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Paper summary
This paper introduces SkillPrism-Bench, a benchmark of 75 public agent skills and 300 capability-grounded tasks organized by artifact form, verification support, execution dependency, and control flow. It evaluates paired skill availability across six models. The paper also proposes SkillPrism-Opt, which consolidates measured source-skill edits into reusable editing strategies and rewrites held-out skills without accessing their test tasks or execution feedback.
Critical strengths
The benchmark offers a useful structural perspective beyond domain-level aggregation. The explicit F/V/E/C definitions, selected-skill roster, and capability-grounded construction procedure make the intended coverage inspectable, and the combination of rule-based and rubric-based tasks accommodates different kinds of skill outputs.
Critical weaknesses
W1. The evaluation is self-referential and does not resolve the limitation the paper attributes to prior work. The introduction criticizes existing benchmarks for organizing coverage around declared capabilities (lines 51–53). Yet SkillPrism-Bench builds each task from the evaluated skill's own declared capabilities, and the references and rubrics are derived from these tasks. The skill under evaluation therefore defines the standard it is graded against. A positive gain shows that the skill can get the agent to do what the skill itself claims, not that the skill is useful or well designed. This undermines the category-level design recommendations and the claim that rewritten skills are better. The existing safeguards do not address this:
- Generating references and rubrics without access to the skill prevents direct answer leakage. However, the task requirements already come from the skill.
- Removing claims that are answerable without the skill keeps exactly the skill-specific content. It also drops the cases where the skill adds nothing.
- The taxonomy changes which skills are sampled. It does not change the fact that each skill is graded against its own claims.
W2. There is no human annotation or validation. The V/E/C labels, tasks, references, and rubrics are all LLM-generated, and many tasks are graded by an LLM judge. The paper reports no inter-annotator, LLM–human, or human–judge agreement, and no expert review of tasks. For a benchmark paper, and for a gain of only few points, this is a substantial gap.
Questions for authors
- What exactly does the benchmark measure: the skill's quality, the model's ability to use skills, or whether a skill can transmit its own claims? Which decision is it meant to inform, for example model selection, skill screening, or skill authoring?
- Could you audit a sample of claims and rubric items for correctness independently of the skill? What fraction of rubric items encode conventions that are not stated in the task?
- Do the main category differences and the optimization gain persist on tasks that were not built from the skills, such as taxonomy-blind or externally defined tasks?
- Which models were used in the paired pilots? How many tasks in each category were adjusted, and in which direction? Do the results hold on tasks that were never adjusted?
- What are the inter-annotator and LLM–human agreement scores for the V/E/C labels on a sampled subset?
- What is the human–judge agreement on rubric-graded tasks, and how sensitive are the results to the 0.8 threshold? Does the optimization gain hold on the rule-based subset alone?
4 comments
Response to fxcQ (Part 2): Human audits, task calibration, and scoring sensitivity
To address W2, we added quantitative human audits of skill labels, capability claims and scoring criteria, and output grading. Part 1, Q2 reports the claim and criterion audits; below we report label agreement, task calibration, and scoring reliability, addressing Q5, Q4, and Q6, respectively.
W2 & Q5. LLM–human and inter-annotator agreement on V/E/C labels
Two annotators used the paper’s taxonomy definitions and skill packages to review all 225 V/E/C labels for the 75 skills. F is determined by rules over the resource types in each package.
| Comparison | Labels compared | Exact matches | Agreement (%) |
|---|---|---|---|
| Annotator 1–LLM | 225 | 205 | 91.11 |
| Annotator 2–LLM | 225 | 206 | 91.56 |
| Annotator 1–Annotator 2 | 225 | 195 | 86.67 |
Overall inter-annotator κ is 0.775. Appendix A.2, Table 5 reports results separately for V, E, and C.
Q4. Which models were used in the paired pilots, how were tasks adjusted, and do results hold on unadjusted tasks?
The paired pilots used a single-turn, tool-free setting, comparing responses with and without the original skill. Most pilots used Claude-Sonnet-4.6; some tasks used Qwen3.7-Plus or DeepSeek-V4-Flash. When both conditions passed, the original task offered little opportunity to reveal whether the skill helped, so we prioritized these tasks for hardening. Their initial ease also helps explain why the calibrated group’s final no-skill pass rate remained higher.
Of the 300 tasks, 147 had materials or constraints adjusted following the pilots: 142 were only made harder, two had adjustments in both directions, and three received requirement clarifications or feasibility fixes. No task was only made easier. Appendix D.4, Table 22 reports counts and directions by skill category.
Both gains remain positive on the other 153 uncalibrated tasks. The source comparison measures the mean success-rate gain from providing the original skill over no-skill; the held-out comparison measures the mean pass@1 gain of Opt over Original:
| Evaluation split | Calibration status | Tasks | Gain (pp) |
|---|---|---|---|
| Source | Calibrated | 96 | +6.42 |
| Source | Uncalibrated | 104 | +20.83 |
| Held-out | Calibrated | 51 | +4.79 |
| Held-out | Uncalibrated | 49 | +1.81 |
We added calibration counts (Table 22) and a breakdown of existing evaluation results (Table 21) to Appendix D.4; the latter also reports each group’s success rates. Source results aggregate six models; held-out results aggregate three models with three runs per task.
