acceptodds
Under review as a conference paper at ICLR 2027

When Does Cross-Examination Beat Self-Assessment? A Text-Surface Visibility Law for Training-Free Agent Trustworthiness

Abstract

Detecting when an LLM agent is about to fail—without ground truth or extra training—is central to deploying agents safely. Two training-free signals compete: self-assessment (the acting model reports its own confidence) and cross-examination (a separate model audits the trajectory). We ask when one beats the other, and find that neither wins universally. Across five agentic settings spanning conversational tool use (τ-bench retail/airline), step-level failure attribution (Who&When), and code generation (BigCodeBench), we establish a monotone visibility law: the net benefit of cross-examination over self-assessment is determined not by whether the task has an objective notion of correctness, but by whether the error signal is exposed at the text surface readable by the auditor. Ordering domains by a semi-quantitative visibility rubric yields a strictly monotone gain curve, from a significant negative gain in low-visibility conversational trajectories (−0.156, P=.02) through a near-zero point in code—a high-objectivity but low-visibility counter-example (+0.024, ns)—up to a significant positive gain in action-rich retail dialogues (+0.305, P=1.0). We further show that naive multi-judge aggregation does not beat the strongest single judge, and that inter-judge agreement itself tracks visibility. Finally, we give a first partial solution: a deploy-time observable proxy (trajectory depth) routes each domain to the better signal, reaching 97% of an oracle's within-domain AUROC and significantly outperforming always-self (P=.999). All findings are training-free and pure-API.

Primary area:
foundation or frontier models, including LLMs
Keywords:
LLM agents, trustworthiness, failure detection, LLM-as-a-judge, error visibility, training-free evaluation

Reviews

Among:
Shape:
1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_NxdUOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

The paper asks which better predicts an agent’s failure: the agent’s own confidence, or an outside LLM judge that reads the agent’s transcript. Across five settings, the authors give each a hand-assigned “visibility” score (how readable errors are from the transcript) and find that the judge’s advantage over self-confidence rises steadily with that score. Code is their key example: correctness there is objective, yet the judge gains almost nothing, which they take to mean visibility matters more than objectivity. They also find that combining several judges does no better than the best single judge. Also the conclusion is that choosing between judge and self-confidence based on trajectory length matches the best possible choice.

Critical strengths

The code example is informative -- even with objective correctness (unit tests), an external judge reading the source does no better than self-assessment (AUROC .59 vs .58), because many bugs only appear at runtime. This is a useful caution for deploying LLM judges.

Critical weaknesses

W1. The visibility scores look chosen after the fact. The paper says the scores were assigned from task structure before any results were seen, but several things undercut that:

  • Airline and retail are hard to tell apart structurally. Airline gets all zeros and retail all twos, yet both use the identical τ\tau-bench setup (policy document, tool calls, database outputs). The real difference is that airline has more complex policies and more tasks where the correct response is to refuse.
  • The airline judges point the wrong way. Two judges score well below chance (AUROC 0.39 and 0.46), and the aggregate is 0.43. That suggests judges systematically misread correct runs, for example treating a correct refusal as a failure.
  • Two tables disagree. Table 1 and appendix Table 3 give Code and Who&When-deep different sub-scores that happen to add up to the same totals.

W2. Statistical significance and the concern that the paper’s own numbers don’t support the “law.” Two of the five points measure something different. The Who&When points compare the best of four judges, picked after seeing results, against an unclear baseline rather than against self-assessment. Their values also change between sections (0.31 and 0.45 in Table 2 vs. 24.1% and 41.3% in Section 5(iii)), and the Who&When-deep point rests on only 16 examples with no confidence interval. When restricted to cases scored by all four judges (Table 4), code’s gain (+.086) exceeds retail’s (+.039), so the ordering breaks, and neither extreme remains significant.

W3. The routing result fairness concerns. The depth cutoff is tuned on the same three domains it is evaluated on. Routing each example individually, which is what a real deployment would need, gives essentially no gain (+.006, not significant). Depth also conflicts with the paper’s own scores, since the longer Who&When Hand-Crafted traces are rated less visible, not more. Finally, the paper reports “97% of oracle,” but its routing score equals the oracle’s exactly.

Questions for authors
  1. Do the judges see the airline policy? What is judge accuracy on tasks whose correct outcome is a refusal?
  2. Self-assessment is elicited in a separate call where the acting model rates its own finished trajectory, so the “self vs. judge” gap may partly reflect self-preference bias (models favor their own outputs) rather than visibility. Could the authors specify which models generated each domain’s trajectories and add a control in which each model rates both its own and other models’ trajectories?
  3. Tables 1 and 3 give different sub-scores for Code and Who&When-deep that happen to sum to the same totals. Could the authors describe the scoring protocol? Could the authors clarify which table is correct and whether the ordering holds when results-blind raters redo the scoring?
  4. Please report the ordering under complete panels with a task-clustered bootstrap. Does code still fall below retail?
Reviewer_WRGWOpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

The paper compares self-assessment and external auditing across τ-bench retail and airline, code generation, and two Who&When subsets. It proposes a domain-level text-surface visibility rubric and reports a monotonic relationship with headroom-normalized audit gains. It additionally studies judge aggregation and incomplete panels, and evaluates a depth-based domain routing heuristic intended to select the better reliability signal.

Critical strengths

The research question is important and has practical value. The different results in airline and retail settings show that adding an external judge does not always help detect failures. I also appreciate that the authors report negative results and cases with little improvement, as these findings are useful for real-world applications. The authors also make a good effort to examine their results from different perspectives. They study judge-panel coverage, compare attribution methods using the same generation, and test several routing approaches that did not work well. These experiments help address some possible concerns. Overall, I think the paper could still provide useful insights into how auditing performance differs across domains, even with a more limited scope.

