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Under review as a conference paper at ICLR 2027

Unmasking the Hidden Bias, Fairness, and Safety Costs of Compression with Mixture-of-Expert Models

Abstract

Mixture-of-Experts (MoE) language models are often compressed for deployment, yet the fairness, bias, and safety effects of these interventions remain poorly understood, particularly for Expert Compression (EC) algorithms and their required calibration data. We investigate how compression algorithms and calibration data mixtures affect fairness and safety behaviour in MoE language models. Across three diverse MoE architectures, we find that EC is highly sensitive to calibration data composition. Expert merging produces the largest regressions on average, although the relative behaviour of merging algorithms varies substantially across architectures. Expert pruning is generally less disruptive, while quantization and weight sparsity are more stable and less sensitive to calibration data. We show that benchmark level improvements can be misleading: some aggressive compression settings appear more stable on selected fairness benchmarks while degrading task accuracy and instruction following, and prompt matched generation diagnostics reveal greater behavioural drift from the uncompressed baseline. Targeted interventions show that pruning just three of the 6,144 experts in Qwen3-30B-A3B can turn a refusal of a harmful AdvBench request into compliance, whereas quantizing the same experts to 2 bits preserves the refusal. These results demonstrate that the fairness and safety effects of MoE compression are neither simple nor monotonic and highlight calibration data, model architecture, and algorithm selection as key considerations when compressing MoEs for deployment.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
bias, fairness, moe, compression, quantization, sparsity, pruning, expert merging

Reviews

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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_vkH6OpenReview ↗
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Paper summary

This paper investigates the effects of post-training compression on Fairness, Bias, and Safety (FBS) in Mixture-of-Experts (MoE) language models. The authors compare Expert Compression (EC)—specifically expert merging (HC-SMoE, M-SMoE) and expert pruning (REAP, Frequency Pruning)—against fine-grained parameter-level compression (weight quantization: AWQ, GPTQ, Dynamic FP8; weight sparsity: WANDA, SparseGPT). Evaluated on three MoE architectures (Qwen3-30B-A3B, ERNIE-4.5-21B-A3B, Gemma-4-26B-A4B), the authors report that:

  • Expert merging causes the most severe benchmark regressions on average, whereas expert pruning is less disruptive, and 8-bit quantization is the most stable.
  • EC algorithms exhibit high sensitivity to the proportion of safety data present in the calibration set.
  • Pruning as few as 3 of 6,144 experts in Qwen3-30B-A3B switches an AdvBench harmful prompt from refusal to compliance, whereas quantizing those same 3 experts to 2 bits maintains refusal.
  • Apparent improvements on individual fairness metrics (e.g., lower BBQ ambiguous bias) often mask severe capability collapse.
Critical strengths
  • This paper studies a timely and important topic. While compression effects on bias have been studied in dense models, the intersection of MoE routing/expert mechanics with fairness, bias, and safety is an important, emerging area.
  • This paper reports multi-seed runs with error bars, which provide helpful insight into variance of post training compression.
  • This paper discusses the insight that apparent "improvements" in bias benchmarks often coincide with catastrophic capability degradation.
Critical weaknesses

On benchmark selection

  • This paper uses benchmarks that are slightly outdated. For example AdvBench consists of mostly simple direct prompts, which are trivial for modern LLMs as of 2026. Relying solely on AdvBench to make overarching claims about "safety costs" is inadequate. Modern safety research demands standardized, multi-faceted benchmarks that evaluate nuanced risks, multi-turn elicitation, and red-teaming. Some additional benchmarks for consideration: HarmBench, StrongREJECT, WildJailbreak.
  • The evaluation is overreliant on substring/Regex matching, which the authors have also discussed in Appendix A, I wish the authors can provide more insights on evaluation metrics themselves.

On general capability retention benchmarks

  • The authors only evaluate on IFEval, which is close to saturation and only evaluates a narrow notion of instruction following, i.e., strict format constraints. This does not reflect model's general capability IMO. Please refer to prior works such as XU et al., 2024 and Hong et al., 2024

On problem framing

  • This sentence "Pruning just three of Qwen's 6,144 experts (0.049%) is sufficient to change a refusal into compliance... whereas 2-bit quantization does not." IMO is misleading and cheery picking according to appendix F.
  • On comparison compression, the authors apply 2-bit quantization to only the 3 isolated experts and remaining 6k experts are uncompressed BF16, this IMO is not a reasonable way to evaluate low-bit quantization.

