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Under review as a conference paper at ICLR 2027

Learning to Test: Sequential Monitoring of Generative Models and Agents

Abstract

As AI models scale and are deployed with increasing autonomy, their opaque decision-making can pose risks to users and providers, motivating guardrails and continuous task monitoring for compliance with safety and deployment protocols. However, monitoring quality can fluctuate depending on the model and problem at hand, and generally lacks formal assurances. We recast deployment monitoring as a statistical testing problem, viewed in particular through the lens of sequential hypothesis testing, or 'testing by betting'. Leveraging the framework’s error-control qualities, we equip monitors with verifiable false alarm controls such that benign model behavior triggers interventions only at a prespecified, tolerable rate. Challenged by the ambiguity of defining complex black-box monitoring problems in statistical terms, we investigate data-driven test designs with learned reference, betting, or evidence-normalization components. Empirical evaluations span diverse models and monitoring targets, including language generation, chain-of-thought reasoning, multi-turn interactions, and agentic tool use. Our results affirm that learned tests exhibit error-controlling and adaptive properties, while highlighting the nuances of translating raw monitoring scores into statistically valid evidence.

Primary area:
probabilistic methods (Bayesian methods, variational inference, sampling, UQ, etc.)
Keywords:
agentic monitoring, sequential hypothesis testing, testing by betting

Reviews

Among:
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1234this paper, Top 15%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
Reviewer_vek8OpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper studies sequential monitoring during the execution of generative models and agents, aiming to detect anomalous behavior as early as possible while controlling the false alarm rate on normal trajectories. The authors transform black-box scores into stepwise accumulated statistical evidence, identify historical dependence within trajectories as a key obstacle to ensuring test validity, and propose two learning schemes: a conditional mean test and an Actor–Critic test. On tasks such as mathematical reasoning, code generation, multi-turn interaction, and tool calling, it generally demonstrates good empirical false alarm control and anomaly detection capability.

Critical strengths
  • It explicitly distinguishes cross-trajectory monitoring from within-trajectory monitoring, reveals that marginal calibration cannot substitute for history-conditioned normalization, and provides a clear framework for understanding the validity of sequential monitoring.

  • It separately learns evidence growth and normalization under the normal distribution, and explains the Actor–Critic initialization through a conditional likelihood ratio, balancing interpretability and expressive power.

  • The method is validated across multiple models, tasks, and scorers, demonstrates the potential of combining evidence from multiple scorers, and also reports cases where false alarm control fails.

Critical weaknesses
  • Strict validity depends on the sufficiency of historical states and an upper bound on conditional normalization, but training with limited data and empirical drift correction cannot yet certify these conditions, and the false alarm rate on some tasks still exceeds the target.

  • The method depends on the distribution of calibration data and coverage of trajectory lengths, limiting its applicability to distribution shifts and longer tasks; the experiments also do not demonstrate that actual interventions after alarms can improve task success rates or safety.

Questions for authors

Please see the weaknesses.

1 comment
AuthorsOpenReview ↗

Response to Reviewer vek8

Dear reviewer vek8, we thank you for your time and comments and are glad you appreciated our “clear framework for understanding validity” and it “balancing interpretability and expressive power”. We address your remarks below.

validity depends on the sufficiency of historical states and an upper bound on conditional normalization, but training with limited data and empirical drift correction cannot yet certify these conditions, and the false alarm rate on some tasks still exceeds the target.

It is entirely correct that learned normalization is an approximation, and the reviewer identifies precisely the sufficiency and normalization conditions stated in Prop. 1. As we note in the paper, “finite-data optimization certifies neither condition, and our learned factors therefore remain empirical” (L360-L361). The proposition and controlled synthetic recovery results nevertheless suggest a route toward certification in more constrained settings. Regarding real-world experiments, we consider our empirical results favorable overall. Our reported FPR rates are at or below target in most cases, and only small violations occur (≤5\leq 5 % exceedance in Table 1). We believe this supports the practical promise of our test designs.

