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Under review as a conference paper at ICLR 2027

Skills Are Executor-Relative: Diagnosing and Bridging the Writer-Executor Gap

Abstract

Language agents reuse skills written by other models, but these skills do not always transfer effectively. We identify the Writer–Executor Gap: different executors benefit from different skills, and skills produced by a stronger writer do not necessarily lead to better execution. Task success alone does not explain why this gap occurs or how to address it. We propose SKILLDIAG, a diagnostic method grounded in an information-theoretic view of skill transfer, to examine three sources of failure: insufficient evidence in the original experience, important information omitted during skill writing, and difficulty using information already present in the skill. We further introduce SKILLTUTOR, which uses the executor’s failure feedback to clarify and reorganize skill instructions, helping the executor use them more effectively. We conduct experiments with multiple language models across ALFWorld, WebShop and DAPO-Math. The results reveal the Writer–Executor Gap across diverse settings and show that SKILLTUTOR can improve skill use and task success. Our work provides a framework for understanding and improving skill transfer through diagnosis and adaptation to the executor.

Primary area:
foundation or frontier models, including LLMs
Keywords:
large language models, skills

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.25 over 4 reviews, above 96% of the others.
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Paper summary

The paper:

  • Introduces the Writer–Executor Gap, showing that the utility of a reusable skill depends on the model executing
  • Proposes SKILLDIAG to analyze potential sources of transfer failure, and SKILLTUTOR to adapt skill presentation using executor feedback.

Experiments across multiple benchmarks, model scales, and model families demonstrate executor-dependent skill utility and show improvements in action prediction and, in some settings, end-to-end task success. However, minor clarifications and corrections would improve the understandability and readability of some specific parts of the paper.

Critical strengths

The major strength is the breadth of the empirical evaluation, which covers several benchmarks, writer–executor matrices, model families, and both local and end-to-end metrics. The study also employs shared-source comparisons, controlled interventions, held-out selection and evaluation sets, repeated executions, matched baselines, and source-faithfulness audits. These choices make the central evidence for executor-relative skill utility convincing and demonstrate substantial experimental rigor and transparency.

Critical weaknesses

Overclaiming

Some conclusions appear stronger than the evidence supports. The diagnostic measures do not directly estimate the theoretical failure components, diagnosis-based treatment selection is not consistently validated, and repair gains vary substantially across task families and benchmarks. The authors should therefore distinguish aggregate diagnostic insights from reliable instance-level diagnosis and avoid implying that the repair method is uniformly effective or broadly generalizable.

Questions for authors

Clarification requests

  • Sec. 2: The cited works appear to provide related foundations in informativeness and decoding with side information, but do they directly support the claimed distinction between information retention and decoder mismatch? Especially the two oldest, Blackwell (1953) and Wyner–Ziv (1976). I am not convinced that they should be cited in this context.
  • Evaluation: How should the action-NLL improvements be interpreted in relation to end-to-end task success? The former appear more consistent, while the latter are heterogeneous across benchmarks and task families.
  • Appendix: Is SKILLDIAG intended to support instance-level intervention selection or only aggregate analysis? Most instances receive no dominant diagnosis, and the preliminary matched-treatment experiment does not validate diagnosis-based treatment selection.

Suggestions

  • Sec 3.1: The paper should define the first p explicitly, especially because pϕ is separately introduced.
  • Sec 3.1: Please define H, I, the expectation distributions, and the interpretation of p(⋅∣S,Ye) more explicitly. It would also help to distinguish standard information-theoretic quantities from the paper’s proposed labels for them. It would improve readability.
  • The aforementioned claims should be narrowed
3 comments

We thank Reviewer w8bk for the careful reading and constructive suggestions.


W1: Scope of the claims about diagnosis, intervention selection, and repair gains

Some conclusions about the empirical diagnostics, single-instance intervention selection, and the generality of the repairs go beyond the available evidence.

We appreciate the distinction among these three levels. We will revise the abstract, §§3–4, §6.4, and the conclusion as follows.

LevelEvidence in handWording we will use
Theoretical decomposition and empirical diagnosticsThe decomposition holds under ideal conditions. The empirical scores are operational contrasts under a finite reference model (see Q3).The correspondence requires explicit ideal conditions. We do not claim that the empirical scores directly estimate the theoretical terms.
How the diagnosis is used85.5% of instances have no dominant component. The new calibrated selection is made per task family × writer × executor (see Q3).The diagnostics are used mainly for group-level analysis. Single-instance routing has not been validated.
End-to-end gainsAfter the expanded evaluation, all three contrasts on ALFWorld, WebShop, and DAPO-Math have intervals entirely above zero.Report results by dataset and contrast. Do not summarize them as generally effective.

New end-to-end evaluation after expansion. The evaluation sets are disjoint from the development, confirmation, and repair-construction sets. Intervals use 20,000 paired task-bootstrap samples under greedy decoding.

