acceptodds
Under review as a conference paper at ICLR 2027

EdgeGuard-Agent : Edge-Level Verification and Policy Learning for Tool-Using Agents under Incomplete Information

Abstract

Tool-using agents are increasingly applied to stateful tasks such as order management, flight rebooking, and customer support, where requests are often incomplete, states are partially observable, and write actions may cause real side effects. Existing methods typically handle clarification, correction, and safety separately, making unified verification difficult. We propose EdgeGuard-Agent, an edge-level verification and policy learning framework for tool use under incomplete information. It treats each action as a state-transition edge and checks whether it is legal, grounded, executable, task-advancing, and non-redundant. At runtime, it focuses on risky or abnormal actions, including unsupported writes, invalid tools, missing arguments, state conflicts, and repeated actions, and then either accepts the action, replaces it with a safe executable repair, or blocks it if no safe option exists. Deterministic checks further prevent ungrounded arguments, unsafe writes, invalid confirmations, and cross-turn inconsistencies. During training, the same checks identify the first invalid action, restore the environment, apply a verified repair, and regenerate a causally consistent trajectory for supervised fine-tuning and GRPO with both task-level and edge-level rewards. Experiments on CAR-Bench, STATE-Bench, and -Bench-Ambiguous show improvements in task success of 29.60, 8.13, and 10.43 percentage points, respectively, with fewer premature actions and incorrect writes. On CAR-Bench, EdgeGuard-Agent-guided SFT improves task success from 27.69% to 35.30%, and GRPO further raises it to 40.42%. These results show that edge-level verification is a simple and effective way to improve both runtime reliability and policy learning in multi-turn tool-using agents.

Primary area:
foundation or frontier models, including LLMs
Keywords:
tool-using agents, edge-level verification, incomplete information, state-transition edges, runtime safeguards, trajectory repair, policy learning, supervised fine-tuning, GRPO, process rewards, multi-turn agents, stateful tool use

Reviews

Among:
Shape:
1234this paper, Top 30%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_HJmuOpenReview ↗
Rating
3
Confidence
3
Informativeness
3
Presentation
2
Soundness
3
Read review
Paper summary

The paper proposes EdgeGuard-Agent, a framework that treats agent actions as state-transition edges to be verified, repaired, or blocked. It distinguishes missing user information from facts recoverable through tools and checks grounding, execution conditions, and safety before acting. The same auditor also supports trajectory repair and policy learning through SFT and GRPO. Evaluation covers three stateful tool-use benchmarks, with additional component ablations and cross-model comparisons.

Critical strengths

The shared formulation for runtime protection and training supervision is well motivated. Distinguishing user-owned information from environment-recoverable facts addresses a practical problem: asking more questions does not necessarily resolve uncertainty correctly. Local repair preserves valid earlier decisions, while re-executing repaired actions avoids inconsistent downstream observations in training data. These choices form a coherent design, supported by improvements in task success and write safety across the evaluated environments.

Critical weaknesses

The policy-learning experiments do not isolate the contribution of EdgeGuard-Agent supervision. Table 4 compares an untrained model with EdgeGuard-Agent-curated SFT and subsequent GRPO, but lacks standard SFT and task-reward-only GRPO controls under matched training budgets. There is also no training ablation separating trajectory filtering, causal repair, and edge-level rewards. Consequently, the reported improvement from 27.69% to 40.42% demonstrates that the full training pipeline helps, but does not establish how much comes from the proposed supervision rather than additional training. This leaves a central contribution less convincingly validated than the runtime method.

Questions for authors
  1. Do you have comparisons with standard SFT and task-reward-only GRPO using the same initialization and comparable data and training budgets?

