acceptodds
Under review as a conference paper at ICLR 2027

Beyond a Single Attack: Generalizable Backdoor Detection via Single-Attack Meta-Classification

Abstract

Backdoor attacks pose a serious security threat to deep neural networks, motivating model-level detection methods that identify whether a target model contains a hidden backdoor before deployment. Meta-classifier-based approaches are particularly attractive because they learn reusable detectors from model-level representations extracted from benign and backdoored reference models. However, we find that existing representations generalize poorly across heterogeneous attacks. Under cross-attack evaluation on CIFAR-10 with ResNet-18, the existing work MNTD and WeightMM achieve average AUCs of only \(0.479\) and \(0.729\), respectively. Our analysis suggests that these representations tend to capture attack-specific characteristics rather than model changes shared across different backdoor attacks. To address this limitation, we propose a novel model-level backdoor detection method by leveraging class-wise decision-space probing. Our key insight is that although backdoor attacks may differ substantially in their triggers and injection mechanisms, a successful attack must ultimately alter the model's decision behavior. We therefore isolate the final classifier and, for each output class, optimize a classifier-input representation that maximizes the corresponding class response. The resulting class-wise representations are aggregated into a model-level representation for meta-classifier training. We evaluate our method under a strict cross-attack protocol covering six dataset–architecture configurations and 12 representative backdoor attacks. Across the evaluated settings, our method achieves an average cross-attack AUC of 0.966, with the best performance reaching 0.998.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
backdoor detection, meta-classifier, generalization

Reviews

Among:
Shape:
1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_hoYAOpenReview ↗
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Paper summary

This paper proposes a model-level backdoor detection method that aims to generalize across unseen backdoor attacks. The key motivation is that existing meta-classifier-based methods often capture attack-specific features, leading to poor cross-attack generalization. To address this, the authors propose class-wise decision-space probing, which extracts representations from the final classification layer by optimizing a feature vector for each class. These representations are then fed into a meta-classifier to distinguish clean and backdoored models. Experiments across 12 backdoor attacks demonstrate strong cross-attack generalization, achieving an average AUC of 0.966. However, the method relies heavily on the final classification layer and can be bypassed by adaptive attacks that leave this layer unchanged.

Critical strengths
  • Addresses the important problem of cross-attack generalization in backdoor detection.

  • A simple and effective method with strong experimental results across 12 attacks and multiple architectures.

  • Includes useful ablation studies and adaptive attack evaluations.

Critical weaknesses
  • Insufficient explanation of why the proposed representation improves cross-attack generalization.

  • Important experimental details, such as the number of training and testing models in Table 1, are unclear.

  • Vulnerable to adaptive attacks that freeze the final classification layer.

Questions for authors

Thank you for submitting the interesting work to ICLR 2027. I still have a few concerns.

  1. Limited utilization of backdoor-related information. Prior studies have shown that backdoor-related behaviors can be encoded in feature extraction layers, and techniques such as convolutional layer pruning can effectively mitigate backdoors. However, this paper focuses only on the final classification layer, potentially discarding substantial backdoor-related information from earlier layers. It is unclear whether the improved efficiency justifies this information loss. The authors should provide stronger motivation for this design choice and investigate whether incorporating features from earlier layers could further improve detection robustness.

  2. Limited experimental evaluation. The experimental evaluation is not sufficiently comprehensive. Although multiple architectures are considered, the experiments are mainly restricted to relatively small CNN-based image classifiers. Evaluations on more diverse and modern architectures, such as Vision Transformers, would strengthen the paper's claims about generalizability.

  3. Insufficient experimental details. Several important experimental settings are unclear, particularly the number of clean and backdoored models used for training and testing in Table 1, as well as how these models are split. These details are essential for assessing the reliability and reproducibility of the reported results.

4 comments

We thank you for your careful review and for recognizing the importance of cross-attack detection, the effectiveness of our method, and the useful ablation studies. In response to your comments, we have clarified the probing scope and the default choice of the final classifier, added a ViT-B/16 evaluation, and specified the model counts and training/evaluation splits. We hope these additions address your concerns and respectfully ask you to consider raising your score in light of the new evidence.

Q1:\textcolor{blue}{\text{Q1:}} Incorporating earlier-layer information and motivating the default probing location.

Thank you for highlighting the importance of backdoor-related information in earlier layers. We have clarified that our framework supports probing a continuous classification subnetwork extending from a selected intermediate location to the output. All parameters within this subnetwork remain fixed, while its input features are optimized separately for each class. Choosing an earlier probing location changes the subnetwork and its input shape, while retaining the same class-wise optimization and representation construction procedure.

