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Under review as a conference paper at ICLR 2027

What Individual Adapter Evaluations Miss: Composition-Only Failures in LoRA

Abstract

LoRA composition offers a way to reuse separately trained task adaptations, but evaluating the composed model raises a question that individual adapter checks leave open: does composition change which requests fail, even when average harm changes little? We study composition-only failures, where a composed response is labelled harmful on a request for which the base and every constituent alone are not. A request-level audit aligns base, member, and composition responses while keeping harmful compliance, refusal, and task performance distinct. Across several base models, we observe these failures in task-trained adapters and screened public adapter banks. The failures persist on additional requests, under two harm judges, and with regenerated responses. They are most pronounced when a composition includes an adapter that already produces some harmful responses alone: on average, harm stays close to that member's own rate while the set of failing requests shifts. They also occur in some compositions without such a member. Interventions expose a second gap. Retraining a member without safety data can lower the composition-only rate while increasing total harm, whereas adding refusal data lowers both and, in a tested summarization pair, retains the partner's task gain. Averaging composition weights removes most composition-only failures but leaves total harm above the base. Composed models should therefore be audited jointly for failure overlap, total harm, and retained adaptation.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
LoRA, Adapter Composition, Compositional Safety, LLM Safety, Refusal Behavior

Reviews

Among:
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1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_dU8vOpenReview ↗
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2
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Paper summary

One can train different LoRA adapters ΔWi\Delta W_i corresponding to distinct tasks ii for the original backbone weights WW. This paper studies the effect of composing these weights (W+∑iΔWiW+\sum_i\Delta W_i) on safety failures, which are not captured by either the base model weights or the individual adaptations W+ΔWiW+\Delta W_i for any task ii. The paper highlights that composition can introduce new failures. Additionally, they study interventions involving adapter retraining with safety data and composition-weight scaling, showing that reducing composition-only failures does not necessarily reduce overall harmfulness or preserve task utility.

Critical strengths
  1. The paper highlights a practical risk in modular LLM deployment, individually evaluated LoRA adapters may exhibit previously unseen harmful behavior when composed (linearly) together.
  2. Extensive evaluation across model families and different task adapters.
Critical weaknesses
  1. Limited novelty and theoretical contribution. The main formalisation and Proposition 1 are straightforward set-theoretic consequences of the definition of composition-only failures.
  2. Unnecessarily complicated presentation with limited novel results. The paper is very difficult to follow, due to use of unnecessary definitions, terms and fragmented experimental discussions. I suspect heavy use of AI, making the presentation highly unnatural.
    Despite the considerable length and number of evaluations, however, after reading the paper, I am left with three fairly intuitive findings:
  • Combining adapters can introduce new harmful responses.

  • Aggregate harmful-response rates can conceal these failure rates.

  • Adding safety data or reducing adapter weights can improve safety, sometimes at the expense of task utility.

All three findings are reasonable, but the paper does not offer much explanation beyond demonstrating them empirically.

Questions for authors

refer to the weaknesses

3 comments
AuthorsOpenReview ↗

Reply to Reviewer dU8v, part 1 of 2. W1: “limited novelty and theoretical contribution”. (Part 2: W2.)

Reply to Reviewer dU8v, part 1 of 2. W1: "limited novelty and theoretical contribution". (Part 2: W2.)

Short answer. The contribution is a measurement, with a control, that we did not find in the closest prior work. When separately trained task adapters are summed, the sum fails on requests that the base model and every member pass. On Qwen2.5-7B a trained partner adds two to three times as many such failures as a random update of the same size.

Theory. We agree: Proposition 1 is now a Remark (Sec. 3.4) and is not listed as a contribution.

The closest work (Hammoud et al., Findings of EMNLP 2024, is now cited):

WorkCombinedRelationshipUnitRandom partner found
Qi et al.one fine-tunefine-tune vs. its baserate per modelno
CoLoRALoRAs trained by one adversaryco-trained: benign alone, comply togetherrate per modelno
Hammoud et al.full models, some poorly alignedweak source carries into mergerate per modelno
Safe LoRA, SaLoRA, SafeMERGEone fine-tune + safety referencerepairrate per modelno
Oursseparately trained task LoRAs, summednone designed; trained separatelyone request vs. base and every memberyes

Your three findings, set against that work.

