acceptodds
Under review as a conference paper at ICLR 2027

SITE-AIT: SITE-BOUND LATENT TOKENIZATION AND JOINT OPTICAL INFERENCE FOR DENSE QUBIT READOUT

Abstract

Dense fluorescence images of large qubit registers violate the independence assumption behind per-site thresholding: neighboring point-spread functions overlap, emitter coordinates drift, and local observations depend on unknown neighboring states. Moreover, pixel-based representations and generic object queries fail to maintain a persistent one-to-one correspondence with dense physical sites, hindering high-fidelity readout. We propose Site-AIT, a representation that binds one latent token to each dense site and resolves coupled decisions via register-wide self-attention. Tokens are constructed via offset-corrected, point-spread-function-weighted Top-16 selection from a candidate field, reducing local features from 2,704 to 256 dimensions. When labeled data are scarce, a detector-aware noise prior initializes the image backbone, while a differentiable optical reconstruction objective guides training without adding inference overhead. Evaluated on a 2,000-frame benchmark from a 300-site trapped-ion register, Site-AIT achieves per-ion accuracy of , with pixel localization error and ms FPGA latency. Extensive ablations and physical perturbation experiments confirm that aligning the inference unit with the physical measurement unit provides an effective design principle for calibrated, densely overlapping emitter arrays.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
Quantum Machine Learning, Tokenization, Deep Learning, Transformers

Reviews

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1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_WcekOpenReview ↗
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Paper summary

I strongly suspect that it is AI generated, way beyond what is stated in the AI-use clause "Generative AI was used to polish grammar and tone". I strongly suspect that the introduction is fully AI generated, as well as large parts of the methods section. The introduction contains sentences like:

"Our key idea is to make the model’s unit of inference coincide with the instrument’s unit of measurement"

which has no relation to anything in the paper and does not make much sense in any interpretation i have tried and I suspect that this is an artefact from a part of the method prompting getting stuck in model memory. This is not the only instance of this issue, but the most blatant to point out. So if ChatGPT "polished grammar" the authors have not checked the outcome.

At this point, I decided to check the code, just to find that the code-base is AI generated as well. As an example, the comments in this code are clear claude-structured and contains code patterns that claude loves to use.

https://anonymous.4open.science/r/Site_Dia_4_Qubit_Readout/Reproduce_baseline_code/bayesian_pi/pi_network.py

The README has similar issues, spending a lot of space to discuss tests that have to fail because some code is not imported, which is very AI-like.

I do not mind AI generated contents, as long as the authors are truthful about it, but I do not see a reason to spend time reviewing a paper when the authors are not even faithfully describing the tools they use, since I cannot trust anything the article states.

If it is not AI, the article is poorly written, the method is only introduced but not reasoned for. The contributions section summarizes the steps of the method but does not argue for what is actually contributed as novel, and the method description itself and the rest of the paper never compares any of their choices to the literature. In its best reading, the article represents a purely engineering application to the readout problems in ion qubits, which could make it a good case for an applied journal in the field, but there is not much novelty here on the ML side. However, even on this axis, the article is poorly written.

The method description itself is hard to understand, and contains sentences like: "For site k, a pooled feature around c0k is passed through a shared multilayer perceptron g∆."

And i am still asking myself what the pooled feature is supposed to be at this point, since it is never defined in the paper. Undefined quantities is a repeated pattern, Figure 5 mentions pi/2 binomial for the first time in the article, and it is never defined in the main paper what that means.

Missing references to the methods compared to (lines 320-323, "D-FINE+MAL" never referenced in the main paper and "DETR-style (2020)" being a broken reference).

Critical strengths

I cannot summarize critical strengths since i do not trust the paper contents.

Critical weaknesses

I do not trust the papers contents.

Questions for authors

What is the meaning of the following sentence?

"Our key idea is to make the model’s unit of inference coincide with the instrument’s unit of measurement"

Reviewer_RMFSOpenReview ↗
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Informativeness
2
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Paper summary

This paper tackles the inverse problem of recovering the binary state and the drift of each individual qubit in an array, given a fluorescence image captured by a camera. For dense arrays, overlapping PSFs hinder the classical per-site approach (individual ROI + threshold), hence the authors propose to train a deep learning model in a supervised manner on labeled data. Their method combines several components to address various difficulties: a pre-trained unet backbone to reduce the amount of labeled data needed, selective feature extraction to reduce the computational burden (the final model is deployed on a hardware chip), transformer modules that leverage self-attention to exchange evidence between sites, fixed per-site prediction to preserve each qubit's identity, and an additional physics-based reconstruction loss function. The authors compare their method to non-deep baselines from the field, and to architectures adapted from object detection and semantic segmentation, on a custom experimental dataset.