The final classifier is our default based on the layer-wise comparison of detection performance and computational cost. On CIFAR-10/ResNet-18, using a common budget of 1,000 steps per class, FC-only probing achieves an AUC of 0.9640.964 in 8.568.56 seconds. Including the last residual block improves AUC to 0.9830.983 but increases the cost to 31.0331.03 seconds. These results show that incorporating earlier-layer information can improve detection, while extending the probing scope increases computational cost. We therefore recommend the final classifier as the default choice balancing effectiveness and efficiency, while retaining the flexibility to probe from earlier intermediate locations.

The frozen-suffix experiment directly investigates whether earlier-layer information improves robustness. When the attacker freezes only FC, the backdoored models retain an ASR of 93.8393.83\\%, while FC-only detection yields an AUC of 0.2660.266. Extending probing to B4.2 and B4.1 raises AUC to 0.7440.744 and 1.0001.000, respectively.

These results establish an experimentally supported choice: FC-only probing provides an efficient default for the standard cross-attack setting, while the same framework can incorporate earlier-layer information to improve detection against attacks that deliberately preserve the final classifier. We have clarified this flexibility and the associated computational trade-off in the revised manuscript.

Q2:\textcolor{blue}{\text{Q2:}} Evaluation beyond CNN architectures.

Following your suggestion, we added an evaluation on ViT-B/16 with CIFAR-10, reported in Appendix C.4. We use a pretrained ViT-B/16 with a ten-class classification head and fine-tune 20 clean models and 20 BadNets models. The backdoored models use a 1010\\% poisoning ratio and cover all ten target classes with two random seeds per target class.

We apply the same class-wise probing procedure to the final linear head. Its input dimension is 768, producing a 10×76810\times768 representation. Probing uses the same all-ones initialization and 20,000 Adam steps per class, and detection uses the same 1D-CNN meta-classifier design and training procedure.

We sample six clean and six backdoored models without replacement for detector training. Evaluation uses only the remaining 14 clean and 14 backdoored models, with no overlap between detector training and evaluation. The detector achieves an AUC of 1.0001.000 on these held-out models.

This experiment demonstrates that the probing procedure and meta-classifier design also support effective backdoor detection on a pretrained transformer architecture, extending the architectural evidence beyond the CNN-based configurations in the main evaluation.

Q3:\textcolor{blue}{\text{Q3:}} Model counts and training/evaluation splits.

We have expanded the experimental details to specify the model pools and detector-training protocol. For each ten-class configuration, the standard pool contains 256 clean models and 1,830 backdoored models. Each of the twelve attacks contributes 100 class-agnostic models. BadNets, Blended, BPP, Filter, LF, Refool, and SSBA additionally contribute 90 class-specific models each, giving 1,200 class-agnostic and 630 class-specific backdoored models.

For the full GTSRB configuration, the pool contains 256 clean models and 3,240 backdoored models: 172 class-agnostic models per attack and 168 class-specific models for each of the seven applicable attacks. For CIFAR-100, the pool contains 100 clean models and 943 backdoored models: 50 class-agnostic models per attack and 49 class-specific models for each of those seven attacks. Across the six main configurations, this gives 1,380 clean and 11,503 backdoored models, totaling 12,883 models.

All compared methods use the same sampling procedure, with a sampling ratio of 0.30.3 and sampling without replacement. For source attacks containing both backdoor subtypes, we sample from each subtype a number equal to 3030\\% of the smaller subtype pool, rounded down, and construct the detector-training set with a clean:class-agnostic:class-specific ratio of 2:1:12:1:1. For attacks containing only one subtype, we sample 3030\\% of that pool and an equal number of clean models. For example, on CIFAR-10/ResNet-18, a BadNets detector uses 54 clean, 27 class-agnostic, and 27 class-specific models, totaling 108 training models. An LC detector uses 30 clean and 30 backdoored models, totaling 60.

All models used for detector training are excluded from evaluation. Source-attack evaluation uses the remaining clean and source-attack models. Cross-attack evaluation uses the same held-out clean models and all models from the corresponding non-source attack, without further subsampling or balancing.

The model-generation settings and sampling protocol are detailed in Appendix B.1 and B.2.

Hi,

Thanks for your detailed rebuttal. I tend to keep my current rating.

Dear reviewer, Do you have any remaining concerns that we can address? We’d be happy to continue the discussion.

Reviewer_hqcmOpenReview ↗
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Paper summary

This paper proposes a model-level backdoor detection framework that aims to generalize from a single known attack to previously unseen backdoor attacks. The authors argue that existing meta-classifier-based detection methods tend to capture attack-specific characteristics, resulting in poor cross-attack generalization. To address this limitation, the paper introduces class-wise decision-space probing, which extracts the final linear classifier from a target model and independently optimizes a feature representation for each output class. These class-wise representations are then aggregated and used to train a binary meta-classifier for backdoor detection.

Critical strengths
  • Important research problem and practical significance. The paper addresses a meaningful challenge in model-level backdoor detection: generalizing from known attacks to previously unseen attack types.

