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Withdrawn from ICLR 2027

Neural Fields for NV-Center Inverse Sensing

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

Inverse problems in scientific sensing are often solved with either hand-designed regularizers or supervised networks trained on simulated labels, yet both can fail when the forward model is nonlinear, spectrally coupled, and physically delicate. We study this issue for noise sensing based on nitrogen-vacancy (NV) centers in diamond, where a quantum sensor measures magnetic-noise spectra generated by sparse spin sources. We show that replacing a common scalar/coherent forward approximation with a tensor power-summed dipolar operator changes the inverse landscape and exposes a center-collapse failure mode in free-density optimization. We propose NeTMY, an amortization-free coordinate neural field coupled to the differentiable NV forward model, with annealed positional encoding, multiscale optimization, sparsity/gating, and spectrum-fidelity losses. On a 512-sample benchmark generated by a direct source-side simulator and inverted under the tensor operator, NeTMY achieves the best localization and distributional metrics. Mechanism experiments show that NeTMY's parameterization filters the raw density-space gradient and avoids the center collapse reached by free-density solvers. These results position NV quantum sensing as a testbed for physics-faithful neural inverse problems.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
inverse problems, scientific machine learning, implicit neural representations, differentiable physics, quantum sensing, sparse reconstruction

Reviews

Among:
Shape:
1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_kmbwOpenReview ↗
Rating
2
Confidence
2(−1)
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper argues that an incoherent tensor power-summed operator F₂ is more faithful than a coherent scalar operator F₁ for NV relaxometry inversion. It diagnoses a “center collapse” of free-density solvers under F₂ and proposes NeTMY, a per-instance coordinate neural field whose parameterization filters the density gradient through a PSD kernel G_θ = J_θJ_θᵀ (Lemma 2). Evidence comes from an F₃-generated 512-sample cross-fidelity benchmark, matched-operator benchmarks, and an 8-NV α-RuCl₃ cross-check.

Critical strengths

The forward-model gap is spelled out explicitly (Eq. 12), and the failure mechanism has measurable diagnostics (iter-0 center/outer ratio 18.29× vs 1.6×; SVD energy split). The paper also reports unfavorable results (the F₂→F₁ cross, PnP/RED, failure modes). This makes the experimental setup more credible. The mathematical derivations are correct, though fairly basic.

Critical weaknesses

Weaknesses

    1. The collapse mechanism is not separated from the choice of loss and optimizer. ω_L is a per-pixel unknown field (B.7), constant only within each ground-truth source (line 1471), and the Lorentzian γ²/((ω − ω_L)² + γ²) is nonlinear in ω_L (Eqs. 2–3), so the joint (ρ, ω_L) problem is generally non-convex. For a fixed ω_L, however, the unnormalized F₂ is linear in ρ (line 1314). The diagnosed collapse (peak coupling plus first-step center bias) is tied to two design choices: log-MSE on max-normalized maps, and Adam from a uniform start. Please add a diagnostic: with oracle ω_L (or alternating ω_L updates), solve for ρ with NNLS or non-negative ℓ₁ (FISTA) and compare on the primary metrics. Please also report free-density controls with random initialization and with an unnormalized linear loss. This is only a diagnostic, since oracle ω_L + NNLS changes the information available, the loss and the solver at once. If it also collapses, the mechanism claim is strengthened; if not, these three factors need to be controlled separately (e.g., oracle ω_L with the normalized log-MSE and Adam) to locate the cause. Separating the mechanism correctly would make the conclusions deeper.
  1. The three real-data axes disagree, and the main text should present them evenly. The main text reports the depth-amplitude and conditioning axes, points to the slope axis in F.10, and qualifies the conclusion to those two axes. On the slope axis the measured value is b_exp = 1.43 ± 0.21. Treating the reported ± as standard deviations, assuming independent errors and propagating α = 1.06 ± 0.22 to first order gives 1.89 ± 0.39 for F₁ (~1σ away) and 3.77 ± 0.78 for F₂ (~2.9σ away). This is an order-of-magnitude estimate, not a formal test. Meanwhile, F₂ also fails 7/8 NVs on depth-amplitude, and Hessian conditioning under a Gaussian ansatz measures identifiability rather than correctness. The 8-NV data therefore do not discriminate between the operators, and the axis that directly tests the scaling is closer to F₁. Please report all three axes side by side in the main text, including the prediction uncertainty.