On experiment setup

  • All compression methods are calibrated using only 128 samples with 2k tokens max, this setting is far from sufficient with the model sizes studied.
  • The paper tests calibrating compression using 100% safety data (128 purely safety prompts). It is entirely expected that calibrating a compression algorithm exclusively on refusal prompts will overfit expert retention to safety and destroy general capabilities (IFEval collapses by >20–50%). Presenting this as an insightful "trade-off" is unconvincing to me.

On conclusion

  • Several prior works have reported similar insights and those are missing from references, for example Xu et al., Findings of EMNLP 2024,

References

  • Beyond Perplexity: Multi-dimensional Safety Evaluation of LLM Compression, XU et al., Findings of EMNLP 2024
  • Decoding compressed trust: Scrutinizing the trustworthiness of efficient llms under compression. Hong et al., ICML 2024
  • Pruning Weights but Not Truth: Safeguarding Truthfulness While Pruning LLMs. Fu et al., Findings of EMNLP 2025
Questions for authors
  • Whole model low-bit quantization
  • Generalization of refusal experts
  • General capabilities evaluation
3 comments

Thank you for your detailed review.

Safety beyond AdvBench (Appendix F.1). HarmBench and StrongREJECT now cover all three models. We report HarmBench over its standard and contextual behaviours, and its copyright behaviours separately, since reproducing copyrighted text requires the model to have memorized it. At 50% with the default mixture:

  • Qwen HC-SMoE raises HarmBench from 0.117 to 0.307, and its StrongREJECT score from 0.067 to 0.405 under refusal suppression and from 0.048 to 0.466 under prefix injection.
  • Gemma HC-SMoE raises HarmBench from 0.067 to 0.546.
  • Weight sparsity can also raise harm that AdvBench misses: Qwen WANDA 2:4 raises HarmBench from 0.117 to 0.312 while AdvBench refusal falls only from 0.998 to 0.987.

The AdvBench findings therefore hold on held-out and harder benchmarks, and HarmBench also exposes harm that AdvBench misses. We did not use WildJailbreak because Tulu 3 WildJailbreak is one of our three safety calibration subsets, so it would not be held out.

We have not evaluated adaptive attacks or multi-turn attacks and agree these would be interesting extensions. Limitations and Future Work now include reference to both attacks.

Refusal matching. We rescored all 390 runs with three fine-tuned LLM judges. This exposes refusals the phrase list misses (uncompressed ERNIE refuses 0.771 under refusal phrase matching and 0.981 under the WildGuard classifier) and separates harmful compliance from degenerate output. Default ERNIE M-SMoE falls to 0.014 refusal under refusal phrase matching, but only 0.160 of its responses are harmful and 0.741 are degenerate (Appendix E). Refusal phrase matching counts every response without a refusal phrase as compliance, including degenerate output from a model that has lost capability. The LLM judges label harmful compliance directly, so we no longer mistake capability loss for harmful compliance.

General capability (Appendix F.2). GSM8K, HumanEval+ and MBPP+ show that expert compression leaves capabilities highly uneven. Under the default mixture, quantization retains at least 96% of the uncompressed score on every capability measure, and weight sparsity at least 76%, with its largest losses in coding under 2:4 masks. The weakest measure of an expert compression method, usually coding, retains 0 to 91%:

  • Gemma HC-SMoE keeps GSM8K at 0.782 but drops HumanEval+ from 0.933 to 0.035.
  • Qwen M-SMoE loses nearly all coding ability.
  • Qwen REAP keeps most of its coding ability under the default mixture (HumanEval+ 0.795, MBPP+ 0.852 vs 0.866 and 0.926). Calibrated only on safety data, it falls to 0.079 and 0.167 while GSM8K stays at 0.931.

IFEval alone understated how uneven this loss is, which is why we highlight that every bias and safety result must be considered holistically with the capability benchmarks.