  • Interesting methodological perspective. The proposed class-wise decision-space probing provides an interesting alternative to existing query-response-based and parameter-based model representations.

  • Strong and comprehensive experimental results. The authors evaluate the proposed method across twelve representative backdoor attacks and six dataset–architecture configurations.

Critical weaknesses
  • The fundamental assumption underlying generalizable backdoor detection is insufficiently justified.

The central claim of this paper is that class-wise decision-space probing can capture generalizable backdoor characteristics shared across heterogeneous attacks. However, the underlying assumption is not sufficiently established. While successful backdoor attacks must alter the overall decision behavior of a model, such changes do not necessarily manifest in its final linear classifier. A backdoor can potentially be implanted entirely within the feature extractor while preserving the original classifier. In fact, the adaptive attack evaluated in Section 5.5 and Appendix E demonstrates this limitation: when the final classifier is frozen, the attacker can still achieve an attack success rate of 93.83%, while the proposed final-layer detector achieves an AUC of only 0.266. Although the authors show that expanding the probing range can recover detection performance, this requires modifying the default probing strategy and introduces additional computational overhead. Therefore, the strong cross-attack results on the evaluated benchmarks do not necessarily establish that the proposed representation captures characteristics that generalize to fundamentally different backdoor implementations.

  • The unique contribution of the proposed decision-space probing mechanism requires further investigation.

The proposed method optimizes class-wise feature vectors using only the final linear classifier while keeping its parameters fixed. Consequently, the resulting representation is entirely determined by the final-layer parameters and the predefined optimization procedure. Although the authors describe this as characterizing decision-space behavior, it remains unclear what additional backdoor-relevant information is captured beyond a transformation of the original classifier parameters. Interestingly, Table 2 shows that directly using the final-layer weights already achieves strong average cross-attack AUCs of 0.973 and 0.977, compared with 0.992 for the proposed representation. I acknowledge that the proposed method substantially improves the worst-case cross-attack performance, which is a meaningful advantage. However, the paper does not sufficiently explain why this optimization procedure produces more transferable representations.

  • The experimental evaluation does not sufficiently rule out training-specific artifacts as an explanation for the observed generalization.

Although the paper evaluates twelve different backdoor attacks, the experiments are conducted within relatively controlled model generation settings. As described in Appendix B.1, target models are primarily generated using the same BackdoorBench framework, with relatively consistent training configurations and poisoning ratios. Furthermore, the cross-attack evaluation keeps the dataset and model architecture fixed, with separate meta-classifiers trained for different dataset–architecture configurations. Therefore, it remains unclear whether the learned representation captures generalizable backdoor characteristics or statistical patterns shared by the particular model training and attack generation procedures. This distinction is particularly important because the proposed representation depends directly on the final-layer parameters, which may also be influenced by benign variations in training configurations. Evaluations involving different training procedures, optimizers, fine-tuning strategies, or independently generated model checkpoints would help establish whether the observed generalization extends beyond the controlled benchmark settings. Such experiments would provide stronger evidence for the broader generalizability claims.

Questions for authors
  1. How do the authors justify the generalizability of final-layer decision-space probing given that the adaptive attack in Section 5.5 successfully implants a backdoor without modifying the final classifier?

  2. What makes the proposed class-wise optimization more effective than simpler transformations or statistical representations of the final-layer parameters?

  3. How robust is the proposed detector when benign and backdoored models are generated using different training configurations, optimizers, or fine-tuning strategies?

2 comments

We thank you for your careful review and for recognizing the importance of our research problem, our methodological perspective, and the comprehensiveness of the evaluation. In response to your comments, we have clarified the probing scope and the rationale for using the final classifier as the default, added mechanistic and geometric analyses of the representation, and evaluated generalization across training optimizers. We hope these additions address your concerns and respectfully ask you to consider raising your score in light of the new experimental evidence.

Q1:\textcolor{blue}{\text{Q1:}} Generalizability when the final classifier is preserved.

Thank you for raising the question about the relationship between probing location and generalizability. We have clarified in the revised manuscript that our method probes a continuous classification subnetwork extending from a selected intermediate location to the model output. All parameters of this subnetwork remain fixed, and only its input features are optimized for each class. The same class-wise optimization and representation construction procedure applies across different probing locations.

Our layer-wise ablation examines how probing location affects detection performance and computational cost. With a fixed budget of 1,000 steps per class, probing only the final fully connected layer (FC-only) achieves an AUC of 0.9640.964 in 8.568.56 seconds. Extending the probed subnetwork to include the last residual block increases AUC to 0.9830.983, but also increases runtime to 31.0331.03 seconds. These results show that incorporating earlier-layer information can improve detection, while extending the probing scope increases computational cost. We therefore recommend the final classifier as the default choice balancing effectiveness and efficiency, while retaining the flexibility to probe from earlier intermediate locations.

