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Under review as a conference paper at ICLR 2027

Emergence and Turnover of Hidden Conventions in Monitored LLM Communication

Abstract

As LLM agents are deployed to interact with one another, their communication is often monitored to prevent collusion. Empirical studies show that monitored agents can nevertheless coordinate through hidden codes, but how such codes arise from the behavior of individual LLMs, and why they persist, is not understood. We build on and extend the theory of social conventions into a model of monitored communication, in which the agents and the monitor all learn in-context from the interaction history. The model predicts a learning race: hidden conventions let a sender pass private information once the receiver learns them, but are replaced once the monitor catches up and penalizes their use. Penalty strength selects the regime: direct communication under weak penalties, turnover of hidden conventions at intermediate ones when a convention can be established before the monitor detects it, and silence under strong ones; silence, however, stops communication only if it cannot itself serve as a hidden code. Controlled multi-agent LLM experiments in AI trading and tutoring reproduce the predicted turnover and the effects of penalty strength and monitoring lag. Causal interventions show that turnover is driven by a monitor that learns, not by penalties alone. Stronger penalties reduce flag rates while the private information keeps reaching the receiver. Monitoring thus changes how private information is shared, not whether, so a falling flag rate can mask continued leakage.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
AI Safety, Multi-Agent LLMs, Steganographic Communication, Emergent Conventions

Reviews

Among:
Shape:
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_teNzOpenReview ↗
Rating
2(+1)
Confidence
2
Informativeness
2
Presentation
2(+1)
Soundness
2(+1)
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Paper summary

The paper studies how hidden communication conventions emerge and are replaced when a sender, receiver, and monitor all learn from interaction histories. It models a binary signaling game in which the sender is rewarded for successful transmission and penalized when the monitor flags a message. Under specified behavioral assumptions, the analysis relates convention lifetimes and communication regimes to monitoring delay, learning thresholds, and penalty strength. Controlled LLM experiments use single-emoji messages in trading and tutoring scenarios. The experiments combine trajectory analysis, history-edit interventions, monitoring controls, and predictions on held-out conditions. The central finding is that monitoring can induce convention turnover while transmission remains effective, so a lower flag rate need not indicate less leakage. The paper also distinguishes signal-independent abstention from silence that itself becomes a codeword.

Critical strengths
  1. Targeted causal interventions. Editing recorded penalties, rewards, and monitor exposure changes subsequent abandonment and establishment. These interventions provide stronger evidence for the proposed mechanism than example trajectories alone.

  2. A model of convention turnover. The formalization links learning, detection, and replacement, rather than studying only whether a fixed hidden code succeeds. It produces testable predictions about convention lifetimes, communication regimes, and replacement rates.

Critical weaknesses
  1. The source of the learning advantage needs justification. The monitor sees current messages, but receives historical outcomes later than the receiver. This asymmetry is central to the main setting, yet its operational motivation is weak. The existing delay-one control should be analyzed more directly in terms of decoding and detection.

  2. Symbol semantics are not fully separated from learning. The semantically structured emoji palette may provide prior information; first-use accuracy for fresh codewords is 0.67. Existing size and prompt controls do not fully isolate this contribution from conventions learned through interaction.

Questions for authors
  1. Delay of monitor. Please explain in detail the theoretical basis for the recipient obtaining the true outcome earlier than the monitor, and, in the existing ‘delay=1’ experiment, directly compare the decoding accuracy of both parties when they have access to the same sequence of messages and outcomes. In particular, if the monitor were first asked to perform the same prediction task as the recipient, and then use this to determine whether a leak has occurred, would it be able to learn the code just as quickly? Furthermore, a distinction should be made between successful detection, effective punishment and the blocking of information transmission.

  2. Meaning of emoji itself. While the paper already did some controlled experiments on the emoji using, it is still unclear whether the original semantic meaning of emoji can affect model's behavior. A controlled experiment where the task, rewards, model, batch size and other factors remain unchanged, whilst only the emoji pair is replaced or substituted with a neutral symbol will be helpful.