Targeted expert interventions vs whole model quantization. We included whole model 8-bit quantization results in our initial submission to ensure a comparable compression ratio across all compression method families. Our targeted expert quantization interventions at 2 bits were not intended to replace our whole model quantization results nor be representative of an actual deployment scenario. Rather, we were attempting to causally link the absence of specific experts in the REAP pruned checkpoints to negative fairness and safety outcomes. By applying increasingly aggressive quantization and weight sparsity to these same experts, we identify how sensitive these experts are to increasing levels of compression.

To improve the robustness of these results and avoid any potential inadvertent cherry-picking, we repeated the targeted expert interventions over the original request and 20 paraphrases for each of the two cases (Appendix J). Our original 2-bit expert quantizer was symmetric round to nearest with absmax scales and no calibration data, so at 2 bits it keeps three levels and zeroes 84% (one scale per group of 128 weights) to 93% (one scale per output channel) of those experts' weights. Pruning the selected experts flips 16 of 40 refusals, while 2-bit quantization flips 6 with group scales and 9 with channel scales, 4-bit quantization only one, and 8-bit none. None of the ten random control sets per case, drawn from experts active in the refusal and matched by layer, flips any of these refusals. We agree the original sentence overstated the contrast. The revised text reports these counts in place of the original statement that 2-bit quantization preserves refusal. The abstract now states that 8-bit and group-wise 4-bit quantization of the same experts never change the refusal, and 2-bit changes it less often than pruning. We do not claim a general causal mechanism of refusal, but these results highlight that expert pruning appears more capable of removing entire functionalities than fine-grained compression at the same compression ratio.

For a more aggressive whole model quantization setting, we added AWQ W4A16 on all routed expert projections for Qwen and Gemma under all three data mixtures; it stays near the uncompressed level:

Gemma, default mixtureExpert weight reductionDisamb. BBQ acc.IFEval
Uncompressed0%0.7720.889
AWQ W4A1675%0.7720.885
REAP 50%50%0.6810.651
HC-SMoE 50%50%0.3590.320

AWQ W4A16 is a single run; REAP and HC-SMoE average three seeds. Qwen W4A16 matches its baseline on HumanEval+ (0.902 vs 0.866) and HarmBench (0.112 vs 0.117). These 4-bit results also keep capability at a larger nominal reduction in expert weight storage than expert compression at 50%, reinforcing our finding that fine-grained compression is more robust than expert compression. The W4A16 results now appear in tables 6, 8, 9, and 11.

Calibration size (Appendix I). We use 128 calibration samples for all data mixtures to calibrate the compression methods, the number used by GPTQ and SparseGPT. To test whether expert compression needs more, we recompressed REAP and HC-SMoE at 50% with 1,024 samples for all three models, and with 256 and 512 for Gemma. REAP and HC-SMoE are insensitive to calibration size over this range. Results stay within seed noise across all three models, both methods and all nine metrics, and safety shows no trend with budget. The effects we report persist at eight times the calibration data. See Appendix I and Figure 6 for more details.

Safety-only calibration. We vary the safety data proportion to show that expert pruning and merging are more sensitive to calibration data than quantization and weight sparsity. At 50% compression, the spread of AdvBench refusal across the three mixtures reaches 0.89 for merging and 0.56 for pruning, but at most 0.13 for weight sparsity and 0.02 for quantization. The bias benchmarks show the same sensitivity, in opposite directions across methods: safety-only calibration lowers Qwen frequency pruning's biased rate on SocialStigmaQA from 0.53 to 0.09 but raises Qwen HC-SMoE's from 0.06 to 0.60, while AWQ W4A16 stays within 0.01. We agree that the capability loss under safety-only calibration follows from how REAP and HC-SMoE select experts: Qwen REAP calibrated only on safety data keeps refusal and GSM8K (0.931) but loses coding (HumanEval+ 0.079). A moderate share of safety data largely avoids this cost. The default data mixture, with 21 of 128 samples from safety data, raises AdvBench refusal over no safety data by 0.05 on average without lowering IFEval or BBQ accuracy, so we recommend it for expert compression and concretely state as much in the discussion and conclusion.