When the attacker preserves the final classifier, FC-only probing cannot capture backdoor modifications confined to earlier layers. However, the same probing procedure can recover detection performance by extending the probed subnetwork to include those modifications. When the attacker freezes only FC, extending the defender's probing location from FC to B4.2 and B4.1 increases AUC **from 0.2660.266 to 0.7440.744 and 1.0001.000, respectively.

Taken together, the experiments covering twelve attacks support the effectiveness of FC-only probing under the standard cross-attack evaluation, while the frozen-suffix experiments demonstrate the potential of the same framework to recover detection by incorporating earlier-layer information. We have clarified the distinction between the default configuration and the extensible probing scope, together with the associated computational trade-off.

Q2:\textcolor{blue}{\text{Q2:}} Why does class-wise probing improve upon direct parameter representations?

Thank you for recognizing the improvement in worst-case cross-attack performance. To explain this advantage, we have added analyses of the probing mechanism and representation geometry. Under FC-only probing, the representation is determined by the weights and biases (W,b)(W,b) and the fixed optimization procedure. Its core value lies in using class-relative responses to organize existing parameter information into a representation that better supports cross-attack generalization.

For target class kk, the probing gradient is ∇zL(z;k)=∑j≠kpj(z)(wj−wk).\nabla_z \mathcal{L}(z;k) = \sum_{j\ne k}p_j(z)(w_j-w_k).

Each update therefore combines weight differences between the target class and its competitors, weighted by class probabilities that evolve along the optimization trajectory. This procedure characterizes class competition and is invariant to parameter components that add the same shift to every class logit.

In the controlled comparison, all three representations use exactly the same meta-classifier, data splits, normalization procedure, and training protocol. Although vec⁡(W)\operatorname{vec}(W) and vec⁡(W,b)\operatorname{vec}(W,b) achieve average cross-attack AUCs of 0.9730.973 and 0.9770.977, their minimum cross-attack AUCs fall to 0.1680.168 and 0.2490.249, respectively. In contrast, class-wise probing achieves an average cross-attack AUC of 0.9920.992 and a minimum of 0.9170.917, demonstrating more stable transfer across attack pairs.

We further analyze Input-Aware, the source attack with the weakest transfer under direct parameter representations. After normalization by the coordinate-wise variability of clean-model representations, probing increases the distance between the Input-Aware and clean-model centroids from 0.3020.302 to 1.0771.077. The mean cosine similarity between its clean-referenced centroid shift and the corresponding shifts of other attacks increases from 0.3490.349 to 0.7210.721. In the 50-dimensional PCA space, the silhouette score between Input-Aware and clean models also increases from 0.1260.126 to 0.6280.628.

These observations provide an empirical explanation for the improved transfer: probing makes the Input-Aware-induced deviation more distinguishable from benign variation, while aligning its direction more closely with deviations induced by other attacks. These analyses have been added to the representation comparison in Section 5.4 and the mechanistic analysis in Appendix D.2.

Q3:\textcolor{blue}{\text{Q3:}} Robustness to changes in model-training configurations.

Following your suggestion, we added a cross-optimizer evaluation on CIFAR-10 with ResNet-18. We trained an additional set of clean and BadNets models using SGD, whereas the reference models used for detector training were trained using Adam. The additional evaluation set contains 50 clean models and 50 BadNets models, with the latter covering all ten target classes using five random seeds per target class. The poisoning ratio is 1010\\%, and the remaining model-training settings are unchanged.

We directly apply the twelve detectors trained on the original Adam-generated reference models to the new evaluation set. Both clean and backdoored evaluation models are trained using SGD, so the optimizer choice itself does not distinguish the two evaluation labels.

As reported in Appendix C.3, eleven detectors achieve an AUC of 1.0001.000, and the LC-trained detector achieves 0.9990.999. For the eleven detectors whose source attack is not BadNets, this evaluation changes both the attack type and the target-model training optimizer.

These results directly address your concern about dependence on a fixed training configuration: detectors constructed exclusively from Adam-trained reference models remain effective at distinguishing newly trained SGD clean and backdoored models, without adaptation to the new optimizer.

Reviewer_BxNyOpenReview ↗
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Paper summary

The paper is about deciding whether a trained classifier contains a backdoor by training a meta-classifier on representations of benign and backdoored reference models. The starting observation is that the usual representations do not survive a change of attack: when the detector is trained on one attack and tested on the other eleven, MNTD and WeightMM drop to average AUCs of 0.479 and 0.729 on CIFAR-10/ResNet-18. The authors' reading is that learned query responses and raw weights pick up attack-specific artifacts rather than what different backdoors have in common. Their alternative is to isolate the last linear layer and, for each class, optimize an input to that layer until it maximizes the class response; the K optimized vectors are stacked and flattened, and a small 1D CNN is trained on the result. Under this protocol, with BackdoorBench attacks across six dataset and architecture settings, the method reaches an average cross-attack AUC of 0.966 (best 0.998) while both baselines degrade sharply. The ablations cover probing depth, a comparison against simply vectorizing the last layer's weights (vec(W), vec(W,b)), and an adaptive attack that freezes a suffix of the network during poisoning. Complete 12×12 source-to-target matrices are given in the appendix.

