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Under review as a conference paper at ICLR 2027

From Evidence to Action: How Tool-Using Agents Fail

Abstract

Tool-using agents make consequential changes to external state, yet correct outcomes do not guarantee that their actions were supported by evidence established beforehand. We study where this evidence-to-action chain breaks as agents move from deciding whether to act to executing single actions and dependent workflows. Across ten model–harness configurations, strong static action assessment can coexist with much weaker interactive execution. Failures often begin before execution: agents stop with incomplete investigation or act before required evidence is established. Once required evidence is obtained, single-action execution is usually reliable, while multi-action workflows additionally expose unresolved prerequisites and incomplete execution. For this analysis, we introduce SafeActBench, comprising 656 cases across six operational domains and five protocols that progress from static action judgment and investigated non-action to single- and multi-action workflows. A provenance-bound Evidence Ledger and deterministic trajectory evaluator track what information was established, when actions occurred, and whether downstream dependencies were satisfied. These results show that failures arise not only from missing information, but also from how agents use established evidence when deciding and executing actions.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
Tool-Using Agents, Evidence-Grounded Decision Making, Trajectory-Level Evaluation, Agent Evaluation

Reviews

Among:
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1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_mQ1vOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

The paper frames consequential tool use as an evidence-to-action chain and asks where it breaks. It introduces SafeActBench, 656 synthetic cases across six domains and five protocols: static ALLOW/BLOCK/DEFER judgment (Legacy), investigated non-action (V0), a single action (V1), and linear and DAG-structured multi-action workflows (V2/V3). A provenance-bound Evidence Ledger and a deterministic evaluator check whether required evidence was established for the right entity and state before each action, whether tools, targets, and arguments were correct, and whether results and dependencies were propagated. Across ten model–harness configurations (five models, each with its family-associated harness and a shared Inspect ReAct harness), the paper reports high static accuracy alongside much lower interactive success; failures concentrated in incomplete investigation and premature action; reliable execution once evidence is complete (conditional success 83–100%); unresolved prerequisites and partial execution in workflows; and substantial, model-dependent harness effects. In interventions on 43 V1 cases, agents often still act when decisive evidence is withheld, and they respond more to a requester's claim than to an evidence package.

Critical strengths
  1. A verifiable and validated evaluator. Scoring is deterministic and was audited against human judgments on 300 trajectories (2.0% false acceptance, 1.3% false rejection); case specifications were checked on 120 cases (κ 0.74–0.87); and alternative evidence paths are accepted while wrong-entity and stale-evidence controls are rejected. This makes the benchmark a credible, reusable artifact.

  2. Uncertainty-quantified behavioral analyses. The paired harness comparison (570 shared cases, three rollouts, case-paired bootstrap intervals) and the evidence interventions show that harness choice and evidence presentation change agent behavior in model-dependent ways, which is useful for agent builders.

Critical weaknesses
  1. The success criterion conflates substantive evidence gaps with procedural ones. ECS credits investigation against an author-defined set of required reads (5.6–7.1 per case on average), although Table 8 accepts some alternative retrieval paths. The illustrative failures in Appendix D.5 and D.6 are otherwise correct workflows that fail because one designated rule source was not credited, and D.1 fails only on BLOCK vs. DEFER after complete investigation. Requirement-level agreement before adjudication is 86.7–93.4%, and validation was performed by the research team. Without a breakdown of the BSR (21.7–62.9%) and PAR (37.0–66.9%) failures into missing decision-relevant evidence versus missing designated sources, it is unclear how much of the headline finding reflects agent behavior rather than the strictness of the specification.

  2. The main comparisons are confounded. On the same 100 V1 cases, static accuracy is 95–99% versus 28–52% interactive success (Sec. 5.2), but in the class-balanced control (Appendix C.2.1) the gap shrinks to +5 to +13 points for most fully covered configurations and reverses for GLM–Inspect (−10.1), with output-format reliability as a co-factor. SCGR-EG lifts GLM–ZCode from 12.1% to 58.0% on V2 and from 34.1% to 68.0% on V3, suggesting that much of the low performance reflects interface handling rather than evidence reasoning. The interventions cover only 43 V1 cases (22 for contradiction), with a single replicate for each manipulated condition.

Questions for authors
  1. For failed V0/V1 episodes, what fraction lacked evidence that annotators outside the research team judge decision-relevant, versus only a designated source or a terminal label (as in D.1, D.5, D.6)? This answer would most change my assessment.

  2. How do ECS and the diagnostics change if any semantically sufficient evidence path is credited, for example with requirement sets reduced to the minimal decision-relevant subset?

  3. The V0 rules (Table 1; p. 19) imply that an agent that finds a violated condition early and stops before completing the remaining required investigation fails ECS and counts toward BSR. Is that the intended behavior, and how many BSR failures are of this kind?