  1. "Combining adapters can introduce new harmful responses." New here: this happens for adapters that nobody designed to interact, and more than for a random update. CoLoRA shows it for adapters co-trained to be benign alone and comply together. Its own control, a colluding adapter merged with an unrelated benign one, does not reproduce the effect; it concludes that the degradation "depends on a specific interaction pattern rather than arising from arbitrary merging" (v2, Sec. 4.4). We measure that case. On Qwen2.5-7B each real pair gives 2.3–3.1× the composition-only rate of its norm-matched random partner (Table 2, App. L); a spectrum-matched random partner stays as low (Table 34). New run (Table 37): every real pair is above all six random draws, and all 12 paired differences with the four new draws remain significant after Holm correction. In an audit of judge-flagged events, all three readers confirmed 64 of 70: 25 of 25 for the Dolly-free compositions and 19 of 25 for the selected compositions containing Dolly, the weak adapter (Table 36).

  2. "Aggregate harmful-response rates can conceal these failure rates." New here: the converse. A count of new failures can conceal a rise in total harm, because it counts only requests that no reference model fails. When the weak adapter is retrained without refusal data, the count falls (0.104 to 0.062) while total harm rises (0.185 to 0.318; Table 4). The works above report one rate per model; we found none that counts requests on which only the composition fails.

  3. "Adding safety data or reducing adapter weights can improve safety, sometimes at the expense of task utility." New, as far as we found: the test on sums of task adapters. Prior repairs act on one fine-tune, and Gudipudi et al. (2025, now cited) observe over-refusal when fusing a safety adapter. On sums, averaging removes most composition-only failures but leaves harm above the base (Table 16). Retraining the weak member with refusal data lowers both (Tables 4, 5) but raises over-refusal (8.9% of safe XSTest prompts vs. 1.2% before; Table 21). Safe LoRA matches this repair on total harm (0.057 vs. 0.056; Table 20) with less over-refusal.

Scope. We propose no attack or defence. That summing updates raises total harm is expected from Qi et al.; a merge less safe than every source is in Hammoud et al. The excess over random partners is general on Qwen2.5-7B only; on Qwen2.5-14B and Phi-4 it depends on the partner (Table 31). The audit has no non-event rows, and one of its three readers is an author.

Sec. 1 contributions, verbatim:

  • A request-level account of the member-audit gap. We define composition-only failures and measure these failures in task-trained and public adapter banks, with a random-partner control on three in-house banks and a spectrum-matched control on one.
  • A pitfall of counting only new failures. The count covers only requests that no reference fails, so it can fall as a member worsens: member retraining can lower the composition-only rate while total harm rises. New-failure counts must be read with total harm.
  • Intervention evidence with explicit task references. Retraining a member with refusal data lowers the rate and total harm and retains a summarization partner's gain, at the cost of over-refusal; averaging composition weights removes most composition-only failures but leaves total harm above the base.

On novelty, the revision establishes two results we did not find in the work above: on Qwen2.5-7B a trained partner adds more composition-only failures than a random update of equal norm or spectrum, and a count of new failures can fall while total harm rises.

AuthorsOpenReview ↗

Reply to Reviewer dU8v, part 2 of 2. W2: presentation, the three findings, explanation. (Part 1: W1.)

W2, "unnecessary definitions, terms and fragmented experimental discussions." We agree it was hard to follow. Changes: Table 6 (App. A) now lists, for each result, the adapters, requests, judge and references used; Sec. 3 is shorter; the Fig. 2 curves are labelled.

W2, "heavy use of AI." The AI Use Statement discloses AI help with writing; the scientific content is ours.

W2, "three fairly intuitive findings." e12e_{12} is the composition-only rate: the share of requests on which the composition is harmful (both judges) while the base and every member are not. Dolly is the weak member; "plain" Dolly is retrained without refusal data, "repaired" with it ("safe" in Tables 4–5).