Critical strengths

The paper’s main ideas are well motivated.

  1. Directly predicting the quantity of interest: in my opinion, a network whose outputs are exactly the quantities of interest is preferable to a general-purpose network followed by post-processing.
  2. Leveraging prior information: if prior information is available, such as a fixed number of qubits and their initial locations, it makes sense to use it. The authors build it into the architecture as an inductive bias.
  3. Pre-training on a related task: initializing the network from weights pre-trained on simple denoising objectives has been shown to yield performance gains [1], especially when annotated data is expensive and scarce.
  4. Reconstruction-guided training: traditional frameworks for inverse problems minimize a data term plus a prior term. As the forward model is known and differentiable in this setup, using frame reconstruction as an auxiliary training signal is natural and well justified.

Additionally, applying machine learning tools to practical physics applications is not an easy task: finding the right modules to build a coherent, working structure is extensive work that deserves recognition.

Finally, I appreciate that the authors released their code and dataset as open source.

Critical weaknesses

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 rkr_k, 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 LreconL_{recon}, Site-AIT (F1 0.8934) falls below DETR, DEIM, TransUNet, SegMAN-T and the matched filter (0.8992). As no baseline is trained with LreconL_{recon}, 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 eke_k, 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.
  • hkh_k 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.

Questions for authors
  • Q1. Could you test the importance of long-range information exchange? For example, by restricting the attention to the k nearest neighbors, or by comparing the average attention distance to the receptive field of a CNN.
  • Q2. Could you compare your method to CNN-array [2], scaled to roughly 5.6M parameters and with the same backbone?
  • Q3. How do you explain that removing a single component drops the performance far below the DETR-style baseline, which has none of these components?
  • Q4. Could you train DETR-style and CNN-array with the same reconstruction loss? For DETR, it should be easy, since it already shares the prediction heads.
  • Q5. Could you ablate the top-k selection alone, i.e. keep the tokenizer but use all 169 candidates instead of the top 16?
  • Q6. Could you clarify the coordinate perturbation result? Could you add ablations that remove ϕcoord\phi_{coord} and/or eke_k ? If the coordinates are not used, why keep this branch?
  • Q7. How is the threshold of Site-AIT calibrated, and is it the same strategy for all baselines?
  • Q8. What are the FLOPs of Site-AIT, and how does it compare to the FLOPs of each variant in the ablation study, and to the baselines in Table 1?

References

[1] He, Kaiming and Chen, Xinlei and Xie, Saining and Li, Yanghao and Dollár, Piotr and Girshick, Ross. Masked Autoencoders Are Scalable Vision Learners. IEEE/CVF Conference on Computer Vision and Pattern Recognition (CVPR), 15979-15988. 2022.

[2] Phuttitarn, Linipun and Becker, B. M. and Chinnarasu, Ravikumar and Graham, T. M. and Saffman, Mark. Enhanced Measurement of Neutral Atom Qubits with Machine Learning. Physical Review Applied 22, 024011. 2024.

[3] Su, Xiaolu and Liang, Mingcheng and Zhang, Tengyu and Zhao, Zhengran and Yin, Peng and Yang, Yunkun and Dai, Wenqing and Luo, Xiaoqin and Li, Xiangliang and You, Li. Field-programmable gate array-accelerated exposure-aware convolutional neural network for fluorescence-based qubit readout. Physical Review Applied 25, 054004. 2026.

Reviewer_eD91OpenReview ↗
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Confidence
3
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Paper summary

Site-AIT addresses bright/dark state readout for a dense 300-ion register from a single sCMOS frame. Each persistent physical site is represented by one token constructed by selecting 16 features from an offset-corrected 13×1313 \times 13 candidate field and applying learned PSF weighting. Register-wide self-attention then jointly predicts state and coordinate for all 300 sites. The method additionally uses detector-aware denoising pretraining and a training-only differentiable PSF reconstruction loss.

On the 2000-frame Real1600-Hard400 test benchmark (1600 experimental frames and 400 synthetically degraded frames), the paper reports accuracy 0.9978 and F1 0.9979, compared with accuracy 0.9792 for its DETR-style baseline and 0.8913 for a matched filter.

Critical strengths

The formulation of readout around persistent physical-site tokens is well motivated for a calibrated dense register. However, the quantitative inconsistencies I discuss below prevent me from relying on the reported experimental evidence in its current form.