Critical strengths

S1. The evaluation protocol is strict and the evidence is checkable. Training on one attack and testing on the other eleven, over six dataset/architecture settings, with every 12×12 matrix published (App. C and D), is a harder test than this literature usually runs, and the quantified failure of two standard baselines (MNTD at 0.479, WeightMM at 0.729 average cross AUC on ResNet-18) is a result practitioners should know about. I verified the aggregates myself and they reproduce. This supports the paper's value as an evaluation study; it does not by itself carry the proposed method as the contribution.

S2. The ablations are unusually honest. Table 2 and App. D.1 test the obvious alternative explanation head-on by feeding the last layer's raw parameters to the same meta-classifier, and App. E openly demonstrates when the method fails (freezing the probed suffix drops FC-only probing to AUC 0.266) and what recovers it. I appreciate this; it is also worth noting that these same ablations are what expose how small the method's margin over vec(W) actually is.

Critical weaknesses

W1. The contribution is thinner than the framing suggests. Since the probed layer is linear and frozen, each optimized vector is a deterministic function of (W, b), the fixed all-ones initialization, and the optimizer. The method therefore examines the last layer's weights under another parameterization; no information from the feature extractor or from the model's behavior on data is involved. The paper's own Table 2 then shows how much that buys over the raw weights: average cross AUC 0.973–0.977 for vec(W) and vec(W,b) versus 0.992, so about 0.02 on the mean. The real difference is in the worst pair (0.168 and 0.249 versus 0.917), and looking at Tables 10–12, that worst case sits almost entirely in the Input-Aware source row. Nothing in the paper explains why the optimization-induced view is more stable than the weights themselves, yet the text claims the representation "captures model changes shared across different backdoor attacks" and is "not a direct encoding of its raw parameter values" (Sec. 4.5), which asserts more than this evidence supports. Read as what it is, a stability-oriented transformation of last-layer parameters, the contribution is incremental for ICLR.

W2. The evidence base is too narrow for the paper's claims. Several gaps, in rough order of importance:

  • Only two baselines. ULPs is cited as one of the three existing representation families (Sec. 2) but never compared, and apart from WeightMM, no post-2021 baseline is evaluated.
  • The attack suite is all-to-one or clean-label at 5–10% poisoning with ASR near 97%. All-to-all attacks and low poisoning rates (0.5–1%), which are the practically hard cases, are absent.
  • Worst-case transfer is reported for one of the six settings. On CIFAR-100 (Table 9) several transfers are far from the headline numbers: the LC column runs 0.464–0.873 and the Blended-source average is 0.841.
  • The single adaptive attack is constrained: the attacker must start from a clean checkpoint and freeze a suffix. The obvious adaptive attack in this threat model, retraining freely while regularizing the probing representation toward a clean model's, is not attempted (MNTD was itself tested against stronger adaptive attacks). With five positive models per setting, Table 16 is also noisier than it looks.
  • Reproducibility gaps: reference-model counts and evaluation-set sizes for the main tables are never stated, and the cost figure (8.56 s/model at 1,000 steps) does not correspond to the method's actual 20,000-step budget, under which FC probing itself moves from 0.964 to 0.995.

None of these is fatal alone. Together they mean the two headline claims, near-universal cross-attack generalization from a single attack and a usable screening tool for model supply chains, are demonstrated only on a narrow slice of the threat model the paper sets up for itself.

Questions for authors

First some clarifications:

  1. How many benign and backdoored reference models train each detector in Table 1 and Appendix Tables 5–9, and how many evaluation models per attack? What does "balanced across clean, class-agnostic, and class-specific models" (Sec. 5.4) mean exactly?
  2. What is the per-model probing cost at the actual budget of 20,000 steps, and how sensitive are the results to that budget? Fig. 2 and the 8.56 s figure are measured at 1,000 steps, where FC probing gives 0.964 instead of 0.995.
  3. Sec. 5.1 cites (Liu et al., 2019; Fu et al., 2023) for the "Filter" attack, but both are defense papers (ABS, FreeEagle). Which implementation is this?