  1. Composition adds failures that no member shows, and a trained partner adds more than a random one. On Qwen2.5-7B, adding a real task adapter to Dolly gives e12e_{12} 0.074–0.111; adding a random update of the same norm gives 0.020–0.057 (Table 2). Real stays above random with two more Dolly seeds and on 375 fresh requests (Table 33). New: with six random draws per partner, each real pair exceeds every draw, and all 12 paired differences with the four new draws (+0.054 to +0.084) survive Holm correction (Table 37). Scope: of the 12 earlier cells, 10 survive Holm; the other two are the weakest Dolly seed with GSM8K and Alpaca. On Qwen2.5-14B and Phi-4 the excess depends on the partner (Table 31). A new Dolly seed alone gives e12e_{12} up to 0.084 (Table 32), which overlaps the composition means, and a composition's failing set shifts about as much when it is reseeded (App. C.1); so we argue from the random-partner control, not seed noise. The revision no longer claims that mean harm "stays close" to the weak member's; it now states that the sign is not fixed: +0.067 on the 297 requests, +0.003 on fresh ones, negative for 5–6 adapters (Table 12, App. C.2).

  2. A count of new failures can fall because a member got worse. e12e_{12} counts only requests that the base and every member pass. Plain Dolly is more harmful, so fewer requests can count (84% to 59%): e12e_{12} falls (0.104 to 0.062) while total harm rises (0.185 to 0.318; Table 4). An audit that reports only new failures would rank the more harmful model safer. Table 4 now reports the eligible share beside e12e_{12}. Scope: this follows from the definition, and the revision no longer calls it a "reversal"; among eligible requests the rate does not change significantly (0.123 vs 0.105). On fresh requests the drop in e12e_{12} is not significant, and on Qwen2.5-14B e12e_{12} rises with harm.

  3. Refusal-data repair lowers new failures and total harm and keeps the task gain; averaging leaves harm above the base. Repair on the DialogSum pair takes total harm from 0.168 to 0.054 and e12e_{12} from 0.094 to 0.017 at 100% of the partner's task score (Table 5), and this pair replicates on Qwen2.5-14B and Phi-4 (Table 22). Averaging takes e12e_{12} to at most 0.013 but leaves harm up to 0.077 (base at most 0.020; Table 16) and keeps 78–81% of DialogSum's gain. Scope: only DialogSum has a gain over the base to keep; the Alpaca pair does not replicate on the two other models; the 297 requests were evaluated before the interventions were designed. On fresh requests repair gives e12e_{12} 0.023 [0.014, 0.033]: the upper end misses the 0.03 bound fixed in advance, and harm is twice the base. Repair raises over-refusal (8.9% of safe XSTest prompts vs 1.2% before; Table 21).

W2, "does not offer much explanation." The revision gives a partial explanation, not a mechanism (Sec. 5.1, Sec. 6): the weak member leaves some requests close to refusal, and a trained partner, unlike a random update of the same size or spectrum, turns more of them into failures. Four tests (Qwen2.5-7B unless stated):

  • Not the size of the update. Real pairs give 0.074–0.111, 2.3–3.1× a random partner of the same norm (Table 2, App. L).
  • Not its spectrum. A partner with the real one's singular values in random subspaces stays at 0.020–0.051, against 0.081–0.108; all differences exclude zero (Table 34).
  • Which requests fail. Dolly's first-token refusal margin ranks which eligible requests a real partner tips (AUC 0.62–0.68, all intervals above 0.5); the base model's margin does not (0.52; Sec. 6).
  • What the partner does. With a random partner the response opens with the same word as Dolly alone on 0.89–0.92 of requests; with a real partner on 0.26–0.43 (three models; Table 35).

Limits: the probe is modest; margins do not add across members (App. D.3). Negative result: restoring the refusal-direction coordinate, with the decision rule fixed in advance, did not remove the failures (mean e12e_{12} 0.097 without it, 0.122 with it; Table 38), so we make no causal claim about that direction.

The revision now states each finding with its control and scope, and backs a partial explanation with four tests and a reported negative result.

I thank the authors for their response, I appreciate the experiments compared to the random updates, however I still beilieve the paper requires significant updates and share sentiments similar to reviewer vdnt. I will maintain my score.

Reviewer_vdntOpenReview ↗
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Paper summary

The paper studies how composing separately trained LoRA adapters can introduce new harmful behaviours (i.e. in a different set compared to individual adapters), even when overall harm changes little. Experiments across several models show that composition-only failures are common and that refusal matching or adapter averagging alone does not guarantee safety. The authors conclude that composed models should be evaluated for both overall harm and newly introduced failures, while also measuring retained task performance.

