- Rating
- 3(+1)
- Confidence
- 3
- Informativeness
- 3
- Presentation
- 2
- Soundness
- 2
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Paper summary
This paper focuses on defending against backdoors in LoRA adapters for large language models. The authors first find that different backdoors can affect models in different ways. They divide backdoors into two types: INSERT and DIVERT. Based on this idea, the authors propose a defense method called TRIAGE. The main idea is to first train some surrogate backdoors using triggers designed by the defender. The method then compares the LoRA weight features of these surrogate backdoors with those of the suspicious adapter. This helps determine whether the suspicious backdoor is closer to INSERT or DIVERT. For INSERT, the method mainly blocks the backdoor by changing specific directions in the model's hidden layers. For DIVERT, the method mainly reduces the adapter weights, restores normal abilities, and transfers the correction effects learned from the surrogate backdoors. When the match is not strong enough, the method uses a simpler weight decay strategy. The whole defense process does not require knowing the actual trigger of the backdoor. The authors evaluate TRIAGE on three attack goals: Jailbreak, Negative Sentiment, and Targeted Refusal. According to the paper, TRIAGE correctly classifies all tested adapters and reduces the average attack success rates for the three attack goals from 81.6%, 85.2%, and 75.2% to 0.2%, 0.4%, and 0.6%, respectively.
Critical strengths
- Backdoors in third-party LoRA adapters are a real and important supply chain risk. TRIAGE achieves strong defense results on the selected benchmarks without needing to know the triggers used by attackers in advance. These improvements give the method clear practical value.
- The authors connect the changes in hidden states caused by real backdoors with their alignment to the model's original refusal direction and routing in the weight subspace. They also try to use different repair strategies based on the underlying backdoor mechanisms. This work provides a testable framework for mechanism-based backdoor repair.
Critical weaknesses
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The key evidence for Backdoor Nexus does not fully separate the effects of shared training data, trigger positions, and model conditions. Figure 2(b) reports an average cosine similarity of around 0.78 across five real Jailbreak adapters. However, the authors' public training code shows that BadNet, Sleeper, VPI, MTBA, and CTBA share the same 400 poisoned target responses and 400 clean training samples. Their LoRA training settings are also very similar. In addition, train_surrogate.py directly reuses the BadNet poisoning file and only replaces BadMagic with a custom trigger. As a result, the shared attack goal, target responses, and backdoor training setup are not separated from the shared representations across different triggers. It is therefore unclear how much of the observed directional similarity comes from a general backdoor mechanism. The trigger positions in the code are also unevenly distributed. Among the first 99 test samples, BadNet places the trigger at the beginning in 12 samples and in the middle in 87 samples. Sleeper and VPI both place the trigger at the beginning in all 99 samples. The paper does not report systematic experiments grouped by trigger position or experiments that retrain the models with different trigger positions. In addition, the reported cosine similarity of 0.78 is mainly measured on Llama-2-7B. Experiments on other models mostly focus on repair performance. Finding 1 is not further tested on other non-Llama models. The current evidence supports shared representations within the tested benchmarks, but it is not enough to support stronger claims about how well this mechanism generalizes across independently designed attacks, different trigger placement strategies, and model families.
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The causal evidence for INSERT and DIVERT and the independent benefits of mechanism-based routing are still limited. The INSERT route mainly uses Jailbreak surrogates as references, while the DIVERT route mainly uses Targeted Refusal surrogates. The paper lacks controlled experiments that apply the same type of directional intervention to both backdoor types while measuring the model's ability to correctly refuse harmful requests and follow harmless instructions. It also lacks direct comparisons with incorrect routing, uniform weight decay, and a version without the router. In particular, Table 4 shows that weight decay alone reduces the average ASR for Targeted Refusal from 77.27% to 3.28%, while the full method further reduces it to 0.76%. Therefore, the added benefits of the more complex mechanism-based branches and their costs to normal model abilities still need more careful evaluation. Finally, when using only the residual stream of the last prompt token, the authors should also rule out the effects of token identity, token position, and sequence length on the estimated directions.
Questions for authors
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With Jailbreak as the attack goal, could the authors retrain the real victim adapters using poisoning requests that do not overlap with Backdoored LLM, independently generated target responses, and different random seeds, while keeping the existing surrogates and hyperparameters unchanged? Please vary the training data, target responses, and backdoor training setup separately. For each setting, report the directional similarity using the same method as Figure 2(b), Surrogate–Victim alignment, router results, post-repair ASR, and normal model utility. This would help determine whether the claimed "shared mechanism" can be separated from shared training supervision.
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Please report the distribution of trigger positions (prefix, middle, and suffix) in the training and test inputs for both real attacks and surrogates. Please evaluate two settings: changing the trigger position at inference time while keeping the adapter fixed, and separately training Prefix, Infix, Suffix, and Random-Position adapters. For each setting, report the ASR before and after defense, along with the cosine similarity of activation directions, grouped by trigger position. Defense effectiveness should only be compared at positions where the attack can successfully trigger before defense. Could the authors also compare the estimated directions and causal intervention results using the Last Prompt Token, a shared end anchor, and Token Pooling? This would help rule out the effects of measurement position.
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The authors have already reported defense ASR on Mistral-7B. Could they also repeat the cross-trigger activation direction matrix and direction ablation experiments from Finding 1 on at least Mistral and another non-Llama model, rather than only reporting the final defense performance?
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Please provide the original input pair indices for Figure 2(b), the model weights or cached activations, and a calculation script that exactly matches Equation (17) in Appendix D. The paper uses 60 input pairs per adapter and calculates cosine similarity after concatenating the raw mean activation shifts from layers 24–30. However, the public code in surrogate_test.py uses only 12 pairs and averages the absolute cosine similarities across layers 16–30 after normalizing each layer to unit length. These two methods do not measure the same statistic and should not be treated as equivalent. Please also clarify whether overlap between the training data of real victims and surrogates is considered allowed prior knowledge. In addition, please confirm whether the prompts used for direction estimation, recovery training, and final testing are independent of each other.