acceptodds
Under review as a conference paper at ICLR 2027

Skill Libraries Change What an Edit Does: When Should Agent Skill Validation Run In Context?

Abstract

Self-improving language agents keep a skill library of learned instructions, and they keep editing it. Every edit must pass one small test before it enters the library: a validator runs the candidate on a few episodes and accepts it only if performance improves. Current systems run this test in isolation, although at deployment the edit will live inside the library, surrounded by other instructions that share its prompt. In principle that difference matters: prompt context is known to change model behavior. In practice, on ScienceWorld with a 7B model, we present the first controlled measurement of that difference. Library context does reshape edit effects, shifting an edit's measured benefit substantially across contexts, yet in none of the 24 controlled units does it change the accept/reject decision at a practical threshold. A simple risk analysis explains both facts: a verdict survives a context change unless the distortion of isolated testing, or the noise of a small test, rivals the edit's true effect. Pre-registered equal-cost experiments test this analysis; the verdict is budget-dependent. At small budgets both validators are unreliable: run-to-run noise, not context distortion, is the main bottleneck, and both frequently misjudge the sign of an edit's effect. At full budget neither shows an advantage. On 64 edits produced by real updaters the two are statistically equivalent at every decision threshold a deployment would act on, within the single-model, score-granular scope tested here. The result is a simple routing rule: validate in the deployment context only when the distortion of testing in isolation exceeds the noise of a small test; otherwise isolated validation is the cheaper correct choice.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
skill libraries, self-improving agents, LLM agents, validation, context effects, pre-registration, deployment safety

Reviews

Among:
Shape:
1234this paper, Top 30%
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_CDfjOpenReview ↗
Rating
3(+1)
Confidence
4
Informativeness
3
Presentation
3
Soundness
3
Read review
Paper summary

The paper asks when a candidate edit to an agent’s skill library should be validated in isolation versus within the full deployment library. It formalizes the comparison between blind validation, which tests an edit alone, and matched validation, which tests the same edit in deployment context under equal rollout cost. The proposed decision-risk view separates margin-dominated, context-bias-dominated, and noise-limited regimes.

The empirical study primarily uses Qwen2.5-7B-Instruct on ScienceWorld. Across 24 controlled units, library context changes measured edit effects but does not produce practically meaningful accept/reject reversals. The paper then evaluates budget dependence through preregistered experiments and finds that at small budgets both matched and isolated validation are dominated by sampling noise.

A separate natural-edit study evaluates 64 edits generated by two updater mechanisms. Under a preregistered equivalence test, matched and blind validation are statistically equivalent within the stated deployment-relevant margin. The paper therefore recommends contextual validation only when estimated context distortion exceeds small-test noise.

Critical strengths
  • The paper isolates a practically important decision problem that is easy to overlook: validation context may alter measured edit quality even when deployment decisions remain unchanged.

  • The decision-risk formulation cleanly separates edit margin, context distortion, and finite-sample noise, yielding a useful operational criterion for when contextual validation should matter.

  • The preregistered equal-cost experiments directly test the deployment-relevant question rather than merely showing that prompts or context can perturb raw scores.

  • The natural-edit study is substantial, covering 64 edit events and 24,576 episodes, with a preregistered equivalence margin rather than relying on failure to reject significance.

  • The zero-rollout audit is unusually transparent and consequential. It identifies reward-scale, deduplication, retrieval, pool-overlap, and invalid-variation artifacts and documents the resulting pipeline redesign.

  • The paper reports negative results clearly, including a failed out-of-sample risk score and the lack of benefit from matched validation in the tested natural-edit regime.

Critical weaknesses
  • The strongest confirmatory evidence centers on one primary 7B model and ScienceWorld, limiting confidence that the routing rule quantitatively transfers to larger or differently trained agents.

  • Cross-model probing itself suggests model specificity: after parsing fixes, only Qwen3-8B replicates the reported format-cell effect among the additional models.

  • Natural edits are mostly extremely weak, with many effectively zero-effect edits, so equivalence between validators may partly reflect a regime where neither validator has much signal.

  • The study focuses on per-edit binary acceptance. Candidate ranking, top-kk selection, cumulative library evolution, and interactions among multiple accepted edits are explicitly outside scope.

  • The library is modeled as short instruction snippets, so it remains unclear whether similar conclusions hold for larger semantic memories, learned skills, tool traces, or heterogeneous retrieval stores.

Questions for authors

The natural-edit results are dominated by small effects near the noise floor. Do the authors have evidence about naturally generated edits with substantially larger deployment deltas? Such a subset would help determine whether matched validation begins to provide value under realistic rather than constructed high-margin edits.