The method depends on the distribution of calibration data and coverage of trajectory lengths, limiting its applicability to distribution shifts and longer tasks

It is correct that our approach relies on stability between calibration and deployment populations, as discussed in App. A. Like the population assumptions required to transfer CRC or PAC thresholds (e.g., data exchangeability), our data-driven hypotheses and learned components require calibration traces to reflect relevant deployment score behavior. Strong distribution shifts or unfamiliar score dynamics can therefore cause null drift or reduce detection power by inaccurate estimation. Whether our monitor's learned representations can generalize across smaller shifts is an interesting question for future work, especially when incorporating white-box information or moving to higher-capacity models.

For longer traces, the GRU architecture can computationally process histories beyond the active horizon (Hi<t≤TiH_i<t\leq T_i) as it is length-agnostic, and smooth extrapolation may be possible under stable score dynamics. However, formal monitoring of those steps would require “extrapolation assumptions, which we do not consider here” (L112). We therefore restrict monitoring to the active horizon, following the scope of [SP’26]; we also touch upon this in App. A. It is worth noting that this restriction has little practical impact on our evaluation, as motivated by Table B below: actor-critic trace step coverage is close to 100%, with truncation rates of deployment traces virtually zero. PAC baselines record higher truncation rates, but the effect on coverage remains minimal. For example, on Mistral-7B at most 12% of deployment traces are truncated for PAC, but mean per-trace coverage at ~97% implies only few steps are effectively removed.


Table B: Active horizon empirical results. For reasoning tasks on MATH using three different generators, we measure the practical impact of defining an active trace horizon Hi=min⁡{Tcal,Ti}H_i = \min\{T_{\text{cal}}, T_i\} on deployment monitoring. Coverage denotes the mean per-trace fraction of active steps, and truncation indicates the rate of active horizons shorter than the full trace length. Values are means ± 1 SD across ten trial-level averages. PAC splits the calibration data into another two subsets for its protocol, hence active horizons are determined on a smaller data subset and can differ from those for learned tests.

GeneratorActor–Critic, Coverage [%]Actor–Critic, Truncation [%]PAC, Coverage [%]PAC, Truncation [%]
Mistral-7B99.99 ± 0.010.02 ± 0.0397.16 ± 0.9112.31 ± 3.40
DeepSeekMath99.99 ± 0.010.05 ± 0.0798.99 ± 0.232.96 ± 0.52
Claude Haiku 4.5100.00 ± 0.000.03 ± 0.0399.90 ± 0.060.80 ± 0.39

experiments do not demonstrate that actual interventions after alarms can improve task success rates or safety

It is correct that our experiments evaluate deployment monitoring rather than the effects of subsequent interventions. Our research question concerns the design and learning of local evidence for agentic monitoring, and our experiments assess the viability of these designs as flexible alternatives to threshold or event calibration. We leave the discussion on subsequent intervention design and evaluation, or deployment adaptation, for future work.

We appreciate your comments and hope they have been addressed sufficiently. If not, please feel free to follow up for further elaboration.

References

[SP’26] Shuvom Sadhuka, Drew Prinster, et al. E-valuator: Reliable agent verifiers with sequential hypothesis testing. Hypothesis Testing Workshop at ICML, 2026.

Reviewer_gQ5SOpenReview ↗
Rating
3
Confidence
2
Informativeness
3
Presentation
2
Soundness
2
Read review
Paper summary

The paper learns monitors that accumulate black-box scores during model and agent traces. It proposes conditional-mean and actor–critic evidence factors, states conditions for false-alarm control, and tests detection and combinations of scorers on reasoning, generation, interaction, and tool-use tasks.

Critical strengths

The paper explains why marginal score calibration can fail to control false alarms within dependent traces. Its counterexamples and state/filtration conditions clarify what makes local evidence valid and reusable, and how this differs from calibrating one fixed alarm rule.