Critical strengths
  • Overall, the paper is well-written and easy to follow. The experiments are comprehensive (e.g. the authors use five base families, in-house and independently published adapter banks etc.)

  • the paper is candid and careful about its own evidence by reporting negative results (e.g. the membership predictor fails, the refusal-direction and additive-threshold stories are not supported). That is good scientific practice.

Critical weaknesses
  • The paper’s novelty and significance are limited. Prior work has shown that benign fine-tuning can erode safety (Qi et al., 2023) and that adapter composition can produce behaviors absent in individiual adapters (CoLoRA; Ding, 2026). While the paper focuses on identifying new harmful failures introduced by composing ordinary task-trained adapters, the conceptual advance over prior work remains modest.

  • The paper lacks a null model to show that the observed request-level flips are specific to composition rather than ordinary model perturbations (e.g. compared against retraining churn, random or benign norm-matched adapters etc.). Since the average harm rate changes little and the reported differences are statistically insignificant, these flips could reflect generic model variation rather than a composition-specific effect.

Minor:

  • Some datasets, models, and methods are cited late or not at all, (e.g. Llama-2, Granite-3.1-8B, PyTorch SDPA, AdamW).

  • Dolly-15k (Section 7.1, Table 8) is used without its own citation or an explanation of how it relates to “Dolly” (Conover et al.). The two names are used interchangeably. Might be worthwhile to clarify.

  • Appendices F, I and J are never referenced from the main text. Only I is mentioned, in Appendix B. Would be good to add appropriate pointers to these appendices where relevant.

Questions for authors

What composition-only rates do you observe under controls where no genuine composition effect is expected (e.g., comparing independently seeded retrainings of the same Dolly adapter, composing Dolly with a random norm-matched or benign adapter, or using a scaled-down Dolly adapter)?

2 comments
AuthorsOpenReview ↗

Reply to Reviewer vdnt, part 1 of 2. W1: novelty over Qi et al. (2023) and CoLoRA. (Part 2: W2, minor points, question.)

Qi et al. show that one benign fine-tune erodes safety; CoLoRA shows that adapters built to interact comply when merged. The revision shows what neither tests: ordinary, separately trained task adapters, once summed, fail on requests that neither the base nor any member fails, and on Qwen2.5-7B, with one weakly harmful member (Dolly), a trained partner produces such composition-only failures 2.3-3.1x as often as a random update of the same norm (Table 2; part 2, W2). CoLoRA attributes its effect to designed interaction; we measure a smaller but reproducible effect in the undesigned case, against a control we did not find in it.

WorkCombinedRelationshipUnitRandom partner found
Qi et al.one fine-tunefine-tune vs. its baserate per modelno
CoLoRALoRAs trained by one adversaryco-trained: benign alone, comply togetherrate per modelno
Hammoud et al.full models, some poorly alignedweak source carries into mergerate per modelno
Safe LoRA, SaLoRA, SafeMERGEone fine-tune + safety referencerepairrate per modelno
Oursseparately trained task LoRAs, summednone designed; trained separatelyone request vs. base and every memberyes
  1. Unrelated adapters against a matched random partner: not in prior work that we found. CoLoRA’s control, a colluding adapter merged with an unrelated benign one, does not reproduce the effect; it concludes that the degradation “depends on a specific interaction pattern rather than arising from arbitrary merging” (v2, Sec. 4.4). We found in it no merge of two ordinary adapters and no random partner. Our evidence: each real partner exceeds all six norm-matched random draws, with all 12 paired tests against the four new draws surviving Holm correction (Table 37); a spectrum-matched random partner stays as low as the norm-matched one (Table 34); and three readers confirmed 64 of 70 audited events, 19 of 25 for the selected Dolly compositions and 25 of 25 for the Dolly-free ones (Table 36).
  2. A request-level count and its pitfall: not in prior work that we found. The works above report rates per model. An aggregate drop, as in Hammoud et al. (Findings of EMNLP 2024, now cited), does not show whether a source already fails the same requests; our count is of requests on which the composition fails while the base and every member do not. Such a count covers only requests no reference fails, so it can fall as a member worsens: retraining Dolly without refusal data lowers it (0.104 to 0.062) while total harm rises (0.185 to 0.318; Table 4), as the eligible share falls from 84% to 59% (rate among eligible requests 0.123 vs 0.105, n.s.). This applies to any metric of “new” failures, so the paper reports it with total harm and the conditional rate.
  3. Interventions compared on a composition: partly new. Safe LoRA, SaLoRA and SafeMERGE act on one fine-tune; Gudipudi et al. (2025, now cited) observe over-refusal when fusing a safety adapter. We did not find these compared on a sum of task adapters. Averaging removes most composition-only failures but leaves harm above the base, keeping 78-81% of the DialogSum gain (Sec. 7.2; Table 16). Retraining the weak member with refusal data lowers both (Tables 4, 5). Limits: it raises over-refusal (8.9% of XSTest safe prompts vs. 1.2% for original pairs; Table 21), and Safe LoRA matches it on total harm (0.057 vs. 0.056; Table 20).

