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Under review as a conference paper at ICLR 2027

When Motion Accuracy Misleads Downstream Imaging: Evaluating Learned Inverse Models under Slow-Time Near-Equivalence

Abstract

Learned inverse models often predict an intermediate physical state that a known downstream operator consumes, yet they are commonly trained, validated, and selected by state-space accuracy rather than downstream performance. We ask whether state-space accuracy preserves model ranking for the downstream task when the sampled measurement physics admits approximate equivalences between distant states. We study this in a controlled dynamic Wi-Fi synthetic-aperture simulator: a CNN infers target motion from complex channel-state information and coherent backprojection consumes the inferred velocity. At a 31-Hz diagnostic setting, a state-supervised CNN has lower velocity RMSE than a coherence-regularised CNN (0.149 versus 0.332 m/s) yet higher mean image-localisation error (0.474 versus 0.303 m), in all three training seeds. A sampling-rate diagnostic links the large-error modes to approximate bistatic range-rate branches, and an alias-aware range-rate error agrees better with downstream ranking across the tested estimators, although in a sealed selection experiment it chooses the same model as velocity RMSE. The reversal persists under a fixed update-indexed schedule without validation-based selection, for two architectures (paired image gains of 0.07 and 0.09 m on a sealed 3,000-scene test), under image-grid changes, on a disjoint-support speed holdout, and in an independent ray-traced digital twin for phase-dominated measurements; its size depends on the coherence weight. It weakens or disappears in geometries where few scenes approach the first sampled branch, with more in-distribution training data, at a fixed 100-Hz operating point under the stated speed prior, on a direction holdout, and when deterministic amplitude variation or 0-dB static multipath is present; oracle-motion and static-subtraction controls identify a separate clutter-dominated imaging boundary. These controlled synthetic results support a conditional evaluation principle: when sampled physics admits distant near-equivalent states, Euclidean latent-state accuracy should be reported alongside ambiguity-aware and downstream-task evaluation.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
learned inverse models, task-aware evaluation, physics-informed learning, coherent imaging, synthetic aperture imaging, Wi-Fi sensing, motion estimation, sampling ambiguity

Reviews

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1234this paper, Bottom 1%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.00 over 3 reviews, above 0% of the others.
Reviewer_XemjOpenReview ↗
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4
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Paper summary

The goal is to choose a learned inverse solver not based on the immediate output, but the downstream task accuracy. This paper gives a review of this phenomenon in a setting where motion is estimated using a CNN from complex channel-state information, where down the road the velocity is used for an output image. Paper provides no novelty. The contribution is analysis of this phenomenon, which is evident in the literature of inverse problems, diagnostics, and boundaries.

Critical strengths

NA

Critical weaknesses
  1. This challenge is not new. It is obvious that upstream accuracy is not always consistent with downstream task accuracy, something well-studied in decision-focused learning and TaskMet. The whole contribution or the message of the paper is to report ambiguity-aware error alongside state error and downstream error, standard in pose estimation for example.

  2. The mechanism is textbook radar.

  3. The paper presents empirical results showing a coherence-regularised learned estimator settles on alias branches. Then, the model ranking is reversed in one chosen sampling setting. No loss, no evidence, no metric is presented.

  4. This paper is out of scope for ICLR. What is presented is a general evaluation mechanism using one synthetic physical system. No other task is evaluated or presented.

  5. There is no method, no theorem or no novel phenomenon is presented. Paper has no novelty and contribution.

Questions for authors

NA

3 comments
AuthorsOpenReview ↗

Response to Reviewer Xemj

Thank you for the review. Several statements in it do not match the content of the paper, and we would like to correct them.

The review states that no loss, no evidence and no metric is presented. The paper defines a coherence-regularised training objective with a sweep over its weight (Section 3.2), a folded path-rate metric (Section 3.4), and reports paired results on sealed test sets with confidence intervals. The revision adds a five-seed confirmation on 5,000 new scenes, a width sweep of the same architecture, hardware-like perturbations, an energy-matched amplitude intervention, and 30 new runs with a direct imaging-loss baseline.

