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Under review as a conference paper at ICLR 2027

Lie Rates and Selective Censorship Dissociate During Distillation

Abstract

Can censorship pass from a teacher model to a student through training data screened to remove the censored topic? Prior work presents increased false answers about China as evidence of this "subliminal learning," even across model families. Yet that measure alone cannot distinguish selective censorship from a broader loss of accuracy. We test this distinction using a synthetically created benchmark comprised of matched questions about China and other jurisdictions, comparing students trained on filtered outputs from two censoring teachers with students whose training includes explicit China-related examples. Filtered training meaningfully raises instruction-tuned 3B students' false-answer rates, but none of seven filtered students show a detectable increase in censorship specific to China relative to their starting models. Adding explicit China-related examples consistently increases this selective censorship measure, while false-answer rates do not consistently rise. At 120B parameters, we measure selective whitewashing: minimizing or omitting sensitive facts disproportionately for China, which we find explicit exposure increases as well relative to filtered training. Higher false-answer rates alone therefore do not establish that censorship has transferred subliminally across model families.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
knowledge distillation, subliminal learning, trait transfer, censorship, model diffing, interpretability, evaluation

Reviews

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1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_KgCQOpenReview ↗
Rating
1
Confidence
3
Informativeness
3
Presentation
3
Soundness
1
Read review
Paper summary

This paper studies whether censorship can transfer through distillation after target-topic filtering. It introduces a matched China-versus-foreign benchmark and compares filtered and overt training across model scales. The topic is important. However, the main evidence is not sufficient for the central claim: the overt condition changes both content and training dose, while the primary 120B result uses only two seeds and automated labels. The full-panel rejudgment becomes inconclusive, and the reported intervals condition on fixed checkpoints rather than accounting for training-seed uncertainty. I therefore recommend rejection.

Critical strengths
  1. The paper asks a timely and important question and correctly warns that a higher false-answer rate alone does not identify selective censorship.

  2. The matched benchmark, overlap audit, missing-label analysis, and judge-sensitivity checks are useful efforts toward construct validity.

Critical weaknesses
  1. The intervention is confounded. Overt training adds China-related examples, responses, tokens, and optimizer updates, so the overt-minus-filtered contrast cannot isolate subliminal transfer or censorship. There is no same-dose content control or uncensored-teacher control.

  2. The decisive 120B result is not robust enough. It uses two training seeds, automated judges, and complete-case selection. Under the four-judge reanalysis, only 10 and 12 concepts remain complete and the confidence interval includes zero. No human-validation results are reported, and the intervals omit training-seed and judge uncertainty.

  3. The benchmark is narrow and not demonstrably exposure-free. It is synthetic, predominantly English, contains thematic and named overlap with training material, and the finance comparison has no usable complete behavioral cohort. The claims should therefore be much narrower than selective censorship transfer in general.

Questions for authors
  1. What result would remain after matching the overt and filtered arms for training-token count, optimizer updates, and response style, while adding an uncensored-teacher control?

  2. Can the main 120B claim be replicated with additional independent training seeds and blinded human raters, with uncertainty propagated over seeds, labels, and missing answers?

Reviewer_yzW4OpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
1
Soundness
2
Read review
Paper summary

This paper develops a matched-question benchmark for measuring jurisdiction-selective censorship and contrasts filtered with overt distillation, showing that an increased false-answer rate alone does not establish subliminal censorship transfer across model families.

Critical strengths

1.The paper addresses an important measurement issue in the study of subliminal censorship transfer: an elevated false-answer rate need not indicate increased jurisdiction-selective censorship. The benchmark offers a useful framework for testing this distinction, and the comparisons across teachers and student models yield informative empirical evidence. I also appreciate the authors' transparent reporting of evaluation sensitivity, missing answers, and limitations.

  1. The authors respond directly to Conmy's experiments; thus, this article addresses an actual inference rather than a fabricated target.
Critical weaknesses

The authors acknowledge the use of AI assistance in drafting and editing. Several issues, however, suggest that this assistance was not followed by sufficient human review: terminology and benchmark naming vary across sections and tables, references are ambiguous, and the same construct is labeled differently without notice. The manuscript requires thorough revision to meet the standards of ICLR, as the current version is unfriendly to readers.

  1. The Introduction refers to the benchmark as "(anonymized eval name)," while Appendix J uses "matched-v3" and "matched-v2." Please unify the naming, or state explicitly that these denote different benchmark versions.