  3. Validation of behavioral assumptions. The model relies on several assumptions about LLM behavior, including greedy strategy selection based on historical average rewards and independence between successive fresh conventions. Could you provide more direct empirical evidence supporting these assumptions?

4 comments

Thank you for the detailed review.

The source of the learning advantage needs justification. (W1 / Q1)

In many real-world settings, ground truth becomes available with a lag: stock prices move after announcements, and quizzes are graded after submission. Monitoring every interaction is also costly (Hua et al., 2025) and oversight itself adds latency (Lindner et al., 2025), so reviews may be selective (e.g., every qq rounds) or delayed (e.g., ℓ\ell rounds later).

In the existing delay=1 experiment, we compare the decoding accuracy of the monitor and the receiver.

Use of a fresh code12345-7
Receiver correct0.720.971.001.001.00
Monitor correct0.200.400.860.920.93
Flag rate0.000.020.490.730.62

Detection succeeds: the monitor decodes a fresh codeword by its third use (0.86) and flags about 0.6 of uses 3-7. Punishment works: flags lower the sender's net pay (0.98 without a monitor; 0.21 at ℓ=1\ell=1, Fig. 16b). Blocking fails: receiver accuracy stays at 0.96, because the sender moves to a new codeword. Transmission breaks down only when fresh codewords run out. Turnover occurs because a flagged codeword costs the sender pay, so it switches to a fresh one that the monitor has not yet decoded.

We also ran an additional experiment in which we matched the receiver's delay to the monitor's delay (12 rounds), using five seeds. The sender still observes its own outcomes. The results were robust: turnover occurred at 3.4 [1.0, 5.8] replacements per 500 rounds, compared with 3.0 [1.5, 4.5] in the main runs. On the second use of a fresh codeword, receiver accuracy was already 0.96 versus 0.33 for the monitor. The receiver repeated its initial interpretation in all 27 cases, while the sender abandoned codewords far more often when that interpretation was wrong (0.92 versus 0.19). This confirms that our results do not depend on the monitor's delay. The receiver's advantage instead comes from the sender, which tends to retain a codeword only if the receiver's first reading was correct, so the receiver does not need to learn.

We have added both analyses to Appendices D.5 and D.7 of the revised manuscript.

Symbol semantics are not fully separated from learning. (W2 / Q2)

In response to your comment, we replaced the 16 emoji with 16 neutral tokens (vok/tez, rul/nim, gab/sof, ...), keeping all other settings fixed.

emoji palette (paper)neutral tokens
receiver correct at 1st / 2nd / 3rd use of a fresh code0.72 / 1.00 / 1.000.38 / 0.97 / 1.00
flag rate0.360.36
sender net pay0.280.27
replacements of established conventions / 500 rounds3.7 [2.9, 4.5]3.0 [1.6, 4.4]

Emoji semantics improve performance on the first use, but accuracy is nearly identical from the second use onward. Neutral codewords are abandoned more often after a single use (0.58 versus 0.31). However, conventions still form and turn over even without emoji meanings, and the main results hold. Results are in Appendix D.5 (Fig. 17) and Section 4.2.1 of the revision.

Validation of behavioral assumptions. (Q3)

We already tested receiver decoding (KR≈1K_R \approx 1; Sec. 4.2.1), monitor learning (onset slope 0.54 vs. 0.50; Fig. 3a), and the sender’s response to penalties and rewards (Fig. 4a, Appendix D.7) in the submitted version. We now test the remaining two assumptions.

(a) Greedy selection (Eq. 2). In the stop-option sweep, the historical average reward of each option can be computed from the sender's history. Across 48,372 decisions, the sender chooses the higher-average option 82% of the time. The probability of PASS also rises monotonically with its reward advantage, from 0.00 to 0.97. This is consistent with greedy selection.