The review also states that the reversal is shown in one chosen sampling setting. The paper reports four sampling rates (15, 31, 62 and 124 Hz). The 31-Hz setting was not chosen after the fact: it is where the textbook branch spacing predicts the effect in advance, and the other rates serve as contrasts. At 62 and 124 Hz the secondary error mode disappears, as predicted (Figure 3).

On novelty: we agree that a gap between upstream and downstream accuracy is expected in general, and the paper cites decision-focused learning, TaskMet and symmetry-aware pose metrics. The natural remedy suggested by that literature is to train on the downstream task directly. We tested this (Appendix O). A differentiable image-localisation loss also pushes velocity estimates onto distant sampled branches, yet it localises worse than the coherence-regularised model in every main comparison, by 0.036 to 0.140 m. That endpoint supervision does not fix the problem is, in our view, not obvious from the prior work. The paper also shows at the scene level where the RMSE penalty and the localisation gain come from, and which measurement content switches the reversal on and off.

On the radar mechanism: the ambiguity itself is textbook, and we describe it as such. We use the textbook branch spacing as a prediction and test it against the learned errors. The observed first-branch medians (0.81 and 1.67 m/s at 15 and 31 Hz) sit at 0.96 of the predicted spacing. What radar theory does not tell us is whether and when a trained network lands on those branches, and how this changes model rankings. That is what the experiments measure.

On scope: the paper is an empirical study of how learned estimators should be evaluated and compared, which is an ML question, studied in a physical system where the mechanism can be controlled. We do not claim a new algorithm or theorem. A single physical system limits generality, and we state this as a limitation.

Given that the central factual points of the review do not correspond to the paper, we would ask the reviewer and the area chair to take this into account.

The authors fails to address any of the concerns raised.

  • There is no revision uploaded. The paper at the time of the response by the authors is the same as the uploaded one. Therefore, " The revision adds a five-seed confirmation on 5,000 new scenes, a width sweep of the same architecture, hardware-like perturbations, an energy-matched amplitude intervention, and 30 new runs with a direct imaging-loss baseline." all these promised experiments don't exist for the reviewers to assess.

  • "No loss, no evidence and no metric": It is not clear what is the contribution of the paper! Is it a new Loss, a new Metric, new evidence contrary to what is expected to happen? No new insight is given. To be perfectly clear, paper mentions that selecting by state accuracy can choose the worse image producing model, however, the one experiment that tests selection shows that the velocity RMSE picks the test-best imager in every seed. How can this be taken as a new loss or metric for choosing? or even The experiments shows against what the paper warns? Examples are:

  1. "....yet they are commonly trained, validated, and selected by state-space accuracy rather than downstream performance." (Abstract)
  2. "Such models are usually trained, validated, and selected with a state-space distance d_z (ˆ z, z), whereas deployment cares about dy (G(ˆ z), y)." (lines 048–049)
  3. "when coherent imaging is the endpoint, it alone can choose the worse image-producing model." (lines 463–464)
  4. "selecting among eight candidates per seed on 512 labelled selection scenes by velocity RMSE, folded range-rate RMSE, or direct image error chooses the same model, with zero paired sealed-test image difference and zero regret to the hindsight test-best candidate" (lines 373–376)

Result point contrary to what is motivated in introduction or the abstract. While the experiments does not support what is being motivated, no new loss or metrics is given, what is really the significance and novelty? "We do not propose a universally superior loss, a universal ambiguity metric, or a clutter-robust imaging system."

  • Where is appendix O exactly? There is only up to J!

  • Where does the paper exactly cite "symmetry-aware pose metrics"?

  • What paper promises is a general evaluation principle for learned inverse models, but test is only on "one controlled physical instantiation", no generalization to the cited systems, As an application paper, where no new insight or novelty ingredient is given, it falls below the line.

AuthorsOpenReview ↗

Revised PDF now uploaded; where each point is addressed

Thank you for the quick follow-up, and our apologies: the revised PDF had not been uploaded when we posted our responses. It is now on the paper page (33 pages). Below we list where each of your points is addressed, so that it can be checked directly.