DatasetTasksP-BaseP\text{-Base} [95% CI]P-GenericP\text{-Generic} [95% CI]P-ShuffledP\text{-Shuffled} [95% CI]
ALFWorld274 → 685+3.04 [+0.84, +5.32]+2.79 [+0.68, +4.90]+1.29 [+0.30, +2.28]
WebShop150 → 323+2.82 [+1.72, +3.96]+2.27 [+1.07, +3.51]+1.34 [+0.38, +2.30]
DAPO-Math240 → 1,200+1.2 [+0.24, +2.16]+0.99 [+0.14, +1.88]+1.18 [+0.34, +2.03]

Units are percentage points. For all three datasets, the P-BaseP\text{-Base}, P-GenericP\text{-Generic}, and P-ShuffledP\text{-Shuffled} intervals lie entirely above zero.


Q1: Do Blackwell and Wyner–Ziv directly support the decomposition?

Do Blackwell (1953) and Wyner–Ziv (1976) directly support the distinction between retained information and decoding mismatch?

The reviewer's judgment is correct. The two papers are conceptual motivation. The mathematical basis of our decomposition is the standard conditional cross-entropy identity, and it does not depend on the specific results of those papers.

ChangeRevision
Blackwell (1953)Remove from the relevant discussion
Wyner–Ziv (1976)Remove from the relevant discussion
Mathematical basisAttribute the decomposition in §§2–3 to the conditional cross-entropy identity, citing Cover and Thomas (2006)

Q2: How do action-NLL gains relate to end-to-end success?

NLL gains are more stable, while task-success gains differ across settings. How should the two be understood?

Using records from the original method, we compute paired associations on the three benchmarks. The standardized pooled correlation between the NLL decrease and the success increase is +0.1200 [+0.0640, +0.1724], entirely above zero. The pooled correlation between low NLL and high success is also above zero.

DatasetPairsLow NLL ↔ high success, rr [95% CI]NLL decrease ↔ success increase, rr [95% CI]
ALFWorld60+0.005 [−0.071, +0.087]+0.196 [+0.083, +0.286]
WebShop150+0.487 [+0.426, +0.554]+0.089 [+0.021, +0.155]
DAPO-Math240+0.094 [+0.014, +0.173]+0.075 [−0.034, +0.181]
Equal-weight standardized pool450+0.195 [+0.154, +0.241]+0.120 [+0.064, +0.172]

The records use the original skill, capsule, selection, and fallback policy. ALFWorld and WebShop use action NLL at fixed oracle-prefix states. Math adds 2,640 deduplicated answer NLLs, averaged over the correct tokens. We remove configuration means, standardize within each dataset, and average the three datasets with equal weight. Intervals use 20,000 paired task-bootstrap samples.

NLL measures the probability assigned to the correct action. Task success measures the completed execution. Raising the probability of the same correct action from 0.6 to 0.8 lowers NLL without changing the greedy choice, and a full trajectory also depends on later states and decisions. NLL is evidence of a local change in decision probability. Task success is the direct measure of its task-level return. The two are not interchangeable, and their directions agree. We will add this analysis and explanation in §6.4.


Q3: Is SkillDiag used for single-instance diagnosis or for group analysis?

Most instances have no dominant diagnosis, and the early matched-intervention trial did not validate treatment selection. At what level is SkillDiag used?

It is used mainly for group analysis. In Appendix E, 85.5% of state–cell instances have no dominant component. The single-instance matching trial and its limitations will be reported together. The new calibrated selection chooses an intervention per task family × writer × executor and does not depend on the answer at a single instance.

SettingDescription
Discovery and selection60 discovery tasks supply the three diagnostic scores; 30 separate selection tasks supply the realized intervention benefits
Selection ruleFit a fixed linear predictor to the three scores and choose the positive-benefit intervention with the highest predicted benefit; otherwise fall back to Base
Candidate interventionsAdd independent training evidence / restore content from training experience / reorder the original skill
EvaluationExclude the 60 tasks in the original routing Final set. Evaluate 214 held-out tasks and 497 critical states; nine writer–executor pairs; 54 group decisions
ComparatorAction-NLL advantage of calibrated selection, nats [95% CI]
vs Base+0.1049 [+0.0683, +0.1432]
vs uniform random repair+0.0488 [+0.0328, +0.0660]
vs the original maximum-score rule+0.0688 [+0.0359, +0.1022]
vs the content repair fixed on the selection set+0.021 [+0.013, +0.029]

S1: Define the joint distribution pp and the writer distribution pϕp_\phi

Define pp at its first use in §3.1, and distinguish it from pϕp_\phi.

Accepted. Before the Strict Skill Protocol, we add the following definitions. psrcp_\mathrm{src} denotes the fixed source distribution, so that it is not confused with the writer distribution.