  2. Can you isolate the effects of causal trajectory repair and edge-level rewards in the policy-learning results?

Reviewer_bGg3OpenReview ↗
Rating
2(+1)
Confidence
4
Informativeness
1
Presentation
3
Soundness
1
Read review
Paper summary

EdgeGuard-Agent checks each action of a tool-using agent before it runs. For risky actions (writes, repeats, missing arguments) a verifier rebuilds the state, checks 6 criteria, and accepts, repairs or blocks the action. The same checker repairs training trajectories for SFT and gives per-step rewards for GRPO. It reports +29.6, +8.1 and +10.4 points of task success on CAR-Bench, STATE-Bench and tau3-Bench-Ambiguous, and 27.7 to 40.4 after GRPO on CAR-Bench.

Critical strengths
  • The problem is real, tool-using agents often act too early, guess arguments or write to the database without enough information.
  • Re-running the environment after fixing a bad step (instead of just editing the text) is a sensible way to build training data, since later observations stay consistent with the fix.
  • Tested on 3 benchmarks and 5 model families, with an ablation for each component.
Critical weaknesses
  • Not novel enough. EdgeGuard's abstract motivates the method with "unsupported writes", "unsafe writes" and "write actions [that] may cause real side effects". SABER (arXiv:2512.07850) presented these findings in prior work, showing that deviations in mutating (write) actions drive task failure while deviations in non-mutating actions have little effect, and proposed verifying mutating steps before execution. That is the core of EdgeGuard's runtime component. The paper cites SABER only inside a list of safeguards, never discusses it, and never compares against it. The "Write-Only Guard" ablation is the authors' own version, not SABER.
  • The training side is also not new. SAGE (Suri et al., 2026), already a baseline here, uses the same signal for runtime decisions and for GRPO rewards. The remaining pieces (ask-vs-read split, rule-based gate, no write escalation, fail-closed) are sensible engineering, not research contributions.
  • The headline gains are against no method. Against the strongest baseline (SAGE), success is 52.5 vs 51.5, which the authors themselves call "statistically comparable", and SAGE is better on Pass@3 (69.6 vs 65.6). No confidence intervals are reported.
  • The ablation table looks inconsistent. Removing any single component makes wrong writes 72-78%, worse than no method (66.9%), and premature calls drop to 11-15% vs 36.7% for the full method. These look like a different setup (they are close to the Table 4 Qwen3.5-27B numbers).
  • Missing training baselines: SFT on plain successful trajectories and GRPO with only the task reward. Without them we can't tell if the edge-level rewards help. Also not clear if train and test use different CAR-Bench tasks.
  • Appendices A-P are referenced for the algorithm, gate rules, rewards, baselines and metrics, but the PDF ends after the references.
  • Smaller issues: Ask Precision and Over-asking add to 100% (same metric counted twice as "wins" in Figure 2), ERASER has no citation, and it is unclear which tau version and task fixes tau3-Bench-Ambiguous is built on.
Questions for authors
  • How does EdgeGuard compare to SABER under the same backbone, simulator and benchmarks? What does the runtime component add beyond write-gated verification?
  • Which model is the verifier in each experiment? Is it the same model as the base agent?
  • Can you report confidence intervals, especially for EdgeGuard vs SAGE?
  • Can you add SFT on plain successful trajectories and task-reward-only GRPO as baselines?
  • Can you explain the ablation numbers (wrong writes worse than no method when removing one component)?

Lastly,

  • Can you include the appendices?
1 comment
AuthorsOpenReview ↗

Follow-up on Our Latest Response and Remaining Questions

Thank you again for the time and care you have devoted to reviewing our paper and engaging in this discussion. We appreciate your willingness to revisit the evidence, and your detailed questions have helped us make the experimental support much clearer.

We would like to briefly follow up on our 18 November morning response. We clarified how the original training settings were checked against server configurations and checkpoint parameters, and reported three-seed results for all training methods, including the full methods. Causal replay and edge rewards improve over their respective standard controls by 3.73 and 2.84 TSR points on average, with positive differences at every seed. The new paired intervals also support the improvement over SABER (+9.33 points; 95% CI [1.4, 17.0]) and the contribution of local repair (+12.27; [4.2, 20.0]). We additionally provided the scenario breakdown, exact corrected-benchmark version, and annotator agreement you requested.