  2. The tables are inconsistent and the statistics are unclear. Table 9 is a 128-scene subset of Table 1's benchmark. Its F₁ columns match Table 1, but its F₂ MSE column differs by two to three orders of magnitude: NeTMY 4.46 vs 0.0078, Tikhonov 1.13 vs 0.0082. The authors note that Table 9 consists of reruns on the subset (line 1578) and that means exceed medians, which does not account for a gap of this size. Possible sources include the subset composition, the rerun settings and the MSE scale correction (Eq. 30); please explain.

Some intervals in Table 1 (“95% CI across 3 seeds”) are very wide with negative lower bounds (Tikhonov F1 0.465 ± 0.436; ADMM MSE 3.84 ± 4.97), although Tikhonov is deterministic. Please state whether the intervals are computed across seeds or across samples, and add the paired bootstrap comparisons already used in F.6. The ablation (Table 3) uses MSE/SSIM rather than the primary metrics, and its protocol is not stated. The full-model MSE of .0039 is close to the F₂/F₂ value in Table 2, which suggests a matched-operator setting. Please state the protocol and report the ablation on the F₃→F₂ benchmark with the primary metrics.

  1. Baseline tuning is unequal. NeTMY's hyperparameters are swept on held-out data (Table 13). Tikhonov's and ADMM's regularization weights are fixed, with Tikhonov's explicitly set to NeTMY's values, and ADMM uses a different Larmor construction. This makes the comparison clearly unfair; I hope the authors align the settings for a fair comparison, which would substantially strengthen the paper's credibility.

Minor comments

  • The supervised baselines are trained on dense scenes and tested on sparse ones, although sparse training pairs are free to simulate; a distribution-matched amortized baseline is needed, especially given the 2.6-query compute crossover.
  • The runtimes in Table 8 (780 s, A6000) and Table 14 (141 s, L40) use different protocols.
  • ADMM and DeepDecoder give near-identical F₂/F₂ MSE (0.2555/0.2558); please explain.
  • Cite the concrete prior equations or code that use F₁.
  • The scope (2-D, single 20 nm standoff, 64×64 grid) should be stated in the abstract.
Questions for authors

(1) With oracle (or alternating) ω_L, do NNLS or non-negative ℓ₁ also collapse? (2) What are the slope-axis deviations once the uncertainty of α is propagated, and can all three axes be reported in the main text? (3) What explains the ~570× gap between the F₂ MSE in Table 9 and Table 1? Are Table 1's intervals across seeds or across samples, and which operator setting does the ablation use? (4) Does the ranking change when the baselines receive equal tuning?

Reviewer_WQntOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper studies reconstruction of sparse spin-source density and a Larmor field from NV-center noise measurements. It contrasts a scalar coherent forward approximation with a tensor power-summed operator, then proposes NeTMY, a coordinate neural field optimized separately for each measurement. The solver combines annealed Fourier features, multiscale optimization, gated density outputs and additional measurement-derived losses. Synthetic experiments generate observations using a source-side simulator and invert them with approximate operators. Gradient and optimization diagnostics investigate center collapse. A real-data study uses eight NV sites to compare operator consistency under a Gaussian density ansatz. The localization results are promising, but objective matching and the scope of physical reconstruction remain important uncertainties.

Critical strengths

S1. The main synthetic evaluation addresses operator mismatch and sparse localization

The principal benchmark generates spectra with the source-side simulator F3 and inverts using F1 or F2, rather than using the identical inversion operator for both tasks (Appendix B.4, p. 17). Under F2 inversion, NeTMY reports Hungarian F1 of 0.882 versus 0.762 for Tikhonov and SWD of 0.036 versus 0.100 (Table 1, p. 7). Evaluating localization and mass distribution, rather than relying only on background-dominated pixel MSE, is appropriate for the stated sparse reconstruction problem.

S2. The paper investigates optimization behavior and reports limitations

Figure 4 (p. 8) and Appendix F.7 (pp. 31–32) examine initial gradients, realized neural-field updates, center mass and operator changes. These diagnostics make the proposed parameterization explanation more concrete than a leaderboard alone. The paper also reports directional rank reversals, reconstruction artifacts and substantial runtime, and explicitly limits the real-data study to a consistency check rather than spatial validation (pp. 31, 33–34).