SymbolDefinition
psrc(x,a∗,ye)p_\mathrm{src}(x,a^*,y_e)Fixed joint distribution of source, target action, and side information
pϕ(s∣x)p_\phi(s\mid x)Conditional distribution with which the writer generates a skill from the source
p(x,a∗,ye,s)=psrc(x,a∗,ye) pϕ(s∣x)p(x,a^{\ast},y_e,s)=p_\mathrm{src}(x,a^{\ast},y_e)\,p_\phi(s\mid x)Full joint distribution induced by a fixed writer
p(⋅∣S,Ye)p(\cdot\mid S,Y_e)Bayesian posterior of the target action given the skill and side information
qe(⋅∣S,Ye)q_e(\cdot\mid S,Y_e)Action distribution of the actual executor

S2: Define HH, II, the distribution inside the expectation, and the theoretical labels

Define entropy, mutual information, and the distribution used in expectations, and distinguish standard mathematical quantities from the interpretive labels in this paper.

Accepted. In §3.1, HH is conditional entropy and II is conditional mutual information. Both are computed from the joint distribution pp and its marginals, with the natural logarithm and units of nats.

Standard quantityInterpretive labelMeaning
H(A∗∣X,Ye)H(A^*\mid X,Y_e)Source insufficiencyUncertainty about the target action that remains given the full source and side information
I(A∗;X∣S,Ye)I(A^*;X\mid S,Y_e)Writer compression lossAction-relevant information in the source that the skill has not retained
De(pϕ)=E(S,Ye)∼p[DKL(p(⋅∣S,Ye),∥,qe(⋅∣S,Ye))]D_e(p_\phi)=\mathbb{E}_{(S,Y_e)\sim p}\bigl[D_{\mathrm{KL}}(p(\cdot\mid S,Y_e)\\,\Vert\\,q_e(\cdot\mid S,Y_e))\bigr]Executor decoding mismatchExtra log loss of the executor relative to the Bayesian posterior

The expectation will be written uniformly as

Le(pϕ)=E(A∗,S,Ye)∼p[−log⁡qe(A∗∣S,Ye)]L_e(p_\phi)=\mathbb{E}_{(A^{\ast},S,Y_e)\sim p}\bigl[-\log q_e(A^{\ast}\mid S,Y_e)\bigr]

§4.1 will state the conditions under which the empirical diagnostics correspond to the theoretical terms: canonical action loss, a Bayes-optimal reference, and other ideal conditions. Identifying absolute decoding mismatch from EDM further requires De(X)=0D_e(X)=0.


S3: Align the abstract and conclusion with the evidence

Narrow the claims above that are stronger than the evidence.

Accepted. The abstract and conclusion will use one statement: skill utility depends on the writer–executor pair; SkillDiag supports group-level diagnostic analysis; the local-decision and task-success gains of SkillTutor are reported separately by dataset, task family, and method version. The locations of these edits are given in W1.

Reviewer_w8bkOpenReview ↗

Concerns addressed

Thanks for the additional experiments. I also notice that the claims have been sufficiently narrowed. My concerns are therefore addressed. Soundness and overall scores have been raised accordingly.

Best regards

Reviewer_C4HXOpenReview ↗
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Paper summary

This paper considers a problem where instructions that come from one language model then get passed to another model, the executor. In the same way that we have hierarchical architectures in reinforcement learning, here we have a setup where we have a writer and an executor. The authors identify what they call the writer-executor gap, where the quality of the the writer's skill is ultimately bottlenecked by the executor. They show that in an ALF world, where using a stronger writer need not give better execution. They then design a diagnostic that they call Skill Diag, which will represent the executive loss in three parts: The evidence that is missing from the source experiment . The information that gets lost when writing the skill. The difficulty of using the information that is already expressed within the skill. These parts are difficult to quantify, so they estimate them by swapping context and, in some cases, using a larger model as a reference. They also propose a repair method called Skill Tutor, which writes something that looks like a teaching capsule based on the failures observed during execution. Then selects one of those failures on a separate task, and it evaluates it on held-out tasks. Through these "teaching capsules," the skill tutor is capable of improving the executor's performance and raising performance in the synthetic domain webshop by about 2 points, but shows smaller or no significant gains in Alf world and math.

Critical strengths

Experimental methodology is quite good. For example, their evaluation protocol is quite careful in that it uses separate sets for constructing, choosing, and evaluating repairs. They also use:

  • a selection rule that they fix in advance
  • confidence intervals
  • repeated runs
  • a control with a generic reminder
  • a capsule built for another executor to disambiguate the effect
Critical weaknesses

Now there's a mismatch between the the main thesis, and the experimental results. If I understand correctly, the main thesis is really that good skills are executor-relative. If you want to improve and repair them, you'd want to do it from the perspective of the failure observed in the executor. However, in experiments, you show that if you were to use a teaching capsule built for a different executor, it seems to be doing just as well on a different executor. The difference is about under a point on all three benchmarks, and the confidence intervals can't tell them apart.

It looks like not only is the gap small, but it also seems to show mostly in the context where the executor is the weakest. When studying, for example, the Gemma-31B and Gemini together, you see that the skills change: Gemini's success goes up by about 1 point, and Gemma's by about 3 points. It's really as you go to a smaller Gemma 12B model that you see a stronger effect, going from 31% to 46%. So the headline is probably true, but there's another fact that seems to be hiding in those results, which is that a when the effect is present, for example, in ALFWorld, it's mostly on models that already barely benefit from skills.