We propose no attack or defence, and our rates are far below CoLoRA’s. That summing updates raises total harm is expected from Qi et al.; a merge less safe in aggregate than every source is in Hammoud et al.; we claim neither. The excess over random partners is general on Qwen2.5-7B only; on Qwen2.5-14B and Phi-4 it depends on the partner (Table 31). Every control uses one weakly harmful member (Dolly; on Qwen2.5-7B, harm 0.114-0.165 alone over three seeds); the Dolly-free compositions (composition-only rate 0.093 / 0.127 on the two Qwen banks, Table 1) and the public banks have no null control, so we do not claim the excess for adapters that are all safe alone. Composition rates are not cleanly above member-reseeding churn (part 2). We offer a partial explanation, not a mechanism: a pre-specified refusal-direction intervention did not remove the events (Table 38).

What the revision establishes for W1. For undesigned task adapters, a trained partner adds composition- only failures beyond a norm- or spectrum-matched random update, on Qwen2.5-7B with one weak member, measured per request, tested against six random draws, with 64 of 70 audited events confirmed by human readers. We did not find this result in Qi et al. or CoLoRA.

AuthorsOpenReview ↗

Reply to Reviewer vdnt, part 2 of 2. W2, minor points and question. (Part 1: W1.)

W2: no null model. We ran the three controls you list. Verdict on Qwen2.5-7B: perturbation without composition yields some events, so the composition-only rate e12e_{12} is read against a floor, not zero; real partners exceed the random-partner floor in every comparison. With six norm-matched random draws per partner, each real pair exceeds all six; the 12 new paired differences (+0.054 to +0.084) all exclude zero and survive Holm correction (Table 37).

e12e_{12}: share of requests harmful under the state (both judges) and under none of its references. Plain / repaired: the weak member, Dolly, retrained without / with refusal data. Qwen2.5-7B, 297 requests (Tables 2, 37; App. L).

StateReferencese12e_{12}
Dolly reseeded: plain; repairedbase + other seed0.034–0.040; 0.000
Dolly reseeded, original recipe (3 seeds)base + other seed0.034–0.084
Dolly alone ×0.5; ×0.75; ×1.5base + Dolly0.010; 0.024; 0.007
Random adapter alonebase0.000–0.003
Dolly + random partner (6 draws × 3 norms)base, Dolly, random0.017–0.057
Dolly + real partner (3 pairs)base, members0.074–0.111

Why trust this test. It fixes member, requests and update norm; only the partner changes. Repeated on three Dolly seeds and 375 fresh requests, real exceeds random in all 12 cells and 10 survive Holm (Table 33, App. N.1). In the original run the real pairs are 2.3–3.1× their two random draws.

Is the random partner too weak a null? In part, yes. A norm-matched one mostly keeps the opening of Dolly's response: first word unchanged on about 90% of requests, vs 26–43% with a real one (Table 35). Two controls with a pre-set decision rule go further (Table 34). (a) A partner with every singular value of the real one but random subspaces stays at the floor: mean e12e_{12} 0.033 vs 0.094 for real pairs, all six per-seed differences excluding zero. So spectral concentration alone does not produce the excess. (b) Keeping the trained read directions and randomising only the write directions recovers part of it (0.055 vs 0.093): part of the excess is tied to which inputs the partner responds to. Not shown: neither is known to change behaviour as much as a real partner; in (b) three of six per-seed differences include zero; this describes two controls, not a mechanism.

