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Paper summary
The paper studies a sequential detection game in which an agent maximizes reward accumulated before a monitor detects deviation from a reference policy, subject to a type-I error constraint. In the high-confidence asymptotic regime, the analysis connects reward per unit KL divergence to KL-regularized RL with an endogenous regularization coefficient. A stochastic bisection procedure estimates this coefficient through RL-oracle calls. Experiments with Qwen3-8B and Llama-3.2-1B illustrate length-coherence trade-offs from a fixed story-completion prompt and model auditing with an independently trained monitor policy.
Critical strengths
- Relating the agent’s accumulated reward to the statistical evidence needed for detection gives a concrete meaning to the reward-to-KL ratio and the resulting regularization coefficient in Section 3. The paper explicitly limits its equilibrium characterization to leading order as tends to zero (p. 4, lines 176–184), which helps delimit the theoretical contribution.
- The auditing experiment distinguishes a detector using the true deployed policy from a monitor using an independently trained policy, and evaluates the detectors on the same observed completions (Section 5.2, p. 8, lines 410–425). This is a useful design for studying the gap between the proposed idealization and a monitor without access to the agent’s realized policy.
Critical weaknesses
1.What stopping or interval-update rule handles an exact or statistically unresolved root hit in Algorithm 1, and what coefficient-error and complexity guarantee holds for that rule?
2.Does Appendix B.1 intend only prescribed-policy utility comparisons, or an approximate Nash guarantee? For a lower-coefficient monitor , the drift under an agent policy with mean reward is $
$.
3.Since , feasible policies with $ $ can yield unbounded gains as approaches zero from above. Such policies exist in the bounded binary example above. The displayed B.8–B.9 inequalities do not rule out these deviations. Please clarify the intended scope. This observation does not contradict those narrower inequalities or the exact-root equilibrium.
4.What explains the grid mixture’s excess null rejections? Please specify the null-trial count and independence, monitoring horizon, treatment of non-detections, and how sequence likelihoods account for sampling, EOS and truncation. Reconcile the existing null results before interpreting detection times.
5.What operational preference or per-round cost determines the calibration margin , and how is it chosen before examining coherence? The reward shift preserves the optimizer for a fixed , but changes and hence the selected root (p. 7, lines 337–342). Please also specify whether the reward uses characters or tokens and give the normalization units needed to interpret and .
Questions for authors
See in weakness.
2 comments
Thank you for answering my question.
Thank you for taking the time to review our submission. Our responses to your questions and comments are below.
In Section 4 (L268) we mention that Algorithm 1 needs O(M(β^)−2) samples per iteration, so the sample count will grow as β^→β∗. As a practical relaxation, in our experiments we skip the confidence sequence and simply bisect based on the sign of M^n(β^) using a fixed, large n (and terminate if it equals zero exactly). While this approach does not come with coefficient-error guarantees, we found that it worked well in our experiments.
And
Thanks for raising this point and giving us the opportunity to clarify. As written, Appendix B.1 is a prescribed-policy utility comparison which shows that their utilities are close to the equilibrium values. However we believe that it is possible to get an approximate Nash equilibrium guarantee and rule out the unbounded deviation gains in your example if the monitor instead uses βhigh while the agent plays πβlow. The monitor’s side of this calculation carries over directly from Theorem B.9 (part 2), and the agent side requires a short corollary showing that no deviation earns more than βhighlog(1/α). We’ll be sure to clarify this in the revision.
We rechecked our code and found that this behavior was coming from some oddities in the Tinker API we used for model fine-tuning and serving. In short, we were computing the probabilities of token sequences under the null hypothesis model by using an untrained Tinker “training client”, which should have been fine in theory, but introduced some non-determinism in practice. We fixed this by using a Tinker “sampling client” instead. After re-running, the high-level takeaway is the same: our SPRT comes close to the skyline performance while significantly outperforming the grid mixture baseline. The updated results for Qwen are below. (Unfortunately Tinker has deprecated the Llama endpoint we were using, so we could not rerun those results.)
We used 200 independent null trials, each with a fresh completion from πref. A completion’s log-likelihood is the sum of the log-probabilities of its generated tokens (including EOS). Completions truncated at the 2048 token cap are scored by the probability of the observed sequence.
This is a good point worth clarifying: ρ is the empirical counterpart to the constant c in our discussion of Assumption 3.1 (L168). There, c is interpreted as the minimum improvement in expected reward required for the agent to want to update the reference policy. In practice, c could be a proxy for the (monetary, time, effort) costs associated with model training. In our experiments, we chose the values of ρ to span small-to-moderate costs relative to the reward scale, and did not tune them.
Reward uses characters not tokens in our experiments. We will clarify this in the revision. ρ is in normalized reward units, i.e. one unit corresponds to 2048 tokens. β is in normalized reward units per nat of KL.