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Withdrawn from ICLR 2027

Teaching the Harness: Student-Aware Skill Transfer for LLM Agents

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

Effective teaching requires reasoning about the learner as well as the task, a capacity that Theory of Mind describes as inferring another agent's latent state from its behavior. We ask whether a stronger LLM teaches a fixed student better when it applies this principle. The student is an LLM agent acting through a harness that fixes its tools, context, and action budget, so a procedure that helps one model can exhaust the budget of another. We introduce Student-Aware Teaching (SAT). The teacher builds a learner model that pairs an empirical profile with hypotheses about the student's limitations, tests these hypotheses with diagnostic probes, and writes reusable skills for the diagnosed failures. A skill enters the library only after it raises success on matched development tasks. With Claude-Sonnet-5 teaching DeepSeek-V4-Flash, SAT reaches 86.46% task success across four primary runs, leading both a profile-free teacher with the same framework (81.04%) and the untaught student (75.00%) in each run. Removing the analytical learner model lowers both prediction and success, and under misleading learner profiles none of the 48 candidate skills passes admission. When DeepSeek-V4-Flash and Gemini-3.8-Flash exchange libraries, each performs better with its own. Saved libraries keep average gains of up to 11.1 points after the teacher leaves. The benefit depends on a student that can follow instructions and a deployment route that delivers them.

Primary area:
foundation or frontier models, including LLMs
Keywords:
LLM Agents, Machine Teaching, Learner Modeling, Agent Harnesses, Strong-to-Weak Transfer

Reviews

Among:
Shape:
1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_QtZ2OpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
1
Soundness
2
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Paper summary

Authors proposes a framework (SAT) in which a stronger LLM such as Claude-Sonnet-5 which acts as a teacher and it generates reusable skills for a weaker student agent, such as DeepSeek-V4-Flash, which is operating in a fixed harness. The teacher builds a model of the student taking motivation and inspiration from ToM and teaching principlesand forms hypotheses about why and how the student fails. It then tests these hypotheses with targeted probes and adds a skill to the library only if it improves the student’s success on matched tasks from development set.

Critical strengths

The paper tackles a practical problem of how big and stronger models can help weaker agent to improve perfroamnce without any fine tuning. Their methid is also cost effective and cheap to run.

Critical weaknesses
  1. The paper is hard to follow and read. The introduction does not clearly motivate the problem or explain how Theory of Mind and teaching principles connect to the proposed method. Some terms are not well defined. For example, what Runs S1–S4 are and how they are different is unclear in the experimental setup. The results section has many paragraphs without main takeaways and findings.

  2. Their primary comparison in Table 2 uses only 60 test tasks with two executions each and reports no confidence intervals or statistical significance tests. Also, The aware teacher method receives additional context and information that their baseline teacher does not - extra student executions through probes and a more detailed prompt, so I am not sure if the comparison is fair. There is also no comparison to the prior methods that the authors discussed in Related Work and Table 1.

Questions for authors
  1. can youu define Runs S1–S4 more clearly? Do the runs differ only in seed?
  2. Can you report confidence intervals or significance tests for the comparison in Table 2?
Reviewer_JZJdOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper asks whether a strong teacher model transfers competence to a frozen student agent (model + harness) more effectively if it first builds an explicit model of that student. The proposed SAT loop is: observe the student's trajectories → infer a learner model (a Beta-Bernoulli profile of what fails, plus free-text hypotheses about why) → test those hypotheses with single-axis probes (e.g. inventory size 2→16) → teach up to three ≤900-char natural-language skills per round → verify, admitting a skill only if it beats an empty library on 1–4 development tasks. The teacher then leaves, and a selector delivers the saved skills. Against an agnostic teacher sharing the same framework minus modeling and probing, SAT reports 86.46 vs 81.04 vs 75.00 untaught over four runs.

Critical strengths
  1. Well-posed problem. Studying capability transfer at the harness/skill level rather than in weights is practical, auditable, and cheap. Table 1 is an unusually clear positioning of the contribution.
  2. Concrete, transferable procedural findings. The bulk-stock-query and recursive-find skills, and the observation that when to verify is itself a learner-dependent teaching decision, are genuinely useful engineering knowledge.
Critical weaknesses

W1. The paper never measures what it is an alternative to. The motivation is explicitly "many deployed models cannot be retrained," and Table 1 positions SAT against distillation. Yet there is no distillation baseline (SFT, or OPD per Agarwal et al. 2024, which the paper cites) and — more damaging — no teacher-direct baseline. Across 26 pages, the teacher's own task accuracy is never reported. The entire practical case therefore rests on a number that is absent. Appendix K even defines the amortization threshold in terms of C_strong, then leaves it unfilled. Three further points make this a structural, not incidental, gap:

OPD requires teacher logits, which a closed teacher (Claude-Sonnet-5) cannot provide. The flagship configuration is thus incapable by construction of supporting the comparison. The authors already ran an open-weight pair (Qwen3-14B → Qwen3-8B, their largest gain at +15.0) with matched splits. LoRA SFT or OPD there is a few GPU-days, not infeasible. The evidence base contradicts the premise. Largest gains (+15.0, +11.7) occur on open-weight students that users can fine-tune; on the two genuinely closed students (GPT-5.4-Mini, +1.7 ties agnostic; Gemini-3.8-Flash, +4.2 with agnostic ahead at 92.5 vs 91.7) the benefit vanishes. The headline student, DeepSeek-V4-Flash, is itself open-weight. Headroom and weight-openness are confounded here, and only the missing distillation arm can disentangle them. W2. The headline number is not statistically supported, and the paper's own control says so. Per-run aware−agnostic is +10.00, +2.50, +0.83, +8.33: sign test p = 0.0625, paired t = 2.44 (df=3, p ≈ 0.09). Mean +5.42 points is ≈3.25 of 60 tasks. Meanwhile Appendix H.2 reports a fixed six-skill library varying 71.7–82.5% (10.8-point spread) across four seeds and calls it "the scale of evaluation noise"; Table 23 shows the identical agnostic procedure reading 85.0 / 73.3 / 80.8 across three jobs. The seed noise exceeds the effect. Since the same frozen 60-task split is shared across conditions, a task-level paired bootstrap — already used in Appendix G — would be far more powerful and is simply missing from Table 2.