Where the new material is. Appendix O (pages 32-33) is the direct imaging-loss baseline, and Section 5.5 (page 9) summarises it. Appendix L (page 28) contains the width sweep and the hardware-like perturbations, Appendix M (page 31) the five-seed confirmation on 5,000 new scenes, and Appendix N (page 32) the energy-matched amplitude intervention, summarised in Section 5.4 (pages 7-8). The symmetry-aware pose metrics (Hodan et al.) are cited in Related Work, page 3, with the reference on page 11.

On the selection result, we agree with you that the original text and the selection experiment were inconsistent, and we have corrected the text rather than the result. All four passages you quote overstated the claim and are no longer in the paper:

  • "commonly trained, validated, and selected by state-space accuracy" (old abstract): removed;
  • "usually trained, validated, and selected with a state-space distance" (old lines 048-049): removed;
  • "it alone can choose the worse image-producing model" (old lines 463-464): removed;
  • the selection paragraph (old lines 373-376) is rewritten in Section 5.5, page 8.

The selection experiment itself is unchanged and is now reported as a null result in four places: the last sentence of the abstract (page 1), the third contribution, "it distinguishes diagnostic agreement from selection utility" (page 3), Section 5.5 (page 8), and the conclusion (page 9). Section 5.5 also explains why it gives a null result. Picking one model from the pool only depends on the top of each ranking, and in that pool the best candidate (the residual CNN with alpha = 0.1) was best on both criteria, so every rule chose it.

The claim of the revised paper is narrower and is what the experiments show. When two learned estimators are compared, for example a coherence-regularised and a state-only CNN, velocity RMSE can order them the opposite way from image localisation. This holds on 3,000 sealed scenes for two architectures (Table 1, page 5; Figure 2, page 6) and reproduces with five seeds on 5,000 new scenes (Appendix M). Such pairwise comparisons are how training objectives are chosen in practice. The new imaging-loss experiment (Appendix O) shows that training directly on a differentiable image loss does not avoid the problem: that loss also selects distant sampled branches and localises worse than the coherence penalty. The contribution is therefore an evaluation finding and the conditions under which it appears, not a new loss or metric, and the paper says so.

On generality, we agree that a single physical system limits how far the result extends. The revised paper states this as a limitation in the introduction (page 3) and the conclusion (page 9), rather than claiming a general principle for all learned inverse models.

Reviewer_GLnQOpenReview ↗
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Paper summary

The motivating sentiment of this work is that, in the general area of learning-based physical inverse problems, the physical state estimation accuracy does not necessarily imply downstream inverse task performance. This work illustrates this phenomena for a very specific, simple inverse problem: moving target localization given channel state information (CSI). The authors use synthetic experiments with two model architectures to support the observation.

Critical strengths

The authors are very transparent about the limits of their approach. For example, in lines 363-366, α=0.1\alpha = 0.1 improves both velocity RMSE (physical state) and image error (downstream task), which does not support the rank reversal in the physical state and downstream task performance.

Critical weaknesses

-- The novelty of the main observation is unclear. At a high level, that tuning algorithms for “physical state estimation” rather than downstream processing tasks does not strike me as very novel. This type of observation is what motivates the entire construct of “end-to-end learning”. So the main question, in my mind, is what is observation can do for you for the particular problem of radar imaging. This is problem for which there are many established methods, both data driven and classical, and the paper does not use this “main observation” to advance the state-of-the-art.

We cite here a few established models on learning based channel estimation are directly trained and evaluated on the downstream radio frequency (RF) domain estimation, but note also that this literature is far more extensive. Representative examples are section 2.3 of [1], section V-A of [2], and section 4.4 of [3]. The distinction between physical state recovery and reliable RF domain prediction is also well documented. Examples are section IV-D of [4] and section 4.1 of [5]. As compared to the related works cited above, the novelty of the main observation from this paper that “lower physical-state estimation error does not necessarily imply lower downstream-task error” is unclear.

