acceptodds
Under review as a conference paper at ICLR 2027

Where Documentation Ends: Source-Derived Behavioral Specifications for LLM Tool Simulation

Abstract

A common way to evaluate, and increasingly to train, LLM agents is to replace the tool backends in their sandboxes with an LLM that simulates each tool response, because real backends are costly, unstable, or unsafe to call at scale. These simulators are usually conditioned on API documentation, while real backends also enforce rules that no document states. We study this documentation gap on three author-built tool servers with 38 frozen hidden rules, 31 of which never fire in any demonstration. Doc-only failures concentrate on rules that contradict a documentation-shaped prior (17.2% vs. 69.6% accuracy), reference-free plausibility judges do not detect them (Youden J <= 0.04), and they change what agents do under real-backend replay. Comparing channels for teaching a simulator the never-triggered rules, specifications derived offline from source reach 80.3% first-encounter accuracy, against 22.7% for documentation and 59.1% for 64-call active probing; a generic summarization prompt does as well, so the gain comes from the channel, not the compilation method. Downstream, source-derived specifications repaired both focal doc-only failures, with success depending on whether a rule fired rather than on its exact value. On three public MCP servers, undocumented behavior, judge blindness, and false-success outcome changes all recur.

Primary area:
foundation or frontier models, including LLMs
Keywords:
LLM simulators, hidden backend rules, source-derived specifications, tool-use agents, agent evaluation

Reviews

Among:
Shape:
1234this paper, Bottom 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.25 over 4 reviews, above 49% of the others.
Reviewer_ZVYwOpenReview ↗
Rating
3
Confidence
3
Informativeness
3
Presentation
3
Soundness
2
Read review
Paper summary

This paper examines how undocumented backend behavior affects LLM tool simulators, whether plausibility judges detect the resulting errors, and which information channels improve simulation. The controlled testbed contains three author-built SQLite servers with 38 hidden rules, including 31 that never trigger in the demonstrations. Source-derived specifications substantially improve first-encounter fidelity over documentation alone and outperform the tested probing configurations on the main student. Generic source summarization performs similarly to the specialized compilation prompt. Downstream experiments show repairs on two selected failure cases and regressions from incorrect probing-derived rules. A public-MCP pilot reproduces documentation gaps and simulation-induced agent failures, but does not reproduce the specification-based repair result.

Critical strengths
  1. The study separates several questions that are often conflated. The protocol distinguishes teacher-forced response fidelity, reference-free error detection, real-replay task success, agent-declared completion, and simulator-side grading. Section 6 gives a consequential example: a source-conditioned simulator can return the wrong exact capped value yet still provide enough information for the agent to recover. Conversely, a plausible success response can suppress recovery and produce false completion. This is more informative than reporting a single simulator accuracy score.
  2. The controls support an information-channel interpretation and expose important negative results. Generic summaries, raw-source prompting, a second teacher family, a second student, and artifact redraws help distinguish access to source from the particular SIBYL prompt. The manuscript also reports that the preregistered downstream crossover fails and that source-derived cards do not reliably transfer to public servers. These results sharpen the contribution: readable source is useful in the controlled setting, but compiling it into a reliable simulator specification is not automatically solved.
Critical weaknesses
  1. The practical repair claim has a substantial external-validity gap. The synthetic servers contain roughly one thousand tokens of source each, with explicitly enumerable author-designed rules. In the public-server pilot, generic summaries improve exact match only modestly, SIBYL lowers outcome agreement, and most raw-source gains concern wording or layout rather than semantic hidden behavior. More importantly, Appendix C reports 113/126 real-replay successes with docs+source versus 116/126 with documentation alone. Thus, the public experiment establishes that simulation errors matter, but does not establish that the proposed information channel repairs them. This does not invalidate the controlled findings, but it weakens the concluding recommendation to provide source as a practical remedy. A targeted analysis of why source fails on the public semantic cases would be more valuable than simply expanding aggregate exact-match evaluation.
  2. The evidence supports a local channel comparison more strongly than a general hierarchy of channels or compilation methods. Section 5 deliberately gives source arms complete implementation information while probing must discover rules, and teacher effort is not normalized. That is legitimate for comparing available access regimes, but cannot establish greater resource efficiency or superiority over stronger exploration. The source-over-probing contrast also weakens on strict-29, with the second student, and under server-blocked resampling. Similarly, the wide interval for generic-summary versus SIBYL in Table 3 does not establish equivalence between compilation methods. The appropriate conclusion is that no reliable advantage of the specialized prompt was detected, while source access produced large gains over documentation in this inventory.
Questions for authors
  1. Scope clarification: Would you explicitly separate the three supported conclusions—documentation gaps exist, reference-free checks can miss them, and source helps on the controlled testbed—from the unestablished claim that source-derived specifications improve real-server agent outcomes?
  2. Mechanism clarification: For public-server semantic errors that remain under raw-source prompting, how much failure comes from missing dependency behavior, incorrect state computation, or failure to apply behavior present in the supplied source? This distinction would materially affect the practical recommendation.
Reviewer_9m2BOpenReview ↗
Rating
2(+1)
Confidence
3
Informativeness
1
Presentation
2
Soundness
1
Read review
Paper summary