Critical weaknesses
  1. The Raw/CLR critic loss can underestimate the normalizer needed to control false alarms. B.6 downweights steps from longer traces; if stronger evidence occurs in longer normal traces with the same history, the fitted normalizer can be too small even with unlimited data, inflating evidence against normal behavior.

  2. The practical gains over calibrated baselines are limited: PAC matches or exceeds the highest-power learned monitor at the same or lower reported mean FPR on MATH probing, DBBench, red teaming, and WebShop (Tables 1/5). Composition improves on individual scorers, but its real-data evidence covers only one Mistral scorer pair (Figs.4/16)

Questions for authors

Questions

  1. Why does Chess Raw power fall from 0.61 under Ville to 0.51 under RandVille (Tables 4/1)? Were the model, correction and test data identical, and were earlier Ville alarms retained?

Minor comments

  1. The abstract overstates the real-data guarantee. “Verifiable false alarm controls” is stronger than p.5's description of fitted factors as empirical approximations. Qualify this claim, including for composition: B.8's correctly stated common-filtration conditions do not certify the fitted components.

  2. The stated interval excludes the default value. B.5 (p.22) specifies c∈(0,1) but uses c=1 by default. Is the intended interval (0,1]?

4 comments
AuthorsOpenReview ↗

Response to Reviewer gQ5S (1/2)

Dear reviewer gQ5S, we thank you for your time and insights and are glad you deem our work informative and sound. We address your remarks below.

The practical gains over calibrated baselines are limited: PAC matches or exceeds the highest-power learned monitor at the same or lower reported mean FPR on MATH probing, DBBench, red teaming, and WebShop (Tables 1/5)

We kindly refer to our first response to reviewer TM3C regarding the PAC baseline and method comparison.

Composition improves on individual scorers, but its real-data evidence covers only one Mistral scorer pair (Figs.4/16)

Relating to our second response to reviewer TM3C, we extend the existing composition experiment for Mistral-7B with paired scorers Qwen2.5-PRM and Math-Shepherd to an entirely different combination of generator and scorer models: math reasoning traces generated by DeepSeekMath-7B-Instruct, scored by two related LLM-as-a-Judge models, Phi-4-mini-reasoning and Phi-4-mini-instruct [AA’25]. Within each generator-scorer combination, the same ten trial splits and composition policies are evaluated.

Table A below reports RandVille results at α∈{0.1,0.2,0.3}\alpha\in \{0.1,0.2,0.3\} and shows that compositionality can once again yield (small) power gains over any one individual Phi-4-mini scorer (positive Δ Power). Naturally, the benefit depends strongly on scorer pairing, and combining a strong and weak scorer can lead to the strong model uniformly dominating results. This is seen for the combination of DeepSeekMath traces with Qwen2.5-PRM (a very strong math-specific scorer) and Phi-4-mini-instruct (a reasonable, but weaker general-purpose scorer). While the design of effective but valid composition strategies warrants future attention, we believe our testing framework’s ability to support such flexible composition directly during deployment to be a very powerful and practical property.


Table A: Extended evidence composition results. RandVille threshold results for target rate α∈{0.1,0.2,0.3}\alpha \in \{0.1, 0.2, 0.3\} across additional model combinations. Each metric cell shows FPR / Power, with each value reported as mean ± 1 SD across ten trials. Bold power values identify the best individual and best composition, while Δ\DeltaPower is the absolute power difference of the composition over individual scoring (in percentage points).