  2. Several terms and labels are used inconsistently throughout the manuscript. For example, "false-answer rate" and "lie rate" are used interchangeably for the same endpoint; the equivalence is marked only once, in the Introduction, while Figure 1 reports "False-answer rates" on data that Table 8 labels "Lie rate." The same comment applies to "selective censorship," "selective gap," and "whitewashing interaction," which name the same construct across two distinct operationalizations (the 3B ordinal index and the 120B four-cell categorical interaction), and to "refusal," which functions both as a category within the historical lie-rate pipeline and as a separate endpoint in the matched benchmark. Because these terms carry the paper's central claims, a short naming convention would improve readability. In the same vein, please clarify whether "finance-adjacent concepts" and "finance/financial concepts" denote different categories across benchmark versions; if not, use a consistent label.

  3. The comparison jurisdiction is referred to as “comparison,” “other,” “foreign,” and “control.” Please standardize these terms, especially since “control” could also be interpreted as referring to the benign condition.

  4. The paper’s organization and coherence could be improved. For example, Section 4.3 moves from the primary effect to missing-label sensitivity analyses, component rates, full-panel rejudging, subgroup analyses, and adapter replacements without a clear progression or sufficient transitions. It should more explicitly distinguish robustness checks that hold the original labels fixed from rejudging that changes both labels and sample coverage, and explain what these findings jointly support. The exploratory subgroup and adapter-replacement analyses address questions beyond the section’s stated focus on judging and answer coverage and would be better presented in separate subsections.

Questions for authors
  1. The number of training seeds varies across experiments: the Qwen-to-Llama-3B comparisons use three seeds, the V4-to-Llama-3B and GPT-OSS-20B comparisons use one, and the GPT-OSS-120B comparison uses two. The manuscript reports these configurations but does not explain the rationale for the differing numbers of runs. Please clarify this experimental design choice and its implications for assessing robustness to training randomness, particularly in the single-seed comparisons.

  2. The 20B evaluation uses a partial-frame eligibility rule, while the 120B evaluation requires all six answers to be scorable in both models. Although sensitivity analyses are provided, these rules retain different concept cohorts and limit direct comparability. Please explain why different primary criteria were chosen and summarize the findings under a common rule.

  3. What motivated the choice of one epoch of response-only LoRA finetuning? Please clarify whether this setting was inherited from prior work or selected based on preliminary experiments.

  4. Most seriously, although the proposed benchmark is a central contribution, the submission lacks an accessible dataset or code link and does not include supplementary materials with the full evaluation prompts, matched concept pairs, reference cards, and scoring implementation, which substantially limits reproducibility.

Reviewer_u8EfOpenReview ↗
Rating
1
Confidence
2
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

This paper investigates whether censorship-related behavior transfers from teacher LLMs to students through distillation data that excludes explicitly sensitive topics. It introduces a matched benchmark to distinguish general factual degradation from jurisdiction-selective censorship. Experiments with 3B, 20B, and 120B students show that filtered distillation increases false-answer rates without a statistically detectable increase in selective censorship. The paper also finds that changes in internal representations do not reliably predict censorship behavior.

Critical strengths
  1. The problem is important. The distinction between factual accuracy and selective censorship is important for interpreting prior results.

  2. The experiments cover multiple teachers, student architectures, and model scales. The paper evaluates Llama-3.2-3B, GPT-OSS-20B, and GPT-OSS-120B. The 3B experiments also include pretrained and instruction-tuned students. These settings provide useful evidence that lie rates and selective-censorship measures can behave differently.

  3. The paper provides extensive robustness and diagnostic analyses. These include paired bootstrap intervals, missing-label sensitivity bounds, alternative judge panels, training-data overlap audits, and representation-level analyses. The authors explicitly report inconclusive results and failed experiments rather than treating them as supporting evidence.

Critical weaknesses
  1. The paper does not establish a causal connection between its measured behavioral tendencies and censorship. This paper makes an assumption that "behavioral tendencies" means "censorship". The central evaluation operationalizes censorship through selective whitewashing, defined by omissions, minimization, or presentation of particular accounts. However, these response patterns can arise from multiple mechanisms, including factual knowledge gaps, differences in training distributions, general safety alignment, and evaluation bias. The proposed country-by-sensitivity interaction captures statistical differences in model outputs, but it does not identify the underlying mechanism. Although the overt vs. filtered training intervention produces measurable behavioral changes, it cannot establish that censorship itself was transferred from the teacher. The additional training examples also change topic exposure and training dose. Consequently, the evidence primarily supports an association between distillation conditions and measured response patterns, rather than a causal explanation of censorship transmission. The paper should distinguish behavioral selectivity from censorship more rigorously and avoid interpreting the former as direct evidence of the latter.