We understand that the contribution itself remains important to your assessment. The scenario results locate the largest gains in missing-capability and missing-evidence tasks, while the training controls provide evidence for causal replay and edge supervision beyond ordinary training. We hope these findings help clarify the value of the shared runtime-and-learning formulation.

Could you let us know whether this latest response resolves your remaining concerns, or whether there is any specific issue we can still clarify? If the additional evidence has addressed those concerns, would you consider whether a more favorable score is now warranted?

Thank you once again for your sustained, careful reading and constructive suggestions. We have learned a great deal from this exchange and sincerely appreciate your effort.

Reviewer_4FgBOpenReview ↗
Rating
3
Confidence
1
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper proposes EdgeGuard-Agent to improve tool-using agents under incomplete information. It treats actions as state-transition edges and selectively checks risky or abnormal proposals, deciding whether to accept, locally repair, or block them before execution. The framework also proposes reusing the auditor for causal trajectory repair and supervision in SFT and GRPO. The authors report improvements in task success and reliability across three benchmarks and multiple base models.

Critical strengths

The paper is clearly presented, with Figure 1 making the overall workflow easy to follow. The distinction between user-owned and environment-recoverable information is intuitive and practically motivated. Reported improvements across three benchmarks and multiple base models also provide encouraging evidence of the framework’s applicability.

Critical weaknesses

Table 3 compares the full method with variants evaluated on a different task set, so the reported drops cannot be attributed solely to removing components. The same-task results in Appendix P.6 show more mixed trade-offs and do not fully support the component-level conclusions in §4.4.

Extra model calls may improve performance simply by providing another opportunity to check and revise actions, but a matched-compute control is missing to isolate the benefit of the proposed edge mechanism. The training results also lack comparisons against simpler data filtering or outcome-only GRPO, making the specific contributions of causal repair and edge-level rewards difficult to assess.

Questions for authors
  1. Can you clarify the differences in task sets and evaluation denominators between Table 3 and Appendix P.6? Which same setting results support the component-level conclusions in §4.4?
  2. How does EdgeGuard compare with a generic action checker using the same auxiliary model and a similar call/token budget? How much benefit comes specifically from the structured state and six-dimensional audit?
  3. Did the reported training runs use causal trajectory re-execution and the complete edge-level reward? Can you provide comparisons against simpler trajectory filtering and outcome-only GRPO to clarify their contributions?
1 comment
AuthorsOpenReview ↗

Follow-up on Your Questions and New Controlled Evidence

Thank you again for your constructive review and for recognizing the practical value of distinguishing user-owned from tool-recoverable information. Your questions helped us strengthen the evidence for the individual mechanisms. Following our initial response, we would like to highlight three points directly relevant to your concerns.

  1. Component attribution on the same tasks. All new ablations use the same 125 test tasks and 375 scheduled episodes. Removing local repair lowers TSR from 52.53% to 40.27%; the paired improvement is 12.27 points, with a 95% CI of [4.2, 20.0]. This supports a contribution from local repair within a common evaluation population. We distinguish improvements in task success from effects on write safety, rather than claiming that every component improves every metric.
  2. Controlling the additional checker. The Generic Checker uses the same auxiliary model, output-token cap and verification opportunities. EdgeGuard achieves 52.53% versus 48.53% TSR and 43.4% versus 47.7% Wrong Write. The TSR interval [-2.5, 10.5] crosses zero, so we report this as an observed improvement, not established statistical superiority. This comparison directly addresses your question about the benefit beyond another opportunity to inspect an action.
  3. Training contributions across three seeds. All training methods now have results for seeds 42, 123 and 2026 under matched actual token and update budgets. Causal-replay SFT reaches 35.38 ± 0.81% TSR, compared with 31.64 ± 1.11% for standard SFT, 33.16 ± 0.67% for filtering only, and 33.60 ± 0.71% for textual repair. Edge-level GRPO reaches 40.44 ± 0.77%, versus 37.60 ± 0.96% for outcome-only GRPO. These are means ± sample SD from training runs, including the full methods; causal replay and edge rewards outperform their respective standard controls at each of the three seeds. The comparison therefore goes beyond the original single-checkpoint training progression.