Critical weaknesses

1. Several quantitative results cannot be reconciled under the given evaluation protocol.

First, Tables G.1 and G.2 disagree for the deterministic baselines. Real1600 consists of 250 all-dark, 1_000 π/2\pi/2, 100 174Yb+^{174}\mathrm{Yb}^{+}, and 250 all-bright frames. Weighting the matched-filter subset accuracies in Table G.2 by these subset sizes gives

250(0.8620)+1000(0.9105)+100(0.9290)+250(0.9360)1600=0.9081,\frac{250(0.8620)+1000(0.9105)+100(0.9290)+250(0.9360)}{1600} = 0.9081,

whereas Table G.1 reports 0.9014. Analogously, the IPM subset values give 0.8954, whereas G.1 reports 0.8878. Given these estimators are deterministic, seed averaging cannot account for the discrepancy. Moreover, the G.1 confusion counts reproduce the aggregate values in Table 1.

Second, Tables 2 and I.2 appears inconsistent with the class prevalence of the stated Real1600-Hard400 benchmark. The G.1 confusion counts imply 253_388 positive labels in Real1600 and 60_000 in Hard400, i.e. 313_388 positives among 600_000 site decisions (~52.23%). The image perturbations in Table I.2 and the architectural changes in Table 2 do not change these labels. However, the accuracy/precision/recall triples reported for the perturbed rows of Table I.2 are algebraically consistent with a 50/50 class balance instead. For example, U-Net at 3:1 reports accuracy 0.5900, precision 0.5865, and recall 0.6100. These values correspond almost exactly to 50% positive prevalence; with the stated ~52.23% prevalence, the latter precision and recall would imply accuracy of ~0.572 rather than 0.590. The same pattern occurs across the perturbed rows.

Hard400 on its own is exactly balanced (60_000 positives among 120_000 decisions). If these rows were computed on Hard400 alone, they cannot be compared with the full-model reference in Table 2 or with the 1:1 rows of Table I.2, which use the combined benchmark. Unless a balanced subset or a different evaluation protocol was used but not documented, I do not see how these tables can all describe the stated benchmark. This is significant, because the ablations are the main evidence for the individual components, the perturbation results are used as evidence for robustness, and the classical results contribute to the paper's comparative evaluation.

2. The coordinate-sensitivity experiment appears to undermine the proposed mechanistic interpretation, while the localization result cannot reflect physical localization.

Appendix I.1 states that the "random" condition replaces the calibrated lattice by 300 coordinates sampled uniformly over the full image, sorts them, assigns them to physical-site indices, and replaces all coordinate-dependent inputs, including tokenizer sampling centers, coordinate positional encodings, and coordinate-head reference centers. Nevertheless, Sec. 4.3/Fig. H.1 reports accuracy/F1 around 0.997 even for this condition.

This is difficult to reconcile with the paper's explanation that high accuracy arises from offset-corrected collection of local optical evidence around each physical site: the tokenizer correction is bounded while the supplied centers can now be unrelated to the actual ions. It may be possible for the globally contextual DW-UNet features and persistent site-index embeddings to carry enough information to make the supplied coordinates largely irrelevant, but if so this changes the interpretation of why the architecture works. The authors should establish whether predictions actually depend on site-local evidence rather than predominantly on global backbone features plus site identity.

There is also an important distinction between benchmark localization and physical localization accuracy. The reference states and centroids are obtained by human annotation of the fluorescence images rather than by an independent state/position measurement. The independent annotation study reports centroid discrepancies up to 0.30 px MAE and 0.38 px RMSE. Meanwhile, the headline 0.0152 px "localization error" subtracts the pooled mean residual before taking the RMS and is explicitly defined by the paper as a dispersion statistic rather than absolute centroid error. I therefore do not think 0.0152 px supports a claim of 0.0152-pixel absolute localization accuracy, the abstract suggests.

Questions for authors

Q1. Please reconcile Tables G.1 and G.2 for the deterministic matched-filter and IPM estimators, preferably by providing the exact per-subset counts used to construct both tables.

Q2. What exact examples and labels are used to compute the perturbed rows of Table I.2? If the full Real1600-Hard400 benchmark is used as stated, please provide the confusion counts for each row and explain why the reported accuracy/precision/recall triples appear consistent with 50% class prevalence rather than the benchmark's ~52.23% positive prevalence.

Q3. How does the fixed Site-AIT checkpoint retain ~0.997 accuracy when all coordinate-dependent inputs are replaced by coordinates sampled uniformly random over the image? In particular, can the authors quantify whether the classifier uses the sampled local feature content, the persistent site-index embeddings, or globally contextualized DW-UNet features? This result appears important for interpreting the claimed role of site-bound local tokenization.

Q4. Please state whether the 100_000 laboratory images used for detector-aware pretraining exclude all Real1600/Hard400 source images and, preferably, acquisition stacks containing those frames.

Q5. On prepared all-dark frames there is no bright neighbour to cause spillover, yet the per-site tuned matched filter misclassifies 13.8% of sites and IPM 15.8% (Table G.2). What causes these errors? Please provide per-site photon-count histograms for the all-dark and all-bright frames.

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

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