Target Rate αGeneratorScorer A, Scorer BScorer AScorer BWealth MixtureFactor MixtureWealth LeaderΔ Power
0.10Mistral-7BQwen2.5-PRM, Math-Shepherd0.12 ± 0.03 / 0.57 ± 0.060.11 ± 0.02 / 0.43 ± 0.040.12 ± 0.02 / 0.54 ± 0.060.13 ± 0.02 / 0.64 ± 0.050.11 ± 0.02 / 0.43 ± 0.05+7.01
0.10DeepSeekMathPhi-4-mini-instruct, Phi-4-mini-reasoning0.11 ± 0.01 / 0.39 ± 0.020.10 ± 0.01 / 0.31 ± 0.040.11 ± 0.01 / 0.37 ± 0.020.11 ± 0.01 / 0.40 ± 0.020.10 ± 0.01 / 0.34 ± 0.02+0.49
0.10DeepSeekMathQwen2.5-PRM, Phi-4-mini-instruct0.11 ± 0.01 / 0.66 ± 0.020.11 ± 0.01 / 0.39 ± 0.020.11 ± 0.00 / 0.59 ± 0.020.12 ± 0.00 / 0.60 ± 0.020.10 ± 0.01 / 0.51 ± 0.03−5.63
0.20Mistral-7BQwen2.5-PRM, Math-Shepherd0.19 ± 0.03 / 0.77 ± 0.030.21 ± 0.03 / 0.68 ± 0.040.21 ± 0.03 / 0.79 ± 0.030.22 ± 0.03 / 0.84 ± 0.030.20 ± 0.03 / 0.68 ± 0.04+6.50
0.20DeepSeekMathPhi-4-mini-instruct, Phi-4-mini-reasoning0.19 ± 0.02 / 0.58 ± 0.020.20 ± 0.01 / 0.55 ± 0.040.20 ± 0.01 / 0.59 ± 0.020.20 ± 0.01 / 0.61 ± 0.020.19 ± 0.01 / 0.54 ± 0.02+2.61
0.20DeepSeekMathQwen2.5-PRM, Phi-4-mini-instruct0.18 ± 0.01 / 0.87 ± 0.020.19 ± 0.02 / 0.58 ± 0.020.19 ± 0.01 / 0.80 ± 0.020.19 ± 0.01 / 0.81 ± 0.010.19 ± 0.01 / 0.74 ± 0.03−6.53
0.30Mistral-7BQwen2.5-PRM, Math-Shepherd0.26 ± 0.03 / 0.85 ± 0.020.29 ± 0.04 / 0.79 ± 0.030.30 ± 0.04 / 0.88 ± 0.020.29 ± 0.04 / 0.90 ± 0.020.28 ± 0.03 / 0.82 ± 0.03+5.04
0.30DeepSeekMathPhi-4-mini-instruct, Phi-4-mini-reasoning0.27 ± 0.02 / 0.68 ± 0.020.28 ± 0.01 / 0.71 ± 0.030.28 ± 0.02 / 0.72 ± 0.020.28 ± 0.02 / 0.72 ± 0.020.27 ± 0.02 / 0.69 ± 0.02+1.06
0.30DeepSeekMathQwen2.5-PRM, Phi-4-mini-instruct0.24 ± 0.02 / 0.91 ± 0.010.27 ± 0.02 / 0.68 ± 0.020.26 ± 0.02 / 0.90 ± 0.010.26 ± 0.02 / 0.90 ± 0.010.26 ± 0.02 / 0.83 ± 0.02−1.12
AuthorsOpenReview ↗

Response to Reviewer gQ5S (2/2)

The Raw/CLR critic loss can underestimate the normalizer needed to control false alarms. B.6 downweights steps from longer traces; if stronger evidence occurs in longer normal traces with the same history, the fitted normalizer can be too small even with unlimited data

In our implemented critic objective LC1\mathcal{L}_{\text{C1}} (App. B.6), each null trace's stepwise losses are indeed averaged over its active trace length HiH_i, as are the corresponding actor objectives above it (L1227). This design choice prevents long traces from dominating gradient contributions and is motivated by optimization stability across heterogeneous traces. However, the reviewer rightly identifies a case in which trace balancing may at the same time affect the critic’s population-level normalization target. As discussed in the same section further above (L1202 ff.), constructing an effective empirical analogue of the population target involves several challenges, and alternative designs (e.g., a non-balanced variant or some other form of weighting) are possible and worth exploring in the future.