Could you let us know whether any of your original concerns remain unresolved, or whether there is another aspect we can clarify? If these comparisons address your concerns about component attribution and training supervision, would you consider whether they warrant a stronger acceptance recommendation?

Separately, if the additional evidence allows you to assess the work with greater confidence, we would appreciate an updated confidence assessment, as you judge appropriate. Thank you again for your time and for helping us make the empirical case more precise.

Comments on the paper

2 comments

Thank you for the detailed answers. Several of them change my assessment.

What I accept:

  • The Qwen3.6-plus actor result (61.15 -> 68.64 with the same model as verifier) shows the gain is not only a stronger verifier helping a weaker actor. My explanation was overstated.
  • You are right that the SAGE interval cannot be transferred to other comparisons, since paired variance depends on the per-task results. I withdraw that argument.
  • Thank you for clarifying that the SABER reimplementation uses Qwen3.6-plus for verification and reflection with the same actor and call limits. That resolves my mismatch concern.
  • The new 125-task ablations (write-only 45.9, no local repair 40.3, no deterministic gate 48.0) show that several components matter, and the write-only gap suggests that checking non-write actions helps on CAR-Bench.
  • The reward ablations (e.g., removing the risk penalty: TSR 40.60 but WW 76.20) show that Wrong Write carries information beyond TSR.
  • The Always-Guard trade-off, the SAGE training framing, and the annotator information are answered.

What remains open:

  1. Training recipe provenance. M.3 states that "a matching Qwen3.5-27B training recipe and wall-clock log are not present in the retained artifact set", and N.1/N.3 state that the reward coefficients and GRPO settings are not exposed. The rebuttal now says the original and new runs shared the stated recipe and gives exact values. Could you clarify how the original runs' recipe and coefficients were recovered, given the appendix statements? This matters for reproducibility of the main policy-learning result.
  2. Seed variance. The gaps over trained controls (+3.60 over standard SFT, +2.82 over outcome-only GRPO) compare single original checkpoints (*) against three-seed control means. Could you report the std of the controls and rerun the causal-replay SFT and edge-level GRPO with the same three seeds? Without this, it is hard to tell whether 2.8-3.6 points is meaningful.
  3. Confidence intervals for the new comparisons. Since the SAGE interval does not transfer, could you report the same task-paired bootstrap for EdgeGuard vs SABER, vs the Generic Checker, and for the component ablations?
  4. Per-scenario breakdown vs SABER. SABER scores below the Generic Checker (43.2 vs 48.4) under the same model and budget. A breakdown by CAR-Bench scenario (Base, Disambiguation, Hallucination subtypes) would show where EdgeGuard's gains come from, in particular on write-heavy Base tasks.
  5. Benchmark name and version. Since tau3-Bench-Ambiguous is derived from tau2-Bench and not from Sierra's tau3, I suggest renaming it to avoid confusion. Please also state the exact tau2-Bench commit, since earlier versions contain known ground-truth errors in airline and retail that were later fixed.
  6. For the 600-action audit, please report agreement between the two annotators.

Overall, the new comparisons address most of my empirical concerns: EdgeGuard improves over SABER and over a matched generic checker, and several components contribute. I still see the novelty as incremental (write-gated verification extended to more action types, plus causal-replay training with a shared signal), and the training-recipe question is important. I will therefore update my score to weak reject I still think their novelty is lacking, but if the other reviewers strongly argue for acceptance I wont be opposed.

AuthorsOpenReview ↗

Further Evidence on Training Robustness, Runtime Gains, and Benchmark Provenance

Thank you for your patience and for reconsidering the earlier concerns. We appreciate the specific remaining questions and have added the following evidence.