-- The experimental analysis is insufficient, and some results are presented poorly. Although the matched comparisons demonstrate a ranking reversal in physical state accuracy and the downstream target localization under the tested conditions, the experiments do not systematically establish how its occurrence and magnitude depend on model capacity. The experimental design uses two CNN architectures, each evaluated at one parameter count. Moving from CNN to ResCNN changes both the model architecture and the parameter count. Therefore, this comparison does not isolate the influence of model capacity, leaving its role in the observed reversal unclear.

For the presentation, one example is Figure 3(a) and (b). The caption states that “each point is one estimator,” but the individual gray points are not mapped to named estimators, making it difficult to inspect the comparison and understand which methods produce the reported ranking agreement. Another example is Figure 4(b), where the legend overlaps with the validation velocity RMSE curves.

-- The experimental design is too simplistic. The ranking reversal disappears when the ray-traced spreading-loss amplitude variation is retained (Table 9), indicating sensitivity to the phase-only measurement assumption. The paper does not demonstrate that the reversal survives a practically relevant acquisition pipeline, leaving the finding’s practical significance unclear.

References: Zhao, X., An, Z., Pan, Q., and Yang, L. (2023). “NeRF²: Neural Radio-Frequency Radiance Fields.” ACM MobiCom. DOI: 10.1145/3570361.3592527.

Wen, C., Tong, J., Hu, Y., Lin, Z., and Zhang, J. (2025). “WRF-GS: Wireless Radiation Field Reconstruction with 3D Gaussian Splatting.” IEEE INFOCOM, pp. 1–10. DOI: 10.1109/INFOCOM55648.2025.11044513.

Yang, K., Dong, G., Ji, S., Du, W., and Srivastava, M. (2025). “GSRF: Complex-Valued 3D Gaussian Splatting for Efficient Radio-Frequency Data Synthesis.” Advances in Neural Information Processing Systems, 38. Official proceedings.

Hoydis, J., Aït Aoudia, F., Cammerer, S., Euchner, F., Nimier-David, M., ten Brink, S., and Keller, A. (2024). “Learning Radio Environments by Differentiable Ray Tracing.” IEEE Transactions on Machine Learning in Communications and Networking, 2, 1527–1539. DOI: 10.1109/TMLCN.2024.3474639.

Liu, Z., Singh, G., Xu, C., and Vasisht, D. “FIRE: Enabling Reciprocity for FDD MIMO Systems.” ACM MobiCom ’21, pp. 628–641. DOI: 10.1145/3447993.3483275.

Questions for authors

As the main contribution of the work is unclear, I do not have questions that the answer from the author can materially change my evaluation to the paper in its current form.

1 comment
AuthorsOpenReview ↗

Response to Reviewer GLnQ

Thank you for the detailed review and the references, which we now cite and discuss (NeRF², WRF-GS, GSRF, Hoydis et al. and FIRE). These works evaluate RF-domain prediction as the endpoint. Our setting is different: the learned output is a physical motion state that a fixed imager consumes, and the question is whether comparing models by state error gives the right answer for the image. We do not propose a new imaging method.

Your main argument is that the observation is what motivates end-to-end learning, and is therefore not novel. We tested this directly (Appendix O). We trained the same networks with a differentiable localisation loss computed on the image formed from the predicted velocity, instead of the coherence term. Training data, initialisation, minibatch order and the 3,000 test scenes were kept identical to the original models (30 runs, design written down before running). With a loss weight of 0.5 or 1, this endpoint loss also pushes velocity estimates onto distant sampled branches (14-17% of scenes). Yet the coherence-regularised model localises better in every main comparison, by 0.036 to 0.140 m, and for the residual CNN the endpoint loss makes localisation worse than plain state supervision. A full-resolution version of the loss and a combination with the coherence term did not change this. In other words, end-to-end training on the downstream task does not resolve the problem here. The objective that serves the imager best is found only by evaluating the endpoint directly, not through state error and not through naive endpoint supervision. This result covers one family of image losses, and we say so in the paper.

On capacity: we added a width sweep of the same CNN (Figure 2e, Table 13). The reversal holds for widths 4 to 32, with paired localisation changes from -0.209 to -0.059 m, and it shrinks mainly because the state-only model improves with width. At width 64, one of the three seeds failed to train; we report it rather than drop it.

