While I find the problem well motivated and the physical reconstruction interesting, I think most claims and design choices are not sufficiently supported.
Novelty of the main contribution.
The main claim of the paper (first part of the title L001, first contribution in the abstract L018 and in the introduction L113) is the fixed site identity, i.e. each site is assigned to one predictor of the model. However, other methods already do this, such as CNN-array [2]. The authors add that the real difficulty is to do so “while exchanging evidence across all sites” (L047), but a CNN also exchanges information with neighboring sites during feature extraction, and these adjacent sites are precisely the interesting ones, where PSFs may overlap. Compared to a CNN, the main benefit of self-attention is to enable long-range dependencies, and I could not find where the paper tests whether this property is relevant or not in the dense array setup (Q1).
Missing baselines. The authors compare their method to classical estimators from the field, and to methods adapted from object detection and semantic segmentation. However, deep learning methods designed for this task, such as CNN-array [2] or the more recent [3], are not compared in Table 1 (although they are cited by the authors). Given the point raised above, it seems to me that CNN-array would be a relevant baseline (Q2).
Validity of the ablation study. The DETR-style baseline is surprisingly good (F1 0.9804), given that it does not share most of the main contributions of the authors: no "tokenizer", no per-site identity, no reconstruction loss function. By contrast, in the ablation, removing a single component yields F1 scores below this baseline (for 7 out of the 9 experiments). Such variations are hard to explain: for example, if my understanding is correct, removing the adaptive Top-16 tokenizer yields a model that still keeps 1) the site identities rk, 2) the fixed query-to-site assignment, 3) the full-resolution features and 4) the reconstruction loss, which compose most of the paper's contributions, yet it reaches F1 0.908, well below the DETR baseline. These may suggest an issue in the evaluation pipeline (Q3).
Furthermore, the reconstruction loss function alone seems worth about 10 points of F1: without Lrecon, Site-AIT (F1 0.8934) falls below DETR, DEIM, TransUNet, SegMAN-T and the matched filter (0.8992). As no baseline is trained with Lrecon, it is impossible to assess whether the gain comes from the loss function rather than from the architecture, which is the main point defended by the paper (Q4).
Finally, I could not find an ablation on the top-16 selective feature module (Q5) (if I understand correctly, the tokenizer ablation L406 removes the whole module, not just the selection process).
Coordinate perturbation experiment. Replacing all "coordinate inputs" with 300 uniformly sampled coordinates gives almost the same performance as the calibrated inputs. If my understanding is right, this suggests that the model memorizes the register geometry within ek, rather than using the explicit coordinate anchors presented as a design principle, i.e. that the use of prior information encoding the position does not yield any benefit (Q6).
Dataset and labels. The main text does not explain how the dataset was annotated, but the appendix mentions a semi-automatic pipeline involving human experts.
Thus, the labels rely on human judgement, which may introduce errors in the all train/validation/test datasets. The 0,09% disagreement between the two experts does not show that the labels are correct, since both could be fooled by the same difficult spots. Moreover, the inter-expert RMSE on the centers is 0.38 px, while the method claims a localization error of 0.0152 px. An error smaller than the uncertainty of the reference should not be interpreted, hence I find it misleading to use it as a major result in the abstract.
Metrics and reported numbers. All the detection metrics in Table 1 (accuracy, precision, recall, F1) depend on a detection threshold. Calibration of this threshold may vary from method to method, and arbitrary choices may bias the results. I found no indication on how the threshold of Site-AIT is calibrated (Q7). Furthermore, the validation and test sets have quite different compositions, so there's no reason than a calibrated threshold on the validation set transfer to the test set. Moreover, the AUROC is a threshold-independent metric, but is only reported in the appendix: I think it should be moved to the main Table 1.
Regarding latency, the times in Table 1 are measured with PyTorch on GPU, which is very different from the target hardware (the FPGA). As far as I know, there is no guarantee that the inference speed ranking will transfer to a different hardware. Reporting the FLOPs and the number of parameters for all models would be more informative (Q8).
Finally, as for the localization error above, the abstract reports a latency of 0.31 ms (L026) next to the accuracy of the full model. However, this latency comes from a quantized version of the model, whose performance is lower. Again, I find the formulation of the abstract misleading, as a first-time reader may understand it as numbers from the same model.
Additional, minor remarks:
- Figures 1, 3 and 6 are hard to read: I printed the paper and could not read them. Figure 1 and Figure 3 are too small, and they do not use the full page width. Figure 1 is not colorblind-friendly. Figure 6 is very dark and its colors are hard to tell apart.
- Why does Figure 6 not compare Site-AIT to the strongest baseline?
- The existence head (L145) is a dead head as the authors acknowledge (L241). Why did the authors keep it in the derivations? It makes the math harder to follow.
- hk is not defined (L237).
- The references have not been cleaned: they contain urls and missing uppercases (e.g., Jeong et al. (2023) should be "Using machine learning to improve multi-qubit state discrimination of trapped ions from uncertain EMCCD measurements").
Conclusion. Overall, I found that the experimental section contains too many flaws to accept the current version. The main issues is the ablation study, where removing any single component makes performance collapse below an adapted DETR baseline that lacks most of the authors' contributions, yet performs almost as well as the proposed method.
Furthermore, the paper lacks deep learning baselines, details on the dataset, and experiments to independently validate each contribution.
The general presentation, especially the figures, should also be improved.