I think the information-theoretic framing could be substantiated. I think the intuition is correct and could be the right framing, but it adds little to the experimental protocol.

Questions for authors

So my question is: in what sense is repair truly executor-relative? Because it looks like, as you use a capsule built for another executor, it seems to help just as much as the executor's own capsule. Have you seen any instances where personalized capsules would beat a shuffled one?

Also, do you have numbers for the setting where the Quan executors use no skill? That would be a useful baseline to have because if you see that skills don't really help, then the variation you observe across writers would most likely be due to noise.

2 comments

We thank Reviewer C4HX for the careful reading and the pointed questions about experimental specificity.


W1: Does the main claim conflict with transfer of capsules across executors?

Other executors' capsules can also work. Is that inconsistent with the claim that skill utility depends on the executor?

The central claim is that skill utility depends on the writer–executor pair, not that each executor must have an exclusive repair. Shared effective repair rules between two similar executors are compatible with this claim. The question is whether the same writer's relative advantage changes across executors, not whether a repair can transfer.

QuestionSetupResult
Does a stronger writer help every executor?Table 3, writer × executor interaction tests on three benchmarksALFWorld p=0.0038p=0.0038; WebShop p=5.43×10−5p=5.43\times10^{-5}; Math p=0.0464p=0.0464
Does the interaction remain when the source is controlled?Table 4, three Gemma/Gemini writers reading the same 100 trajectories, 274 tasksNew per-task analysis: χ2(4)=38.47\chi^2(4)=38.47, p=8.96×10−8p=8.96\times10^{-8}
Is the interaction robust to repeated execution?New Qwen evaluation, nine pairs, 274 tasks, three executions per conditionχ2(4)=22.07\chi^2(4)=22.07, p=0.000194p=0.000194

Whether a repair must match the target executor exactly is a separate question, tested by P-ShuffledP\text{-Shuffled} (see Q1). In the contribution list and §6.4 we will separate relative utility, repair construction from failure feedback, and the additional gain from matching.


W2: Are the effects small and limited to the weakest executor?

The gains seem to concentrate on the weakest executor, with little benefit for stronger models.

The new No-Skill comparison (see Q2) shows that Qwen3-14B, the executor with the highest base success among the three Qwen executors, still gains +12.33 percentage points from skills on average. The gap between the 4B and 8B writers is +9.25 percentage points. The gains do not decrease monotonically with model scale.

ExecutorMean skill gain over No Skill, pp [95% CI]
Qwen3-4B+7.22 [+3.85, +10.58]
Qwen3-8B+1.95 [−1.34, +5.23]
Qwen3-14B+12.33 [+8.39, +16.34]

In Table 4, the Gemini executor already succeeds on 97.8% of tasks without the compared skill, so only 2.2 percentage points of headroom remain. A small gain near that ceiling is expected. On the shared-source matrix restricted to the two Gemma executors, writer effects still differ: χ2(2)=26.30\chi^2(2)=26.30, p=1.95×10−6p=1.95\times10^{-6}.


W3: How does the information-theoretic framework guide the experimental design?

The information-theoretic intuition is reasonable, but its concrete contribution to the experimental protocol is not clear enough.

The theory states the assumptions of the three interventions and what each control must hold fixed, and those statements determine the experimental structure.

Theoretical basisExperimentQuestion tested
Proposition 1: the writer loss difference is −ΔIe+ΔDe-\Delta I_e + \Delta D_eShared-source writer–executor matrices (Tables 3–4)Can a larger decoding mismatch offset the gain from retained information?
Equation 18: source term H(A∗∣X,Ye)H(A^*\mid X, Y_e)Relevant evidence versus repeated evidence (Table 6)Does adding source information required for the decision improve prediction?
Equation 19: compression term I(A∗;X∣S,Ye)I(A^*;X\mid S, Y_e)Deleting and restoring decision rules (Tables 5–6)Does the correct content have value beyond structure or repetition?
Equation 20: decoding term DeD_e; a fixed bijection preserves informationReordering the same lines, comparing the reference and the executor (Table 6)Does changing the presentation of existing content improve the executor's use of it?

A new content-restoration experiment measures the executor-NLL improvement of correct task-family content over wrong-family content on all 274 ALFWorld tasks and 1,000 WebShop tasks.

DatasetTasksMean advantage of matched content, nats [95% CI]
ALFWorld274+0.0502 [+0.0238, +0.0764]
WebShop1,000+0.0143 [+0.0076, +0.0210]

All nine Qwen combinations, equal-token content controls, and 20,000 paired task-bootstrap samples. We will add the theory–experiment correspondence table in §§3–4.1.


Q1: Is there a result in which Personalized is significantly better than Shuffled?

In what sense does the repair depend on the executor? Is there a case where Personalized is significantly better than Shuffled?

Yes. On 214 held-out tasks, under the source-constrained version (verbatim excerpts of complete source rules, with deployment selected on 30 separate tasks):

ContrastNLL improvement, nats [95% CI]After Bonferroni correction [95% CI]
P-ShuffledP\text{-Shuffled} (source-constrained version)+0.0295 [+0.0110, +0.0499][+0.0071, +0.0542]

The table below gives the expanded end-to-end results. The evaluation sets are disjoint from the development, confirmation, and repair-construction sets. Intervals use 20,000 paired task-bootstrap samples.