Related work. Thank you for pointing out these additional related works. We added Xu et al. (2024) and Fu et al. (2025) and sharpened the comparison with Hong et al. (2024). Those studies compress dense weights. Our study isolates structural expert removal and merging in MoEs, compares it with quantization and sparsity across three architectures, calibration mixtures and seeds, and tests individual experts causally.

Reviewer_gd1vOpenReview ↗
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Confidence
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Informativeness
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Paper summary

This paper systematically studies how MoE compression affects fairness, bias, and safety behavior. Experiments cover three architectures—Qwen, ERNIE, and Gemma—and compare quantization, weight sparsification, expert pruning, and expert merging, with safety-data proportions of 0%, 16.4%, and 100% in the calibration set. Evaluation includes BBQ, AdvBench, XSTest, IFEval, ToxiGen, and diagnostics of generation drift. The paper also presents a targeted intervention case study on Qwen: disabling 3 of 6144 experts changes one harmful request from refusal to compliance, whereas 2-bit quantization of the same experts preserves refusal.

Critical strengths
  • The topic is timely and practically relevant to deployment. Existing MoE compression work typically reports only capability and efficiency, whereas this paper adds an important safety-evaluation dimension.
  • The experimental matrix is broad: three substantially different architectures, four compression families, three calibration mixtures, and three sampling seeds, while jointly examining harmful-request refusal, benign over-refusal, bias, and instruction following.
  • The conclusions are generally appropriately restrained. Sections 6–8 do not interpret an improvement in one metric as an overall gain in fairness or safety, and explicitly note dependence on architecture and algorithm.
  • The targeted intervention evaluates not only one compressed output, but also proper subsets, random sets, quantization, and several sparsity levels. However, the random-set control for the three-expert case is weak, as discussed below.
  • The limitations, ethics, reproducibility, and AI-use disclosures are thorough, particularly the explicit discussion of dual-use risks from publishing the coordinates of safety-relevant experts.
Critical weaknesses
  1. The aggregate metric across compression families is somewhat arbitrary. Section 6.1 aligns the directions of changes in BBQ accuracy, bias distance, AdvBench/XSTest refusal, and IFEval, then takes an unweighted average and averages methods within each family. Although all metrics are approximately within [0,1], they have different statistical meanings, variances, and baseline difficulty. The claim that “merging causes the greatest average degradation” should be accompanied by per-metric robustness results, confidence intervals, and sensitivity to other reasonable aggregation schemes.
  2. Safety measurement remains fragile. AdvBench and XSTest rely primarily on refusal-phrase matching. Appendix E shows that switching to the original XSTest prefix parser reverses some trends. The ToxiGen base model is near random. IFEval helps identify capability collapse, but cannot fully distinguish genuine safety changes from inability to answer or degenerate output. Key conclusions need support from a stronger behavioral classifier or blinded human annotation.
  3. Safety-data proportion is confounded with changes in the overall distribution. The 0% and 100% conditions alter not only “safety” content, but also domain, task format, and language distribution. Claims that “safety data causes a given change” should therefore be narrowed to calibration sensitivity under these three specific mixtures, or supplemented with non-safety controls matched for topic, length, and format.
  4. The minimal-expert intervention is post hoc and prompt-specific evidence. The search begins with known REAP failure prompts and experts that were already pruned, and is ultimately confirmed only on two Qwen prompts. Appendix A also reports that the set of 172 experts changes only 4 of 520 AdvBench prompts. This is a valuable existence case, but does not establish a general safety mechanism.
  5. Statistical inference is limited. Three seeds characterize variation in calibration sampling, but no formal tests are reported; the uncompressed model is evaluated only once. The paper appropriately avoids interpreting small differences, but its main conclusions should still quantify uncertainty across seeds and prompts.
  6. The random control for the three-expert case is insufficiently rigorous. Of the 30 random experts reported in the paper, 23 were not active in the original refusal trajectory. Therefore, the observation that “random pruning still refuses” is not an equally difficult counterfactual to pruning candidate experts. The seven-expert case uses controls matched among active experts and is more convincing.
Questions for authors
  1. Does the conclusion that “merging causes the greatest degradation” hold under per-metric analyses, alternative aggregation weights, and bootstrap confidence intervals?
  2. Can the authors conduct blinded human annotation of the key AdvBench/XSTest changes, or validate them with an independent safety classifier, and report disagreement with phrase matching?
  3. Can the authors construct a non-safety control set matched to the safety data in topic, length, and format, to separate “safety content” from general distribution shift?
  4. Do the three-expert/seven-expert interventions replicate on paraphrased prompts, other harmful categories, and other random seeds?
2 comments

Thank you for your detailed review.

