- Rating
- 3
- Confidence
- 2
- Informativeness
- 2
- Presentation
- 3
- Soundness
- 2
Read review
Paper summary
This paper addresses a limitation of previous industrial benchmarks, which mostly measure the simple question-answering abilities of LLMs. Solving real industrial problems requires LLMs to execute tasks that are more complex than simple question answering, for example, integrating various sources of data, instructions, or manuals, or clarifying or confirming the user’s intent when necessary. Motivated by this concern, the authors propose AssetArena, a benchmark consisting of 231 scenarios across seven workflow families, which mimics real industrial settings through an MCP-native environment. The benchmark provides a controlled sandbox with 85 tools across six MCP servers and heterogeneous industrial data, including work orders, telemetry, and failure-mode catalogs, together with challenging user queries that contain some degree of ambiguity. To avoid queries that seem plausible but are in fact unsolvable, the authors constructed each query only after its supporting evidence and reference answer were fixed (an evidence-first process), and eight domain experts participated in building the benchmark. The authors also provide a controlled testbed for comparing agent designs, along with a deterministic evaluator that scores trajectories against hidden references without an LLM judge. They report that even frontier models achieve only 16.5–29.9% Pass@1 across the benchmark, and their controlled experiments further show that agent-design choices mainly affect efficiency rather than accuracy.
Critical strengths
- Expert-constructed benchmark. The benchmark was constructed by human domain experts rather than synthesized by LLMs, and it is grounded in real industrial records and physics-based simulations.
- Vendor neutrality. The tool environment is built on the open MCP protocol rather than tied to a specific commercial platform.
- End-to-end industrial workflows. The benchmark provides end-to-end industrial workflows that have been validated by human domain experts.
- Reproducible evaluation. Scoring relies solely on deterministic rules rather than LLM judges, which can introduce inherent biases.
- Principled construction methodology. The authors construct the benchmark through an evidence-first methodology that extends Agents' Last Exam (ALE), adopting its three criteria: representativeness, verifiability, and workflow completeness. Building on these criteria, the work introduces admission predicates C1–C7, which operationalize them for industrial tasks.
- Substantial headroom. Even frontier models achieve only 16.5–29.9% Pass@1, indicating that the benchmark leaves substantial headroom before saturation.
- Extensive experiments and analysis. The work evaluates various open- and closed-weight models, reporting Pass@1, Pass@3, Pass^3, and Bradley–Terry Elo ratings, together with a failure analysis suggesting that failures stem mainly from grounded reasoning rather than from tool calling.
- Cost reporting. The work reports inference costs, enabling practitioners to select suitable models according to their budget.
Critical weaknesses
- The main weakness of this paper is the inconsistency of the reported numbers, especially between the main text and the appendix. For example, Table 3 (p. 8) reports 425 passing and 1,423 failing runs, whereas Appendix G (p. 47) reports 333 successful and 1,515 failed runs, although both sum to 1,848. Similarly, Figure 14 reports 444 of 1,336 failed non-FMEA runs with output-contract mismatches, whereas the text of Appendix G (p. 46) reports 444 of 1,428. Furthermore, Table 2 lists 65 WO scenarios, but Appendix B.2 states that “the work-order scenario set contains 60 manually authored tasks.” More importantly, the per-model Pass@1 values in Figure 15 (12.6–22.1%) differ from those in Table 2 (16.5–29.9%), suggesting that results from different experimental runs may have been mixed. Since the main conclusions rely on these numbers, the authors should clarify which runs the reported results are based on, resolve these discrepancies, and verify the consistency of all reported numbers throughout the paper.
Questions for authors
Questions
Q1. Benchmark Composite Index (Figure 1). Figure 1 presents a Benchmark Composite Index, but the paper does not specify how this index is measured, including how many sub-criteria each axis contains and what they are. Could the authors clarify the criteria used to measure each axis and report the grounding and agency scores for each benchmark?
Q2. Horizontal and vertical composites (p. 3). The paper states that "Only ITBench reaches the top of the horizontal composite, and no benchmark passes half of the vertical one." However, it does not define what the horizontal and vertical composites refer to. Please clarify these terms.
Q3. Scope of the agent-design comparisons (pp. 6 and 8). In "Controlled Agent Interfaces" (p. 6), the authors evaluate skills, gateway access, and domain sub-agents. Since each of these is a design pattern with many possible implementations, the experiments compare one specific implementation of each pattern rather than the patterns themselves. However, the statement in Section 5.3 (p. 8) that "flat access dominates it outright" for sub-agents reads as a general comparison between approaches. I recommend revising such statements so that they are restricted to the implementations evaluated in this paper.