W3. The aware/agnostic contrast confounds modeling with more information and compute. Aware receives σ, probe outcomes (i.e. additional student rollouts), and opens with 2.2× the teacher input tokens (119.4k vs 54.7k). No equal-budget control exists: an agnostic teacher given the same number of extra rollouts but no learner model. The 2×2 is also incomplete (no-probes/no-model cell). The main comparison is additionally against an author-designed ablation, not against published skill-optimization methods (SkillOpt, EvoSkill, Trace2Skill) that the paper itself cites — and SkillOpt's reported transfer-across-model-scales result directly tensions with the student-specificity claim here.

W4. The gain is one small task family. Decomposing Table 30 (S2–S4, 180 records, weighted): +2.22 of the +3.89 advantage (57%) comes from extension rename, a 6-record category, while aware is worse on the largest category, dependent workflow (94.44 vs 98.61, 36 records), and on mixture arithmetic (82.14 vs 92.86). Remove extension rename and the advantage is +1.66. Table 13 shows 6 of 12 aware skills target renaming. The extended run shows the same pattern: aware wins only on terminal (73.3 vs 50.0), and ties or loses elsewhere (inventory 55.0 vs 56.7). A single rename skill, not a general modeling capability, is carrying the result.

W5. The admission gate is too weak to bear the claims placed on it. Each task runs once with the skill and once empty; 8 of 12 aware skills were admitted on a single development task, and each terminal category has exactly one dev task reused across candidates. At p≈0.6, a useless skill is scored +1.0 with probability ≈0.24. The flagship rename result (0→100) therefore rests on one binary comparison. The gate also measures standalone utility against an empty library, never marginal utility in the deployed 2-skill configuration — likely why L2 student-selection is −0.8 and Qwen2.5-7B flat injection is −14.2. Generated/admitted/rejected counts and utility distributions are not reported.

W6. The library-swap control cannot isolate student-specificity. Both libraries were selected by a gate evaluated on the owning student's dev tasks. "Own library wins" is therefore equally explained by selection overfitting; a same-student, different-seed swap baseline is needed to set that floor. Two of six intervals have a lower bound at exactly 0.0, with no multiplicity correction.

Questions for authors
  1. What is the teacher's own accuracy on the test suites — Claude-Sonnet-5 alone, Qwen3-14B alone? And what does matched-budget SFT/OPD achieve on the Qwen3-14B → Qwen3-8B pair?
  2. Task-level paired intervals for Table 2?
  3. Why exactly four runs, and were other seeds run and excluded?
  4. Aware run-level SD (1.25) is 4.5× smaller than agnostic (5.58) on the same frozen tasks. Mechanism? (My guess: aware converges to the same two skills each run — which would narrow the claim.)
  5. If the agnostic teacher received the same number of extra rollouts but no analytical model, how much of the gap survives?
  6. Are probe instances disjoint from the test split? Is probe compute charged to the teaching budget?
  7. Does the library still help after SFT? This is the paper's real question.
Reviewer_9g9bOpenReview ↗
Rating
1
Confidence
2
Informativeness
1
Presentation
2
Soundness
1
Read review
Paper summary

The core methodology is highly intuitive. Using a larger LLM to systematically observe mistakes, diagnose the root cause, and formulate instructional rules to prevent the student model from repeating them is a practical and easily understandable approach.

Critical strengths

The core idea is highly intuitive. Using a larger LLM to diagnose issues by observing mistakes, diagnosing those mistakes, and lastly, adding instructions to help prevent the student model from making the same mistake. It is a practical and straightforward heuristic approach. This makes the method easy to understand and apply.

Critical weaknesses
  1. Lack of External Baselines and Scientific Rigor

There are no external baselines and no strong comparisons. Without proper benchmarking against existing state-of-the-art frameworks, the paper reads merely as a description of a method rather than a rigorous scientific work. Furthermore, there is no new theory introduced, and the work omits direct empirical comparisons to the related works it cites.

  1. Reliance on Custom, Unverifiable Datasets

The empirical evaluation relies almost entirely on five custom-built task suites generated programmatically for this specific study. Because these are not established open-source benchmarks, the difficulty of the tasks and the overall trustworthiness of the results cannot be independently verified or compared against the broader literature, leaving the paper feeling incomplete.

Overall, the paper does not introduce any new theory or new framework. Because it operates strictly as an application paper, its experimental design is its strongest weakness.

Questions for authors
  1. Why are there no external baselines or strong comparisons included in the evaluations to prove the method's effectiveness against existing state-of-the-art frameworks?

  2. Are there specific related works that were omitted from empirical comparison, and how would your method perform against them?

  3. Given that the primary task suites are custom-built, how can the community verify the difficulty of these tasks or trust the performance metrics without comprehensive evaluation on established open-source agent benchmarks? To establish a reliable baseline and build trust in the results, the authors need to evaluate recent state-of-the-art works on these custom datasets as well.

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

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