Answers to the following would move my score:

  1. What does the probing transformation change relative to vec(W)? For instance, is it invariant to rescaling, permutation, or rotation of the feature space, and does that explain the worst-pair improvement? And why is the improvement concentrated in the Input-Aware source row? Without such an analysis, I would want the contribution repositioned as a transformation of last-layer parameters rather than "decision-behavior probing."
  2. Please evaluate an adaptive attack that retrains without freezing but adds a loss term pulling the class-wise probing representation toward a clean model's, and report the ASR/accuracy cost to the attacker. Please also give some uncertainty for the adaptive AUCs, given five positives per setting.
  3. Please add a ULPs comparison on at least one configuration, and report worst-case pairs for all six settings rather than only CIFAR-10/ResNet-18. Table 9 already shows where the current claims break.
  4. Please test at least one all-to-all attack and one low-poisoning setting (0.5–1%). If the method holds up, the generalization claim becomes much more credible; if not, the claims should be scoped accordingly.
3 comments

We thank you for your careful review and for recognizing our evaluation protocol and ablation studies. In response to your comments, we have added comparisons with ULPs, representation-matching adaptive attacks, optimization-budget sensitivity experiments, and evaluations under low poisoning rates and all-to-all attacks. We have also clarified the probing scope and the default choice of the final classifier, and expanded our analysis of representation geometry, worst-case transfer, and limitations. We hope these additions address your concerns and respectfully ask you to consider raising your score in light of the new evidence.

Q1:\textcolor{blue}{\text{Q1:}} Model counts and sampling strategy.

For each ten-class configuration, the standard model pool contains 256 clean models and 1,830 backdoored models. Each of the twelve attacks contributes 100 class-agnostic models. BadNets, Blended, BPP, Filter, LF, Refool, and SSBA additionally contribute 90 class-specific models each, giving 1,200 class-agnostic and 630 class-specific models in total.

The full GTSRB pool contains 256 clean models and 3,240 backdoored models: each of the twelve attacks contributes 172 class-agnostic models, and the seven attacks listed above additionally contribute 168 class-specific models each. The CIFAR-100 pool contains 100 clean models and 943 backdoored models: each attack contributes 50 class-agnostic models, and the same seven attacks additionally contribute 49 class-specific models each. Across the six configurations, there are 1,380 clean models and 11,503 backdoored models, totaling 12,883 models.

All compared methods follow the same sampling procedure, with a sampling ratio of 0.30.3 and sampling without replacement. For a source attack containing both backdoor subtypes, we sample from each subtype a number equal to 30% of the smaller subtype pool, rounded down, and construct the training set with a clean:class-agnostic:class-specific ratio of 2:1:12:1:1. For attacks containing only one subtype, we sample 30% of that pool and an equal number of clean models. For example, on CIFAR-10/ResNet-18, the BadNets detector uses 54 clean models and 27 models from each backdoor subtype, totaling 108 training models. The LC detector uses 30 clean and 30 backdoored models, totaling 60. This is what “balanced sampling” in Section 5.4 means: the binary clean/backdoored labels are balanced in the detector-training set.

All models used for detector training are excluded from evaluation. Source-attack evaluation uses all remaining clean and source-attack models. Cross-attack evaluation uses the same held-out clean models and all models from the corresponding non-source attack, without further subsampling or balancing.

The model-generation settings and sampling protocol are detailed in Appendix B.1 and B.2.

Q2:\textcolor{blue}{\text{Q2:}} Default probing cost and optimization-budget sensitivity.

The default budget is 20,000 optimization steps per class. On CIFAR-10/ResNet-18, extracting the complete representation across all ten classes takes 235.6 seconds per model on average using an RTX 4090 D GPU.

The layer-wise ablation uses a common budget of 1,000 steps per class. Extending the probed subnetwork toward earlier layers increases the computational cost per iteration, so this smaller budget makes comparisons of detection performance and efficiency across probing depths tractable. The previously reported 8.56 seconds and 0.964 AUC correspond to this ablation setting. We have explicitly distinguished these two budgets in the manuscript.

We additionally evaluate budget sensitivity on CIFAR-10/MobileNetV2 with BPP as the source attack. Table 1 reports the mean and standard deviation over five random seeds. Increasing the budget generally improves source-attack detection: Seen AUC rises from 0.98600.9860 at one step per class to 0.99890.9989 at 20,000 steps. Unseen AUC remains high across the evaluated budgets.

Steps per classSeen AUCUnseen AUC
10.9860±0.00220.9860 \pm 0.00220.9681±0.00750.9681 \pm 0.0075
50.9853±0.00280.9853 \pm 0.00280.9677±0.00990.9677 \pm 0.0099
100.9854±0.00200.9854 \pm 0.00200.9683±0.00820.9683 \pm 0.0082
500.9804±0.01040.9804 \pm 0.01040.9559±0.01650.9559 \pm 0.0165
1000.9857±0.00580.9857 \pm 0.00580.9643±0.00520.9643 \pm 0.0052
5000.9931±0.00380.9931 \pm 0.00380.9597±0.00650.9597 \pm 0.0065
1,0000.9946±0.00340.9946 \pm 0.00340.9607±0.00670.9607 \pm 0.0067
2,0000.9956±0.00270.9956 \pm 0.00270.9612±0.00760.9612 \pm 0.0076
20,0000.9989±0.00100.9989 \pm 0.00100.9677±0.00620.9677 \pm 0.0062

Q3:\textcolor{blue}{\text{Q3:}} Filter attack implementation and citations.

