Initial Skill's Construction: We have added the initial skill for each benchmark to Appendix C (line 1198).

Many thanks for addressing my comments. I will raise my rating to 3.

Thank you for your thoughtful feedback and for raising your rating to 3. Your questions and suggestions helped us clarify our contributions and strengthen the paper.

Reviewer_fCE3OpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper proposes SkillGrace to optimize a reusable text skill for a frozen LLM agent. It collects multiple trajectories per task, uses within-task relative rewards to guide atomic skill edits, and selects edits through teacher-forced replay with an empirical KL constraint. Experiments with a Qwen3.6–35B-A3B executor on SearchQA, SpreadsheetBench, and ALFWorld report higher test scores and fewer optimization environment rollouts than SkillOpt.

Critical strengths
  1. The method addresses a practical bottleneck in skill optimization. Grouped trajectory evidence and replay offer a clear way to reduce full environment executions (Algorithm 1; Table 2).

  2. The method reports gains across three task types using a frozen executor that also serves as its editor (Table 1). This supports the practical value of self-editing text skills.

Critical weaknesses
  1. The efficiency comparison reports fewer environment rollouts, but not the total cost of optimization or deployment (Table 2). A proposal can require several editor generations and replay evaluations (Table 5), yet actual token use, compute time, and test-time overhead are absent. This makes the quality-per-compute benefit difficult to assess. The ALFWorld rollout count in Table 2 also appears inconsistent with the batching protocol in Appendix B and should be reconciled.

  2. Replay evaluates a candidate skill on actions from trajectories collected under the old skill, including their original reasoning and environment history (Eq. 4). This is an efficient selection proxy, but a candidate may behave differently when it generates a fresh trajectory. The paper does not test whether replay scores predict online returns for proposed edits, so it is unclear how much of the observed gain is attributable to reliable replay selection rather than to the editor's proposals.

  3. The ALFWorld ablation changes more than whether compared trajectories come from the same task: the cross-task editor receives separate success-only and failure-only requests and does not use the same zero-advantage exploration (Table 3; Appendix C). The reported 13.4-point gap therefore cannot be assigned specifically to same-task contrast. Since the group-relative and clipped objectives draw on established GRPO/PPO ideas, isolating what the new skill-level construction contributes is important. Uncertainty estimates would also help interpret the smaller gains on SearchQA and ALFWorld.

Questions for authors
  1. Could the authors report actual input/output tokens and compute or wall-clock time for the executor, editor, and replay stages, along with final-skill test-time overhead? This would make the quality-versus-total-cost comparison assessable.

  2. For a representative sample of accepted and rejected edits, how well do replay scores or rankings agree with their online task returns under fresh execution? Even a limited diagnostic would help establish whether teacher-forced replay is a useful selection signal beyond the quality of the editor's proposals.

  3. Could the authors compare same-task and cross-task evidence while keeping the success/failure mix, exploration slots, and editor budget as similar as possible? This would clarify whether task pairing drives the ALFWorld result.

3 comments

Thank you for the constructive feedback. We address each question in order below.

W1&Q1. Could the authors report actual input/output tokens and compute or wall-clock time for the executor, editor, and replay stages, along with final-skill test-time overhead? This would make the quality-versus-total-cost comparison assessable.

Optimization Cost and Test-Time Overhead: We added Appendix F (line 1404) to report aggregate optimization token usage alongside rollout counts. The totals include input and output tokens from rollout and patch generation, plus tokens processed during teacher-forced replay. Across the three benchmarks, SkillGrace uses 77.8% fewer optimization rollouts and 32.3% fewer optimization tokens overall than SkillOpt.

BenchmarkSkillOpt rolloutsSkillGrace rolloutsSkillOpt tokensSkillGrace tokens
SearchQA10,52096043.7M9.5M
SpreadsheetBench92096061.2M52.3M
ALFWorld1,39693653.1M45.1M
Avg.4,27995252.7M35.6M

We did not include wall-clock time because we did not benchmark the two methods under matched serving conditions. SkillGrace runs its Qwen editor through vLLM, whereas SkillOpt calls GPT-5.5 through an API. A timing comparison in this setup would reflect both the optimization methods and differences in serving and API latency.

Reconciling the ALFWorld Rollout Count: We updated Table 2 to report 936 ALFWorld rollouts: 27 full batches of 32 and three partial batches of 24, one at the end of each sampling cycle, as described in Appendix B.

