acceptodds
Withdrawn from ICLR 2027

When to Act, Not What to Act: Prospective Authorization for Tool-Using Language Models

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

Tool-using language models must distinguish permission to act now from a promise of authorization later. We formalize this as prospective authorization: a user introduces an action but reserves permission until a future, action-linked signal. Existing tool-use evaluations assume all instructions authorize immediate execution and do not sufficiently evaluate such temporal constraints. We introduce I24, a benchmark of 1,764 multi-turn episodes spanning three authorization expressions, three signal conditions, and four tool-use domains. On the 306-episode held-out set, a frozen Qwen3-8B model reaches 34.6% episode-level transition error, while rule and few-shot prompting retain substantial errors. State-explicit supervision represents authorization force, pending actions, and execution decision; it reduces transition error from 34.6% to 5.8% across three independent trainings, while corrupting this supervision removes the gain. Building on this, we implement a modular Prospective Authorization Gate (PAG) that separates authorization tracking from native action generation and exactly-once execution. PAG achieves 2.6% mean transition error on native I24 execution across three seeds, passes non-inferiority tests on five general capability benchmarks (all deltas within ±1.5%), and component ablations confirm removing any core module increases error by 9.8–15.5 percentage points.

Primary area:
foundation or frontier models, including LLMs
Keywords:
large language models, tool agents, prospective authorization, multi-turn dialogue, authorization timing, exactly-once execution, benchmark construction, supervised fine-tuning

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_c7FBOpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
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Paper summary

This paper studies prospective authorization, where a tool-using LLM must wait for a later authorization signal before executing a proposed action. It introduces I24, a benchmark of 1,764 episodes across three authorization modes, three signal conditions, and four domains. State-explicit supervision reduces the reported symbolic transition error from 34.6% to 5.8% on 306 held-out episodes. PAG combines a frozen planner, learned authorization tracker, pending-action ledger, and exactly-once executor, with a reported 2.6% native error on all 1,764 episodes, including tracker-training episodes. The paper also reports transfer experiments, component ablations, comparisons across planner models, and tests of general capabilities.

Critical strengths

1. A practical problem with a clear definition and a controlled benchmark design.

Knowing when an action is authorized is a practical problem that deserves evaluation alongside choosing the right action. The paper formally defines three episode-level error types. Its paired 3×3 design varies the authorization mode and signal condition while keeping the action and dialogue context fixed. This helps identify errors in when the model acts. The problem definition and benchmark design are useful contributions even apart from the proposed training method.

2. The breakdown of baseline errors is useful.

Rule prompting reduces pre-signal errors from 14.4% to 3.9% but leaves duplicates at 23.2%. Few-shot prompting reduces duplicates from 22.2% to 10.8% while increasing missed errors to 20.9%. Reporting these errors separately shows that a prompting method can reduce one type of error while increasing another. This makes it easier to see where each method succeeds and fails.

Critical weaknesses

1. The experiments do not show whether state-explicit supervision improves on ordinary fine-tuning.

The main improvement from 34.6% to 5.8% compares C1 with a frozen model. The rule and few-shot baselines also receive no task-specific fine-tuning. What is missing is a plain/action-only SFT baseline trained on the same 1,458 episodes, with the same base model and training budget, but without the intermediate state targets.

MechDel does not answer this question. Shuffling the intermediate state labels produces 66.7–72.5% error. This shows that incorrect state labels hurt performance, but it does not show that correct state labels improve performance over ordinary SFT.

The results in Table 1 make this comparison especially important. C1 with 3B and 8B Llama models reaches 0.0% error, three of four leave-one-domain-out settings reach 0.0%, and OOD-v2 error (3.1%) is lower than the main held-out error (5.8%). C1 therefore achieves near-perfect performance in several controlled settings. Whether ordinary SFT can do the same without explicit state targets is still an open question (see Q1).

The paper also needs to explain how the full-state training objective in Section 3.3 relates to the decision and action-matching losses for PAG's tracker in Appendix C.1. These may describe different models, but the authors should state which training setup was used for each experiment. The results show that C1's training procedure works better than the tested baselines. They do not show how much the state targets add, or whether those targets are necessary. This missing comparison directly affects the paper's claim that state-explicit supervision is a useful contribution beyond ordinary fine-tuning.

2. The native evaluation does not show how PAG performs on unseen episodes, and the ablations are not fully described.

Section 4.3 evaluates PAG on all 1,764 I24 episodes, including the 1,458 episodes used to train the tracker (Appendix C.1). About 82.7% of the evaluation episodes were therefore used in tracker training. Testing native execution is useful, but the overall 2.6% error combines results from training and held-out episodes. It does not tell us how well PAG performs on unseen episodes. The component ablations and comparisons across planner models also need results on the held-out episodes to show whether their findings hold beyond the training data.

Table 3 lists which modules are removed but does not explain what the system does in their place. The ledger stores pending actions, and the executor checks whether an action has already been executed. These rules already provide part of the required behavior, so the ablations must be described clearly to show what the learned tracker adds. Held-out results and these implementation details are needed to assess PAG's performance on unseen episodes and the claim that each component is necessary.

The current experiments do not show whether state-explicit supervision improves on ordinary SFT or how well PAG performs on unseen episodes in native execution. Answering these questions requires the missing SFT comparison and separate results for the held-out native episodes. Those results could change the conclusions about both methods. The current evidence is therefore not sufficient to support acceptance.