“Filter” denotes a backdoor attack using an image filter as its trigger, a setting studied in ABS (Liu et al., 2019). Our experiments use the filter-based attack implementation provided in the official FreeEagle codebase (Fu et al., 2023). The two citations therefore identify the attack setting and the implementation source, respectively.

Q4:\textcolor{blue}{\text{Q4:}} What does probing change relative to raw parameters?

We have added analyses of the probing mechanism and representation geometry. Under FC-only probing, the representation is determined by (W,b)(W,b) and the fixed optimization procedure. Its value lies in organizing existing parameter information into a form that better supports cross-attack transfer, rather than introducing information beyond those parameters.

For target class kk, the cross-entropy gradient with respect to the input zz is

∇zL(z;k)=∑j≠kpj(z)(wj−wk).\nabla_z \mathcal{L}(z;k) = \sum_{j\ne k} p_j(z)(w_j-w_k).

Thus, each update combines parameter contrasts between the target class and its competitors, weighted by class probabilities that evolve along the optimization trajectory. The procedure is invariant to a common logit shift across all classes. We do not claim invariance to arbitrary parameter rescaling, feature permutations, or rotations.

To explain the improvement when Input-Aware is the source attack, we compare the geometry of the two representations. Using the clean-model centroid as a reference, the mean cosine similarity between the Input-Aware shift and other attack shifts increases from 0.3490.349 to 0.7210.721. The ratio of its distance to other attack centroids to its distance to the clean centroid decreases from 1.561.56 to 0.760.76. Meanwhile, the silhouette score between Input-Aware and clean models, computed in a 50-dimensional PCA space, increases from 0.1260.126 to 0.6280.628.

These observations provide an empirical explanation for improved transfer: probing aligns the clean-referenced deviation of Input-Aware more closely with those of other attacks while improving its separation from clean models. We have also clarified that the method can probe classification subnetworks extending from different intermediate locations to the output. The final linear classifier is the default choice balancing detection performance and computational cost.

Q5:\textcolor{blue}{\text{Q5:}} Representation-matching adaptive attacks and detection uncertainty.

Following your suggestion, we added an adaptive attack that trains a backdoored model from random initialization with all parameters, including the final classifier, trainable. The attacker adds a regularization term aligning its class-wise probing representation with that of a fixed clean reference model. We evaluate matching strengths λ∈0,0.1,1,10\lambda\in\\{0,0.1,1,10\\}. For computational tractability, the matching objective unrolls 128 differentiable Adam steps, whereas final detection and representation-distance measurements use the default 20,000 steps per class.

λ\lambdaACC (%)ASR (%)Relative probing distanceDetection AUC
089.65±0.5289.65 \pm 0.5296.07±0.7996.07 \pm 0.793.852±0.1213.852 \pm 0.1211.0000
0.189.23±0.3489.23 \pm 0.3495.77±0.7195.77 \pm 0.710.901±0.0280.901 \pm 0.0280.9857
189.80±0.1789.80 \pm 0.1795.64±0.9195.64 \pm 0.910.892±0.0400.892 \pm 0.0400.9935
1089.38±0.1589.38 \pm 0.1596.20±0.4096.20 \pm 0.400.874±0.0860.874 \pm 0.0860.9987

Each AUC pools the three attack models against all clean models excluded from detector training. Representation matching reduces the mean relative distance from 3.8523.852 to 0.8740.874–0.9010.901, while largely preserving ACC and ASR. Nevertheless, detection AUC remains 0.98570.9857–0.99870.9987. Thus, moving the representation closer to the clean reference does not yield effective detector evasion under the evaluated attack settings.

For the frozen-suffix attack, we constructed 95% percentile bootstrap intervals using 20,000 resamples. Each attack model was jointly resampled with its corresponding clean initialization model to preserve their dependence, while the remaining clean models were resampled separately. When the attacker freezes only FC, FC probing achieves an AUC of 0.266 [0.152, 0.410], whereas B4.2 probing achieves 0.744 [0.480, 0.920]. B4.1 probing achieves an AUC of 1.000 on this evaluation set, with a degenerate bootstrap interval of [1,1] because the observed samples are completely separated. This degenerate interval does not imply that population performance has no uncertainty; these intervals reflect evaluation-sample variability conditional on the trained detector.

Q6:\textcolor{blue}{\text{Q6:}} ULPs comparison and worst-case cross-attack transfer.