W2&Q2. For a representative sample of accepted and rejected edits, how well do replay scores or rankings agree with their online task returns under fresh execution? Even a limited diagnostic would help establish whether teacher-forced replay is a useful selection signal beyond the quality of the editor's proposals.

Thank you for your insightful suggestion! To investigate the relationship between replay objective and task performance, we added Table 5 (line 444) in our revised manuscript to report how gains in the replay objective proposed in SkillGrace and validation reward correlate with reward gains over iterations on the test set. Appendix D (line 1332) defines these gains and details the scoring protocol. It can be observed that the replay objective correlates positively with fresh test reward gains. Moreover, it can also be observed that replay objective’s correlation is higher than that of validation. This supports replay as a useful selection signal without interactions with the environment.

Pearson rr with fresh test reward gainIter. 5Iter. 15Iter.25Mean
Replay objective gain0.2970.4400.5130.417
Validation reward gain0.3080.2150.3220.282

W3&Q3. Could the authors compare same-task and cross-task evidence while keeping the success/failure mix, exploration slots, and editor budget as similar as possible? This would clarify whether task pairing drives the ALFWorld result.

Thank you for your comments. To clarify whether task pairing drives the ALFWorld result, we added an additional comparison in Appendix E (line 1369) in our revised manuscript that ****keeps the trajectories, success/failure mix, and editor budget fixed, and the mean test success gains over the unchanged parent are reported in Table 9 (line 1394). It can be observed that each patch of same-task pairing improved mean test success by 0.9 percentage points more than cross-task pairing in a matched ALFWorld diagnostic.

Evidence pairingMean test success gain over unchanged parent
Cross-task+0.2 percentage points
Same-task+1.1 percentage points

The results support same-task pairing for skill editing: patches generated from same-task evidence improved test success by 1.1 percentage points on average over the unchanged parent skill, compared with 0.2 points for patches generated from cross-task evidence. To reduce uncertainty from relying on a single checkpoint, we evaluated the effect at five optimization iterations.

Thank you for the detailed rebuttal and additional experiments. The expanded token accounting, including editor generation and replay, substantially alleviates my concern about optimization cost. The replay-correlation analysis and the more controlled same-task pairing comparison also provide useful evidence for the proposed mechanisms. These additions partially address my concerns and strengthen the paper’s empirical support.

However, some important uncertainties remain. I would appreciate further clarification on the SkillOpt comparison protocol, particularly whether it was re-optimized under the same harness and how the initial skills were constructed. For the new diagnostic experiments, please clarify the candidate sample sizes, how candidates and parent skills were matched, and the variability of the reported effects. My assessment has moved toward the borderline, but these remaining uncertainties prevent me from directly raising my rating to acceptance at this point.

Thank you for your follow up questions.

Fair comparison with SkillOpt. To ensure a fair comparison, we strictly follow the benchmark setup in SkillOpt’s official repository. For each benchmark and executor setting, both methods start from the same initial skill and use the same executor configuration, dataset splits, and benchmark adapter. Both run in direct-chat mode, which SkillOpt also uses for Qwen3.6–35B-A3B. We evaluate the learned skills on the same held-out tasks using the same scoring protocol. Thus, Table 1 compares the two optimization methods under matched execution and evaluation conditions. We added a paragraph, “Fair comparison with SkillOpt” (line 734) to Appendix B to clarify this point. To make the initialization reproducible, we have added the initial skill for each benchmark to Appendix C (line 1198).

Regarding skill initialization, for each benchmark, we generated the initial skill in a single GPT-5.5 call and used that exact same skill to initialize both SkillOpt and SkillGrace. We also evaluated it before optimization and reported its score as “LLM Skill” in Table 1. The higher scores achieved by our proposal show that one-shot generation leaves substantial room for improvement.

Protocol of diagnostic experiment. We used five saved outer iterations and generated 4-8 candidate patches per iteration (5.2 patches on average). At each iteration, both conditions shared the same parent skill, the rollout trajectories collected under that skill, and the same anchors. The only change was whether each anchor’s opposite-outcome comparator came from the same task or a different task. We applied each patch independently to its unchanged parent and evaluated the resulting candidate skill on all 134 held-out ALFWorld tasks. Each candidate’s gain was its test success rate minus its own parent’s success rate. In light of your question, we have also included the standard deviation to reflect the variability of the reported effects, as shown in Table 9.