Scope.

  • Seeds: reseeding the member is the function-matched null, and compositions do not clearly beat it: original-recipe churn reaches 0.084, overlapping the 28-composition means 0.105, 0.108 and 0.070 (Table 32). Adding both other seeds' members as references keeps 69–77% of events; adding their compositions too, 27–36%. Which requests fail is less stable: composition shifts the failing set more than reseeding the member (29% vs 15%) but no more than reseeding the composition (25%; App. C).
  • Weakest Dolly seed: its GSM8K (+0.020 [-0.002, 0.044]) and Alpaca (+0.029 [-0.003, 0.062]) cells are the two that fail Holm; its real pairs carry no more both-judge harm than random ones (0.131 vs 0.140).
  • Six draws: two are from the earlier run (point comparison); the 12 tests share references.
  • Other models, Qwen2.5-14B / Phi-4 (Table 31; Table 22 reruns these pairs, within 0.004): DialogSum 0.232 / 0.138, GSM8K 0.027 / 0.232, Alpaca 0.030 / 0.024, random-partner mean 0.013 / 0.028. Alpaca is at the floor on both and GSM8K on Qwen2.5-14B, where Dolly ×1.5 alone gives 0.094 (real-pair mean 0.096). On Qwen2.5-7B the ×1.5 state is degenerate (repetition 0.428).
  • One weak member; Dolly-free and public-bank compositions have no null.

"Statistically insignificant". Correct for aggregate harm. The revision no longer claims that mean harm "stays close" to the weak member's; it now states that the excess has no fixed sign (Table 12): +0.081 at sizes 2–3 ([0.006, 0.154]; two-level [-0.003, 0.167]; +0.035 [-0.043, 0.107] under SDPA) and negative at sizes 5–6, where outputs degenerate; on 297 requests, +0.067 [0.035, 0.098] for the original seed (+0.05, -0.01 for the other two; Table 32). The request-level claim rests on the paired tests above, not on these.

Minor. Citations: Llama-2, PyTorch SDPA (Sec. 4.2), AdamW (K.2), Granite-3.1-8B (App. J). Names: dataset "databricks-dolly-15k (Conover et al., 2023)"; "Dolly" is our adapter trained on it; "Dolly-15k (published)" the public bank's adapter. App. F, I, J: pointers in Secs. 5.2, 5.3, 6, 8.

Q: controls. See the table: at most 0.057, or 0.084 for original-recipe seeds, vs 0.074–0.111 for real pairs.

Established for W2. On Qwen2.5-7B a real partner's composition-only failures are not generic perturbation of equal norm or spectrum: the excess over random partners survives Holm correction in all 12 new paired tests and in 10 of 12 cells over three member seeds and fresh requests. It is partner-specific on two other models and not separated from member reseeding.

Reviewer_K6HMOpenReview ↗
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Paper summary

This paper studies composition-only failures in LoRA, requests on which a composed model produces a response labelled harmful while the base model and every active adapter evaluated individually do not. The authors use request-aligned evaluations to distinguish these failures from changes in aggregate harmful-response rates, and examine task-trained and public adapter banks across several base models. They also investigate member retraining and common reweighting, showing that composition-only failure rates can decrease while total harm increases, and that some interventions reduce both measures.