Aggregation and uncertainty (Appendix G). At 50%, merging has the largest mean regression in every variant:

AggregationGroups where merging regresses most
Equal metric weights27/27
LLM judges for AdvBench harm and benign XSTest refusal27/27
Drop any one metric except IFEval27/27
Drop IFEval25/27
Metrics standardized by spread21/27
Mean rank across metrics21/27

A paired bootstrap (2,000 replicates, resampling prompts and calibration seeds) confirms that merging regresses more than pruning: the 95% interval of the gap excludes zero under both the aggregate over the six metrics and the LLM judges. The aggregate credits merging whenever its BBQ bias scores move toward zero as accuracy falls; without both bias scores the gap widens, so the aggregate understates the regression of merging. Section 6.1 now reports the claim with these checks.

Statistical inference. The paired bootstrap quantifies uncertainty over prompts and calibration seeds for the main ranking claim. It resamples the uncompressed model's prompts with the same draws, so it also covers the single baseline evaluation. Elsewhere we report seed standard deviations rather than significance tests.

Independent safety scoring (Appendix E). Refusal phrase matching and the WildGuard classifier agree on 93–100% of AdvBench responses for Qwen and Gemma, but only 66–78% for ERNIE, whose refusals often use wording outside the phrase list. Uncompressed ERNIE refuses 0.771 under refusal phrase matching and 0.981 under the WildGuard classifier. Our conclusions therefore do not rest on phrase matching. The ranking holds under the LLM judges, and where the two disagree, phrase matching undercounts refusals before compression (ERNIE) rather than producing compression effects. The XSTest prefix-parser reversals depend on where the parser looks for a refusal. The WildGuard classifier reads the whole response and sides with our matcher, raising Gemma HC-SMoE's benign refusal from 0.024 to 0.171 where the prefix parser shows a fall.

The LLM judges also separate refusal loss from harm. Default ERNIE M-SMoE falls to 0.014 refusal under refusal phrase matching, but only 0.160 of its responses are harmful and 0.741 are degenerate. The ranking of compression method families is unchanged under LLM judge scores. We unfortunately did not have time to setup blinded human annotation during the rebuttal period.

Safety data as a confound. All three mixtures draw the same number of samples from one parent SFT dataset, the Tulu 3 SFT mixture. We agree they are not perfect comparables in domain and task format. We have narrowed the claims to the three mixtures we study (Limitations). The evidence still ties the effect to safety content. At 50% compression, safety-only calibration raises AdvBench refusal over the 0% mixture for every model and method, for example Qwen M-SMoE from 0.109 without safety data to 0.369 at the default mixture and 1.000 with safety data only. REAP shows the same ordering at the level of individual experts. In every seed, REAP without safety data prunes two or three of the three experts whose removal flips the sample 26 refusal (Section 6), the default mixture prunes one, and the safety-only mixture prunes none.

Paraphrases and active expert controls (Appendix J). We held each expert set fixed over the original request and 20 paraphrases; the uncompressed model refuses 40 of these 42 prompts. New random controls, ten per case, are drawn from REAP-pruned experts the router selected during the original refusal, matched by layer. All quantizers are symmetric round to nearest, with each scale set by the largest absolute weight in its output channel or group, and use no calibration data.

Intervention on the selected expertsRefusals flipped to harmful compliance
Pruning16/40
Zeroing weights17/40
2-bit, one scale per output channel9/40
2-bit, one scale per group of 1286/40
4-bit, one scale per output channel1/40
MXFP4, block of 321/40
4-bit, one scale per group of 1280/40
8-bit, per channel or group of 1280/40
Random sets of experts active in the refusal0/40

The new controls answer your concern about the targeted expert interventions: they are now drawn only from experts active in the refusal and matched by layer. None of them flips any of the 40 refusals, while pruning the selected experts flips 16. The effect generalizes across wording for both cases. We claim it for these two Qwen behaviours, not as a general set of refusal experts.