Reviewer_VmcVOpenReview ↗
Rating
3
Confidence
3
Informativeness
3
Presentation
3
Soundness
3
Read review
Paper summary

This paper introduces SkillGRACE, a method for optimizing agent skills without updating model weights. The authors formulate skill editing as group-relative policy optimization over an external language policy. For each task, the agent samples multiple rollouts; within-task standardized rewards yield group-relative advantages (GRPO-style), which organize trajectories into same-task contrastive evidence. This evidence guides an editor (in this paper, the executor model itself) to propose atomic add/remove/replace patches. Candidate patches are then selected by replaying stored trajectories under candidate skills with a clipped, advantage-weighted likelihood objective, eliminating a separate validation set and fresh environment interaction. Experiments on SearchQA, SpreadsheetBench, and ALFWorld with a Qwen3.6–35B-A3B executor show SkillGRACE outperforming SkillOpt while using much fewer optimization rollouts, despite SkillOpt using a strong editor.

Critical strengths

The idea is well motivated, and the methodological design is elegant. Mapping GRPO/PPO machinery (group-relative advantages, clipped surrogate, KL trust region, epoch reuse) onto discrete text-space skill editing is conceptually clean.

Scoring candidate skills by teacher-forced likelihood shifts on already-stored trajectories requires no new rollouts, no validation set, and no environment interaction; it also enables multiple local updates per batch. This turns each expensive rollout into reusable supervision and drives the 77.6% rollout reduction versus SkillOpt while still improving performance.

The experimental results are promising.

Critical weaknesses

The paper does not seem to state whether SkillOpt was fully re-run under the authors' harness or whether released skill artifacts were re-evaluated. Since all baseline numbers differ from the SkillOpt paper (harness/protocol differences), this ambiguity undermines the fairness of the central comparison.

Questions for authors
  • Is it possible to adapt the method to harness optimization [1,2], and how? Harness could involve components beyond skills, for example, tools, subagents, and more.

  • Due to the design, more hyperparameters are involved. How sensitive is the method to them?

  • How do you ensure a fair comparison with SkillOpt?

[1] Lee, Y., Nair, R., Zhang, Q., Lee, K., Khattab, O., & Finn, C. (2026). Meta-harness: End-to-end optimization of model harnesses. arXiv preprint arXiv:2603.28052.

[2] Ye, H., Lu, Y., Dong, H., Su, Z., & Song, G. (2026). Harness-Zero: Harness Distillation via Agent-as-Harness. arXiv preprint arXiv:2609.24974.

3 comments

Thank you for the thoughtful questions.

Response to W1, Q3

W1. The paper does not seem to state whether SkillOpt was fully re-run under the authors' harness or whether released skill artifacts were re-evaluated. Since all baseline numbers differ from the SkillOpt paper (harness/protocol differences), this ambiguity undermines the fairness of the central comparison.

Q3. How do you ensure a fair comparison with SkillOpt?

W1. We ran SkillOpt’s optimizer from the initial skills and evaluated the resulting skills for Table 1. Executor decoding settings can materially affect task performance. Since SkillOpt does not disclose the exact settings used for its published scores, we applied Qwen’s official thinking-mode presets to all methods using Qwen3.6–35B-A3B within each benchmark:

  • General tasks (SearchQA and ALFWorld): temperature=1.0, top_p=0.95, top_k=20, min_p=0.0, presence_penalty=1.5, repetition_penalty=1.0.
  • Coding tasks (SpreadsheetBench): temperature=0.6, top_p=0.95, top_k=20, min_p=0.0, presence_penalty=0.0, repetition_penalty=1.0.

We added a paragraph “Matched executor decoding” (line 721) to Appendix B to document these settings.

Q3. To ensure a fair comparison, we strictly follow the benchmark setup in SkillOpt’s official repository. For each benchmark and executor setting, both methods start from the same initial skill and use the same executor configuration, dataset splits, and benchmark adapter. Both run in direct-chat mode, which SkillOpt also uses for Qwen3.6–35B-A3B. We evaluate the learned skills on the same held-out tasks using the same scoring protocol. Thus, Table 1 compares the two optimization methods under matched execution and evaluation conditions. We added a paragraph “Fair comparison with SkillOpt” (line 734) to Appendix B to clarify this point.

Response to Q1

Q1. Is it possible to adapt the method to harness optimization [1,2], and how? Harness could involve components beyond skills, for example, tools, subagents, and more.