  2. The benchmark is geographically and topically narrow, raising concerns about selection bias and generalizability. All 72 concepts center on specific countries, while other jurisdictions serve only as comparison cases. This asymmetric construction makes it difficult to separate general censorship mechanisms from country-specific model behavior. Furthermore, the benchmark relies on predefined reference facts and automated judgments to classify politically sensitive responses as whitewashing. These definitions may introduce subjective framing bias, particularly for contested historical and political issues. The authors should evaluate multiple censorship regimes, diversify the sensitive topics, and independently validate the reference facts.

  3. The main censorship measurements lack human validation, and the conclusions depend on automated judging. The primary 120B evaluation uses a tiered judging protocol. Responses initially labeled Answered by Kimi receive no additional judgments. Under the four-judge reanalysis, 45 of 415 jointly scorable responses originally labeled Answered become Whitewashed. The primary overt-minus-filtered effect is 15.83 percentage points with a 95% CI of [6.80, 25.10]. However, the four-judge majority produces 12.92 [-6.33, 34.13], which is inconclusive. Only 10 and 12 complete concepts remain across the two seeds. Although individual judges and the non-Kimi majority generally support a positive effect, the primary result remains sensitive to the judging procedure. The paper reports no completed human-validation results. This is a major concern because whitewashing often involves subtle omissions rather than explicit falsehoods.

  4. The overt vs. filtered comparison does not isolate censorship transfer from ordinary supervised finetuning. The overt condition adds 670 examples, and also increases training by 59,978 supervised tokens and 84 optimizer updates at 120B. The experiment changes both training content and training dose. More importantly, it lacks an uncensored teacher trained on exactly the same additional prompts. Without this control, the observed increase cannot be attributed specifically to the censoring teacher's behavior. It could result from direct exposure to sensitive topics or from the general effects of additional finetuning. A matched-dose condition with nonsensitive examples would further separate these explanations.

  5. The absence of a statistically detectable censorship increase under filtered training is not strong evidence against subliminal transfer. All seven 3B filtered-minus-baseline selective-gap confidence intervals include zero. However, these intervals are relatively wide. The estimates therefore remain compatible with nontrivial positive effects. The paper does not perform equivalence testing or establish a minimum detectable effect. Furthermore, the main 120B comparison uses only two training seeds, and its bootstrap intervals do not capture training-seed uncertainty. These limitations make it difficult to distinguish genuinely absent transfer from insufficient statistical power.

  6. The four-cell benchmark does not fully control for general response degradation. The proposed interaction subtracts the benign vs. sensitive difference for other jurisdictions from the corresponding difference. However, the reported benign-cell whitewashing rates are exactly zero across the evaluated teachers and the paired 120B students. The benign cells provide little additional information for this endpoint. Moreover, the foreign-sensitive cases can differ in factual difficulty, historical ambiguity, and model familiarity. The reference-based whitewashing rubric may also classify factual omissions caused by poor knowledge as censorship. Additional measures of ordinary factual accuracy and reference completeness would strengthen the interpretation.

  7. The representation analyses provide limited mechanistic insight. The paper finds widespread activation changes but no corrected association with censorship behavior. However, the 3B analysis uses only 16 held-out concepts across 672 association tests. The 20B analysis retains only five common behavioral test concepts. These sample sizes are too small to support informative negative conclusions about representation-behavior relationships. The adapter-replacement experiments are also inconclusive as mechanistic tests. Early- and middle-layer replacements both attenuate whitewashing, while the planned reverse transplantation fails because of severe output degradation. These results do not identify a specific causal representation or mechanism for censorship transfer.

  8. The paper describes planned human validation but reports no completed results. If human annotators are used, the authors should clarify whether institutional ethics approval or an exemption is required.

Questions for authors

How robust is the main 120B result to independent human judgments and alternative missing-label handling? Can the authors report human-validated whitewashing rates on a shared cohort across the filtered and overt students? This would clarify whether the positive interaction persists independently of the asymmetric automated judging procedure.

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