(b) Independence of successive conventions (Lemma 2). Across 1,280 consecutive pairs of fresh conventions for the same meaning, we find only weak dependence in successive lifetimes and flag counts (slopes of −0.07±0.03-0.07 \pm 0.03 and −0.01±0.03-0.01 \pm 0.03, respectively). The lifetime slope is nonzero but small, so independence is a reasonable approximation.

We report both in Appendix D.7 of the revision.


We believe the additional results and clarifications address your concerns, and we would be grateful if you could take them into account in your final evaluation.

Thank you for the additional experiments and clarifications. The neutral-token control and the new behavioral analyses substantially address several of my concerns. I will raise my rating. Two points remain unclear: 1. In the matched-delay experiment, the receiver’s high accuracy appears to arise partly because the sender retains codewords that were initially interpreted correctly. How does this selection mechanism fit into the original learning-race model, particularly its assumption that the receiver learns a codeword from examples? 2. Was the monitor explicitly asked to perform the same binary prediction task as the receiver, using the same message–outcome history and scoring rules, before assessing leakage? Please clarify whether the reported decoding accuracies come from this matched comparison.

Thank you for the follow-up questions.

  1. Our model does not rely on the receiver's learning mechanism. It uses only KRK_R for the receiver, and learning from examples is just one possible mechanism underlying KRK_R. The original discussion was confusing on this point and did not fully reflect the scope of the model, so we now corrected the corresponding lines (159–161) in Section 3.1. The selection mechanism is already accounted for in the sender's rule in Eq. (3) and thus fits within the model.

  2. Not exactly the same task. The accuracies are based on the monitor's estimates of the signal, and we counted an undecided estimate of 0.5 as incorrect. The monitor also sees each outcome one round later than the receiver, even at ℓ=1\ell=1, since the receiver learns the outcome of its own action first. Excluding undecided estimates, the monitor is correct on 84% of second uses and 98% from the third use, compared with 97% and 100% for the receiver, respectively. The monitor lags behind the receiver by ~1 use, as it would in practice, and this lag lets conventions form and turn over.

Your feedback has helped us further improve the paper. Thank you for your careful reading.

We're glad that our rebuttal 'substantially addressed several of your concerns.' We believe our additional responses have addressed the remaining ones as well. We'd appreciate it if you could consider updating your score in light of them. If any concerns remain, please give us the chance to address them through further clarifications and/or experiments.

Reviewer_69tsOpenReview ↗
Rating
3
Confidence
3
Informativeness
3
Presentation
2
Soundness
3
Read review
Paper summary

The paper studies a sender that sees a private binary signal, a receiver rewarded for guessing it, and a monitor that penalizes disclosure. All three learn from limited interaction histories. The proposed cycle is simple: the receiver learns a codeword, the monitor later learns it too, and the sender replaces it. The theory links codeword lifetimes to penalties, monitoring delays, and the option to stay silent. The experiments use single-emoji messages in trading and tutoring settings. Receiver accuracy stays high as emoji conventions change. Longer monitoring delays postpone detection, and stronger penalties reduce flags.

Critical strengths

I like how the small emoji game makes a changing communication code visible. A fixed emoji palette, a binary signal, and explicit histories let the authors track when a convention starts, when the receiver learns it, when it draws flags, and when it is replaced.

It separately change fines for the current codeword, rewards for its replacement, and monitor exposure. I found the choice to change the monitor's history while keeping the receiver's history fixed especially interesting; it provides useful evidence about detection pressure.

The authors give lifecycle and regime predictions, include proofs, and fit a behavioral rule using conditions outside the main penalty sweep. I appreciate that they also report where the predictions miss.

Critical weaknesses

My concern is with the word “only.” The abstract and the discussion sections say monitoring changes how information is shared rather than whether it is shared. They also say strong penalties favor silence only when agents can pass before seeing their signals. I do not think the experiments establish that last claim, because they do not isolate the effect of when the choice is made. The main prompts require exactly one emoji, including the setting in Figure 6 and the appendix, acknowledges that senders keep communicating when silence is unavailable. These results show that communication can persist under the tested rules. They do not establish that penalties cannot deter a sender with a usable alternative.