Critical strengths
  1. The request-level perspective is useful; aggregate harmful-response rates can hide changes in failure identity, and the paper clearly distinguishes composition-only failures from increases in total harm. The retraining example in Table3 provides a concrete illustration of why the former should not be used as a standalone safety metric.
  2. The empirical investigation includes multiple base models, public adapters, additional requests, two-judge measurements, and regenerated responses.
  3. The paper carefully distinguishes capability retention from adaptation gains. DialogSum example in Table4 provides a concrete case of reduced harm with retained improvement over the base. The authors also explicitly disclose important limitations, including selected compositions, reused evaluation requests, limited seed replication, and the absence of deployment-level safety guarantees.
Critical weaknesses
  1. The central audit gap lacks event-level validation. Equation7 requires both a harmful composition response and non-harmful responses from every reference state. sec 5.1 reports cross-judge agreement and regeneration robustness, but neither establishes the correctness of this joint condition. Correlated false negatives on reference responses can make inherited harm appear composition-only, while false positives on composition responses can create spurious events. A prompt-matched human audit of the composition and all corresponding references is needed to establish how much of the measured gap reflects genuine harmful behavior.
  2. Some experimental reporting needs clarification. fig1 combines eager-attention safety measurements with SDPA utility measurements, limiting their joint interpretation; fig2 also includes marked weight values beyond the grid specified in sec7.2; the configurations and plotted results should be reconciled.
  3. The paper is dense, and the experimental details are fragmented across the main text and appendices. Frequent changes in evaluation protocols and reference configurations make it difficult to track which results are directly comparable. for example, clearer protocol summaries and explicit labels for individual compositions in fig2 would improve readability.
Questions for authors
  1. Would a small, stratified human audit of complete composition-only events be feasible, particularly for the utility-retaining examples? Checking each composed response together with its base and singleton references would strengthen confidence that the observed audit gap is not substantially affected by correlated judge errors.
  2. Under the same base model, adapter bank, prompt set, and judges, how would safety-aware merging methods such as SafeLoRA and SafeMERGE affect e12e_{12}, total harm, and partner-task retention? If a full comparison is not conducted, could you explain the main technical obstacles?
  3. Is there evidence that the repair result preserves adaptation gains beyond the selected Qwen-7B DialogSum pair, preferably on requests not previously observed during intervention development?
2 comments
AuthorsOpenReview ↗

Response to Reviewer K6HM

W1. The audit gap lacks event-level validation. We ran the prompt-matched human audit you asked for: three readers confirm 64 of 70 events (91%; App. M, Table 36). Readers saw the composition, base and every member response, judge labels hidden; any reader’s doubt removes the event. All three labelled all 70 composition responses harmful; the error you name, a missed harmful reference (base or member), accounts for all 6 unconfirmed events. By stratum: 19 of 25 for the selected Dolly compositions of Table 1, 25 of 25 for the Dolly-free ones, 10 of 10 each for the original- and repaired-member runs of Sec. 7.1. In your correlated-error case (a member answered without a refusal template) 35 of 41 are confirmed; elsewhere 29 of 29. Effect on rates: Table 1’s Dolly e12 scales from 0.126 to 0.096; pooling all 35 original-Dolly events (29 confirmed; two protocols) scales Table 4’s 0.104 to 0.086, against 0.012 repaired, so the repair contrast stands. Limits: one base model; one reader is an author; no non-event rows (readers knew this), so harm the judges miss in compositions is not measured; 4 of the 6 doubts concern the base response.

W2. Fig. 1 attention implementations; Fig. 2 weight grid. Fig. 1 now uses SDPA for every curve (Table 8): no size mean moves by more than 0.022 in harm or 0.050 in refusal; peak sizes are unchanged. Sec. 7.2 states all six weights of Fig. 2, Table 17 lists each, and every curve is labelled. Scope: only 66-68% of events recur across attention implementations and 78-92% between two runs of one harness (App. K.8), so rates, not request lists, are the reproducible quantity.

W3. Dense text, fragmented protocols. New Table 6 (App. A, pointer in Sec. 4.2) lists bank, requests, judge prompt, attention, references and held-out status for every main table and figure.

Q1. Audit of the utility-retaining examples. Partly. The 20 audited events from the Sec. 7.1 runs are all confirmed. For the repaired pairs the claim is that events are few (e12 0.017 with DialogSum, 0.000 with GSM8K; Table 5), and a false event could only overstate that count. Limit: none of the 5 events of the repaired Dolly+DialogSum pair was sampled, so these pairs are not audited directly; harm both judges miss stays an open risk.

