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Paper summary
Terminal-World constructs terminal-agent training data from existing agent skills. It pairs filtered skills with personas to generate instructions, environment blueprints, evaluation criteria, and execution guidelines. A generate–verify–repair pipeline builds files, setup scripts, and pytest verifiers, after which a guided teacher collects trajectories. Guidelines are removed from student training inputs, and both successful and failed trajectories are retained. The resulting Terminal-Atlas contains 5,723 tasks from 1,000 skills. SFT produces Terminal-Navigator models at 8B, 14B, and 32B. The 32B model obtains 31.5% Pass@1 on Terminal-Bench 2.0 versus 27.0% for the evaluated Nemotron-Terminal-32B baseline. The paper also evaluates five terminalized benchmarks, training-data ablations, SFT followed by GRPO, environment quality, and synthesis cost.
Critical strengths
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The dataset demonstrates substantial training utility with a compact number of trajectories. Table 3 evaluates three model sizes across six benchmarks, and the 32B model is competitive with a substantially larger training dataset under a common local inference configuration (Appendix B.3). The 5,723/490,520 trajectory ratio is approximately 1.17%, consistent with the rounded 1.2% claim. Regardless of whether this isolates the cause of efficiency, the observed downstream performance makes the proposed data source practically interesting.
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Several design choices receive targeted empirical support. Appendix C.5 compares guided and unguided teacher collection on the same 500 tasks, reporting success of 39.6% versus 27.6%. Table 4 separately tests retaining guidance during SFT and compares a reduced dataset against success-only training at the same approximate size. The paper also includes multiple judges and human checks for task-quality filtering and two downstream evaluation benchmarks. This is more informative than presenting an automated pipeline without investigating its supervision choices.
Critical weaknesses
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The reliability of the generated verification signal remains unresolved, including a concrete false-positive path in the displayed code. In Appendix E.2, p.42,
test_conflicts_json_contentchecks that a list exists and validates entries only if present. The object{"total_conflicts": 0, "conflicts": []}therefore passes this function despite the explicitly documented conflict for student 101. The function does not require that conflict to appear or validate the conflict count. This is a bounded defect in the shown example, not evidence that all dataset verifiers are wrong. Nevertheless, merely failing on the initial state (§3.3) cannot exclude such incomplete-output passes. In the opposite direction, Appendix C.2 reports that LLM judges consider 67.7% of 300 verifier-failed trajectories complete. Without adjudication using task requirements and final artifacts, this could reflect verifier false negatives or judge leniency. It weakens both the reliability claim and the interpretation of low teacher success as evidence of task difficulty, particularly when the same environments supply RL rewards. -
The central explanation of data efficiency is not isolated. Sharing the teacher and base model does not control training tokens, optimization, filtering, task mix, or the contribution of skill-derived guidance. Table 4 studies within-pipeline choices but does not compare joint versus separately constructed specifications under an otherwise matched recipe. Nor is there a matched-size or matched-token comparison with the competing training data. Thus, the 1.2% ratio establishes a trajectory-count comparison, not an 83-fold compute advantage or proof that coherence is the cause. The broad description of prior synthesis as isolated also needs refinement: the already cited Nemotron-Terminal paper includes primitive-skill generation and a common task/test/input/environment format (§§4.2.2–4.2.3). The distinction should focus on the specific use of reusable workflow packages and their measured contribution. Pi et al., original paper.
Questions for authors
- Clarification and limited verifier audit: Does the released verifier include an additional check absent from p.42 that rejects an empty conflict list? Can a small artifact-level audit distinguish real task failures, verifier errors, and judge errors in the 300-case sample, and test known-correct solutions plus deliberately incomplete outputs? This would directly affect my assessment of the environments and RL results.
- Limited validation of the mechanism: Can one controlled training comparison, for example at 8B, hold the teacher, training budget, filtering, and approximate token count fixed while changing joint skill-based specification or using a matched subset of baseline data? This would help determine whether the benefit is attributable to the proposed construction principle.
- Clarification of uncertainty and data independence: How are Pass@3 and its standard error computed from the reported three runs, and what is the paired task-level uncertainty for the 31.5% versus 27.0% comparison? Beyond the stated Terminal-Bench 14-gram filter, what overlap checks were applied to the collected skills and the other evaluation benchmarks?
6 comments
Response to Reviewer qJSW (2/5)
Continued response to W1/Q1: re-examining the 300 verifier-rejected trajectories.
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(2.3) Re-examining the 300 rejected trajectories. We manually checked their final artifacts against the task requirements and reproduced the failed checks to distinguish genuine task failures from verifier errors.
Original LLM verdict Genuine task failures Verifier false rejections Complete 181/203 (89.2%) 22/203 (10.8%) Incomplete 96/97 (99.0%) 1/97 (1.0%) Overall 277/300 (92.3%) 23/300 (7.7%) Of the 203 trajectories originally judged complete, 181 (89.2%) violated explicit task requirements. This explains the discrepancy: the original trajectory-based LLM judges overestimated completion, while the final artifacts support most verifier rejections.
Overall, these checks support most verifier decisions in the reviewed samples and show that most audited teacher failures involved unmet requirements. Table 6 further shows that adding GRPO after SFT improves Terminal-Bench 2.0 Pass@1 by 2.25 percentage points at both 8B and 14B, supporting the environments' utility for RL training.