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

This paper asks whether tool-using agents establish the required evidence before taking consequential actions, not merely whether they reach a correct final state. It introduces SafeActBench: 656 synthetic cases over six domains and five protocols, from static action judgment and investigated non-action to single-action and linear/DAG multi-action workflows, scored by a provenance-bound Evidence Ledger and a deterministic evaluator without an LLM judge. Across ten model–harness configurations, the authors report that near-ceiling static judgment coexists with much weaker interactive execution, that most failures arise from incomplete investigation or premature action rather than execution, and that multi-action workflows add unresolved-prerequisite and incomplete-execution failures.

Critical strengths
  1. A deterministic, provenance-aware evaluator with serious validation. Unlike LLM-judge or endpoint-only scoring, the evaluator binds evidence to entity/state and checks result propagation, and the authors stress-test it.
  2. Careful experimental hygiene that supports a localized claim. Three rollouts per cell, 100% coverage, case-paired bootstrap CIs, within-case harness comparisons on identical cases, failure-mode decomposition, and explicit acknowledgment that Gap/Part. overlap and that V0 ECS is not an unsafe-action rate.
Critical weaknesses
  1. It is unclear what the benchmark measures, because neither the case-construction process nor the substantive correctness of “failed” actions is reported. Appendix B.3 describes only how evidence requirements were authored and reviewed; it does not describe how the 656 cases, their tool interfaces, business records, the 277 “shared-world cases,” or the 2,468 “frozen-evidence deltas” were produced—hand-written, templated, or LLM-generated—nor how diversity across and within the six domains was ensured or how near-duplicate cases were controlled. 2: The empirical findings largely restate concurrent work, and the paper offers no actionable guidance derived from its own diagnostics. The three main conclusions—static judgment does not transfer to interactive execution, agents act before investigation is complete, harness choice matters—are already reported by some of the cited papers.
Questions for authors
  1. How were the cases, tool schemas, and underlying records constructed (manual, templated, or LLM-generated), and what are the “shared-world cases” and “frozen-evidence deltas”? Were cases deduplicated across domains/protocols?
  2. How would the findings guide the optimization? Given the diagnostics in Table 3 and Fig. 5, what concrete harness- or prompt-level change do the authors recommend?
  3. Is the protocol identity (V0 vs. V1) inferable from the task instruction or tool interface? Since every V0 case requires non-action and every V1 case requires exactly one action, leakage would inflate both.
  4. In the Withheld condition, what does the affected tool return—an explicit not-found, an empty candidate set, or a neighboring record? This determines whether continued action is a genuine evidence-grounding failure.
Reviewer_XVGnOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper introduces SAFEACTBENCH, comprising 656 cases across five evaluation protocols. It evaluates agents' ability to establish the necessary evidence before acting and bind that evidence to the correct targets and actions, analyzing behavioral differences across ten model-harness configurations and different evidence conditions. The experiments frequently reveal incomplete investigation and action before evidence establishment, while multi-action workflows additionally exhibit unmet prerequisites and incomplete execution.

Critical strengths
  1. The motivation that final-outcome correctness alone is insufficient to assess the appropriateness of the actions leading to it is important.

  2. The paper develops systematic evaluation protocols to investigate its research questions. The authors evaluate multiple models and harnesses and conduct additional experiments involving evidence withholding and changes in evidence presentation.

Critical weaknesses
  1. Although the paper documents the existence and frequency of failures, it does not clearly establish what new insights it provides beyond existing understanding. Since investigation completion is part of the success criteria, further analysis is needed beyond showing that incomplete investigation is scored as failure. It would be helpful to distinguish more clearly between failures to retrieve necessary information, failures to bind retrieved evidence correctly, and failures to construct the correct action despite sufficient evidence.

The connections among the research questions, control conditions, metrics, and conclusions are not sufficiently clear. Although several analyses are presented, the paper should explain more explicitly which question each analysis addresses and what explanation its results support. Concrete examples contrasting different failure types, together with their interpretation in the main text, would help readers understand the key findings.

The three contributions are presented as the formulation of an evaluation perspective, benchmark construction, and empirical analysis, but their individual novelty and distinctiveness are not sufficiently clear. In particular, the paper should clarify what conceptual contribution the proposed evaluation perspective offers beyond benchmark design and what the empirical analysis reveals beyond existing understanding.

  1. Although the paper includes interventions under insufficient evidence, these experiments have limited ability to separate the effects of information acquisition, evidence use, and action construction. Controlled comparisons that vary the availability of evidence and candidate actions on the same tasks, together with more detailed diagnostic metrics, are needed. Moreover, the high conditional success rate after investigation completion may reflect the selection of relatively easy cases, so this result alone does not establish insufficient investigation as the primary cause of failure.

The specific task content and the rationale for selecting cases for analysis are not sufficiently connected to the interpretation of the main results. In particular, the paper should clarify which cases are used in the intervention experiments, what characteristics they represent, and how failure patterns vary with task characteristics.

The experiments focus on synthetic datasets constructed by the authors, making it difficult to assess the extent to which the observed failure types and frequencies also occur in real-world tool-use environments. Analyzing patterns in real-world data using additional benchmarks would strengthen the motivation and persuasiveness of the study.

Questions for authors
  1. What approaches do the authors think could reduce incomplete investigation and action before evidence establishment?

  2. What criteria were used to select the 43 cases for the intervention experiments?

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