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Paper summary
This paper presents PhosInv, a method that jointly optimizes electrode placement and stimulation patterns for visual cortical prostheses. This work differentiably reimplements a prior phosphene simulator, enabling end-to-end optimization of both placement parameters and a conditional selection network. Based on this simulator, PhosInv achieves higher predicted quality than per-target Bayesian optimization baselines.
Critical strengths
This work try to connect the previously separate problems of electrode placement and selection, bringing the visual cortical prosthesis closer to realistic device constraints. The differentiable simulator may also support further research on electrode implantation and selection strategies.
Critical weaknesses
The experimental results are limited: (1) PhosInv is trained with access to the simulator, potentially biasing the comparison against BO methods. (2) The realism of the differentiable simulator is unverified, yet all main results depend on it. (3) Whether the jointly optimized placements are individually optimal is not assessed.
Overall, only Table 1 is presented in the main text, providing insufficient support for the conclusions.
Questions for authors
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Does PhosInv’s reliance on the simulator during training cause overfitting, making the comparison against BO unfair when both are evaluated on the same simulator?
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How is the biological realism of the modified simulator validated?
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Could BO be optimized on the differentiable simulator before comparison, or could more baselines be added? This would allow a more systematic evaluation of PhosInv.
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Are the jointly optimized placements and selections also individually optimal? If not, what specific improvement does joint optimization bring to each component?
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The paper compares PhosInv on GPU against BO on CPU. Has a GPU-based BO been tested? Such a comparison would be fairer.
3 comments
I thank the authors for the additional experiments, which ensure a fairer comparison by employing the same simulator. However, fixing the the simulator undermines the paper's core innovation: the joint optimization of placement and selection. Therefore, I maintain my original score.
Reply to Reviewer qfkk
Thank you very much for reading our response and for acknowledging that the comparison is now fairer. We would like to clarify one point, because we believe it concerns how the change in the revision is described rather than the evidence itself.
The revision does not alter the simulator; the submitted version did. To make placement differentiable, the submitted version trained through a smoothed reimplementation that averaged pRF properties over nearby voxels. The revision uses the reference simulator of van Hoof et al. (2025) as published, without modification. Under that simulator, the gains of the jointly learned placement reverse (Sec. 6.5, Fig. 3).
The joint problem is unchanged; only the solver changed. Eq. 3 still optimises one shared placement and one stimulus-conditional selection policy for a single objective over the target distribution. We regard this formulation, rather than any particular solver, as the core of the paper. The submitted solver, gradient descent through the smoothed surrogate, learned gains that do not exist in the original simulator. The revised solver addresses the same problem under the original simulator: it searches the placement once per hemisphere and learns the selection through the exact renderer.
An additional result suggests that the two variables remain coupled under the original simulator. We repeated the placement search, scoring each candidate placement with per-target selection in the loop rather than with all contacts active. Under per-target mask search at the shared placement, the placements found this way are better than the placement used in the paper in 19 of 20 hemispheres (letter −0.066, geometric −0.059; seed SD 0.008). This suggests that the shared placement should be chosen for the selection policy, and that this can be done without smoothing the simulator. We will add this experiment to the final version.
We hope this clarifies that the revision keeps the joint formulation and changes only the way it is solved. Thank you again for your time and for the questions that led to these experiments.
Response to Reviewer qfkk
Thank you very much for your review. Your first question turned out to be the most important one for this paper. The overfitting you suspected was real. We found it, traced its cause, and revised the method on that basis rather than defend the submitted joint-learning result. The table summarises what we did for each of your concerns, and short answers follow.
Q1 (overfitting from simulator access). In the submitted version the model was trained through a smoothed reimplementation that averaged pRF properties over nearby voxels. With this averaging about 995 contacts per placement count as valid instead of about 462, and the jointly learned model exploited it. Rescored under the reference simulator, it is worse than BO in all six hemispheres (Sec. 6.5, Fig. 3). We therefore no longer learn the placement through the smoothed renderer. All methods are now fitted and scored under the same reference simulator, on held-out targets, and the selection network is trained through that simulator, which at a fixed placement is an exact sum of single-contact images.
Q2 (biological realism). We do not claim biological validation of the simulator. Our revision instead removes simulator mismatch as a comparative confound: all methods are now fitted and evaluated under the same published reference simulator of van Hoof et al. (2025), without modification. Biological validity remains an explicit limitation (Sec. 7).
Q3 (BO on the same simulator and more baselines). Under one reference simulator, learned selection beats per-stimulus BO in 20/20 hemispheres of 10 subjects (letter -0.140, geometric -0.138; Sec. 6.1, Table 1), including the 10 left hemispheres, where both methods search identical placement bounds. The benchmark compares 14 methods. We also trained a published learned stimulus encoder (HNA, Granley et al., 2022) in place of our CNN on the six original hemispheres. It matches our CNN and beats BO in 6/6 (Appendix E, Table 8), so the result does not depend on our encoder.
Q4 (whether placement and selection are each optimal). A 2x2 analysis separates the two. Once contacts are selected per target, refitting the placement per target improves the loss by only 0.02 to 0.05, while selection improves it by 0.28 to 0.32 (Sec. 6.3, Appendix I). For selection, a per-target mask search at the shared placement serves as a strong search reference (not a guaranteed optimum). Our network is within 0.052 of it on letters and 0.002 on geometric targets.
Q5 (GPU-based BO). We ported the whole BO objective to the same GPU, verified it against the original code to within 4e-8, and reran BO on 72 targets. A search still takes 121 s per target, because 99% of the time is spent in the Gaussian-process optimiser and not in the simulator. Our forward pass remains about 30,000 times faster on the same GPU (Sec. 6.4, Appendix K).
Main text containing only Table 1. The main text now also has three figures: the method overview (Fig. 1), per-hemisphere differences from BO (Fig. 2) and the renderer ladder (Fig. 3).
We hope these experiments address your concerns, and we would be glad to run any further experiment you consider necessary.