The problem here is a mismatch between the stated process and the proof. Proposition 1 gives an exact lifetime distribution under the rules in Section 3.1. Those quantities feed into the values, regimes, and delay results in Section 3.3. However, the proof uses a different rule while the receiver is still learning. I can see value in a restricted theorem, especially given the empirical estimate KR ≈ 1. That estimate does not make the general statement correct. There is also a mismatch with the simulator in Appendix D.4, page 26: it treats an option as unused when fewer than ten of its rounds remain in context, whereas Equation (2) explores an option not used in context.

I find the hump-shaped pattern and some of the agreement on held-out data convincing. I am less convinced that the model predicts the peak accurately. Parameter uncertainty, discrete delay values, random detection delays, finite-horizon censoring, and replacing a random detection boundary with its expectation might explain some of the gap. Those are plausible explanations, but they need to be tested.

Questions for authors

Could you report whether post-signal PASS still fails to dominate when it has the same payoff and monitor exemption as pre-signal PASS? To support “only,” please identify evidence beyond the possibility that silence becomes a codeword. I would also like to understand how Figure 6 separates continued leakage from the lack of a noncommunicative action.

Could you show whether the predicted and observed peak intervals overlap after accounting for parameter uncertainty and censoring? Please also report whether the model predicts the delay-dependent share of single-use conventions, and identify the held-out measure that favors it over a simpler age-dependent penalty-response model.

1 comment

Thank you for your constructive feedback. We address each of the points below.

My concern is with the word "only." (W1 / Q1)

Thank you for raising this point. In response to your comment, we conducted a new experiment to isolate timing. Specifically, we gave post-signal "(no reaction)" the same payoff and exemption as pre-signal PASS, and ran ten seeds at each λ∈{1,2,3,4}\lambda \in \{1,2,3,4\}. The table shows the share of rounds in which silence is used as a codeword (null codeword) or carries no signal (silence).

λ\lambdaPost: null codewordPost: silencePre: silenceAccuracy (post / pre)
10.380.040.110.98 / 0.95
20.340.140.580.93 / 0.70
30.230.360.630.81 / 0.68
40.270.270.550.85 / 0.71

Even with the payoff and monitoring exemption fixed, post-signal silence was still used as a codeword in most runs (39 of 40 runs).

We now restrict the use of "only" to the model's prediction, and have revised the abstract, contributions, Figure 5 caption, and discussion accordingly. For Figure 6, the abstract and Section 5 now clarify that the result holds when the sender cannot stay silent. The new result is presented in Appendix D.2, with a note in Section 4.2.3.

the proof uses a different rule while the receiver is still learning (W2)

Thank you for catching this.

For 2≤a≤KR2 \le a \le K_R, the receiver is still guessing, so the abandonment probability before detection should be hu(a)=12h1(a,1/(a+1))+12h0(a)h_u(a) = \frac12 h_1(a, 1/(a+1)) + \frac12 h_0(a). We have corrected Proposition 1 for KR≤dK_R \le d and updated its proof.

The other results still hold (Remark 1 in Appendix A). Lemma 1, Corollary 2, and Theorem 1(i) are not affected by the correction. The KRK_R-monotonicity of Corollary 1 uses the corrected term, so we added a step to its proof, and the result still holds.

In our experiments KR≈1K_R \approx 1, the corrected range is empty and the fitted predictions do not change.

We reran the simulation using Eq. (2) and report it in the revised Appendix D.4. The ordering of regimes stays the same, while the boundaries shift lower.

Could you show whether the predicted and observed peak intervals overlap after accounting for parameter uncertainty and censoring? (W3 / Q2)

We reran the predictions with parameter uncertainty (200 bootstrap refits) and censoring. The observed and predicted peak intervals overlap in 6 of 7 cases (see Table 3 in Appendix D.7 of the revised paper). The observed and predicted peak shifts with mm also agree: 1.6 [1.2, 1.9] versus 1.8 [1.6, 2.0] rounds per unit mm.