Critical weaknesses

I am not fully convinced by the claimed relationship between visibility and judge improvement. The five data points seem insufficient to support such a general conclusion. Also, the paper combines AUROC improvements over self-assessment with step-accuracy improvements over another baseline. Even after normalization, these are still different metrics and may not be directly comparable.

The core problem is that the visibility scores seem somewhat subjective. For example, the code domain has different scores in Table 1 and Table 3, and the scores for deep Who&When also change. The same-generation results in Section 5 actually show a larger normalized improvement for deep traces than shallow traces (around 0.185 vs. 0.064). This seems to go against the main conclusion. There may be differences in how these results were calculated, but the authors should explain this inconsistency. Overall, I think the current results show some correlation, but the current experiment setup is far from clearly establishing a general or causal relationship with no further theory support, which is apparently over-claiming.

I also have concerns about the routing experiments. The introduction suggests that the method can select a judge without knowing the domain, but Section 6 mainly studies routing at the domain level. It is not very clear how domains are grouped, how thresholds are chosen, or whether the method is evaluated on independent data. Appendix C also shows that the per-sample depth-based routing does not give statistically significant improvements. The method performs close to the oracle on the tested domains, but this does not necessarily mean it will work well on new domains, especially since several routing strategies were explored.

Finally, the abstract mentions achieving 97% of oracle AUROC, while Section 6 says 97% of the improvement over the baseline. These are different measurements, and the authors should clarify which one is correct.

Questions for authors

Could the authors clarify which baseline, dataset, and model aggregation method are used for each point in Table 2? It would also be helpful to compare the visibility relationship using consistent baselines. In addition, how do the results in Section 5, where deep traces show larger improvements than shallow traces, fit with the claimed trend?

I am also a bit confused about how the visibility scores are assigned. Which scores are correct, and who decided them? Were these scores determined before seeing the experimental results? I think it would be more convincing if the authors could test different visibility levels on similar tasks, or validate the scoring method on new domains, rather than relying on only five different settings.

Finally, I would appreciate more details about the routing method, especially how the threshold is selected, how domains are identified, and how the results are combined. It would also be useful to see whether the method still works when tested on a domain that was not used during development. The authors should also clarify how the reported 97% is calculated and what exactly it measures.

Additionally, it would be better if the authors could provide a more up to date literature review as this is rapidly developing area, and this is in fact not a very new research problem.

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

The paper studies when self-assessment and cross-examination are more effective for evaluating LLM agents' trustworthiness. The authors find that their relative performance depends on how clearly errors are exposed in the textual trajectory, with lower error visibility generally favoring self-assessment. They propose a visibility rubric and a simple heuristic based on trajectory depth to choose between the two approaches. They also find that naive multi-judge aggregation does not outperform the strongest single judge.

Critical strengths
  1. Proposes a practical, training-free heuristic for choosing between self-assessment and cross-examination based on trajectory depth.

  2. Shows that naive multi-judge aggregation, through majority or median voting, does not significantly outperform the best single judge.

Critical weaknesses
  1. I am unsure which parts of the findings are non-obvious. It seems intuitive that cross-examination would benefit when enough information about a failure is available, while an external judge with limited evidence would struggle. Although the authors demonstrate a monotonic relationship between their visibility rubric and cross-examination gain, the five settings also differ in other important respects, making it difficult to establish whether visibility itself drives the observed differences. A more controlled experiment, for example, evaluating the same trajectories while systematically revealing or masking relevant intermediate states and tool outputs, would provide stronger evidence for the proposed visibility law.

  2. I am also not convinced by the unified visibility law, since the gains are calculated differently across settings. For the AUROC domains, the authors compare cross-examination with self-assessment, whereas for Who&When, they compare step-attribution accuracy against a baseline rather than self-assessment. How comparable are these two quantities, even after normalizing by the remaining headroom? In particular, can the same conclusions be drawn when self-assessment and cross-examination are evaluated under a consistent task and metric?

  3. The analysis seems somewhat shallow in places. For example, why does GPT perform substantially below random chance in Figure 4 (AUROC ~0.39)? Low visibility might explain why a judge performs close to random, but it is less clear why the predictions would be negatively correlated with correctness.

  4. Some parts of the writing and presentation are unclear: a. Line 360: What exactly does the "strongest single judge" mean? Is this the best-performing judge selected retrospectively on the evaluation set, or is it selected independently? This distinction matters when comparing it with multi-judge aggregation. b. Figure 5: The different three-judge subsets should be explicitly labeled rather than all appearing as "3-judge." c. The visibility-rubric assignments in Table 1 and Appendix Table 3 appear inconsistent for some domains, even though their aggregate scores are the same. These should be reconciled.

  5. Line 460: How does depth routing recover only 97% of the oracle's attainable gain when both achieve an AUROC of 0.665 in Figure 6?

  6. The implementation details of the depth-based routing heuristic are not clear. The authors explain that trajectory depth is the number of steps and that routing is performed at the domain level, but I could not find the exact decision rule or threshold used to choose between self-assessment and cross-examination. How is this threshold selected, and what value is used for the reported experiments?

Questions for authors

What distinguishes self-assessment from cross-examination in terms of the information available to them? Section 3 states that both are given the same trajectory, with self-assessment elicited from the acting model in a separate call. Does the self-assessor actually have access to any information about the agent's internal state that the cross-examiner does not? If both only receive the same textual trace, is the difference primarily the model identity and assessment prompt? This distinction is important because the paper's explanation for the advantage of self-assessment in low-visibility settings seems to rely on the acting model having privileged information ('internal state'). Does providing the external judge with this information about the agent's execution state or tool outcomes change the observed results?

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.