Why does Chess Raw power fall from 0.61 under Ville to 0.51 under RandVille (Tables 4/1)? Were the model, correction and test data identical, and were earlier Ville alarms retained?

As touched upon in response to reviewer TM3C, the Ville and RandVille comparisons permit separately selected actor-critic drift corrections (App. D.3, Fig. 15). As RandVille thresholding increases the probability of null rejection when compared to Ville thresholding, it generally sees a larger drift correction applied to dampen the effect on FPR. A larger threshold-specific correction can thus offset additional terminal rejections, and the reported comparison need not always have nondecreasing FPR or power for RandVille over Ville, albeit this is generally the case across experiments. Note that the same power reversal observed for Chess also affects the actor-critic (CLR) design, which also receives drift correction, but not the conditional mean test, which does not.

The abstract overstates the real-data guarantee. “Verifiable false alarm controls” is stronger than p.5's description of fitted factors as empirical approximations

We agree with the reviewer that “verifiable false alarm controls” could be read as an unconditional theoretical assurance, and will soften the abstract’s wording in the camera-ready version. The abstract deliberately mentions that “learned tests exhibit error-controlling and adaptive properties” (L24) rather than stating them as strictly error-controlling, but the empirical distinction should be made more explicit, in line with how it is stated in the main text (e.g., “treat learned factors on real data as empirical approximations, not certified e-processes” on L232).

The stated interval excludes the default value. B.5 (p.22) specifies c∈(0,1) but uses c=1 by default. Is the intended interval (0,1]?

Thank you for the sharp observation on this typo. Indeed, the constant admits the range c∈(0,1]c \in (0, 1] and denotes an optional upper cap on the betting range to limit overly aggressive betting that can lead to sudden wealth loss [WR’24], with the default cap at c=1c=1.

We appreciate your comments and hope they have been addressed sufficiently. If not, please feel free to follow up for further elaboration.

References

[AA’25] Abdelrahman Abouelenin, Atabak Ashfaq, et al. Phi-4-mini technical report: Compact yet powerful multimodal language models via mixture-of-loras. arXiv Preprint (arXiv:2503.01743), 2025.

[WR’24] Ian Waudby-Smith and Aaditya Ramdas. Estimating means of bounded random variables by betting. Journal of the Royal Statistical Society: Series B, 2024.

Thank you for the response. The explanation of the Chess result is clear, and the changes to the abstract and to the range of c resolve my minor comments.

Two points remain open for me. First, you agree that trace balancing can change the target of the critic, but the response does not show how large the effect is. Reporting the held-out mean null factor separately for short and long traces, or one run with the unweighted loss, would be enough. Section 4.2 should also mention this limit. Second, the new composition gains are small for the Phi-4 pair (+0.5 to +2.6 points) and negative when a strong and a weak scorer are combined, so the practical benefit is still shown mainly for one pair. Since the drift correction is selected separately for Ville and RandVille, please also state this in the main text, because it is a form of calibration for each alarm rule. I keep my rating of 3.

Dear reviewer gQ5S, we thank you for the constructive follow-up and are glad that the Chess explanation and minor corrections addressed those concerns.

Regarding trace balancing, we will aim to extend our training protocol ablation (App. D.3) to compare modified critic objectives, including an unweighted critic loss as suggested, alongside the (coarser) time-binned and learned-state-binned critic losses we evaluated during earlier development. This will help paint a clearer picture of specific loss components and their effects. We will explicitly note in §4.2 that trace balancing gives each trace equal weight in optimization but can change the critic’s target in practice, elaborating on “Suppressing trace-balancing details” (L306). We will also elaborate on the drift correction under “Model design” in §4.2 (alongside the diagnostics in App. D.3), specifically highlighting that the margin is selected separately for each model and alarm rule.

Regarding composition, the additional Phi-4 results show small but consistent power improvements over the better individual scorer, but we agree that negative gains for the strong/weak pairing highlight the importance of complementary evidence and the choice of composition policy (which is expected). We will include our new results and sharpen the discussion to present these experiments as illustrations of composition potential, rather than conclusive evidence.