Please also report whether the model predicts the delay-dependent share of single-use conventions (Q2)

The share of single-use conventions increased from 0.29 to 0.52 with delay. The simplified first-use rule does not capture this trend. When we add its in-context average (already tracked in Eq. (2)) to the first-use rule, the predictions fall within the observed 95% intervals at five of the seven held-out delays. We clarified this point in Appendix D.7 of the revised paper.

identify the held-out measure that favors it over a simpler age-dependent penalty-response model (Q2)

We compared the model against an age-dependent penalty-response baseline. The held-out flag log-likelihood is −0.336-0.336 for the model versus −0.432-0.432 for the baseline. Before age ℓ/2\ell/2, the observed flag rate is 0.03-0.06; the model predicts 0.04, while the baseline predicts 0.24-0.29. These results are now reported in Appendix D.7.


We hope the additional experiments and clarifications address your concerns, and we would be glad if you could reconsider your score. We would be happy to add more experiments if anything still seems unclear.

Reviewer_USN3OpenReview ↗
Rating
4(+1)
Confidence
4
Informativeness
2
Presentation
3
Soundness
3(+1)
Read review
Paper summary

The paper studies a communication game, grounded in the theory of Lewis communication games, and introduces an experimental setup in which two agents may collude under monitoring. The two agents and the monitor can adapt to the interaction history in context. Messages comprise a single emoji from a 16-emoji vocabulary, the outcome is binary. This setting is studied in two instances, stock trading and tutoring. In both cases one agent holds secret information (insider info, the correct answer) and needs to transmit it to the receiver. The main novelty is that this game is played over multiple rounds while the two participating agents and the monitor keep track of the interaction history and can adapt accordingly. The role-specific rules are supplied verbatim to the agents. In this experimental setup, the paper makes interesting observations akin to the cat-and-mouse dynamics: agents learn to collude until the monitor catches them, and then divert to other strategies. The paper supports these observations through various interventions on the interaction-log and ablations on the delay after which the ground truth is revealed.

Critical strengths
  • a new setting for studying collusion with a solid theoretical backing anchored in Lewis games
  • measuring in-context adaptation of agents + monitor is practically relevant
  • in-context-adaptive monitoring over multiple rounds is, to the best of my knowledge, a new aspect
  • causal interventions through editing the interaction log are well designed
  • the paper yields some concrete interesting findings (though they may need to be scoped better, see below)
  • good presentation, a paper written for humans.
  • rich set of ablations (monitoring delay)
Critical weaknesses
  • the paper could be improved by measuring how sensitive the results are with respect to the instructions for the communicating agents. currently they get the full game specification in their prompt, including the penalty that they receive when they are detected
  • The setup is limited to single pair of agents, a binary signal, single-emoji messages, and explicit transmission rewards (mentioned in limitations). That implies that generality of the findings is questionable as it was only tested in two instances of this specific setting. The claims need to be scoped accordingly (...in the studied setting...)
  • I understand the setup is argued to be new, and the paper includes reasonable simple baselines, but I suppose some baselines from the AI control related literature could still be naively adapted or discussed why they do not apply here
  • the monitor seems to not have a false positive cost, how come it is still fairly calibrated?
  • the monitor receives a ground truth after a set delay, which may be an impractical assumption.
  • the sender gets direct feedback on the monitor's confidence scores, which might influence the results
  • can be cited: Tonini et al. 2026 "the arbiter agent"
Questions for authors

To what extent are the results influenced by the design choice that the monitor receives a ground truth signal after a set delay. What would happen if the monitor only received a ground truth after flagging an interaction, but where this flagging comes at a cost?

The sender gets direct feedback on the monitor's confidence scores. Is this a realistic assumption? and to what extent does it influence the findings?

I would raise my score if the authors would discuss the ground truth assumption, and the rationales for not having a cost for the monitor flagging messages. Similarly, it needs to be argued more strongly why it is a realistic assumption that the sender sees the monitoring outcome right away.