Q6. What is the human–judge agreement on rubric-graded tasks?
We sampled 30 rubric tasks from 30 distinct skills, reviewing two outputs per task. Human annotators used the same task-specific rubrics as the Claude-Sonnet-4.6 LLM judge, rating individual items as Yes, Partial, or No. We then compared human and automated pass/fail decisions using the same item weights, mandatory failure conditions, and 0.80 threshold.
| Judgment type | Comparisons | Exact matches | Agreement (%) |
|---|---|---|---|
| Rubric item rating (Yes / Partial / No) | 565 | 518 | 91.68 |
| Final evaluation outcome (Pass / Fail) | 60 | 57 | 95.00 |
Results are reported in Appendix D.5, Table 24.
Q6. How sensitive are results to the 0.80 threshold, and does optimization help on rule-only tasks?
Holding model outputs, item scores, and mandatory failure decisions fixed, we varied the pass threshold from 0.60 to 0.95 across all 159 rubric tasks. Absolute pass rates declined in every condition as the threshold increased. However, at all eight thresholds examined, source Original consistently outperformed no-skill, and held-out Opt consistently outperformed Original (Figure 6).
Optimization gains also occur on tasks graded solely by executable checks. Using the default rubric threshold of 0.80, the results for the two evaluator subsets are:
| Evaluator type | Held-out tasks | Δpass@1 (pp) | Δpass@3 (pp) |
|---|---|---|---|
| Rule-based | 40 | +4.44 | +5.00 |
| Rubric-based | 60 | +2.59 | +5.00 |
Thus, the optimization gain holds on the rule-only subset. Using existing evaluation outputs, we added threshold sensitivity (Figure 6) and results by evaluator type (Table 25) to Appendix D.5.
Thanks for the response. The added analyses addressed some of my concerns, but the main issues remain unresolved. So I will keep my rating.
First, the response still lacks validation on tasks defined independently of the evaluated skills. Although real materials allow correctness to be checked against external facts, task requirements remain derived from each skill's own claims, with requirements solvable by general capabilities filtered out, and the response does not report whether the category differences persist on these tasks. The measured gains therefore do not show whether a skill helps on an independently specified task, such as accurately extracting target information from given web pages.
Second, the response narrows the benchmark's purpose to supporting skill rewriting, but the main evaluation only contrasts providing versus withholding a skill. Even for rewriting, tasks are fixed by the original skill's claims, and the optimizer only enforces stricter adherence to existing rules. The benchmark can therefore reward more faithful execution of the original, but cannot show that the skill itself has improved. I acknowledge the held-out comparison between rewritten and original versions, but it is insufficient in principle: since all versions are evaluated on tasks derived from the original skill's claims, it can only reflect better delivery of those claims, not whether the skill's content or strategy has improved. If the original strategy is suboptimal, stricter adherence may even amplify it.
Finally, the revised results weaken rather than support the central claims. Once all paired runs are included, some category advantages narrow or even reverse. The appendix acknowledges that whether changing a skill attribute improves performance remains a hypothesis, yet the conclusion still claims an empirical foundation for skill design. The optimization gains concentrate on tasks hardened during pilot calibration and become marginal on uncalibrated tasks, and removing either the experience library or the taxonomy guidance yields no significant difference on the primary metric.
Thank you for taking the time to explain your remaining concerns. We agree on the value of independently specified tasks. Where we see things differently is what the present benchmark measures and what rewriting can change.
1. Why construct tasks from skills?
Given an existing skill, developers need to know how much different models benefit from it in a given harness. We therefore construct a task distribution around its declared capabilities to evaluate the work it is intended to support.
The task requirements are informed by the skill’s claims, so they are not independently specified in the sense you describe. Your proposed evaluation starts from user requests and then selects suitable skills, as in SkillsBench. Constructing tasks around the skill gives developers a common basis for comparing models’ gains and examining how those gains vary across skill structures. The Introduction and Related Work explain this choice. The benchmark’s value is to establish where providing skills improves model performance within their intended uses, and where it fails to do so.
2. Benchmark evaluation and skill rewriting
The benchmark measures models’ gains from skills. SkillPrism-Opt uses the results to learn edits transferable to unseen skills.
(1) What does the benchmark measure? Given a model and an agent harness, how much does providing a skill change the model's ability to complete the tasks the skill is intended for? Let denote the expected pass rate of model in harness using skill version on task distribution . For skill and its intended task distribution , the gain is
where denotes no skill. We hold OpenHands fixed and compare six models, each on the same tasks with and without the skill. This shows which models benefit more, which tasks they solve only with the skill, and where it introduces errors on tasks they could already solve. Grouping by taxonomy lets us compare how the models perform with different types of skills (§§5.2–5.3).
(2) Is rewriting limited to helping the model follow the original skill more faithfully? No. The editor can revise the procedure itself. We compare the expected pass rates of the original skill and its rewrite with the model, harness, and task distribution held fixed.
