- Rating
- 2
- Confidence
- 4
- Informativeness
- 2
- Presentation
- 2
- Soundness
- 2
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Paper summary
Agents fail in two ways: a tool call is rejected by the environment, or the task fails without any error. This paper asks whether the agent's hidden state, read before it writes its next action, already signals that the coming call will be rejected. Linear probes on frozen Qwen3 states in -bench retail and airline rank rejection-prone calls well, including on unseen tasks, and beat text baselines within the training tasks. The same representation predicts eventual task failure much less well, a set of propositions explains why call-level records say little about task success, and using the probe to trigger a verification step does no better than random or timing-matched triggers.
Where it sits (October 2026): pre-generation probing for tool use is now an active line. Tool necessity is linearly decodable before generation (arXiv 2605.09252), probes on early activations predict episode failure (arXiv 2607.06503, cited), and concurrent work locates tool-misuse signals in a few neurons (arXiv 2608.00218) and probes tool-calling errors across many models. The distinctive parts here are the target, environment rejection, and the evaluation protocol, rather than the existence of a pre-action signal.
Critical strengths
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The evaluation protocol is the paper's best contribution. Scoring AUROC within the same task and the same call position removes the shortcuts that make most agent-probe results look better than they are: harder tasks fail more, and later calls fail more. With task-grouped folds, permutation nulls and a candid log of the authors' own bugs, this is a protocol the probe-monitoring line should adopt.
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The resampling audit gives an intuition other papers lack. By restoring the same context and sampling again, it shows that whether the first call is rejected is almost deterministic while the probe's probabilities remain miscalibrated, which separates "the outcome is noisy" from "the probe is wrong".
Critical weaknesses
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The headline is that hidden states know more than the text, but that comparison is only made in sample, and a simpler reading is untested. If the context already fixes which tool comes next, and some tools are rejected more often than others, a probe that reads "which call is next" will look prescient without knowing anything about failure. The appendix leans this way: the next tool name is perfectly decodable before the call, and once the call is written a text-only predictor matches the probe. The gains over text are measured on training tasks, with the layer chosen on those tasks, against a baseline that sees only the end of the conversation. The one held-out comparison is post hoc and inconclusive in airline. Everything also rests on one model family and one benchmark, and the cross-family replication could not run because the fixed layer does not exist in a shallower model. With no code or data released, none of this can be checked. I would raise my score with held-out gains, a within-tool control and released code.
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The intervention null is informative, but the study cannot answer its own question. The probe gate fires at the very start of most trajectories, so it tests "verify from the start" rather than "verify when risk rises", and the design can only detect large effects. This leaves the paper without evidence that a pre-action monitor beats the cheaper alternative its own appendix suggests: checking the written call before it executes.
Questions for authors
Questions that could change my assessment:
- What are the gains over the text baseline on the held-out tasks, using the frozen probe and a baseline fitted on all training tasks?
- What remains within groups that share the task, the call position and the realised tool, and how well does a baseline that knows only the next tool's identity do?
- How was the layer chosen, and did the baselines receive a comparable search? Does the result survive a depth-relative layer rule on a second model family?
- Can you release the code, trajectories and extracted states during the discussion?
Recommendations (not affecting my score):
- Compare pre-action monitoring with post-call, pre-execution text checks as deployment policies, including their latency.
- Position the work against arXiv 2605.09252, arXiv 2608.00218 and the recent probe studies of tool-calling errors, and state the rejection target and the within-group protocol as the contribution.
- Use a per-turn rather than persistent trigger in the intervention, and report the smallest effect the design can detect.
- Please confirm that the identical entries across Tables 5, 9 and 13 and Appendix B.15 are not copy errors.
Response to reviewer R1
Q1. Why verification does not beat random triggering, and whether agents follow the instruction. The agent mostly does what the instruction asks, but it already did so without the instruction, so the instruction barely changes its behavior. This is an exploratory analysis of the existing held-out arms. In retail, the agent looks up the relevant record before its first write after the trigger in 86.8% of A2 branches. At the same branch points without the instruction, the rate is 83.5% in the resampling control A6 and 84.2% in the original trajectories A1, so the instruction adds about 3 pp over A6 (+3.2 pp [0.6, 7.1]). The number of rejected writes per branch does not change (A2 − A6, −0.12 [−0.45, +0.22]). Moreover, 87% of A2's rejected writes after the trigger act on an entity the agent had already looked up, and most fail on the kind of state a lookup returns, such as an order that is no longer pending or a product variant that does not exist. The agent therefore often checks the entity and still writes a call that its state does not allow. Because the instruction changes so little, comparing where it is triggered cannot show whether risk-based timing would help a more effective intervention, and the null in Tab. 5 is best read as a null for this instruction. Airline is descriptive (−1.7 pp [−7.3, +3.0]). This measure counts lookups by tool name and matches entities by identifier, so it cannot see which fields the agent read.
Alternative prompts. We tested one alternative instruction on the held-out retail branch points, under a protocol fixed before the run. It asks the agent to re-read the record right before each write and then decide. The instruction reached the model at all 208 trigger prefixes, but the agent did not detectably add the re-read step (27.8% vs 28.5% of writes directly preceded by a lookup of the same entity), and no change in rejection turns was detected (−0.30 per triggered branch [−0.65, +0.10], from 3.19 at the same prefixes without the instruction). This marker counts writes whose immediately preceding call is a lookup of the same entity, which is stricter than the measure above, where any lookup before the first write counts. The design had 80% power only for about −0.55 per branch, so this is a non-detection rather than evidence of no effect. As this first stage showed no change in behavior, the protocol stopped before the second stage, which would have compared probe and random triggers, and airline was not run. The two instructions failed in different ways. The first was largely followed, but the agent already looked up before writing without it, while the second was not followed. Neither detectably reduced rejections, so a useful variant may need to change what the agent writes rather than what it reads, which we leave to future work.
W2 and Q2. A central takeaway and its implications. G1 states the single question and how the three parts answer it, and the analysis above now gives the reason R1 asked for. G1 gives two practical implications. A monitor of the next call should not be read as a task monitor, and an intervention needs outcome evidence against random and timing-matched controls. The analysis above adds a third, that asking for more lookups may not help an agent that already looks up before writing.
W1. Novelty and the expected direction. We agree that the linear probe is standard. We use it as a measuring instrument, not as a new method, and G2 states the contribution as the rejection target, the within-task and within-position protocol, and what the signal does and does not support. We also agree that rejection being easier to predict than task failure is the expected direction. What the paper adds is the size of the gap under a protocol without task and position shortcuts (retail 0.882 vs 0.549 on training tasks and 0.896 vs 0.584 on test tasks, both on the Tab. 3 groups), and the finding that, on the same groups, the hidden state's advantage over a text predictor is detectable for rejection but not for final failure (Tab. 3).
W1. Simple text baselines. We agree that the advantage was partly overstated. Against the strongest pre-action baseline we added, a probe on the model's first-token distribution, the retail gain is +0.069 on training tasks (OOF) and +0.078 on test tasks, about half the gain over the character baseline in Tab. 1. In airline, the gain over text can be explained by which tool comes next, and we have narrowed contribution (1) accordingly. G3 gives the full comparison, including a full-context encoder and tuned n-gram baselines.
Paper changes. Sec. 6.2 adds two sentences on why verification did not help and limits the null to the tested instructions, with both analyses in App. B.15; the new "Implications" paragraph (G1) includes the point about checking; App. E.2 lists instructions that change what the agent writes as future work; contribution (1), Sec. 4.1 and related work change as described in G2 and G3.