Thank you for the thorough and constructive rebuttal. All major concerns have been convincingly addressed. I maintain my rating of 4.

Reviewer_mAzgOpenReview ↗
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Informativeness
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Paper summary

This paper studies how post-training compression techniques (e.g. quantization, sparsification, pruning, merging) affects the fairness, bias, and safety of three MoE LLMs. It finds that expert merging causes the largest performance regressions, followed by pruning, while quantization and weight sparsity are relatively stable. Safety-data calibration improves refusal of harmfful requests but does not restore bias or instruction-following performance. Notably, pruning just three of Qwen’s 6,144 experts can turn a refusal into compliance, while 2-bit quantization of the same experts does not.

Critical strengths
  • The paper addresses a timely and practical question, as the effects of MoE compression on fairness, bias, and safety remain understudied.

  • The paper provides broad and reasonably controled experiments (e.g. three architectures, nine methods, two compression ratios, etc.). The case studies seem to be carefully designed, testing broad range of subsets, including random controls, and manually verifying outcomes. Also, comparisons across pruning, quantization, and sparsity on the same experts help distinguish the effects of removing experts from reducing their precision.

  • The authors highlight important metric limitations, showing that improved bias scores can coincide with lower accuracy and instructtion-following performnce. The limitations are clearly acknowledged. That is good scientific practice.

Critical weaknesses
  • The novelty of the paper is somewhat limited, as the findings are largely descriptive and provide limited actionable guidance. The practical impact could be strengthened by proposing concrete mitigation strategies, such as safety-aware expert selection, or diagnostics to predict FBS degradation before compression.

  • I think there is somewhat limited evidence for fairness and bias claims in the paper. Bias evaluation relies mainly on BBQ, ToxiGen is near chance at baseline (0.521/0.504), and CrowS-Pairs is auxiliary, comes from an earlier evaluation pass, covers only Qwen and ERNIE, and is mostly single-seed. Also, the observed score changes often coincide with capability degradation, and no matched-capability comparisons are provided. Adding broader bias evaluations and matched capability comparisons would help clarify whether the observed changes reflect genuine shifts in fairness or are primarily driven by capability loss.

Minor

  • Missing references: IFEval and ToxiGen have no reference anywhere in the paper. I checked the reference list and neither appears. Both are used in the main results and in Figure 2. Would be nice to add these.

  • BBQ, XSTest, are not cited where they are introduced. Section 5.2 lists them with no citations. In Related Work section, their citations are bundled together in one sentence (Parrish; Nangia; Nadeem; Röttger; Zou) without saying which citation belongs to which benchmark. Would be good to cite these by name at first mention.

  • The Discussion (Section 7) repeats Section 6.2 almost word for word: “With only safety data, REAP retains all three experts, and all seven from the second case, in every seed. Without safety data, the seed 99 checkpoint prunes all of them and the other two seeds prune two of the three and four of the seven.” This wastes space in a paper that already pushes key evidence into the appendix. It also gives the Discussion nothing new on this point.

Questions for authors

(see weaknesses)

Can you separate fairness effects from general capability loss? (Some compressed models show improved bias scores while BBQ accuracy and IFEval performance decline (e.g., BBQ accuracy drops from 0.541 to around 0.40–0.42 (Table 2)). Could the authors compare models at matched capability levels or analyze bias changes while controlling for capability loss? This would help determine whether the observed changes reflect genuine fairness improvements or are primarily a byproduct of degraded performance.

3 comments

Thank you for your detailed review.

Fairness versus capability loss. We agree that a lower bias score with lower accuracy is not a fairness gain and highlighting this mismatch is a central argument in our paper. Appendix H quantifies this in three ways.