DatasetTasksP-BaseP\text{-Base} [95% CI]P-GenericP\text{-Generic} [95% CI]P-ShuffledP\text{-Shuffled} [95% CI]
ALFWorld274 → 685+3.04 [+0.84, +5.32]+2.79 [+0.68, +4.90]+1.29 [+0.30, +2.28]
WebShop150 → 323+2.82 [+1.72, +3.96]+2.27 [+1.07, +3.51]+1.34 [+0.38, +2.30]
DAPO-Math240 → 1,200+1.2 [+0.24, +2.16]+0.99 [+0.14, +1.88]+1.18 [+0.34, +2.03]

Units are percentage points. For all three datasets, the P-BaseP\text{-Base}, P-GenericP\text{-Generic}, and P-ShuffledP\text{-Shuffled} intervals lie entirely above zero. The source-constrained version also has a matched gain at the NLL level. §6.4 will report these results separately by dataset.


Q2: How do the Qwen executors perform without a skill, and are writer differences only run noise?

What are the Qwen executors' no-skill results? Could the differences among writers be only run noise?

We add a No-Skill control on the same 274 ALFWorld tasks, with three matched executions per condition (3 executors × 4 conditions × 3 runs = 9,864 task executions, temperature 0, at most 50 steps per task).

ExecutorNo Skill4B writer8B writer14B writerMean skill gain, pp [95% CI]
Qwen3-4B25.67%34.79%33.82%30.05%+7.22 [+3.85, +10.58]
Qwen3-8B40.63%43.43%45.99%38.32%+1.95 [−1.34, +5.23]
Qwen3-14B49.76%66.42%57.18%62.65%+12.33 [+8.39, +16.34]

The writer × executor interaction over the three repeats is χ2(4)=22.07\chi^2(4)=22.07, p=0.000194p=0.000194. This directly tests whether a writer's relative advantage changes with the executor. Together, the two results support the central claim: the skill gains are real, and the writers' relative effects change across executors. §6.1 will add this table and the interaction analysis.

Reviewer_Lc2POpenReview ↗
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Paper summary

This paper studies the relationship and gap between skill writers and executors. The authors define diagnostics for source insufficiency, writer compression loss, and executor decoding mismatch to investigate why an executor may fail when using a skill produced by a particular writer. They also propose a pipeline that uses the executor’s failure feedback to generate supplementary instructions, checks them against the original skill, and selects them on held-out tasks to improve the executor’s performance.

Critical strengths

The paper provides extensive experiments across multiple datasets and models, with detailed analyses of how skill content and presentation affect different executors. The authors also discuss the interpretation and limitations of the diagnostic measures and report statistical tests and controlled experiments to support their findings. Overall, the analysis is thorough and considers several possible explanations for the observed results.

Critical weaknesses
  1. Some presentations and notations make the paper difficult to follow. Several symbols and experimental settings appear without clear explanation when first introduced. The authors leave important details in the appendix, making it difficult to understand and assess the methods and results while reading the main paper.

  2. The validation of the three diagnostic measures remains limited. The paper acknowledges their differences from the theoretical quantities and provides controlled experiments, but the evidence is mostly indirect. Showing that a diagnostic score improves after an intervention does not establish that higher scores reliably indicate more severe problems of the corresponding type. It therefore remains unclear whether these measures can reliably distinguish source insufficiency, compression loss, and decoding mismatch across skills and executors.

Questions for authors
  1. Examples of some presentation and notation issues that made the paper difficult for me to follow:
  • In Section 4.1, E_e denotes an executor while E denotes the evidence context, which is easy to confuse. The symbols M and t in Eq. 3 also appears without explicit definitions.
  • It is unclear what the “scored candidate commands” and “masked evidence context” contain and how they are constructed. A concrete example would help.
  • In Section 6.2 and Figure 3, the results for G1–G5 are discussed before the settings are explained. Their definitions should be briefly introduced in the main text, with a reference to Appendix G.
  1. The connection between the theoretical quantities in Section 3 and the empirical diagnostics in Section 4 is not clearly explained in the main text. Are the empirical diagnostics intended to approximate the theoretical quantities, or are they separate measures inspired by the theory?

  2. In Table 8, the confidence intervals for P - Shuffled include zero on all three benchmarks. Could this suggest that the tutor’s improvements are not particularly specific to the target executor?

3 comments

We thank the reviewers for their constructive feedback, which has helped us improve the paper.


W1: Symbols and Experimental Settings Introduced Too Late

Several symbols and settings appear without definition when first used, and important details are relegated to the appendix, making the paper hard to follow.

We appreciate the detailed pointers and will add the missing definitions at their first occurrence in the main text, along with a worked example.