1. Training configuration and seed variance. We apologize for not including the actual training parameters in the submitted appendix. We checked the original runs against server configurations and checkpoint parameters. These records were absent from the submitted artifact set; we will add the full recipe and checkpoint mapping. The original and new runs used Qwen3.5-27B, full-parameter BF16 training, AdamW, and matched actual training tokens and optimizer updates within each comparison. SFT used LR 1e-5, batch 64 packed sequences, 16,384-token context and 3% warmup. GRPO used the same SFT initialization, LR 1e-6, group size 8, batch 64 trajectories, KL 0.04 and ratio clip 0.2. Task/legal/source/grounding/progress/risk/redundancy weights were 1/.1/.1/.1/.2/-1/-.1.

All seven methods now have training runs with seeds 42, 123 and 2026, evaluated on the same 125 test tasks with three trials per task. TSR (%) is mean ± sample SD:

MethodMean ± SD
Standard SFT31.64 ± 1.11
Filtering-only SFT33.16 ± 0.67
Textual-repair SFT33.60 ± 0.71
Causal-replay SFT35.38 ± 0.81
Outcome-only GRPO37.60 ± 0.96
Generic-process GRPO38.22 ± 0.67
Edge-level GRPO40.44 ± 0.77

These three-seed results are separate from the original single-checkpoint rows. Causal replay exceeds standard SFT by 3.73 pp and edge rewards exceed outcome-only GRPO by 2.84 pp, with a positive difference at each matched seed. The advantage therefore recurs across all three seeds.

2. Paired uncertainty estimates. For the requested paired comparisons, the TSR differences (pp) and 95% CIs are:

EdgeGuard versusDifference95% CI
SABER+9.33[1.4, 17.0]
Generic Checker+4.00[-2.5, 10.5]
Write-only guard+6.67[-0.4, 13.5]
No local repair+12.27[4.2, 20.0]
No source split+1.60[-4.3, 7.6]
No deterministic gate+4.53[-2.0, 11.1]

The intervals support the gain over SABER and the contribution of local repair. The other intervals cross zero, so those differences are not established as significant.

3. Where the runtime gains arise. Using the same actor, verifier and call limits, the scenario breakdown is:

MethodBase (50)Hallucination (50)Disambiguation (25)
SABER52.0036.0040.00
Generic Checker54.6744.0045.33
EdgeGuard54.0054.0046.67

All entries are TSR (%); Generic Checker's overall rate is 182/375=48.53%. The gain over SABER is 2.00 pp on Base, 18.00 on Hallucination and 6.67 on Disambiguation. Within Hallucination, SABER→EdgeGuard is 18/54→32/54 for Missing Tool, 18/48→24/48 for Missing Tool Parameter, and 18/48→25/48 for Missing Tool Response. These gains concentrate in the missing-capability/evidence cases motivating verification beyond writes (§§3.2–3.3). Removing the source split also lowers Disambiguation TSR from 46.67 to 41.33.

4. Benchmark provenance and naming. Our ambiguous tasks were constructed from [Amazon τ²-Bench-Verified] (commit 864350a), whose documented fixes address ground-truth and task-definition errors, including identical-item exchanges in Retail and policy-inconsistent compensation in Airline. Appendix G describes our subsequent ambiguity transformations. We intended “τ³” to distinguish the corrected source from original τ² tasks, but this created confusion with Sierra's τ3. We apologize and will use “τ²-Bench-Verified-Ambiguous,” cite this exact source and retain the construction protocol in Appendix G.

5. Annotation agreement. The two professional annotators agreed on 565/600 actions: 94.17% raw agreement and Cohen's κ=0.875 across High-Risk, Medium-Risk and Safe. These measure agreement between annotators, separately from the previously reported trigger and repair performance.

A / BHigh-riskMedium-riskSafeTotal
High-risk807390
Medium-risk676890
Safe38409420
Total8991420600

6. Contribution. We agree that the design is simple; simplicity alone does not determine novelty. Our contribution lies in how actions are represented, corrected and learned from. Source-aware checks determine whether to ask or read; local repair changes the earliest invalid edge; causal replay regenerates its downstream observations;. HJmu also highlighted this shared formulation and causal consistency as a coherent design. The new results now connect that design to gains over SABER, local-repair ablations and three-seed training controls. We hope this evidence supports a further reconsideration of the contribution.

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

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