Critical weaknesses

W1. The comparison does not isolate parameterization from objective and optimization choices

NeTMY adds a mean-normalized noise-map loss and a direct-density proxy, and changes the primary fidelity in the fine stage (Appendix E.4, p. 25). The free-density baselines use different regularizers and optimization schedules (Appendix F.2, p. 28). Table 3 (p. 7) removes components cumulatively, so it cannot independently attribute gains to each mechanism. Moreover, the supervised baselines deliberately train on dense scenes and test on sparse scenes (Appendix F.9, pp. 32–33); their failures establish that shift, not general inferiority of amortized reconstruction. A matched-objective free-density or neural-prior comparison is needed for the claimed parameterization explanation.

W2. Joint density and Larmor recovery and physical validation are not sufficiently established

The fidelity sums the frequency axis before spatial normalization (Section 3.2, p. 4; Eq. 19, p. 20), while both density and a spatial Larmor field are unknown. The paper does not show how this compressed observation distinguishes the two fields, nor report a main Larmor reconstruction metric. The real-data check uses eight sites and a Gaussian ansatz, not a recovered spatial source map; F2 places only 1/8 inferred depths in the stated prior window, and the slope axis is closer to F1 (Section 5.5, p. 9; Appendix F.10, p. 33). The authors disclose these caveats, but they leave the physical scope narrower than full joint reconstruction.

Overall assessment

2 / 4. Weak rejection. The application and synthetic localization gains are interesting, but the current evidence does not adequately separate the neural-field contribution from objective and optimization choices, or establish the advertised joint physical reconstruction. Matched controls and a clearer account of spectral identifiability could change my recommendation.

Questions for authors

Q1. With the same fidelity, mean-normalized and density-proxy terms, Larmor handling, initialization protocol and sufficient optimization budget, do free-density solvers still exhibit the same center-collapse gap? Please distinguish representation effects from the objective and schedule differences in Appendices E.4 and F.2 (pp. 25 and 28), ideally using the primary localization metrics rather than only cumulative MSE ablations.

Q2. What identifies the Larmor field after the frequency summation in Eq. 19 (p. 20)? Please state the identifiability assumptions and provide recovery error on the source support. Appendix B.4 (p. 17) gives an exact convolutional form of F3, and Table 14 (p. 34) reports a small forward-evaluation cost relative to a solve. Would inversion using F3 and the full frequency-resolved observations change the density and Larmor results?

Q3. What physical conclusions survive the mixed real-data checks in Appendix F.10 (p. 33)? In particular, how should the 1/8 depth-window agreement and the slope favoring F1 be interpreted, and which calibration uncertainties could explain them? Clarifying this scope would affect how much weight I assign to the physical-fidelity claim.

Reviewer_vkXUOpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
1
Soundness
1
Read review
Paper summary

The authors introduce a per-measurement approach for a nonlinear inverse problem in quantum sensing, in which a coordinate network represents the unknown fields and is fitted to each measurement through a differentiable forward operator. They argue that free-density solvers collapse toward the center of the domain under a more accurate forward operator, and that their network parameterization avoids this collapse by filtering the gradient. Experiments use 512 simulated 64 by 64 scenes and a comparison of the forward operators on published measurements.

Critical strengths

I appreciate that the authors discuss the inverse-crime risk, report the cases in which their method underperforms, and release their code.

Critical weaknesses
  • The motivation for a per-measurement solver is the lack of paired training data, yet all reconstruction results are simulated and the simulator is cheap. The supervised baselines are trained on dense scenes that the authors themselves call out of distribution for the sparse test scenes, so their failure is expected. In addition, the benchmark data come from a simulator that differs from the more accurate inversion operator only in where one factor of the forward model is evaluated, which is close to an inverse crime.

  • The theoretical explanation does not describe the solvers as they were run. The network has about a hundred times more parameters than the grid has pixels, so the rank bound equals the number of pixels. The argument also assumes that free-density solvers take standard gradient steps. However, Tikhonov and the alternating direction method of multipliers are run with Adam.

  • The comparison does not isolate the parameterization. In its second stage the authors' method replaces the max-normalized fidelity, which according to the authors contributes to the collapse, and it runs about twice as many iterations as the main baselines.

  • The computational cost and the statistical support do not match the claims. The method takes minutes per 64 by 64 scene, 25 to 700 times the time of the free-density solvers. The claim that the method gives the best localization rests on 95% intervals from three seeds.

Questions for authors
  • Given that generating training pairs and training a network takes about six minutes, why not train the supervised baselines on the benchmark's own scene distribution? Can author apply the method to real measurements?

  • Could the authors run a free-density solver with the same objective and budget as their method and a traditional preconditioner? If this solver avoids the collapse in seconds, what does the neural field add?

  • How does the cost grow with the grid size in the proposed method? Does the method scale to realistic problem sizes?

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

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