IssueFixLocation
Executor and evidence share the same symbolExecutor becomes Ee\mathcal{E}e (calligraphic); evidence context becomes CevC\mathrm{ev}§4.1, first occurrence
MM, tt, hh undefined in Eq. 3MM: reference model or executor; tt: uniformly sampled task; hh: fixed oracle prefix state within ttBefore Eq. 3
Candidate commands and masked evidence unexplainedDefine A(h)A(h) and A+(h)A^+(h); add a worked example (see Q1)§4.1, new Box 1
G1G_1–G5G_5 referenced before definedIntroduce each level before Figure 3: G1G_1 principles only; G2G_2 adds task-family rules; G3G_3 adds steps; G4G_4 adds state checks; G5G_5 adds recovery examples§6.2, before Figure 3
Theory–diagnostic correspondence only in appendixMove the core argument of Appendix B.7 to §4.1 (see Q2)§4.1

W2: Insufficient Validation of Diagnostic Measures

A drop in score after intervention shows sensitivity, but does not establish that higher scores indicate more severe problems, nor does it directly test the three measures' ability to distinguish failure types.

To address this directly, we ran a graded-validation experiment: we programmatically control problem severity (five levels: 0/25/50/75/100%), compute scores on one half of the queries, and measure error rates on the other half. Total: 67,584 scoring runs across Qwen3-4B/8B/14B/32B.

ScoreManipulationρ\rho vs. severity [95% CI]ρ\rho vs. independent error rate [95% CI]
SIJointly remove source records and corresponding skill rules0.827 [0.788, 0.866]0.799 [0.746, 0.850]
WCLFix full source, progressively remove unique rules from skill0.896 [0.868, 0.921]0.856 [0.814, 0.898]
EDMFix mapping, increase indirect-reference coverage0.696 [0.635, 0.757]0.641 [0.571, 0.713]

All three monotonic trends: p<0.0001p < 0.0001. After removing the unmodified baseline, ρ\rho = 0.668 / 0.804 / 0.538 with all CIs still positive, confirming that the scores track severity and independent error rates, not just intervention sensitivity. For discriminability, a linear classifier trained on 16 calibration groups and tested on 32 held-out groups yields a four-class balanced accuracy of 83.92% [81.84, 85.87] (random baseline 25%).


Q1: Concrete Example of Candidate Commands and Masked Evidence

What exactly do the scored candidate commands and masked evidence context contain, and how are they constructed?

We apologize for the delayed definitions; the symbol fixes are in W1. The following real saved state will be added to §4.1 Box 1:

ItemContent
TaskPut the cellphone on the desk
Executed prefix hhgo to sidetable 1 → take cellphone 2 from sidetable 1 → go to desk 1
Candidate set A(h)A(h) (13 commands)Includes look, use desklamp 1, move cellphone 2 to desk 1, etc.
Acceptable subset A+(h)A^+(h)Only move cellphone 2 to desk 1; verified by branch execution and subsequent plan replay. We do not claim to exhaust all successful actions.
ScoringNormalize single-token candidate-label scores to get qMA(a∣h,C)q_M^A(a\mid h,C); average over fixed states within a task, then average over tasks with equal weight
Masked evidence CevC_\mathrm{ev}The successful oracle plan for the target task with step 4 replaced by [CURRENT TARGET ACTION WITHHELD]; preserves the first three steps, action type move, position 4 of 4, and object IDs
Meaning of the maskHides the specific text of the current command, testing whether the executor can infer the correct action from the remaining context. This evidence is not equivalent to the writer's original source XX.

The state loss is −log⁡∑a∈A+(h)qMA(a∣h,C)-\log\sum_{a\in A^+(h)} q_M^A(a\mid h,C).


Q2: Relationship Between Empirical Diagnostics and Theoretical Quantities

Are the empirical diagnostics approximating the theoretical quantities, or are they independent measures inspired by the theory?

The relationship is one of operational approximation: each score is strictly equal to its theoretical counterpart under a specific condition, and deviates in a controlled direction when the condition is not met.

ScoreTheoretical quantityExact-equivalence conditionBias when the condition is not met
SIProbability that the executor cannot recover the correct action from the sourceMasked evidence faithfully reflects the writer's sourceMonotone: the more insufficient the source, the higher SI; a sufficient source is not flagged as insufficient
WCLInformation loss from source to skillMasked evidence equals the full sourceMasked evidence typically carries less information, so WCL conservatively overestimates compression loss; low loss is not misclassified as high loss
EDMProbability mass the executor assigns to the correct action given the skillA+(h)A^+(h) fully covers the true acceptable action setWith incomplete coverage, EDM underestimates the mismatch; the bias shrinks as coverage increases

None of the three scores is claimed to exactly equal its theoretical counterpart. The graded validation in W2 (ρ>0.64\rho > 0.64, all CIs positive) provides direct evidence for the monotonicity. We will add an explicit paragraph in §4.1 and move the core argument of Appendix B.7 into the main text.


Q3: P-ShuffledP\text{-Shuffled} Confidence Intervals Cross Zero in Table 8

The 95% CIs for P-ShuffledP\text{-Shuffled} include zero on all three benchmarks. Does this suggest the repairs are not particularly specific to the target executor?