  • Regression. Changes in disambiguated BBQ accuracy and IFEval explain most of the variation in ambiguous bias across compressed runs: R² is 0.86 for Qwen, 0.80 for ERNIE and 0.42 for Gemma. Adding compression method family indicators raises R² by at most 0.14.
  • Matched capability. We pair each expert pruning or merging run with quantized or sparse runs of the same model within 0.02 disambiguated accuracy and 0.03 IFEval. Their ambiguous bias changes differ by at most 0.004 on Qwen and ERNIE, and by 0.023 for Gemma merging. Most merging runs have no match: only 9/36 for Qwen, 13/36 for ERNIE and 8/36 for Gemma. The compression method families barely overlap in capability.
  • Answer decomposition (Gemma HC-SMoE, 50%, default mixture):
UncompressedHC-SMoE
Ambiguous bias0.0300.001
Disambiguated accuracy0.7720.359
UNKNOWN rate, disambiguated items0.1560.398
Accuracy of committed answers0.9140.597

The near-zero bias comes from more unnecessary abstention and weaker discrimination between answers. The same pattern runs through the appendix tables, the best bias and safety scores often belong to models whose capability collapsed. ERNIE M-SMoE calibrated without safety data has the lowest AdvBench harmful rate (0.008) while refusing no request, because 92% of its responses are degenerate (near empty or repetitive). Expert compression is also more sensitive to calibration data in its bias scores. Across the three mixtures at 50%, ambiguous BBQ bias moves by up to 0.067 under merging and 0.032 under pruning, against 0.022 under weight sparsity and 0.009 under quantization, and safety-only calibration raises Qwen HC-SMoE's biased rate on SocialStigmaQA from 0.064 to 0.600 while AWQ W4A16 stays within 0.01. This calibration sensitivity is an effect of the compression method family and a core argument of our paper. We agree that it cannot be fully isolated from capability loss, so the two remain confounded to an extent. Therefore, we argue it's crucial that fairness, safety, and bias metrics of compressed models be read in conjunction with more general capability declines.

Broader bias evaluation. We added DiscrimEval and SocialStigmaQA for all three models and report them in the newly added Appendices F.3 and F.4. Both show that a smaller bias score under compression need not mean a fairer model:

  • DiscrimEval, read per demographic term, shows that the uncompressed models favour Black, Asian, Hispanic, Native American, female and non-binary applicants on explicit prompts. Qwen HC-SMoE removes most of this bias (Black 0.25 → −0.04). ERNIE M-SMoE reverses it against non-binary applicants in two of three seeds (0.67 → about −0.17), and Gemma HC-SMoE's terms shrink only because its yes/no answers become less decisive.
  • SocialStigmaQA rises under compression. The uncompressed models answer "can't tell" to most prompts, even when the prompt gives evidence favouring the person (Gemma 0.92, ERNIE 0.85, Qwen 0.61 of these prompts), so their low biased rates reflect abstention. Compression removes much of this abstention, and the answers that replace it are biased more often than the same models' answers to the scenarios without a stigma. On prompts where "can't tell" is intended, ERNIE HC-SMoE gives 0.41 biased answers against 0.24 without the stigma, and Qwen frequency pruning 0.35 against 0.14. Favourable evidence leaves ERNIE HC-SMoE at 0.42. Excluding empty or repetitive output changes these rates by less than 0.01.
  • BBQ per category (Appendix K.3): expert compression lowers the pooled score through age and socioeconomic status, while physical appearance rises under every expert method for Gemma and sexual orientation for ERNIE.
  • CrowS-Pairs now covers the 76 main-result checkpoints of Qwen and ERNIE (Appendix K.2). Default 50% HC-SMoE moves it towards 0.5: Qwen 0.593 → 0.526, ERNIE 0.633 → 0.549. It now uses the same checkpoints as the main results. As CrowS-Pairs was originally designed for pretrained masked language models, we do not include it in our aggregate method rankings and report it as a standalone data point.
  • We agree that ToxiGen is close to chance for all three uncompressed models (0.438 to 0.521), and we do not rely on it for any conclusion, aggregate method ranking or summary.

These benchmarks address the concern that our fairness claims rest on BBQ alone, since neither is derived from BBQ. The above agree with our prior result, but now include more diverse and disaggregated results in the appendices. We hope this extended evaluation suite improves your confidence in our fairness and bias results.