We thank the reviewer for their suggestions to sharpen our exposition and analysis.

Reviewer_TM3COpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper studies sequential monitoring of generative models and agents through learned, history dependent evidence factors. It introduces conditional-mean and actor–critic constructions, states sufficient conditions for statistical validity, and evaluates their detection and composition properties across several domains. The real-data factors are explicitly treated as empirical approximations rather than certified e-processes.

Critical strengths
  1. The paper clearly distinguishes history-conditional evidence normalization from calibration of a fixed alarm event, and explicitly states the assumptions required for validity and composition.

  2. The evaluation covers diverse generators and monitoring targets, with useful ablations on betting rules, initialization, correction, and calibration size, alongside synthetic and real-data composition experiments

Critical weaknesses

Limited Demonstrated Benefit over Event-Level Calibration. PAC baselines are competitive or stronger in several reported settings (Tables 1 and 5). Although the composition results are promising, the paper does not clearly establish when learned local evidence provides sufficient practical benefit to justify its additional modeling and validity assumptions

Questions for authors
  1. Under comparable data budgets and matched false-alarm rates, when does learned local evidence outperform event-level calibration? Can the authors quantify the detection or calibration-cost benefit of composition against freshly calibrated aggregate statistics?

  2. Can the authors specify the exact RandVille procedure and reconcile Tables 1 and 4? Were checkpoints, deployment splits, active horizons, and corrections held fixed when comparing Ville and RandVille?

2 comments
AuthorsOpenReview ↗

Response to Reviewer TM3C (1/2)

Dear reviewer TM3C, we thank you for your time and comments and are glad that you found our work clearly written and empirically well-supported. We address your remarks below.

PAC baselines are competitive or stronger in several reported settings (Tables 1 and 5) […] Under comparable data budgets and matched false-alarm rates, when does learned local evidence outperform event-level calibration?

It is correct that the PAC approach is competitive in several cross-domain settings, and learned sequential monitors do not systematically outperform it on raw power alone. As discussed in the paper (L218-L220), threshold calibration can absorb different sources of monitoring error into calibration of the alarm event, whereas our approach targets stricter, locally valid evidence requirements. This distinction can favor PAC power where local normalization is difficult to learn, but also entails different modeling and data requirements. The PAC monitor following [SP’26] needs both null and alternative traces to fit its likelihood-ratio statistic and stores a separate full-prefix model for each supported step, introducing deployment routing and more indirect treatment of temporal dependencies between trace steps. In contrast, a conditional mean test can be fitted using only null traces and paired with off-the-shelf betting rules (App. D.2, Fig. 10), while our recurrent history design shares parameters across steps (see our likelihood-ratio interpretation in §4.2).

PAC calibration additionally requires a model/threshold subset split and allocation of a shared error budget for the two parameters (α,δ)(\alpha, \delta), with minimum calibration size requirements that depend on this allocation to prevent monitor collapse ([SP’26], App. 8.1.2). Our calibration size ablation illustrates the resulting sensitivity, where smaller calibration pools can materially reduce PAC power, while learned designs retain competitive performance in this setting (App. D.2, Figs. 13 and 14). Ultimately, it is worth re-iterating that “our claim is not that evidence calibration dominates threshold calibration, but that it targets a richer and potentially more reusable object” (L233-L234), which we believe to be consistent with our empirical monitoring and evidence-composition results.

Although the composition results are promising, the paper does not clearly establish when learned local evidence provides sufficient practical benefit […] quantify the detection or calibration-cost benefit of composition against freshly calibrated aggregate statistics?

