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Paper summary
SwiftAD accelerates cross-dataset zero-shot 3D anomaly detection using a frozen CLIP backbone. Rendering-derived visibility first removes unsupported background tokens; a learned selector then retains informative foreground tokens. Decoupled global/local text prototypes and residual adaptation compensate for pruning-induced feature shifts. Evaluation on MVTec3D-AD, Eyecandies, and Real3D-AD demonstrates a strong accuracy-efficiency tradeoff. Training uses labeled source data, with no target-domain adaptation.
Critical strengths
- Substantial practical gains. Relative to the unpruned configuration, computation falls from 1830.65 to 911.60 GFLOPs and throughput rises from 2.57 to 4.47 FPS. Table 1 reports strong performance across three datasets, including 98.4% P-AUROC and 93.7% AUPRO on MVTec3D-AD and 81.8% P-AUROC on Real3D-AD. These results support the practical value of the approach.
- A coherent design supported by ablations. Geometric visibility offers an inexpensive, task-specific pruning signal. Tables 2, 3, and 6 support hierarchical pruning and branch-specific prototype adaptation, while multi-view visualizations illustrate complementary retained evidence. LFP improves localization and reduces computation further, with only a small object-level accuracy tradeoff relative to VGBP plus adaptation.
Critical weaknesses
- The learned selector is not fully specified, and performance attribution needs a stronger control. Appendix B gives loss weights, but the sparsity and anomaly-focus objectives remain described mainly in prose. Equation 13 defines a straight-through mask, yet its connection to hard token compaction and downstream task gradients is unclear. Table 2 isolates the effect of adding LFP to VGBP plus adaptation, but lacks an unpruned model with the same prototype adaptation, leaving the full accuracy gain over the unpruned reference partly confounded.
- The model-selection protocol and robustness comparisons need clarification. Tables 3 and 4 report target-dataset configuration sweeps without stating whether the default was chosen independently of target test performance. This is a missing protocol detail, not evidence of test-set tuning. Table 5 reports robustness under perturbations, but an unpruned control would help quantify additional sensitivity from pruning. The measured efficiency gains are useful; the timing boundary needs clarification to assess end-to-end benefit.
Questions for authors
- Attribution of the accuracy gain. Table 2 already shows the incremental effect of LFP over VGBP plus adaptation. Can the authors add an unpruned configuration using the same decoupled prompts and residual prototype adaptation, with matched supervision and training? This would clarify how much of the full model’s accuracy gain over the current unpruned reference comes from adaptation, alongside the computation savings from pruning.
- Target-independent model selection. In the labeled-source transfer setting described in Appendix A, were the pruning layers, keep ratio, resolution, and view count fixed using source-domain validation before target evaluation? Please distinguish the ablations in Tables 3 and 4 from the selection procedure and clarify whether the same selection rule applies across datasets.
- Selector training and gradient flow. Please provide the exact sparsity and anomaly-focus objectives, including patch-label generation and anomaly coverage. How is the straight-through mask used alongside hard top-k compaction, and which losses provide gradients to selected and discarded token scores?
- Defect preservation and robustness. Can the authors quantify retained defect tokens by defect size and compare the full model with an unpruned model using the same prototype adaptation under Table 5 perturbations? Table 2’s recovery after adaptation is informative, but the VGBP-only drop does not by itself prove that defect evidence was removed. These controls would help assess retention and additional sensitivity caused by pruning.
- Timing protocol. Section 4.2 and Appendix B specify an RTX 3090 and batch size 2. Do the FPS measurements use that inference batch size, what numerical precision and timing procedure are used, and do they include rendering and back-projection? Please separate selector overhead and report typical retained-token counts to make the measured efficiency gains easier to interpret.
2 comments
- Defect preservation and robustness
To assess whether pruning preserves anomaly evidence of different spatial scales, we added a defect-size analysis in Table 5 and Fig. 6. Table 5 stratifies anomalous samples according to the ground-truth defect area and reports object-level and point-level metrics for each size interval, while Fig. 6 visualizes the relationship between defect area, sample count, and anomaly-detection performance. The results show that localization remains strong even for small defects: for the 0–99 pixel bin, SwiftAD achieves 97.5% P-AUROC and 88.8% AUPRO. Since this bin contains only eight anomalous samples, we explicitly caution against over-interpreting its image-level metrics. Across the substantially larger 100–2999 pixel range, P-AUROC remains between 98.5% and 99.2%.
We further provide representative qualitative visualizations for small, medium, and large defects in Appendix G. These examples show the rendered views, view-wise anomaly maps, fused 3D predictions, and ground-truth masks. They illustrate that the retained tokens preserve localized anomaly responses for sparse defects, while also supporting coherent multi-view fusion for larger anomalous regions.