** Q4. Unsolved scenarios (p. 9).** The paper states that "126 of 231 scenarios defeat all eight" models. However, it is difficult to gauge how many of these scenarios human practitioners could actually solve. It would be helpful to have a mechanism that distinguishes whether these failures reflect the limitations of the models or issues with the scenarios themselves, such as ambiguous queries, incorrect references, or overly strict scoring. For example, a human baseline or a root-cause analysis of the unsolved scenarios would address this concern.
Q5. Fine-grained CAR metrics. The CAR family includes scenarios that cannot be answered from the available data, but the paper does not report fine-grained metrics for these cases, such as how often a model answers when it should have abstained. Could the authors include such analyses, for example, a mode confusion matrix?
Q6. Representativeness of the 35-scenario subset. The additional experiments (harness comparison, skills, sub-agents, gateway, and the 30- vs. 60-turn budget) are conducted on a subset of only 35 scenarios. Please disclose the family-level composition and difficulty distribution of this subset. The mean Pass@1 is 23.0% on the full set but 31.1% under the flat setting on the subset, which makes it difficult to regard the subset as representative of the full set's difficulty. For example, p. 50 states that "at the aggregate family level, the gateway improves HLT, TSFM, and FMEA completion while reducing CAR and FMSR completion." In Table 20, however, DeepSeek-V4's HLT result changes from 0 to 50. If the subset contains only two HLT scenarios, this corresponds to solving just one additional scenario, so the result may be over-interpreted. Please clarify this point.
Minor suggestions
- In Table 2, the per-family results are percentages but are rounded to integers, so readers may misread them as counts. Reporting them to one decimal place may help.
7 comments
Response to Reviewer fHSy
Q3: Scope of agent-design conclusions (Section 5.3)
Q3. "In "Controlled Agent Interfaces" (p. 6), the authors evaluate skills, gateway access, and domain sub-agents. Since each of these is a design pattern with many possible implementations, the experiments compare one specific implementation of each pattern rather than the patterns themselves. However, the statement in Section 5.3 (p. 8) that "flat access dominates it outright" for sub-agents reads as a general comparison between approaches. I recommend revising such statements so that they are restricted to the implementations evaluated in this paper."
We agree that the experiments in Section 5.3 evaluate particular implementations, not entire design patterns. We have replaced “flat access dominates it outright” with:
“Sub-agent delegation costs 137.4% more turns and 188.3% more tool calls while yielding lower aggregate completion and mean score than flat access in the evaluated configuration”
(p. 9, lines 446-447)
Q4: Solvability and sources of failure
Q4. "The paper states that "126 of 231 scenarios defeat all eight" models. However, it is difficult to gauge how many of these scenarios human practitioners could actually solve. It would be helpful to have a mechanism that distinguishes whether these failures reflect the limitations of the models or issues with the scenarios themselves, such as ambiguous queries, incorrect references, or overly strict scoring. For example, a human baseline or a root-cause analysis of the unsolved scenarios would address this concern."
We appreciate the reviewer for identifying this and the suggestion. We added five investigations based on solving WO scenarios to access the solvability (Section 5.5, pp. 9–10).
i) Expert assessment ii) An expert-developed, non-generative NLP workflow iii) an enhanced coding environment that provides agents with additional NLP libraries and pretrained models iv) relaxed-pass sensitivity analysis and , and v) question-revision sensitivity.
-
In the expert assessment, five engineers reviewed all 231 Opus 5 trajectories without references or scores, identifying workflow gaps in text interpretation, classification validation, asset-hierarchy scoping, and sensor–failure-mode reasoning.
-
The expert-developed NLP workflow solved 11/65 WO scenarios (16.9%) on its development set.
-
In the enhanced-environment, agents solved 3–4/65, despite confirmed use of added resources.
-
Relaxed scoring increased overall success from 23.0% to 25.5% where eight of the 126 previously unsolved scenarios admitted a passing run under the secondary criteria.
-
Human question revisions informed by Fable feedback produced passing outputs for four previously zero-pass WO scenarios.
These results show that some scenarios can be solved with better workflows, additional tools and resources. Relaxed scoring explains only a small share of the failures. This suggests that the evaluated agents still struggle with industrial reasoning and workflow construction and that further improvements and expert review may help resolve more scenarios.
Codebases for these additional experiments are in ./Additional_experiments in the anonymized repository.
(Response Continue)
Response to Reviewer fHSy
Q5: Fine-grained CAR behavior
Q5: "The CAR family includes scenarios that cannot be answered from the available data, but the paper does not report fine-grained metrics for these cases, such as how often a model answers when it should have abstained. Could the authors include such analyses, for example, a mode confusion matrix?"