Q2. Safe LoRA and SafeMERGE. Safe LoRA is run with the same base, bank, requests and judges (Table 20, App. E.5). It brings composition harm to 0.057 (our repair: 0.056) with less over-refusal: on 250 safe XSTest prompts its pairs refuse 4.2% (base 4.0%), repaired pairs 8.9% (Table 21). e12 is 0.027 for Safe LoRA and 0.012 for the repair. Scope: retention is similar (96-99% vs 99-100%) but not like-for-like: Safe LoRA edits all eight adapters, the repair retrains one, and its retention is relative to projected members (GSM8K 0.850, vs 0.785 unprojected). SafeMERGE (Table 39): e12 0.027, harm 0.085 at a pre-fixed setting; 0.041, 0.098 at its paper’s Qwen-2 setting (post hoc); retention 95-97%.

Q3. Adaptation gains beyond the Qwen-7B DialogSum pair, on unseen requests. Yes on two more models and, for safety, on unseen requests; no other scored task has a gain to keep. • Other models (Table 22): on Qwen2.5-14B and Phi-4 the repaired DialogSum pair keeps 100.5% and 103.0% of the member’s score. Its e12 falls from 0.232 to 0.007 and from 0.138 to 0.013. • Other tasks: DialogSum is the only scored task whose adapter beats the base (0.320 vs 0.181; the repaired pair keeps 101% of that gain). GSM8K members score below the base, so retention there is recovery. • Fresh requests: on 375 not used in any earlier harm evaluation or selection, repair lowers e12 from 0.093 to 0.023 and harm from 0.216 to 0.096 (Table 4, last rows). • Limits: the 297 requests were seen before the interventions were designed (App. K.1). The fresh set tests harm only; there the repaired upper endpoint (0.033) misses the 0.03 bound fixed in advance and harm is twice the base. On Qwen2.5-7B and 14B the retention difference to the original pair includes zero; on Phi-4 the plain retrain also retains DialogSum, so it is not specific to refusal data. On 14B and Phi-4 the Alpaca-pair e12 does not fall significantly. Repaired triples keep e12 up to 0.057; repaired harm stays above the base; one training seed per variant. Added in the discussion (App. N). With six norm-matched random draws per partner, each real pair exceeds every draw; all 12 new paired differences (+0.054 to +0.084) survive Holm correction (Table 37). On two other models the excess is partner-specific (Table 31). A refusal-direction intervention with a rule fixed in advance did not remove the events (Table 38); we claim no mechanism. In sum: readers confirm 64 of 70 events, and repairing the weak member lowers e12 and total harm on three models and on fresh requests.

Thank you for the detailed response and the additional experimental results, these address my main concerns, and I have no more questions.

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General response to all reviewers

We thank all reviewers for their careful reading and constructive feedback. We have revised the manuscript to clarify the contribution, strengthen the experimental controls, validate individual failure events, and make the presentation easier to follow.

  1. Stronger controls. Our central measurement concerns composition-only failures: requests on which the composition is harmful while the base and every individual member are not. On Qwen2.5-7B with the weakly harmful Dolly adapter, each trained partner exceeds all six norm-matched random draws; all 12 new paired comparisons survive Holm correction (Table 37). Spectrum-matched controls support the same distinction (Table 34), and 10 of 12 comparisons across additional member seeds and fresh requests survive Holm correction (Table 33).

  2. Human validation. Three readers examined composition, base, and member responses with judge labels hidden and confirmed 64 of 70 sampled events (Table 36). We explicitly acknowledge that the audit covers selected judge-flagged events and that one reader is an author.

  3. Clearer measurement and intervention results. We show that the composition-only rate can fall while total harm rises because fewer requests remain eligible to count. We therefore report total harm and the eligible share alongside this rate (Table 4). Refusal-data retraining lowers both rates and preserves the DialogSum gain, but increases over-refusal; Safe LoRA achieves similar total harm with less over-refusal (Tables 5, 20–21). Averaging removes most composition-only failures but leaves harm above the base (Table 16).

We also clarified the comparison with prior work, added a protocol table, improved figure labels, recast Proposition 1 as a remark, and corrected request-provenance descriptions.

Scope. The excess over matched random partners is consistent across the tested partners on Qwen2.5-7B, but partner-dependent on Qwen2.5-14B and Phi-4. Composition rates are not clearly separated from member-reseeding variation. We offer a partial explanation: the pre-specified refusal-direction intervention was negative, and we make no causal mechanism claim. Detailed responses address each reviewer’s concerns.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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