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Paper summary
This paper adapts continuous adversarial training to honesty alignment through CATCH. It constructs context-specific honest and dishonest response pairs, optimizes embedding perturbations toward dishonest responses, and trains the model toward honest responses while retaining utility through auxiliary instruction data. Evaluations on Llama-3.3-70B-Instruct and Qwen3.6-27B cover pressured dishonesty in MASK, confession behavior in Among Us, and disclosure of concealed behaviors in AuditBench. The paper also investigates how the source of utility data affects capability preservation.
Critical strengths
Transfer across distinct manifestations of dishonesty is the strongest contribution. Training on roughly 200 contrastive examples transfers from self-reporting scenarios to substantially different settings. The Among Us comparison with SFT-tau is particularly informative: adding adversarial perturbations raises confession rates from 14% to 84% on Llama and from 58% to 85% on Qwen. This supports a benefit beyond the toward/away training losses alone.
The evaluation explicitly investigates several alternative explanations for improved honesty scores. MASK separates honest, ambiguous, and dishonest responses and reports missing-belief rates. The Among Us appendix checks valid actions, participation, and refusals. Together with the capability benchmarks, these analyses provide stronger evidence than a single aggregate honesty score.
Critical weaknesses
The correspondence between the headline honesty and utility results needs reconciliation. Table 3 in Appendix A.4 reports CATCH honesty of 86.0% on Llama and 90.7% on Qwen. Table 5 in Appendix A.7 instead reports 73.9% and 74.1% for the respective on-policy runs, while retaining the same AlpacaEval win rates of 51.3% and 51.8%. The epochs listed there also match the selected epochs in Appendix A.3. Different runs or evaluation settings might explain this, but the manuscript does not make the correspondence clear. Since simultaneous honesty improvement and utility preservation is a central claim, the reported values need to be linked unambiguously to specific checkpoints and evaluation protocols.
The claimed honesty–utility advantage over activation steering needs a matched trade-off comparison. The main evaluation uses a steering configuration with substantial utility degradation on Llama. Section 6 acknowledges that weaker steering could preserve more utility at the cost of honesty. Without comparing representative configurations at matched honesty or utility levels, the results support the quality of the selected CATCH configuration more directly than superiority of the methods’ attainable trade-offs.
Questions for authors
Please identify the exact checkpoints and evaluation settings underlying Table 3, Figure 5, and Table 5. Why do the on-policy runs have different reported MASK honesty values despite matching epochs and AlpacaEval scores? A single table pairing honesty and utility for each selected checkpoint would resolve this concern.
Can you compare CATCH with a small steering-strength sweep at matched MASK honesty or matched utility, using a common configuration-selection protocol?
How were training and validation examples separated, and what criterion selected the final checkpoints? In particular, were splits made at the scenario level, and were MASK or capability benchmark results used for checkpoint selection?
2 comments
Follow-up on author response
Thank you for the detailed response and revisions. The consistent MASK denominator and the paired honesty/utility results from the same checkpoints resolve the table discrepancy. The added steering-strength sweeps provide the requested tradeoff comparison. The clarified checkpoint-selection procedure and the HTP evaluation on 98 held-out scenarios, excluding the 14 validation scenarios, address my concern about the evaluation split.
My original concerns are now largely addressed. The steering comparison supports the conclusions at the evaluated strengths and settings; it should not be interpreted as establishing dominance over the entire Pareto frontier. I retain my weak-accept recommendation.
AI assistance was used to organize the rebuttal evidence and draft this follow-up.
Response to Reviewer Jr3f – table mismatch, steering, and checkpoint selection
Table 3 and Table 5 clarification
We thank Reviewers 1MGG and Jr3f for catching this. Table 3 and Table 5 in the appendix reported the same checkpoints from the same run (CATCH at epoch 3 on Llama-3.3-70B and epoch 2 on Qwen3.6-27B), scored on the same 1,000 MASK responses. However, the honesty scores were computed differently. In Table 3, scenarios for which no consistent belief could be elicited are excluded from the denominator, while in Table 5, no-belief scenarios were kept in the denominator and counted as not honest. We've now updated Table 5 (now Table 7) to follow the same convention as Table 3, as we had initially intended to do, and as described in the experimental setup section. All numbers across tables and figures are now coherent.
Comparison with steering
We thank the reviewer for suggesting this. We have now included a detailed comparison with different steering strengths in Appendix A.7.1, which highlights CATCH’s advantage.
Detail on checkpoint selection
We thank the reviewer for raising this question. No benchmark data is used as a training or validation set. We sample 20 data points from the magpie data as the held-out validation set. The training and validation honesty examples come from two datasets. For training, we use the on-policy data described under Adversarial data in Section 4. Validation uses the 14 self-report scenarios from Herbster et al. (2026)’s test set. For each saved epoch, we sample 10 answers per scenario under the dishonest system prompt and score the share of the 140 answers judged honest. Among epochs whose loss on held-out utility data is within 1.1× that of the base model, we select the one with the highest score, and the earliest one when there’s a tie. We have now included this detail in the experimental setup (Section 4).