Indeed, SkillGrace could extend to harness rules [1, 2] that govern tool choice and subagent delegation without changing model weights. Specifically, we would make the harness editable, compare successful and failed attempts at the same task, and ask the frozen executor to propose a local rule change. For example, a contrast could suggest that the harness should require verification of a tool result before delegating. Replay could screen such edits when the recorded decisions remain valid and comparable under the revised harness. In light of your comment, we added a paragraph at the end of the conclusion (line 537) outlining how the frozen executor could use same-task contrasts to propose rule edits and screen them with replay when the recorded trajectories remain applicable.

Response to Q2

Q2. Due to the design, more hyperparameters are involved. How sensitive is the method to them?

SkillGrace is relatively insensitive to the rollout and evidence-query budgets over the ranges tested on ALFWorld. To illustrate this, we added Appendix G (line 1447) to the revised manuscript. Table 11 (line 1481) reports how ALFWorld test success changes when we halve the number of rollouts per task, the maximum number of evidence queries per proposal, or both.

SettingRollouts per taskMax. evidence queries per proposalTest success
Default8692.5%
Fewer evidence queries8392.5%
Fewer rollouts4691.0%
Both budgets halved4390.3%

Reducing the query budget to half alone leaves test success unchanged. Reducing both budgets to half reduces success by 2.2 percentage points, while retaining a 20.2-point gain over the no-skill baseline (70.1%). The main experiments also use one shared optimizer configuration across all three benchmarks without benchmark-specific tuning.

Reviewer_VmcVOpenReview ↗

Thanks for your response

Thank you for your response, and my concerns have been addressed.

Thank you very much for your feedback and support! We also sincerely appreciate your questions and suggestions, which have substantially improved our work.

Comments on the paper

1 comment

Dear AC/SAC/PC,

We sincerely thank the reviewers, Area Chairs, Senior Area Chairs, and Program Chairs for their time and constructive feedback. Below, we summarize the paper’s strengths, discussion, and substantial revisions.

Contributions and Strengths

SkillGRACE enables frozen agents to improve their skills through same-task contrastive patch generation and replay-based selection, without a stronger external editor. The reviewers recognized:

  • Motivation and design: A well-motivated, coherent framework, with an elegant formulation of discrete skill editing. [VmcV, SiRG]
  • Interaction efficiency: Replay avoids repeated environment execution during candidate selection. [VmcV, fCE3, SiRG]
  • Effective self-evolution: Improvements across different agent tasks while using the executor itself as editor. [VmcV, fCE3, SiRG]

Summary of Discussion

  • VmcV — 3, Weak acceptance: Explicitly confirmed that “my concerns have been addressed.”
  • SiRG — raised to 3, Weak acceptance: Increased their rating after our additional experiments and clarifications.
  • fCE3 — 2, Weak rejection: Acknowledged that expanded token accounting substantially alleviated the cost concern and that the new diagnostics strengthened the empirical support, moving their assessment toward the borderline. Their remaining questions concerned comparison fairness, initialization, diagnostic sample sizes, parent matching, and variability. We subsequently clarified these details and added variability reporting. We have not received further feedback on these clarifications and would appreciate the AC’s assessment of the additional evidence.

Summary of Revisions

  • Replay selection: Added an ablation showing gains of 7.5 points over random selection and 4.6 points over validation-gated selection on SpreadsheetBench. A separate diagnostic finds positive replay–test reward correlations at all three sampled iterations, averaging 0.417, versus 0.282 for validation. [Tables 4–5; Appendix D]
  • Same-task evidence: Added a fixed-checkpoint diagnostic controlling the parent skill, anchors, trajectories, outcome composition, and editor budget. Same-task patches improve test success by 1.1 points on average, versus 0.2 for cross-task patches. We report sample sizes and variability. [Table 9; Appendix E]
  • Efficiency accounting: Added total optimization tokens, including editing and replay. SkillGRACE uses 77.8% fewer rollouts and 32.3% fewer tokens overall than SkillOpt. We also reconciled ALFWorld’s executed rollout count. [Appendix F]
  • Evaluation and sensitivity: Added Qwen3.6–27B results across all three benchmarks and sensitivity experiments on rollout and evidence-query budgets. [Table 1; Appendix G]
  • Fairness and reproducibility: Clarified SkillOpt’s re-optimization under matched conditions, documented shared decoding settings, and provided the identical one-shot initial skills used by both methods. [Appendices B–C]

Thank you for your time and consideration.

Best regards,
Submission 53302 Authors

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