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Withdrawn from ICLR 2027

Spatial–Frequency-Guided Progressive Flow Matching for Accurate 3T-to-7T MRI Synthesis

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

Synthesizing 7T-like images from 3T MRI enhances anatomical clarity and expands the utility of existing 3T datasets. However, since fine tissue details and high-frequency noise occupy similar spectral bands, unconstrained high-frequency enhancement tends to amplify noise and introduce artifacts, whereas excessive smoothing obscures delicate boundaries. Consequently, leveraging source image structures to constrain local detail enhancement remains a major challenge in cross-field synthesis. To address this, we propose a spatio-frequency-guided progressive conditional flow matching framework. By integrating spatial and frequency-domain representations, our approach employs a multi-band generation strategy to schedule updates across distinct frequency bands. This conditions local detail refinement directly on the source structure, enabling adaptive, sequential enhancement. Experiments on paired datasets demonstrate that our method achieves superior synthesize performance in just 5 inference steps, significantly improving pixel-level reconstruction quality and reducing high-frequency error relative to the standard flow-matching baseline.

Primary area:
applications to computer vision, audio, language, and other modalities
Keywords:
3T-to-7T MRI synthesis, flow matching, spatial-frequency modeling

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

This paper studies paired 3T-to-7T brain MRI synthesis with a source-initialized conditional flow model. It introduces separate schedules for low-, mid-, and high-frequency changes, residual refinement moderated by learned source-based support maps, and evidence-weighted endpoint losses applied to a five-step rollout. The support targets are constructed from paired spatial and frequency agreement during training. Experiments use 80 subjects from four data sources, including 16 held-out subjects, and report reconstruction metrics, inference-stage interventions, computational costs, and a two-subject hippocampal segmentation analysis.

Critical strengths
  1. The motivation is specific and relevant: high-frequency energy alone is an unreliable proxy for subject-specific anatomy. Combining source spatial and frequency cues to regulate refinement is a reasonable response to this problem.

  2. The method clearly separates training-only paired supervision from inference inputs. Fixed evidence weights prevent the network from directly reducing terminal penalties through its own support predictions. Supervising the full rollout also matches the stated five-step inference procedure.

  3. The study uses subject-disjoint splits, compares eight methods, and reports computational costs and extensive settings. Table 1 shows a 0.792 dB PSNR gain and approximately 4.4% lower HFEN than RFlow. Table 5 reports 119.62 ms inference on an RTX 3090. The discussion appropriately acknowledges limitations of the anatomical validation.

Critical weaknesses
  1. The ablations do not isolate the claimed contributions. Section 4.3 and Table 2 intervene only at inference in the same trained checkpoint. Setting the support gates to one changes refinement amplitudes relative to training, so the resulting degradation does not establish that the proposed evidence is better than a simpler amplitude-control mechanism. The progressive schedule and endpoint supervision are not separately evaluated. Matched retrained controls, particularly uniform scheduling, constant or unguided support, and removal of endpoint supervision, are needed to distinguish the proposed mechanisms from additional capacity and reconstruction supervision.

  2. The evidence for improved anatomical detail is limited and mixed. In Table 2, removing the detail branch improves HFEN from 0.666 to 0.655 and SSIM from 0.847 to 0.853, while worsening LPIPS. This establishes a reconstruction tradeoff, but not more faithful anatomical detail. Section 4.4 evaluates only two subjects. The manual-reference comparison uses reference-assisted centroid alignment and increases volume error from 35.26% to 40.43%; the other comparison uses the same automatic segmenter on real 7T as its reference. These results provide limited independent validation of anatomy. The authors acknowledge these limitations, but the main interpretation and conclusion should consistently reflect the narrower demonstrated evidence.

  3. The base-model comparison is difficult to interpret. Appendix B.4 states that the backbone is initialized from a base flow-matching checkpoint and augmented with new branches, but Table 5 lists 35.70M parameters for base flow matching and 24.13M for the proposed model. The base configuration also uses five steps with five ensembles, whereas the proposed configuration lists five steps. Please clarify the relationship between this base, RFlow in Table 1, and the initialization checkpoint, and report a comparison with matched backbone and inference settings. The listed runtimes are useful, but these configuration differences prevent attributing the efficiency gain to the proposed mechanisms alone.

  4. The evaluation does not show variability across independent subjects. The test set contains 1,200 slices from 16 subjects, but only aggregate reconstruction metrics are reported. Subject-level paired differences and uncertainty estimates from the existing predictions would establish whether the improvements are consistent across subjects and cohorts. The slice count alone does not establish the reliability of the average gains.

  5. The comparison omits recent methods with public code that address the same task and failure mode. UniField [1] is cited but not compared, although it is a flow-matching method for 3T-to-7T enhancement that explicitly corrects high-frequency over-smoothing. FS-RWKV [2] performs spatial-frequency 3T-to-7T translation on the same UNC and multimodal 3T–7T datasets used here. Dedicated 3T-to-7T models [3, 4] and source-initialized bridge models that support few-step sampling [5, 6] are also missing, and the “VNet” row cites the segmentation V-Net rather than [3]. The method leads Table 1 only in PSNR, by about 0.38 dB, and trails other baselines on SSIM, HFEN, LPIPS, and MAE. The claim of superior performance therefore depends on the baseline set. Comparisons with at least [1], [2], and one bridge model at matched step counts are needed.

References: [1] Lin, Yiyang, et al. “UniField: A Unified Field-Aware MRI Enhancement Framework.” arXiv preprint arXiv:2603.09223 (2026).

[2] Lei, Yingtie, et al. “FS-RWKV: Leveraging Frequency Spatial-Aware RWKV for 3T-to-7T MRI Translation.” arXiv preprint arXiv:2510.08951 (2025).