Questions for authors
  1. Comparison with ordinary SFT (additional experiment; W1). A comparison with plain/action-only SFT using the same base model, 1,458 training episodes, and training budget, but no intermediate state targets, would help show what the state targets add. If such results are available, I would appreciate the transition errors for both methods on the same 306 held-out episodes. A consistent advantage for C1 would support the claimed benefit of state-explicit supervision.

  2. Native results on held-out episodes (reanalysis; W2). It would be helpful to see the results in Tables 2–4 for the 306 held-out episodes only. If PAG's advantage and the effects of removing each component hold on this set, that would address much of my concern about the native evaluation.

  3. Training, evalution and ablation details (clarification; W1–W2). Please clarify the training outputs and losses used for C1 and PAG, including whether Section 3.3 describes C1 and Appendix C.1 describes PAG's tracker. A brief explanation of what the system does when each component is removed in Table 3 would also make the ablations easier to interpret. These details would clarify which training method was tested and what each component contributes. Also, I am wondering why PAG's results in Table 5 differ from Frozen at all (e.g., the 1.3-point drop on MMLU), given that the planner is frozen and the tracker is trained separately.

  4. Symbolic error rates (clarification). Section 4.2 reports 5.8% symbolic held-out error for C1, while Section 4.3 refers to 0.0%. I would appreciate clarification of whether these come from different settings, with the model and evaluation split identified for each, or whether one value needs correction. This would help clarify the comparison with native execution.

  5. Benchmark reproducibility and validity (clarification; Strength 1). The paper says that data construction and annotation details are in Appendices A–D, prompt templates are in Appendix C, and the complete OOD-v2 expression list is in Appendix A, but I could not find these materials. Please provide the I24 generation procedure, including the templates and how distractor signals are created, as well as the evaluation prompts, OOD-v2 expression list, and the ledger's action-matching rule. I consider the benchmark design a main strength, but these details are needed for others to reproduce and check the results.

    It would also help to explain whether matching keywords or phrases in the dialogue templates could produce similarly low error rates. Examples from the benchmark or experimental results addressing this possibility would help support the interpretation of the results.

  6. Model details and figure corrections (minor; requires revision).

    1. Please specify the exact model repository/checkpoint identifier referred to as "Qwen3-8B-Instruct" (e.g., Qwen3-8B with thinking mode enabled or disabled, Qwen3-8B-Base, or Qwen3-VL-8B-Instruct), state whether thinking mode was enabled or disabled where applicable, and use the precise model name consistently throughout the paper.
    2. Please translate all text in Figure 2 into English and use the same decision labels in the text and figures (e.g., ALLOW versus ALLOW_NOW).
Reviewer_qn4LOpenReview ↗
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Confidence
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Informativeness
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Presentation
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Paper summary

The paper proposes prospective authorization as a formalization of deferred tool-use permission, builds the I24 benchmark of templated multi-turn dialogues, trains a model with explicit state supervision, and wraps it in the PAG modular architecture with an external ledger for native execution.

Critical strengths

The problem is real and under-studied, and the paper treats it seriously rather than as a prompt-engineering curiosity. The error taxonomy (pre-signal / missed / duplicate) is crisp and maps cleanly onto the failure modes that actually matter for deployment: a premature payment and a duplicate email are different bugs and it's good to see them separated. I found the few-shot result interesting: few-shot prompting makes things worse (40.8% vs 34.6% frozen) by flipping the error profile toward missed executions. That's the kind of counterintuitive finding that tells you the benchmark is measuring something real. The MechDel control, shuffling the state supervision and watching the gains evaporate, is good causal hygiene that most papers skip. And I appreciate the honest scoping: the authors repeatedly say the evidence is limited to controlled settings and don't oversell the OOD results. The limitations section reads like it was written by someone who actually thought about what could go wrong.

Critical weaknesses

I'm not sure about the benchmark's difficulty. I24 is template-instantiated: 1,764 episodes generated from a 3×3×4 cross product. The authors' own results suggest the task collapses once state is made explicit. 0.0% errors across LODO domains and alternative backbones, 3.1% on paraphrased expressions. A benchmark where the proposed method achieves zero error in nearly every generalization setting is not discriminating enough to support claims about learning transferable authorization regularities. It reads more like the model learned the template schema. The naturalness rating doesn't address this; templated language can be natural-sounding and still structurally trivial.

Also there's no real-world validation. The native execution environment is still I24 episodes with real API calls: same templates, same signal vocabulary. The discussion lists "validate in real user interactions" as future work, but for a paper whose entire motivation is deployment risk, the absence of even a small human-interaction study is a significant gap. The 60% tracker-misjudgment failure share (mostly distractor confusion, per Appendix D) is exactly where real dialogue would be hardest, and it's untested there.

Questions for authors
  1. Can you construct an adversarial or human-authored test set outside the template distribution? Even 100 episodes would help enormously.
  2. Few-shot performing worse than zero-shot. Is it robust across prompt variations, or an artifact of the 9 chosen examples?
Reviewer_LSHkOpenReview ↗
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Confidence
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Informativeness
1
Presentation
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Paper summary

The paper targets for the scenario that user want a tool-use to be delayed. But the whole paper is ai-generated and contains poor readibility figure and hallucination reference.

Critical strengths

No.

Critical weaknesses

This paper is fully AI-generated and is not reasonably supervised by human researchers for the following reasons:

  • AI-generated figure:
    • Figure 2 with unreasonable Chinese breaking readibility.
  • Hallucination reference with completely wrong authors:
    • “Speech acts, commitment and multi-agent communication”
    • “The rational speech act framework”
    • “Pioneering a prospective benchmark to evaluating tool utilization safety in llms”
Questions for authors

No.

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

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