Second, how sensitive is the proposed routing rule to errors in estimating context distortion and validation noise themselves? In a practical deployment, those quantities must also be estimated from limited rollouts, so I would like clarification on the sample complexity or uncertainty needed before routing an edit to matched validation.

Third, the paper deliberately scopes itself to per-edit acceptance. Do the authors expect the same conclusion to hold when the validator chooses among multiple candidate edits, where small context-dependent ranking changes could matter even without sign reversals? This distinction would materially affect how broadly I interpret the recommendation.

Finally, could the authors clarify which conclusions they believe are supported by the exploratory cross-model experiments? The current results appear to establish protocol portability more strongly than effect portability.

3 comments
AuthorsOpenReview ↗

Follow-up on Natural Edits

Dear Reviewer CDfj,

Thank you again for your review. I wanted to follow up on our response to your question about natural edits with larger effects. If you’ve had a chance to read it, is there anything about those results you’d like us to clarify?

Best regards,

The authors

Thanks for the clarification. I have updated my rating accordingly.

AuthorsOpenReview ↗

Thank You for Your Feedback

Dear Reviewer CDfj,

Thank you for taking another look at our work. Your question about natural edits with larger effects led us to test cases we hadn’t covered in the original submission. We’re glad those results are now part of the paper, and grateful that you asked the question.

Wishing you a great rest of the week!

Best regards,

The authors

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

This paper compares two ways to validate an instruction edit: test it in isolation, or test it within its deployment library. It defines deployment value through the edit’s expected reward effect and the validator’s acceptance decision. The controlled ScienceWorld study finds context-dependent changes in edit effects, but no supported decision reversal beyond its practical five-point threshold. An initially favorable small-budget example for matched validation fails to replicate reliably. An 11-pool confirmation finds substantial decision errors in both arms.

Critical strengths

The deployment question is well motivated. An edit’s effect in an otherwise empty prompt can differ from its incremental effect inside a library. Explicitly distinguishing those quantities is useful for evaluating self-improving agents.

The initial matched-validation advantage disappears in a second pool, and the 11-pool confirmation closes the proposed small-budget reliability claim.

The pipeline audit identifies concrete threats to measurement validity. Score-ceiling mismatches, rewrite deduplication, missing retrieval, overlapping pools, invalid environment variants, and execution jitter are documented rather than hidden.

Critical weaknesses

The regime map and related theoretical statements exceed the bound’s scope. The claim that shift correction can never outperform direct matched estimation omits possible covariance and shared estimation structure (§3, p. 4). The displayed variance addition is not a universal result.

The equivalence result is narrower than the abstract and conclusion claim. The natural-edit study supports equivalence of a pooled deployment-value contrast, within a chosen margin, under the tested policy and candidate distribution.

Acceptance-threshold sensitivity in Appendix D concerns a different, 24-cell diagnostic study. It does not establish threshold-uniform equivalence for the 64-event experiment.

The claimed practical routing rule is not operationally validated.

Questions for authors

Can the theoretical claims be corrected to distinguish bound comparison from actual regret ordering? What exact endpoint and acceptance thresholds were covered by the equivalence test?

Reviewer_KP63OpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
3(+1)
Read review
Paper summary

The paper asks whether a new skill-library edit should be tested in isolation or inside the full library it will be deployed with.

It measures how library context changes an edit's effect on ScienceWorld with Qwen2.5-7B: 4 task families, 6 edits and 3 contexts each.

It proposes a simple risk bound and a regime map built on three quantities: context shift, edit margin and test noise.

Pre-registered equal-cost comparisons find no clear advantage for matched validation at full budget, and both validators are unreliable at small budgets.

On 64 natural edits, isolated and matched validation come out statistically equivalent, and the authors turn this into a routing rule.

Critical strengths

The engineering discipline is unusually careful - A/A no-edit gates, frozen pool manifests, pre-registered decision rules and an audit that caught real defects in the authors' own pipeline. This makes the null results more believable than most agent papers.

Negative and failed results are reported honestly, including the failed replication, the closed 11-pool reliability claim, the invalid harmful label and the risk score that did worse than chance. This kind of honest measurement is useful to the self-improving agent community.

Critical weaknesses

The scope is too narrow to support the general routing rule. The study uses one 7B model, mostly one strong task family, very small libraries (about 3 entries) and scores in 0/50 steps where some cells depend on a single task. The case the paper is worried about, large real libraries where context shift is big, is never tested.

The main equivalence result says little. Natural edits are already at noise level (42% zero edits, every effect at most 6 points), so isolated and matched validation will agree almost by construction. The only regime where matched validation should win rests on one cell, and that cell did not replicate in the second pool or the 11-pool check.

The reference truth is unstable. The frozen deployment effect for the harmful edit goes from +16.8 to −20.8 across task pools, the harmful label itself fails, and 20 of the 24 reference labels are uncertain. This weakens every regret and D(b) number that depends on that reference.