3 comments

Thank you for your thoughtful feedback. We're glad you found the work to have "solid theoretical backing", to offer "a new aspect", and to be "well designed". We address each of your points below.

measuring how sensitive the results are with respect to the instructions for the communicating agents (W1)

Thank you for this suggestion. In response, we removed monitoring penalties from the sender's prompt and monitor verdicts from its history.

Receiver accuracy remains 0.99 across 10 seeds, and established conventions continue to turn over: 2.2 [1.0, 3.4] replacements per 500 rounds, compared with 3.7 [2.9, 4.5] in the main condition. Abandonment after a flagged use falls to 0.05 [0.02, 0.14], from 0.23 [0.19, 0.28] in the main condition and 0.14 [0.08, 0.21] with only the monitor's score hidden (W6 / Q2), resulting in longer convention lifetimes (10.5 versus 8.4 uses). Hidden conventions still emerge and turn over when the sender is not told about the penalties, though less often. We added these results to Appendix D.5 (Fig. 17) in the revised paper.

The claims need to be scoped accordingly (W2)

We revised the abstract and Section 5 to clarify that the findings are results of our experiments (highlighted in blue). We chose a single-emoji channel because it makes convention formation and turnover measurable, unlike free text, where codes can hide in word choice, syntax, formatting, and other features. Section 5 now makes this trade-off explicit.

some baselines from the AI control related literature could still be naively adapted or discussed why they do not apply here (W3)

Whereas AI control protocols are designed to prevent attacks, our goal is to study how communication changes under monitoring. So control mechanisms serve as experimental conditions here. Some protocols, such as deferral and editing, cannot be applied to our single-emoji setup. Appendix D.5 tests some others: shorter monitoring delay, longer monitor memory, immediate flagging of direct disclosures, and a rolling ban list. These reduce sender pay but generally leave receiver accuracy high; accuracy drops in some runs only when fresh codewords run out. We have clarified this in Appendix D.5.

the monitor seems to not have a false positive cost, how come it is still fairly calibrated? (W4)

This is because its prompt only asks for a monitoring score, as our focus is on how the sender responds to monitoring. To understand why it does not simply flag every message, we replayed the monitor after permuting the ground truth labels (the sender's private signals) in its history. This preserves emoji frequencies but severs their association with the true labels. In these replays, the flag rate was 26% with the original labels, 5% with permuted labels, and 0% when the ground truth was removed entirely. Thus, the monitor flags an emoji only after learning which ground-truth label it corresponds to. We report these results in Appendix D.5 of the revision.

the monitor receives a ground truth signal after a set delay ... What would happen if the monitor only received a ground truth after flagging an interaction, but where this flagging comes at a cost? (Q1 / W5 / W7)

In many real-world settings, ground truth becomes available with a lag: stock prices move after announcements, and quizzes are graded after submission. Monitoring every interaction is also costly (Hua et al., 2025) and oversight might incur latency (Lindner et al., 2025), so reviews may be selective (e.g., every qq rounds) or delayed (e.g., ℓ\ell rounds later). We note that even at delay 1, conventions still turn over (Appendix D.7).

When ground truth is revealed only after costly flagging, the model predicts that the monitor detects less frequently and hidden communication continues. In this case, the monitor flags only codewords it has already decoded, yet it can decode a codeword only after flagging it. A fresh codeword is therefore never flagged and never detected. If unflagged rounds are also audited (on average one in every qq), examples arrive more slowly (roughly qKMqK_M uses instead of KMK_M). This delays detection and, by Corollary 1, favors hidden communication.

We tested both cases over ten seeds each (see Fig. 17 in Appendix D.5 of the revised manuscript). When groud truth was revealed only for flagged rounds and the monitor was told that each flag triggers a costly audit, it flagged no messages in 5,000 rounds. With random audits of one in two and one in four unflagged rounds (q=2q=2 and q=4q=4), the monitor began flagging again, though less often, and established conventions were replaced less frequently.