In addition, Table 7 compares SwiftAD with the matched unpruned + PA control under Gaussian noise, calibration shifts, and mixed perturbations. The results show that pruning has negligible influence under calibration shifts. Under strong geometric noise, pruning introduces some additional object-level sensitivity; however, point-level localization remains strong. For example, under the most severe mixed condition, SwiftAD retains 95.7% P-AUROC and 87.9% AUPRO, compared with 97.0% and 88.0% for the unpruned + PA control. We have explicitly acknowledged this limitation in the revised conclusion.
- Timing protocol and retained-token statistics
We appreciate the request for a clearer timing boundary. Appendix F now provides the hardware setting, precision, batch size, warm-up, timed sample count, synchronization procedure, stage-wise latency, selector overhead, and token-retention statistics.
Training uses batch size 2, whereas latency is measured with batch size 1 to report per-object online latency. Measurements use one RTX 3090 GPU, FP32 inference, ten warm-up batches, and 100 timed objects with CUDA synchronization at stage boundaries.
The reported 4.47 FPS is cached-view online throughput: it includes device transfer, visibility-mask construction, visual encoding, selector scoring, 2D anomaly scoring, 3D back-projection, post-processing, and image-level scoring. Multi-view rendering itself is excluded because it is a shared preprocessing cost for both the unpruned baseline and SwiftAD; both methods use the same renderer, nine views, and input resolution. Hence, the reported 73.9% gain should be interpreted as an online encoder-side improvement within the same rendering-based CLIP pipeline, rather than as a claim of rendering acceleration.
Finally, Appendix F reports that VGBP retains 71.8% of the original patch tokens, while LFP retains 35.9% on average, corresponding to 206.7 tokens per view. The selector scorer is separately listed for transparency but is not double-counted, since it is part of the visual encoder.
We thank the reviewer again for these insightful suggestions. We believe the additional controls, detailed selector specification, source-only selection clarification, robustness analysis, and transparent timing protocol significantly strengthen the revised paper.
Dear Reviewer,
Thank you very much for your careful and constructive review. We sincerely appreciate your positive assessment of SwiftAD’s practical efficiency gains, coherent design, and comprehensive evaluation. Your comments helped us substantially improve the clarity, reproducibility, and analysis of the paper. All revisions in the resubmitted manuscript are marked in blue. We have also released anonymized code at https://anonymous.4open.science/r/SwiftAD-B754/.
We agree that the original description of the learned foreground selector was insufficiently detailed. We have clarified the selector losses, patch-label construction, hard token compaction, and straight-through gradient mechanism. For each rendered view, the pixel-level anomaly mask is converted to a patch-level label by adaptive max pooling onto the 24×24 patch grid. A patch is labeled anomalous if it contains at least one anomalous pixel. After VGBP compaction, the corresponding patch labels are gathered using the same token indices, so selector supervision is always aligned with the compact visible-token sequence.
In Stage 2, the objective combines the task loss, the sparsity loss (weight 0.1), the anomaly-focus loss (weight 0.5), and the prototype-anchor regularizer (weight 0.5). The sparsity loss contains an MSE penalty between the soft retained-token ratio and the target keep ratio, together with a score-spread term preventing score collapse. The anomaly-focus loss combines positive-class-weighted patch-level BCE, anomaly coverage, and normal-sample regularization. We use a positive-token weight of 5.0, anomaly-coverage weight of 1.0, score-spread coefficient of 0.05, and straight-through temperature of 0.7.
For forward inference, LFP uses an exact sample-wise hard top-k mask and physically compacts the selected tokens before they enter the remaining Transformer blocks; thus, the measured acceleration comes from genuine sequence shortening rather than soft masking. During training, we use a sigmoid surrogate around the sample-wise top-k threshold in the backward pass. Therefore, selected tokens receive task-loss gradients through the straight-through mask, while the selector scores for both selected and discarded tokens are directly supervised by the sparsity and anomaly-focus objectives. Discarded tokens are not processed by downstream Transformer layers after hard compaction.
We agree that an unpruned model with identical PA is necessary to isolate the accuracy contribution of adaptation. We therefore added the unpruned + PA control in Table 2, using the same source-domain supervision, decoupled prompts, and residual prototype adaptation as the full model.
The results show that PA independently improves O-AUROC by 8.9 points over the unpruned baseline, while the full model further improves O-AUROC to 84.5 and reduces computation by approximately half. Thus, PA mainly compensates for cross-domain and pruning-induced representation mismatch, whereas VGBP and LFP provide the principal computational savings.
We confirm that there is no target-domain leakage. No target-domain sample, annotation, validation metric, or test result is used to optimize the prompt learners, residual prototypes, foreground selector, or final configuration. The pruning layers, keep ratio, resolution, view count, optimizer, learning rates, and loss weights are determined using source-domain-only adaptation and fixed before target evaluation. The target-domain ablations in Tables 3 and 4 are diagnostic analyses rather than target-guided model selection. They are reported to characterize sensitivity, not to choose the final operating point.
The only source-dataset-dependent setting is the number of training epochs. Since the source datasets differ in size, their fitting and convergence speeds differ; the epoch count is therefore determined solely by source-domain training behavior. It is never selected according to target-domain performance.