Our composition experiment in Fig. 4, for Mistral-7B with Qwen2.5-PRM and Math-Shepherd scores, illustrates that factor composition can improve power over either component when complementary evidence exists among scorers. Our controlled synthetic experiment likewise shows gains from composition under both oracle knowledge and imperfect state recovery (App. D.4, Fig. 16), suggesting that even small differences in scoring dynamics can be useful. To reinforce our empirical claim, we extend this analysis to DeepSeekMath traces scored by two related LLM-as-a-Judge models, Phi-4-mini-reasoning and Phi-4-mini-instruct [AA’25]. We refer to the results in Table A under reviewer gQ5S, where compositionality yields further (albeit small) power gains over any one scorer. While the specific design of effective but valid composition strategies warrants future attention, we believe the ability of our testing framework for such flexible composition directly during deployment to be a very powerful and practical property [VW’21].

In contrast, borrowing existing mean or componentwise PAC thresholds for a changed aggregate statistic can cause FPR violations or conservative power loss (App. D.4, Fig. 17b). Fresh calibration can indeed restore control and power, but requires recomputing the statistic on all held-out calibration samples (which may include rescoring all trace steps by a complex inference model) and determining a new threshold. This additional offline procedure introduces substantial deployment overhead, and future changes to the statistic or routing policy (e.g., introducing a different scorer or weighting adjustments) would trigger the protocol anew. Hence the approach is substantially less flexible for monitoring in dynamic deployment environments where such changes might occur.

AuthorsOpenReview ↗

Response to Reviewer TM3C (2/2)

Can the authors specify the exact RandVille procedure and reconcile Tables 1 and 4? Were checkpoints, deployment splits, active horizons, and corrections held fixed when comparing Ville and RandVille?

We apologize for any ambiguity in comparing Tables 1 and 4. Indeed, Table 4 keeps most experiment design choices fixed and identical to Table 1, except for switching the rejection threshold from RandVille to Ville, and still permitting separate drift corrections for actor-critic designs (see App. D.3, Fig. 15). As generally expected, Ville thresholding introduces conservatism over RandVille as expressed through both lower FPR and power.

RandVille applies terminal randomization as described in §2 (L141-L143), and follows [RM’26] (see their Corr. 4.1.1). The practical protocol uses the standard Ville threshold 1/α1/\alpha at steps t<Hit<H_i, while, at t=Hit=H_i, we draw an independent U∼Unif(0,1)U\sim\mathrm{Unif}(0,1) and reject if terminal wealth reaches U/αU/\alpha, retaining any earlier Ville alarm. Since U≤1U\leq1, the rejection threshold will be kept or lowered, hence randomization can uncover additional rejections on a given wealth path, including traces whose terminal evidence falls below 1/α1/\alpha. It can therefore increase power, while also exposing insufficient null-normalization that conservative Ville crossing may conceal. Under the required supermartingale conditions, the randomized procedure preserves any false-alarm guarantee valid under Ville.

We appreciate your comments and hope they have been addressed sufficiently. If not, please feel free to follow up for further elaboration.

References

[SP’26] Shuvom Sadhuka, Drew Prinster, et al. E-valuator: Reliable agent verifiers with sequential hypothesis testing. Hypothesis Testing Workshop at ICML, 2026.

[AA’25] Abdelrahman Abouelenin, Atabak Ashfaq, et al. Phi-4-mini technical report: Compact yet powerful multimodal language models via mixture-of-loras. arXiv Preprint (arXiv:2503.01743), 2025.

[VW’21] Vladimir Vovk and Ruodu Wang. E-values: Calibration, combination and applications. The Annals of Statistics, 2021.

[RM’26] Aaditya Ramdas and Tudor Manole. Randomized and exchangeable improvements of Markov’s, Chebyshev’s and Chernoff’s inequalities. Statistical Science, 2026.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Note to reviewers on submission edits

Dear reviewers, our edit to the submission document contains the following changes to support our rebuttal responses:

  • We have updated our calibration size ablation study to also include power results in response to reviewer TM3C: App. D.2, Fig. 13 is replaced by App D.2, Fig. 13 and Fig. 14.
  • We have fixed the typo on the inclusive range of the betting constant in response to reviewer gQ5S (App. B.5, L1140).

We will be glad to update the document as needed should further questions require clarification.

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

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