On the phase-only assumption (Table 9 in the original version): we added an experiment that changes only the slow-time amplitude of the echoes while keeping target energy, phase and noise fixed. The reversal appears at amplitude strengths 0 and 0.25 and disappears at 0.5 and 1 (Appendix N). The sensitivity you pointed out is now a controlled result that identifies which measurement content matters.

Both figure issues are fixed: the scatter plot is replaced by a table naming every estimator, and the overlapping legend is gone.

You wrote that no answer could change your evaluation because the contribution was unclear. Your central objection was that end-to-end training would make the observation trivial, and the new results show that it does not in this setting. We would therefore be grateful if you could take this into account in your assessment.

Reviewer_TTf9OpenReview ↗
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Paper summary

This paper studies when better motion estimates lead to worse downstream localization in a learned Wi-Fi synthetic-aperture imaging pipeline. At 31 Hz, the state-supervised CNN achieves lower velocity RMSE but higher image-localization error than the coherence-regularized model. The paper tries to connect this reversal to sampled phase ambiguity. It evaluates a folded range-rate diagnostic, and examines when the effect disappears.

Critical strengths
  1. The sampling-rate and geometry sweeps provide useful evidence for the proposed mechanism. The independent ray-traced simulator also strengthens the study beyond its original forward model.

  2. I appreciate the clear reporting of null and negative results, including the lack of model-selection benefit and the inconsistent effects of branch correction across geometries.

Critical weaknesses
  1. The folded range-rate metric does not improve model selection in the sealed experiment. It selects the same candidates as velocity RMSE and direct image error in every seed. Better rank correlation is useful, but a practical selection benefit remains undemonstrated.

  2. The reversal occurs within a limited regime. It disappears with weaker coherence regularization, more training data, higher sampling rates under the stated prior, and retained spreading-loss amplitudes in the digital twin. These results help define the phenomenon, but also limit its scope.

  3. All experiments use synthetic measurements of a single translating point target. The digital twin does not address hardware effects such as phase offsets and gain variation. Measured data would substantially strengthen the broader evaluation claim.

Questions for authors

See weaknesses

1 comment
AuthorsOpenReview ↗

Response to Reviewer TTf9

Thank you for the careful review, and for recognising the value of the sampling and digital-twin experiments and our reporting of negative results.

On model selection: it is correct that the folded metric did not change which model was selected, and the revised abstract states this directly. We checked why, and the reason is informative rather than a weakness of the analysis. Picking the best model from a pool only depends on the top of each ranking, and in all six seed/checkpoint cases the model with the lowest velocity RMSE also had the lowest localisation error (in five of them the residual CNN with alpha = 0.1, which does well on both). No metric could have picked differently there. The reversals occur further down the ranking, for example between alpha = 0 and alpha = 0.5, which is exactly the kind of comparison a methods paper reports. Over 32 related models, velocity RMSE orders 52.6% of model pairs differently from localisation, compared with 6.4% for the folded error. These pairs are not independent, so we present this as a post-hoc illustration, but it shows the practical risk of comparing models by velocity error alone.

On the limited regime: the conditions under which the reversal disappears are not a limitation of the study but its main result. We now test them directly. A new experiment changes only the slow-time amplitude of the echoes, keeping target energy, phase and noise fixed; the reversal appears at strengths 0 and 0.25 and disappears at 0.5 and 1. The main comparison also reproduces with five seeds on 5,000 new test scenes for both architectures. The weakening with more training data and at higher sampling rates, which you note, is part of the same picture: the paper identifies when velocity error is a reliable proxy for imaging quality and when it is not.

On synthetic data and hardware effects: we agree that measured CSI is the most important next step and state this clearly. To address the specific effects you raise, we added random per-snapshot gain errors (1 dB) and residual phase errors (0.2 rad), separately and together (Appendix L). The reversal remains in all three cases, with paired localisation changes of -0.066, -0.055 and -0.063 m. These are illustrative settings rather than measurements of a real receiver, so we do not present them as hardware validation.

Since your soundness concerns were described as minor or fixable, and the revision addresses each of them with new experiments, we would be grateful if you could reconsider your assessment.

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

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