The theory adds little. Proposition 1 is a standard sub-Gaussian tail bound. In the format cell, the authors' own check shows the sub-Gaussian bound predicts correction at about b=44, while correction is observed at b=8 (which a normal approximation does match).

Regime-map placement also depends on an ad hoc noise proxy taken from the no-op confidence interval, and the anchor flips between the empty and interfering contexts. The claim that shift-corrected validation is strictly worse is asserted, not proven.

The paper is very dense and history-heavy (audit branches, voided pools, post-hoc relabeling). Some statements also look inconsistent: §5 says no second model passed the parse gate, while the Limitations say all four second models now parse cleanly. The Table 1 positioning also gives the proposed method full marks on criteria it defines itself.

Questions for authors

How large is the deployment library in each experiment? Do you have any evidence, even exploratory, with tens or hundreds of entries, where context shift should be largest?

Why is the deployment effect frozen to the interfering-context value in §7 but anchored to the empty context in Figure 2? Do any regime conclusions change under one consistent choice?

Given that the frozen reference did not transfer across pools, how do you justify D(b) as a measure of deployment value instead of a pool-specific quantity?

The Limitations and §5 seem to disagree about whether second models pass the parse gate. Which is correct, and were any cross-model H1 or H2 numbers rerun after the repairs?

Was the pre-registration recorded somewhere with a public timestamp, and can it be shared anonymously for verification?

Testing a larger model with continuous, non-binary rewards and naturally grown libraries would show whether the bias-dominated regime ever appears in practice.

Comments on the paper

2 comments
AuthorsOpenReview ↗

Any Questions About Our Responses?

Dear Reviewers,

Thank you again for taking the time to read our paper and write your reviews. Your feedback helped us see where we needed to explain our work more clearly, and the paper is better for it.

If you’ve had a chance to read our replies, is there anything you’re still unsure about or would like us to address?

AuthorsOpenReview ↗

Closing Summary for the Area Chair

Dear Area Chair,

Thank you for the time you have devoted to this submission. We are especially grateful that all three reviewers returned with detailed questions during a busy review period. Their continued engagement helped us strengthen the experiments and make the paper’s practical contribution clearer.

Strengths recognized in the reviews and discussion

  • An important problem in evaluating self-improving agents (jSLq, CDfj). The paper examines whether testing a skill edit in isolation misjudges its contribution inside the deployed library, connecting evaluation design to which updates an agent retains.
  • An interpretable account of context and uncertainty (CDfj). The decision-risk formulation explains how context shifts change the margin to an acceptance threshold and how finite-probe uncertainty affects that decision.
  • A comparison grounded in deployment consequences (CDfj). Equal rollout budgets and separate reference evaluations distinguish changes in measured edit effects from decisions that alter the deployed agent’s performance.
  • Concrete findings for practitioners (KP63). The text check identifies changes in retrieved guidance without agent rollouts, and the conductivity cases demonstrate decisions that retained independently confirmed beneficial updates.

Review updates

  • jSLq confirmed that they would maintain their overall rating at 3/4.
  • CDfj raised the overall rating from 2/4 to 3/4 following our clarification and additional evaluation.
  • KP63 raised Soundness from 2/3 to the maximum 3/3, recognizing the improved rigor. The overall rating remains 2/4.

Main concerns and our responses

  • Natural edits and empirical scope (CDfj, KP63). We added Qwen2.5-14B experiments with 32 experience-grown 64-entry libraries, full/top-three comparisons, and same-edit Gemma-2-27B evaluation. A rewrite rejected in isolation and accepted in context gained 13.05 progress points in independent confirmation.
  • Theory and equivalence (jSLq). We corrected risk-bound interpretations and covariance handling, specified the 64-event value-equivalence endpoint, and checked budget and threshold sensitivity on those same events.
  • Noise and practical use (KP63). We added a fresh 32-history replication, retrieval controls, exposure analysis, and token measurements. Our final reply clarifies the interpretation of disagreement counts and connects validation choices to independently evaluated deployment outcomes.

The paper advances the evaluation of self-improving agents by separating the quality of proposed updates from the value of the decisions that retain them. A system can generate a useful edit and still lose its benefit at validation, a distinction that overall task performance alone leaves unresolved. The study gives researchers evidence and a method for investigating that bottleneck under deployment conditions and a fixed budget. This provides a concrete basis for designing and comparing validation procedures as part of agent learning.

Thank you for considering the revised manuscript and the full discussion. The reviewers’ specific follow-up questions changed what we measured and helped us give readers a clearer account of how to use the findings. We appreciate the sustained attention this work has received from them and from you.

Best regards,

The authors

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