We thank the reviewer for the suggestion. We have now analyzed all 400 CAR trajectories using the evaluator’s normalized response-mode keys. Models returned a direct response in 78/240 cases requiring abstention (32.5%) and 48/120 requiring clarification (40.0%). Overall mode accuracy was 170/400 (42.5%), with 64 invalid-mode outputs.
We report the aggregate confusion matrix in Table 1 below and Appendix F.3 (p. 48). Mode accuracy measures response-mode selection only; primary CAR success also requires the relevant decision terms, as described in Appendix F.1.
Table 1: CAR mode confusion over 400 trajectories. Rows are reference modes; columns are predicted modes.
| Reference | Response | Clarification | Abstain | Invalid | Total |
|---|---|---|---|---|---|
| Response | 27 | 1 | 3 | 9 | 40 |
| Clarification | 48 | 41 | 4 | 27 | 120 |
| Abstain | 78 | 32 | 102 | 28 | 240 |
Q6: Subset composition and difficulty
Q6: "The additional experiments (harness comparison, skills, sub-agents, gateway, and the 30- vs. 60-turn budget) are conducted on a subset of only 35 scenarios. Please disclose the family-level composition and difficulty distribution of this subset. The mean Pass@1 is 23.0% on the full set but 31.1% under the flat setting on the subset, which makes it difficult to regard the subset as representative of the full set's difficulty. For example, p. 50 states that "at the aggregate family level, the gateway improves HLT, TSFM, and FMEA completion while reducing CAR and FMSR completion." In Table 20, however, DeepSeek-V4's HLT result changes from 0 to 50. If the subset contains only two HLT scenarios, this corresponds to solving just one additional scenario, so the result may be over-interpreted. Please clarify this point."
The subset contains 9 WO, 8 CAR, 4 FCC, 2 HLT, 5 FMSR, 4 TSFM, and 3 FMEA scenarios. It is family-stratified, but not difficulty-matched to the full suite. We have added this distribution under Appendix D4: “Subset composition”. Flat-baseline Pass@1 is 87/280 (31.1%) on the 35-scenario subset, compared with 425/1,848 (23.0%) on the full 231-scenario suite.
Under the eight evaluated models, the subset contains 15 scenarios solved by none, 17 by one to seven models, and three by all eight. The corresponding full-suite counts are 126, 90, and 15. We have now reported the performance distribution in Appendix H, “Shared baseline and subset difficulty.” Ablation conclusions are restricted to the tested scenarios and implementations.
The reviewer’s HLT example is correct: DeepSeek’s change from 0% to 50% represents 0/2 to 1/2, one additional success (Appendix lines 2903-2904). We have now reported the underlying family-level counts and avoid interpreting these small changes as general advantages (in Appendix H, p. 54, lines 2902–2905). The gateway’s measured runtime and token reductions are reported separately from its small completion changes.
(Response Continue)
Response to Reviewer fHSy
We thank the reviewer for the positive assessment and careful checks. We have revised the paper and all changes are marked in blue. Please see our responses to each weakness and question below.
W1: Consistency of the reported results
Thank you for identifying this discrepancy. We found that Appendix G have used outdated scored aggregates, including scores preceding the CAR evaluator update. We rescored all 1,848 saved trajectories with consistent scenario-specific scoring and regenerated the failure analysis. The verified accounting is 425 passing and 1,423 failing runs, including 1,336 failed non-FMEA runs, of which 444 have missing or extra answer keys.
Appendix Gand the updatedFigures 15–16now use this same cohort.Figure 16’smodel-level Pass@1 values matchTable 2’s16.5–29.9%. We also corrected the WO construction count from 60 to 65(Appendix B.3, lines 1577, 1587). These corrections are based on scoring and reporting of saved trajectories, and did not involve new model runs.Q1–Q2: Composite-index definitions
The index has seven sub-criteria in two groups.
i) Agency has three: Executable (tasks run against tools rather than being answered from text), Harness (more than one agent harness is evaluated), and Underspecified (the request withholds what to retrieve).
ii) Grounding has four: Computed (references computed by a program), Fragility (per-task difficulty measured), Evidence (the execution record is scored, not only the claim), and State (the outcome is scored by the change left in the environment).
Each sub-criterion scores 1.0 satisfied, 0.5 partially satisfied, 0 not satisfied, from the released paper and artifacts as of September 2026; each composite is the mean over its group.
Appendix Table 4now reports every sub-criterion score and both composites per benchmark. The grouping reflects a split in the literature: industrial benchmarks remain largely multiple-choice over a direct LLM call, while the wider agentic community evaluates tool-using agents, and Executable is the sub-criterion that separates the two. Fragility is satisfied by no prior benchmark; averaging grounding over the other three leaves the ordering unchanged and raises the prior ceiling from 0.50 to 0.67, against 1.00 for AssetArena.(Response Continue)