ULPs and MNTD both use query–response-based representations, so our original evaluation selected MNTD as a representative of this family. Following your suggestion, we additionally evaluated ULPs on CIFAR-10/ResNet-18 using the same model pool and training/evaluation protocol, covering all twelve source attacks. Its average source-attack AUC is 0.743, average cross-attack AUC is 0.560, and minimum cross-attack AUC is 0.204, corresponding to Blended →\rightarrow Input-Aware. ULPs therefore also exhibits limited cross-attack performance in this setting. If needed, we will extend the detailed comparison to all six dataset–architecture configurations in a subsequent revision.

We also summarize the worst-case cross-attack results of our method across all six configurations. We agree that CIFAR-100 reveals an important limitation: despite an average cross-attack AUC of 0.8890.889, WaNet →\rightarrow LC achieves only 0.4640.464. The larger number of classes, smaller reference-model pool, and capacity of the chosen meta-classifier may contribute to this result, but the current experiments do not establish the specific cause. We therefore scope our conclusion to strong average cross-attack generalization within the evaluated settings.

ConfigurationMean Cross AUCMin. Cross AUCWorst source →\rightarrow target
CIFAR-10 / CNN0.9830.912BPP →\rightarrow Input-Aware
CIFAR-10 / ResNet-180.9950.981BadNets →\rightarrow Narcissus
CIFAR-10 / MobileNetV20.9390.670LF →\rightarrow Input-Aware
GTSRB10 / ResNet-180.9890.981Filter →\rightarrow Input-Aware; Narcissus →\rightarrow Input-Aware
GTSRB / ResNet-180.9980.993WaNet →\rightarrow BPP
CIFAR-100 / ResNet-340.8890.464WaNet →\rightarrow LC

Q7:\textcolor{blue}{\text{Q7:}} Low-poisoning and all-to-all attacks.

Following your suggestion, we added evaluations with a 1% poisoning rate and all-to-all attacks on CIFAR-10/ResNet-18. The former includes all twelve attacks, with 50 models per attack. The latter includes BadNets, BPP, and WaNet using the cyclic target mapping ytarget=(y+1) mod 10y_{\mathrm{target}}=(y+1)\bmod 10. Each attack contributes 50 models at 5% poisoning and 50 at 10%.

In both settings, each detector is trained on 15 clean models and 15 source-attack models. Cross-attack evaluation uses the remaining clean models and all models from the corresponding non-source attack, excluding all detector-training models.

SettingMean Cross AUCMin. Cross AUCMean ACCMean ASR
1% poisoning0.9850.88191.58%80.80%
All-to-all0.9710.89691.46%87.09%

The two settings cover 132 and six cross-attack pairs, respectively. The minimum AUCs correspond to Input-Aware →\rightarrow Filter and BadNets →\rightarrow BPP. These results extend the empirical evidence for cross-attack generalization to low poisoning rates and all-to-all label mappings.

Comments on the paper

1 comment

We thank the reviewers for their valuable feedback and for recognizing the value of our approach to cross-attack backdoor detection. The reviews raised four main concerns: (1)\textcolor{blue}{(1)} the probing framework and the default setting of probing only the fully connected layer were not clearly described; (2)\textcolor{blue}{(2)} the lack of mechanistic analysis made it difficult to understand why class-wise probing improves cross-attack generalization; (3)\textcolor{blue}{(3)} the experimental coverage was insufficient, particularly regarding adaptive attacks, other network architectures, and different training optimizers; and (4)\textcolor{blue}{(4)} reproducibility details were incomplete, with missing model statistics and insufficient discussion of limitations.

We have systematically addressed these concerns:

(1)\textcolor{blue}{(1)} We have clarified the method in the manuscript. Our method supports probing a continuous subnetwork extending from any intermediate layer to the output, keeping its weights fixed while independently optimizing its input features for each class. The final linear classifier is the default choice as a trade-off between detection performance and computational cost. If an adaptive attacker modifies only preceding layers, moving the probing location earlier can improve detection.

(2)\textcolor{blue}{(2)} We have added mechanistic and geometric analyses to explain the rationale behind our method: class-wise probing uses parameter differences between classes to construct a discriminative representation.

(3)\textcolor{blue}{(3)} We have expanded the experiments by adding comparisons with ULPs, ablations across optimization budgets, and a new adaptive attack strategy. We have also extended the generalization evaluations to cover different training optimizers, low poisoning rates, all-to-all attacks, and ViT-B/16. The additional results achieve high AUCs and further demonstrate the generalization ability of our method.

(4)\textcolor{blue}{(4)} We have completed the experimental details, including model counts and computational costs. We have also discussed worst-case generalization results and limitations, identifying failure cases on CIFAR-100.

We hope these clarifications, additional analyses, and experimental results address the reviewers’ concerns.

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

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