Actionable guidance. Section 7 now states three concrete practices for expert compression. First, include a moderate share of safety data in calibration, as our default mixture does by sampling equally from every Tulu 3 SFT subset: it raises AdvBench refusal over no safety data by 0.05 on average without lowering IFEval or BBQ accuracy. Second, calibration data must cover the capabilities a deployment needs: Qwen REAP calibrated only on safety data keeps GSM8K at 0.93 but drops HumanEval+ to 0.08, against 0.80 under the default mixture. Third, read bias scores together with task accuracy to contextualize bias results and avoid attributing fairness to checkpoints that are simply severely degraded. Our results also point to one mitigation, since the calibration mixture decides which safety-relevant experts REAP keeps. In every seed, REAP without safety data prunes two or three of the three experts behind the sample 26 refusal, while the default mixture prunes one (Section 6). Safety-aware expert selection and diagnostics that predict degradation before compression are natural next steps, and we now list them in Future Work.

Presentation. We added the IFEval and ToxiGen references, cite each benchmark by name where it is introduced, and removed the duplicated Discussion passage.

Thank you for the rebuttal. I appreciate the authors' efforts in addressing my concerns. Since my overall assessment is already positive, I will maintain my original score.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Thanks to all reviewers and updated manuscript summary

We thank the reviewers for their careful reviews. Reviewers found the question "timely and practical" (mAzg) and "an important, emerging area" (vkH6), noting that "existing MoE compression work typically reports only capability and efficiency, whereas this paper adds an important safety-evaluation dimension" (gd1v). They valued the breadth of the study, with "three substantially different architectures, four compression families, three calibration mixtures, and three sampling seeds" (gd1v) and "multi-seed runs with error bars" (vkH6), and the insight that "apparent 'improvements' in bias benchmarks often coincide with catastrophic capability degradation" (vkH6). They also found the conclusions "generally appropriately restrained" (gd1v) and the limitations "clearly acknowledged" (mAzg).

Added text is in blue in the revised PDF. The revision adds:

  • LLM judges on all regex parsed results. Three fine-tuned LLM judges (the WildGuard classifier, the HarmBench classifier and the StrongREJECT evaluator) rescore every AdvBench and benign XSTest response, and a separate check flags degenerate output (Appendix E, Figure 5).
  • An extended benchmark suite on 90 checkpoints across all three models. It covers HarmBench, StrongREJECT, DiscrimEval, SocialStigmaQA, GSM8K, HumanEval+ and MBPP+. The checkpoints include every expert compression method (three seeds under the default data mixture, a single seed under 0% and 100% safety data), GPTQ and AWQ W8A16, dynamic FP8, WANDA and SparseGPT with unstructured and 2:4 sparsity, and AWQ W4A16 for Qwen and Gemma (Appendix F). Other compressed rows are single seeds. The suite repeats the main finding that expert compression can combine lower bias or harm scores with large capability losses. Quantization retains capability; weight sparsity shows larger coding losses with 2:4 masks. We will extend the suite to every checkpoint for the camera-ready version.
  • Robustness and coupling analyses. Alternative aggregations for ranking compression method families, with paired bootstrap intervals (Appendix G), under which merging still regresses most, and bias–capability regressions, capability-matched comparisons and a BBQ answer decomposition (Appendix H), which attribute most of the change in BBQ bias to capability loss.
  • Calibration and intervention experiments. Calibration sets of up to 1,024 samples (Appendix I), which leave our results unchanged, and the expert interventions repeated over 20 paraphrases per request with random controls drawn from experts active in the refusal (Appendix J), none of which flips a refusal.

Together, these results support our original conclusions. The apparent fairness and safety gains of expert compression coincide with capability loss, and this coupling cannot be fully removed by matching. The new capability benchmarks and coupling analyses therefore strengthen our original contribution that apparent improvements on one metric can coincide with substantial losses in task accuracy and instruction following.

We also found and fixed a small bug in how calibration data from different sources was aggregated, which affected the Qwen and ERNIE REAP and HC-SMoE checkpoints. We recompressed these 72 settings so they match the rest of the study. All tables, figures, generation diagnostics and CrowS-Pairs results use the corrected checkpoints. Capability improved as a result of the bug fix while bias scores changed little, harmful request refusal improved for ERNIE, and the ranking of compression method families was unchanged.

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