We re-ran the experiment on expanded evaluation sets (ALFWorld 274→685, WebShop 150→323, DAPO-Math 240→1,200; all disjoint from the development, confirmation, and repair-construction sets), with 20,000 bootstrap resamples and two-sided 95% CIs:

DatasetEval sizeP-BaseP\text{-Base} [95% CI]P-GenericP\text{-Generic} [95% CI]P-ShuffledP\text{-Shuffled} [95% CI]
ALFWorld274 → 685+3.04 [+0.84, +5.32]+2.79 [+0.68, +4.90]+1.29 [+0.30, +2.28]
WebShop150 → 323+2.82 [+1.72, +3.96]+2.27 [+1.07, +3.51]+1.34 [+0.38, +2.30]
DAPO-Math240 → 1,200+1.2 [+0.24, +2.16]+0.99 [+0.14, +1.88]+1.18 [+0.34, +2.03]

Thanks the authors for the detailed responses, which has largely addressed my concerns. I will raise my overall score.

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

This paper asks whether a skill written by one model remains useful to another. It studies writer–executor matrices, develops an information-theoretic account of source insufficiency, compression loss, and decoding mismatch, and introduces reference-relative diagnostic scores. SkillTutor uses executor failures to construct and select short additions to a frozen skill. Experiments on ALFWorld, WebShop, and DAPO-Math show executor-dependent writer preferences. Repairs improve controlled-state action prediction in several settings and yield a small, repeatable improvement in WebShop task success.

Critical strengths

The common-source experiment is a strong part of the study. In Table 4, all writers see the same 100 trajectories, yet their skills have different value for different executors. This removes the source-experience confound in the native Qwen matrices. Together with the interaction analysis in Appendix N, it provides useful evidence for evaluating a skill with its executor. The result includes compatibility with the action interface; it does not isolate procedural understanding alone.

The controls make the results easier to assess. Construction, selection and final evaluation are separated, and repetition, wrong-family, Generic and Shuffled conditions test several alternative explanations. The paper also reports failed routing and repair attempts. Appendix B.7 explicitly explains why the measured scores do not generally equal the ideal entropy and KL terms.

Critical weaknesses

SkillDiag's ability to guide the choice of repair remains unclear. Table 6 supports benefits from added evidence and reordering, but the content-restoration test does not establish an advantage over wrong-family structure: the WCL contrast is +0.02 nats, with a 95% interval of [-0.19, +0.23]. Appendix E also reports negative matched-treatment advantages in an exploratory routing test. That pilot does not invalidate the later protocol, but I did not find a successful follow-up showing that the diagnostic scores reliably select the appropriate treatment. The evidence is stronger for the controlled comparisons than for diagnosis-guided repair.

The repair gains have limited coverage across both task outcomes and task families. In Table 8, the ALFWorld and Math gains over Base have intervals crossing zero, as do the Personalized-minus-Shuffled endpoint gains on all three benchmarks. WebShop does show a +2.30-point gain over Base [0.72, 3.95]. The cross-family action-NLL gains are also concentrated in Light tasks. Averaging the five non-Light family means in Table 79 gives about 0.0044 nats for the Gemma-tutor Qwen matrix and 0.0102 for the mixed matrix, compared with overall gains of 0.2887 and 0.3098. Table 95 shows a similar concentration for Gemini. The authors report these family differences, and some NLL comparisons do favor matched capsules, but a pooled non-Light estimate with uncertainty would clarify how broadly the repair benefit extends.

Questions for authors

Appendix P.7 reports that an unsupported lamp/use rule passed the source-faithfulness auditor in the initial phase. For the capsules actually deployed on locked Final, could you provide a rule-level check against the full source skills, including lamp/use instructions, and report whether the gains remain after removing any unsupported rules? The initial-phase failure leaves this final-stage check unresolved; it does not by itself show that the final results contain the same problem.

2 comments

We thank Reviewer Snjj for the careful reading of the common-source experiment, controls, and appendix details.


W1: Can SkillDiag guide repair selection?

The WCL contrast in Table 6 (+0.02 nats, interval [−0.19, +0.23]) does not establish an advantage of Matched over Wrong-family. The exploratory routing in Appendix E also does not show that diagnostic scores select an appropriate repair.

On the Table 6 WCL contrast. The reported +0.02 nats is the executor NLL contrast on 24 tasks, and its interval crosses zero. We re-evaluate the same contrast on the full task pool with the same diagnostic rule. For each state–writer–executor instance, we take max(0, SI), max(0, WCL), and max(0, corrected EDM). An instance enters the subset only when the largest component is at least 0.05 nats and that component is WCL. The difference is matched-repair NLL minus Wrong-family NLL; a negative value means the matched repair is better. The method is unchanged. The last three rows are the same contrast on the full task pool.

DatasetTasksScopeComparatorDifference, nats [95% CI]
ALFWorld24Original Table 6Wrong-family+0.018 [−0.194, +0.230]
ALFWorld123WCL subsetWrong-family−0.1354 [−0.2106, −0.0687]
WebShop615WCL subsetWrong-family−0.2148 [−0.3515, −0.0803]
DAPO-Math208WCL subsetWrong-family−0.0830 [−0.1577, −0.0173]

On the three enlarged WCL subsets, the intervals lie entirely below zero.