This paper studies how undocumented backend rules affect LLM-based tool simulation and compares documentation, interaction logs, active probing, and source-derived specifications as information sources. Experiments on three synthetic servers show improved simulation accuracy and repairs to two focal downstream failures with source-derived specifications, while tests on three public MCP servers confirm simulation errors but provide limited evidence that these specifications resolve them.

Critical strengths

The use of real-backend replay and deterministic outcome checks is a methodological strength: it tests whether simulated observations change agents’ actual task outcomes, rather than relying solely on response similarity or LLM judgments. This provides concrete evidence that seemingly plausible tool responses can lead agents to report success despite failing the underlying task.

Critical weaknesses
  1. The main conclusion is obvious. A simulator given only documentation will fail on rules absent from that documentation. This follows directly from the setup and provides little new insight.

  2. The solution lacks technical novelty. Asking an LLM to read the source code and supplement the documentation is a straightforward solution. The paper’s own results show that generic documentation generation performs as well as its proposed method.

  3. The paper does not establish a substantive research challenge. The problem is missing information, and the solution is to provide that information. The paper does not demonstrate sufficient technical difficulty or research value beyond this straightforward observation and remedy.

Questions for authors
  1. What non-obvious conclusion does the paper establish beyond the expected observation that documentation-only simulators cannot reliably reproduce undocumented rules?

  2. What technical contribution distinguishes the proposed approach from simply asking an LLM to supplement documentation using source code, given that the generic documentation prompt performs equally well?

  3. What substantive research challenge remains once source-based documentation completion is available, and how does the paper address that challenge beyond supplying the missing information?

Reviewer_HKnvOpenReview ↗
Rating
2
Confidence
3
Informativeness
1
Presentation
2
Soundness
2
Read review
Paper summary

The paper investigates undocumented backend behavior as a source of error in LLM-based tool simulation. It constructs three SQLite-backed tool servers with 38 hidden rules, including 31 rules never triggered in the demonstrations, and compares conditioning information derived from documentation, passive interaction logs, active probing, source-derived specifications, and raw source code.

On the controlled testbed, source-conditioned approaches substantially improve first-encounter response accuracy over documentation alone. However, generic source summaries and direct source prompting perform similarly to the SIBYL rule-enumeration approach. The paper also audits reference-free judges and measures downstream outcomes through real-backend replay, distinguishing actual success from agent-declared completion and simulator-based grading. A preregistered downstream experiment repairs two selected failures but does not establish its primary crossover hypothesis. A pilot on three public MCP servers confirms simulation risks, although the semantic and downstream repair benefits do not clearly transfer.

Critical strengths

1.The controlled protocol isolates information availability carefully. The frozen rule inventory, separation between observed and never-triggered rules, teacher forcing on real interaction histories, and deterministic execution references make the comparisons interpretable. The authors also use rule-level paired analysis and report additional students, artifact redraws, and server-level uncertainty. These choices strengthen the evidence that the supplied information affects simulation fidelity on the constructed inventory.

2.The downstream analysis distinguishes several practically important failure modes. Separating real-replay success, simulator-based grading, and agent-declared completion exposes failures that response plausibility alone can miss. The incorrect probing-derived rule that induces spurious refusals is particularly informative. The price-cap example also illustrates that exact response matching and successful behavioral recovery need not coincide. I appreciate that the authors explicitly report the unsuccessful primary crossover test and limit their repair claims to the observed tasks.

Critical weaknesses

1.The incremental contribution beyond an information-source comparison remains limited. The main intervention changes the information supplied to an otherwise fixed simulator. SIBYL achieves 80.3% first-encounter accuracy, compared with 81.8% for a generic source summary and 80.3% for raw-source prompting. Thus, the experiments do not establish a distinctive advantage for the proposed specification-generation procedure. Moreover, because the evaluated rules are deliberately absent from documentation and demonstrations but present in source, a substantial source-over-documentation advantage is expected, particularly for arbitrary constants.I do not consider a new algorithm necessary for an empirical paper. However, the contribution must then rest on sufficiently novel and robust diagnostic findings. The source-over-probing comparison is less conclusive on strict-29, with the second student, and under server-blocked uncertainty. Taken together, the results provide a useful controlled case study, but the broader empirical insight beyond the value of supplying missing implementation information remains insufficiently established.