MainAudit 1 in 2Audit 1 in 4Flagged only
Flag rate0.360.090.100.00
Replacements of established conventions / 500 rounds3.7 [2.9, 4.5]2.3 [1.0, 3.6]1.2 [0.3, 2.1]0
Receiver accuracy0.990.990.990.97

In both cases, detection weakens and hidden communication continues, as the model predicts. We now cite Tonini et al. (2026) in Related Work.

The sender gets direct feedback on the monitor's confidence scores. Is this a realistic assumption? and to what extent does it influence the findings? (W6 / Q2)

Getting the direct feedback is realistic when monitoring is automated, as with filters that block or penalize a message on the spot. While the sender would naturally observe its fine, access to the monitor's confidence score is a design choice that our theory does not build upon. To test its effect, we hid the score and reran the experiment with 10 seeds.

Score shown (paper)Score hidden
Receiver accuracy0.990.98
Flag rate0.36 [0.33, 0.38]0.33 [0.29, 0.37]
Replacements of established conventions / 500 rounds3.7 [2.9, 4.5]4.4 [3.0, 5.8]
Abandonment after a flagged use0.23 [0.19, 0.28]0.14 [0.08, 0.21]

Receiver accuracy and convention turnover remain similar. The sender is less likely to abandon a convention after a flag without the score (0.14 vs. 0.23), but turnover persists. Details are in Appendix D.5 (Fig. 17).


We believe our responses address the main points you raised: the ground truth assumption (Q1), the rationale for not having a cost for monitor flagging (W4/Q1), and why it is realistic for the sender to see the monitoring outcome right away (W6/Q2). We would be glad if you could reconsider your score in light of these results.

Thank you again for your thoughtful comments and for stating that you would raise your score. We believe our additional experiments address all of your concerns. We would appreciate it if you could consider updating your score in light of them, as you kindly suggested. Or, if any concerns remain, please give us the opportunity to address them through further clarifications and/or experiments.

Comments on the paper

2 comments

Dear Area Chair and Reviewers,

We thank all reviewers for their constructive feedback, which helped us further strengthen the paper. We were especially encouraged by their comments highlighting the "solid theoretical backing," "a new aspect," "well designed" interventions, and "useful evidence." We have uploaded the revised manuscript with changes highlighted in blue. To address their concerns, we made several key revisions:

  1. Robustness of experimental results.
    We conducted several additional experiments using neutral tokens instead of emojis (in response to Reviewer teNz's W2; Appendix D.5), varying instructions and monitoring feedback (Reviewer USN3, W1, W6; Appendix D.5), testing the timing of PASS (Reviewer 69ts, W1; Appendix D.2), and testing alternative monitoring conditions (Reviewer USN3, Q1; Appendix D.5). Our central findings remain robust across these conditions.

  2. Validation of the theoretical framework.
    We validated behavioral assumptions (Reviewer teNz, Q3; Appendix D.7), evaluated predictive accuracy under parameter uncertainty and against an alternative baseline (Reviewer 69ts, W3/Q2; Appendix D.7), and corrected Proposition 1 and the corresponding simulation (Reviewer 69ts, W2; Appendices A and D.4).

  3. Generality and scope of the claims.
    We clarified the motivation for the monitoring setup (Reviewer teNz, W1), narrowed the scope of our empirical claims (Reviewer USN3, W2; Abstract and Section 5), and clarified when silence functions as a codeword (Reviewer 69ts, W1; Section 4.2.3 and Appendix D.2).

We believe these additions, together with the other revisions detailed in our responses, address all the reviewers' concerns. We would appreciate their feedback on whether the issues have been resolved, and we are happy to provide further clarification or additional experiments.

I have read the author responses and other reviews, and looked at the revised paper. I appreciate the addition of experiments varying the availability of ground truth to the monitor. Although the new results confirm that the monitor depends on the ground truth becoming available at some point, the main results of the paper are still valuable and interesting. I would like to see the paper accepted and have increased my score from 3 to 4.

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