On diagnosis-guided repair selection. We add a benefit-calibrated group-level intervention experiment. A fixed linear predictor is fit to the three diagnostic scores on 60 discovery tasks and to intervention benefits on 30 separate selection tasks. Among adding evidence, restoring content, and reordering the original skill, it selects the intervention with the highest predicted positive benefit; otherwise it uses Base. We evaluate 214 held-out tasks (497 critical states), all nine writer–executor pairs, and 54 task-family × writer × executor group decisions.

ComparatorAction-NLL advantage of calibrated selection, nats [95% CI]
vs Base+0.105 [+0.068, +0.143]
vs uniform random repair+0.049 [+0.033, +0.066]
vs the original maximum-score rule+0.069 [+0.036, +0.102]
vs the content repair fixed on the selection set+0.021 [+0.013, +0.029]

W2: Coverage of non-Light tasks and end-to-end results

Cross-model action-NLL gains are concentrated on Light tasks, and the ALFWorld and Math contrasts in Table 8 cross zero. Please provide pooled non-Light estimates and their uncertainty.

Pooled non-Light estimates on the original cross-model matrices. The reviewer computed means of +0.0044 and +0.0102 nats for Gemma/Qwen and Gemma/Mixed. We reproduce these estimates and add confidence intervals. The left column uses 50 non-Light tasks in each matrix. The right column expands the pool to 1,300 non-Light tasks. Each row pools nine writer–executor combinations, including Base fallback.

Tutor / matrixOriginal non-Light score, 50 tasks, nats [95% CI]1,300 tasks, nats [95% CI]
Gemma / Qwen3+0.004 [−0.015, +0.026]+0.004 [+0.002, +0.008]
Gemma / Mixed+0.010 [−0.017, +0.038]+0.006 [+0.003, +0.015]
Gemini / Qwen3.5+0.016 [+0.008, +0.023]+0.009 [+0.005, +0.017]
Gemini / Large-mixed+0.014 [−0.003, +0.032]+0.010 [+0.007, +0.017]
Gemini / Confirm+0.005 [−0.013, +0.023]+0.005 [+0.001, +0.009]

On 50 non-Light tasks the gains are unclear. At 1,300 tasks the action-loss gains remain small. The appendix already states that the gains come mainly from Light.

We re-ran the experiment on expanded evaluation sets (ALFWorld 274→685, WebShop 150→323, DAPO-Math 240→1,200; all disjoint from the development, confirmation, and repair-construction sets), with 20,000 bootstrap resamples and two-sided 95% CIs.

End-to-end success on the full Table 8 evaluation:

DatasetEval sizeP-BaseP\text{-Base} [95% CI]P-GenericP\text{-Generic} [95% CI]P-ShuffledP\text{-Shuffled} [95% CI]
ALFWorld274 → 685+3.04 [+0.84, +5.32]+2.79 [+0.68, +4.90]+1.29 [+0.30, +2.28]
WebShop150 → 323+2.82 [+1.72, +3.96]+2.27 [+1.07, +3.51]+1.34 [+0.38, +2.30]
DAPO-Math240 → 1,200+1.2 [+0.24, +2.16]+0.99 [+0.14, +1.88]+1.18 [+0.34, +2.03]

Q1: Do deployed capsules contain unsupported rules, and do the gains remain after deletion?

Please compare every rule in the locked Final deployment with the full source skill, check lamp/use in particular, and report results after deleting unsupported rules.

We inspected every deployed capsule: all 39 nonempty deployments in the five cross-model matrices, including all 21 Gemini-tutor deployments, for 163 rules in total. The lamp/use rule has no supporting sentence in the source skill and has been deleted.

Audit itemResult
Decision109 supported; 30 unsupported, 3 conflict, 21 uncertain — 54 deleted
ProcedureAI-assisted judgment with the full source skill, the rule text, the supporting sentence, and the reason; manual review, with at least two researchers cross-checking each rule
Re-evaluationDelete the whole rule; do not reselect the deployment; an empty capsule counts as Base

Each matrix uses its original 60 Final tasks and nine combinations. Intervals are 20,000 paired task-bootstrap samples at 95%, in nats.

Tutor / matrixNLL after deletion, nats [95% CI]Original ExecGain, nats [95% CI]
Gemma / Qwen3+0.241 [+0.068, +0.401]+0.2887 [+0.1730, +0.3938]
Gemma / Mixed+0.303 [+0.071, +0.512]+0.3098 [+0.2281, +0.3898]
Gemini / Qwen3.5+0.110 [+0.023, +0.181]+0.0703 [+0.0540, +0.0879]
Gemini / Large-mixed+0.072 [+0.012, +0.123]+0.0898 [+0.0371, +0.1553]
Gemini / Confirm+0.026 [+0.011, +0.039]+0.0357 [+0.0108, +0.0633]

The gains remain roughly unchanged after the unsupported rules are deleted.

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

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