Response to Reviewer qJSW (3/5)
W2: The central explanation of data efficiency is not isolated. Sharing the teacher and base model does not control training tokens, optimization, filtering, task mix, or the contribution of skill-derived guidance. Table 4 studies within-pipeline choices but does not compare joint versus separately constructed specifications under an otherwise matched recipe. Nor is there a matched-size or matched-token comparison with the competing training data. Thus, the 1.2% ratio establishes a trajectory-count comparison, not an 83-fold compute advantage or proof that coherence is the cause. The broad description of prior synthesis as isolated also needs refinement: the already cited Nemotron-Terminal paper includes primitive-skill generation and a common task/test/input/environment format (§§4.2.2–4.2.3). The distinction should focus on the specific use of reusable workflow packages and their measured contribution. Pi et al., original paper (https://arxiv.org/html/2602.21193v1).
Q2: Limited validation of the mechanism: Can one controlled training comparison, for example at 8B, hold the teacher, training budget, filtering, and approximate token count fixed while changing joint skill-based specification or using a matched subset of baseline data? This would help determine whether the benefit is attributable to the proposed construction principle.
Thank you for these suggestions. Following your recommendation, we conducted a controlled synthesis ablation and trained two Nemotron-Terminal-8B baselines with matched budgets. Unified synthesis improves task-environment consistency and downstream performance, and our data-efficiency advantage persists under matched trajectory and token budgets.
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(1) Contribution of unified synthesis. We compare unified and isolated synthesis using the same agent skills, synthesis models, environment construction and verification pipeline, and teacher settings. In isolated synthesis, we first generate the task instruction and then derive the environment blueprint from that instruction alone. Both settings use 2.3K trajectories to fine-tune Qwen3-8B with identical SFT hyperparameters; inference follows Table 14.
Synthesis Environment-task consistency TB2.0 Pass@1 (%) TB2.0 Pass@3 (%) Isolated synthesis 2.54 8.99 14.61 Unified synthesis 2.97 12.36 17.98 With the same skill source and trajectory count, unified synthesis produces more consistent task-environment pairs and more effective training data.
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(2) Matched training budgets. The reported 1.2% compares 5,723 with 490,520 training trajectories. To evaluate efficiency under matched budgets, we additionally trained two Nemotron-Terminal-8B baselines matching our trajectory count and training-token budget, respectively, using the same SFT and inference settings.
Model Trajectories Training tokens (M) TB2.0 Pass@1 (%) Nemotron-Terminal-8B (matched trajectories) 5,723 97.86 7.87 Nemotron-Terminal-8B (matched tokens) 13,421 229.50 8.99 Terminal-Navigator-8B (Ours) 5,723 229.49 15.73 Our model exceeds the trajectory-matched and token-matched baselines by 7.87 and 6.74 percentage points, respectively, supporting greater training-data efficiency under both budgets.
We have added both comparisons to secs. 5.2 and 5.5 (Tables 5 and 9), with the accompanying discussion marked in blue.
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(3) Contribution of execution guidelines. Using agent skills as a unified primitive is one of our core contributions. Their procedural knowledge supports task and environment synthesis while guiding efficient teacher trajectory collection. Appendix C.5 (Table 20) measures this guidance effect: guidelines increase teacher success from 27.6% to 39.6% and reduce average steps on successful trajectories from 14.27 to 12.66. As described in sec. 3.4, we remove execution guidelines from the student SFT inputs before training.
Response to Reviewer qJSW (1/5)
We sincerely thank the reviewer for the careful and constructive feedback. We appreciate your recognition of our dataset's training utility with relatively few trajectories and the empirical support for our design choices. Following your suggestions, we have added verifier checks and controlled comparisons, and clarified the evaluation protocol and data overlap checks. We address each concern below.
Thank you for identifying this issue. We manually inspected this task's SFT trajectories and Qwen3-8B/14B RL rollouts and found no false positives caused by the empty-conflict-list loophole.
Our synthesis pipeline includes checks of both task specifications and executable environments. Following your suggestion, we added three experiments to assess verifier reliability. We present the existing quality controls and new quantitative evidence below.
(1) Qualitative measures.
(1.1) Joint synthesis and cross-model filtering. As stated in lines 208-215, we jointly generate task instructions, environment blueprints, and evaluation criteria, then apply LLM-based quality filtering. DeepSeek-V3.2 generates the specifications; Gemini-3.5-Flash judges them and constructs the environments. The filter explicitly checks Evaluation Criteria Quality, including whether completion conditions are clear and can be translated into reliable pytest checks (Appendix D.3, lines 1519-1527). We retain only specifications scoring at least 4 out of 5 on every dimension.
(1.2) Execution checks and repair. As stated in lines 248-260, we check initial-file correctness, cross-file consistency, dependencies, and runtime states. We also verify that the tests execute correctly and reject the initial state. Detected issues trigger repairs, and tasks that remain invalid after three iterations are discarded (lines 236-244).
(2) Quantitative evidence. We independently reviewed verifier decisions, tested deliberately incorrect outputs and task solvability, and re-examined the 300 failed trajectories in Appendix C.2.
(2.1) Reviewing verifier decisions. We sampled 50 verifier-passed and 50 verifier-failed trajectories. Codex with GPT-6-Astra (medium effort) independently checked their final artifacts against the task requirements.
The review supported most acceptance and rejection decisions in this sample.
(2.2) Testing modified outputs and solving failed tasks. Using the same samples, we asked Codex with GPT-6-Astra to introduce one explicit requirement violation into each verifier-passed output, then reran the verifier. For each originally failed task, the model made three independent attempts from the initial environment. We independently checked the resulting artifacts before counting successes.
The verifier rejected 96% of deliberately flawed outputs, while the successful retries confirmed that at least 90% of the sampled tasks were solvable despite the original teacher failures.