We use a skill’s claims to choose what to test. For example, the XLSX skill supports linking data across sheets, so one task asks the model to build a linked workbook from campaign data. We check the values and formula references in the submitted workbook. Even when a task closely matches the claim, the original instructions may omit a step needed to complete it. When a source trace reveals such an omission, the editor can add the missing step and rerun the same model on the same task to test whether the revised procedure works better.
3. Additional analyses
(1) Category findings and conclusions about skill design. Including all paired runs changes the scope of some category findings. Section 5.3 now limits the script-backed advantage to runs where the agent accesses the skill, while the lower regression rate associated with static verification support holds in both analyses. Figure 4 and Appendix D.1 show which patterns persist and where they vary across models and tasks. These results provide evidence about how models benefit from different skill structures. We will revise the Conclusion to reflect these findings and their scope more precisely.
(2) Does the rewriting gain persist on uncalibrated tasks? Yes. When increasing difficulty, we prioritized tasks the model could solve both with and without the skill in the pilot. We revised materials or constraints on 51 held-out tasks and left 49 unchanged. On those 49, rewriting raised pass@1 from 48.98% to 50.79% (+1.81 pp). The gain was larger on calibrated tasks (+4.79 pp) and positive in both groups (Table 21). Across all 100 tasks, the gain was 3.33 pp (paired 95% CI [1.11, 5.67]).
(3) What do the ablations show? Removing the source experience library lowers pass@1 for all three execution models, by 2.67 pp on average. Keeping the same library and removing only the target skill's taxonomy attributes and guidance also lowers pass@1 for all three models, by 2.11 pp on average. The full method retains its advantage in both comparisons when any one held-out skill is omitted (Tables 2 and 20). The ablations suggest that source execution feedback helps the editor learn useful edits and that a new skill’s taxonomy attributes help it choose which of those edits to apply.
Response to fxcQ (Part 1): Evaluation goals, scoring criteria, and tasks grounded in real materials
Thank you for recognizing the taxonomy’s structural perspective and the transparency of our benchmark construction. We clarify the evaluation goal, explain claim filtering, and report audit and real-material results below.
Q1. What the benchmark measures, diagnoses, and helps optimize
We measure how much providing a skill improves task performance for a specified execution model and agent harness within the skill’s intended uses. Paired evaluations with and without the skill reveal gains, repaired failures, and newly introduced failures. The taxonomy helps diagnose how these outcomes vary across skill structures and models, identifying where skills provide useful guidance and where execution needs improvement. We demonstrate this across six source models with OpenHands held fixed.
On source skills, we inspect execution failures, revise instructions, and test whether the revisions help. SkillPrism-Opt consolidates this experience into editing strategies that can be reused on unseen skills without collecting their task execution feedback. As the benchmark and experience library grow, the aim is to reduce the repeated rollout and revision needed to adapt each new skill to its execution setting.
W1 & Q2. Task grounding, claim filtering, and independent audit
Claim filtering focuses evaluation on capabilities where skill guidance could contribute. Tasks unrelated to a skill’s capabilities, or resolved by general knowledge alone, offer little insight into how models use its guidance. We therefore exclude claims answerable from the request alone, bundled-script outputs, or general model knowledge. Retained claims identify potential contributions; paired execution measures whether providing the skill yields gains or regressions. Pilots calibrate task difficulty (Q4); final task selection uses coverage and diversity, not measured gains (Appendix A.4).
Our introduction identifies a gap in structural coverage, not a flaw in capability-grounded task construction. Claims establish the skill–task match, while task requirements, material facts, and conditions necessary for correctness provide grounds for judging completion.
We randomly sampled one task per skill, covering all 75 skills. Using task inputs and independently verifiable domain facts, we checked whether each claim applied in its setting and whether the task exercised that capability. Among these tasks, 38 used rubric grading. We audited all 451 criteria, including scoring items and mandatory failure conditions:
Appendix A.4, Table 9 illustrates all three categories with one task requesting research notes on Hacker News articles:
Thus, 84.92% of criteria are grounded in task requirements or necessary for correctness. G3 covers additional conventions or preferences, including those concerning domain practice or presentation; it does not mean all such criteria are skill-specific rules. We added this audit and its examples to Appendix A.4.
Q3. Task independence and gains on real materials
We further examined whether gains occur on tasks grounded in external facts and materials.
We analyzed tasks using public code, documents, packages, and real data. Source tasks use open-source code and tests, incident reports, and upstream configurations; held-out tasks use public app repositories, Debian/OpenWrt packages, and vulnerability records. Their code behavior, records, and operational constraints provide evidence for judging completion independently of skill claims.
Six models evaluated 64 tasks from 16 source skills; three models ran each of 29 tasks from 8 held-out skills three times. Gains compare Original with no-skill on source tasks and Opt with Original on held-out tasks:
All six source models improve, as do mean held-out pass@1 and pass@3. Gains on public real materials support the benchmark’s practical testing and adaptation uses. From existing evaluation results, we added rates and gains for both non-generated and synthetic materials to Appendix D.4, Table 23 (p. 26).