2.The public-server results do not validate the central intervention at the semantic or downstream level. Appendix C reports that only 7 of the 29 raw-source exact-match gains occur on calls exercising semantic undocumented behavior; the remaining 22 concern formatting or calls outside that category. Generic summaries provide little improvement, while SIBYL reduces error/success outcome agreement by 11.8 percentage points. After excluding the two tasks with invalid checkers, docs+source achieves 113/126 real-replay successes, compared with 116/126 for docs-only.These findings support the existence of simulation risks, but do not demonstrate that source-derived specifications reliably repair them outside the author-built testbed. The controlled downstream repair is also confined to two tasks selected using earlier results, with a task-level repair test of p = .25. The authors appropriately disclose these limitations, but they substantially restrict the practical significance and generalizability of the intervention.

Questions for authors

1.Semantic versus formatting improvements: Using the existing public-server outputs, can you report formatting-normalized semantic fidelity and separate behaviors implemented in server code from those determined by libraries or the SDK? How much of the source benefit remains on the undocumented semantics targeted by the paper?

2.Downstream transfer: Can you provide task-level paired outcomes for the 42 valid public tasks and explain why docs+source obtains 113/126 replay successes versus 116/126 for docs-only? Do improvements in single-step semantic fidelity correspond to downstream improvements on any tasks?

3.Scope of the source-over-probing conclusion: How should this comparison be interpreted given the strict-29 results, the second-student results, and the server-blocked confidence interval? Please distinguish conclusions supported for the frozen inventory from those intended to generalize across servers.

4.Practical value of specification compilation: Can you quantify the cost and context trade-off between compiled specifications and direct source prompting, including teacher calls and student prompt lengths? Table 9 shows that the controlled specification cards are often longer than the source, while their fidelity is similar. Clarifying the setting in which compilation offers a practical advantage would affect my assessment of its significance.

Reviewer_rMz6OpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

this paper focus on realving the observation that simulating tool responses from API documentation alone misses rules the documentation never states. The authors build three SQLite servers with 38 hidden rules, 31 of which never fire in any demonstration, and compare documentation, passive logs, 64-call active probing, and specifications compiled from source.

On the 31 never-triggered rules, first-encounter accuracy roughly 4/5 for source, 1/5 for documentation, and 3/5 for probing. A state-blind plausibility judge accepts 540 of 588 hidden-rule errors. Downstream, a real-replay agent test (E1) and a pilot on three public MCP servers follow.

Personally I find it is an interesting read

Critical strengths
  • The primary metric is exact canonical-JSON match against real execution, inference runs over rules, Tables 2 and 3 are consistent with the per-rule counts in Table 5 (p. 14), and the failed crossover is reported plainly (Table 4), which keeps the protocol tight.
  • One wrong item in the probing-derived card produced spurious sold_out refusals in 12 of 14 booking episodes (p. 9), a useful warning about LLM-written notes.
Critical weaknesses
  • The source-over-probing gap is less certain than the abstract suggests. Its server-level interval, includes zero (p. 14); the draw-averaged per-rule gap is +30.6 points (Table 7). The abstract's "the gain comes from the channel, not the compilation method" depends on a null result, and generic-summary draws span 64.5 to 85.5 (Table 7).

  • E1 supports the downstream claim only descriptively. The crossover failed, with probing matching source at 8/8 on price (Table 4), and the repair evidence is two focal tasks chosen using channel results and historical failures, with task-level p = .25 (p. 9). The abstract still reports "repaired both focal doc-only failures" without the failed hypothesis.

  • The conclusion appears to go past the public-server evidence. It credits raw source on public servers with "the most correct and fewest wrong rules" (p. 9), but the item-level audit covers only testbed cards (p. 7).

  • The abstract contains too many numbers for human readers

Given other reviews and rebuttal, we may reconsider the rating as needed.

Questions for authors
  1. Which simulator and step pool give 71/102 and 124/720 in Table 1, and which 5 rules count as prior-compatible?
  2. What setup gives "29/32 vs. 25/32" for real-backend agents (p. 9)?
  3. Does "preregistered" mean more than hash-frozen files, e.g., a dated external deposit?

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

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