[3] Cui, Qiming, et al. “7T MRI Synthesization from 3T Acquisitions.” International Conference on Medical Image Computing and Computer-Assisted Intervention. Cham: Springer Nature Switzerland, 2024.

[4] Gicquel, Malo, et al. “Converting T1-weighted MRI from 3T to 7T Quality Using Deep Learning.” arXiv preprint arXiv:2507.13782 (2025).

[5] Liu, Guan-Horng, et al. “I²SB: Image-to-Image Schrödinger Bridge.” International Conference on Machine Learning. PMLR, 2023.

[6] Zheng, Kaiwen, et al. “Diffusion Bridge Implicit Models.” International Conference on Learning Representations, 2025.

Questions for authors
  1. Are there matched-training results that isolate the effects of the progressive schedule or learned support gates while keeping the backbone, initialization, and endpoint supervision fixed?

  2. How should the anatomical-detail claim be interpreted given that the full model has lower LPIPS but higher HFEN than the variant without the detail branch in Table 2, and the manual-reference segmentation results are mixed?

  3. What is the relationship between RFlow in Table 1, Base flow matching in Table 5, and the checkpoint used to initialize the proposed model? Please explain the parameter-count difference of 35.70M versus 24.13M and the five-ensemble setting for the base model. Are reconstruction quality and latency results available for the base model with a single ensemble under matched evaluation settings?

  4. Can the authors report results for UniField (Lin et al., 2026), FS-RWKV (Lei et al., 2025), and one few-step bridge model such as DBIM (Zheng et al., 2025) under the same subject split and a matched number of network evaluations, and clarify whether the “VNet” baseline in Table 1 is the 3T-to-7T model of Cui et al. (2024) or the original segmentation V-Net?

Reviewer_LvigOpenReview ↗
Rating
1
Confidence
4
Informativeness
1
Presentation
2
Soundness
1
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Paper summary

Generating 7t images from 3t is an old topic but very useful. Not every center have overly expensive 7t scans.. the problem can be considered similar to superresolution in fact. The main problem is that in 3T and 7T images, correspondence is lost as you have to do scan twice. In super resolution one to one correspondence (voxel) is often sought if not one of those methods like cycle GAN is used. Anyhow, the problem is important and useful. 80 subjects from two public sources are used. images are processed slice by slice, that is the biggest concern later I explain below, and it does some arguably improvements in some metrics overall.

Critical strengths
  • clinically important topic
  • The motivating observation is sound. High-frequency magnitude does not establish anatomical correspondence.
Critical weaknesses

-The experimental evidence does not support any of the three claimed contributions, because the only ablations switch components off at inference in one trained checkpoint. That switch shows the detail pathway raises HFEN and lowers SSIM, while about 90% of the PSNR gain over rectified flow, and all of the HFEN gain, is present with the pathway removed. -The paper wins only one of five metrics and is 23% worse than its own flow-matching baseline on LPIPS. -The data protocol mixes two different 7T contrasts as a single target, quantizes per-slice-normalized images to 8 bits, and reports no variance or subject-level statistics. -we live in multidimensional world, 2D processing is old and not really acceptable not appreciating 3D anatomy.

  • bridge formulation is not discussed. Important: I2SB, DDBM, and BBDM (Li et al., CVPR 2023). These are the standard paired-translation generative frameworks.
  • baseline training details are absent. not reproducible paper, thus.
  • most importantly: technical novelty is low.
Questions for authors
  • On what statistical basis is the improvement over the flow-matching baseline described as significant?
  • The conclusion claims superiority in high-frequency error control. How is this reconciled with GDiff (0.636) and SelfRDB (0.662) having lower HFEN than the proposed method (0.666)?
  • Which experiment shows that the cited 2026 flow-matching methods (Imre et al.; UniField) oversmooth or distort fine boundaries, as the introduction states?
  • How 7T-space volumes become 320×256 slices (crop, pad, or resize) ?
  • why not compare with Qu et al., WATNet (MedIA 2020), and Bahrami et al. (TMI 2016) ?
  • how about VicTR ICCV 2025 that can be used for flow based translation and generation works. -How were q_L, q_M, and q_H chosen? How do linear-in-k or uniform schedules perform when retrained? -Box filters have large spectral sidelobes. How much do the bands overlap in frequency, and do Gaussian or wavelet bands change the results? -Because 53% of the high-band change occurs in the last step, what is the per-step error profile at inference? -scanner type and sequences are not mentioned. -How does one model handle MP2RAGE targets for UNC subjects and MPRAGE targets for Beijing subjects? -What do retrained variants without the multi-band schedule, without gating, and without the evidence-weighted terminal loss achieve?
Reviewer_ygEZOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper proposes a spatial–frequency-guided progressive flow-matching framework for paired 3T-to-7T MRI synthesis. The method combines frequency-dependent interpolation schedules, source-guided soft gates for local detail refinement, and evidence-aware endpoint supervision through a complete five-step rollout. The support gates are supervised using spatial and frequency agreement between paired training images. Experiments use 80 subjects from four cohorts, with subject-disjoint training, validation, and test sets. The method achieves the highest reported PSNR among the compared approaches and improves HFEN over RFlow using five inference steps. Additional evaluations include inference-stage component interventions and a preliminary hippocampal segmentation study on two test subjects.

Critical strengths
  1. Coherent design for controlling detail refinement. The combination of progressive frequency scheduling, source-conditioned support, and supervision through the complete inference rollout is well motivated for paired MRI translation (Sections 3.1–3.3). Using fixed agreement targets to weight endpoint losses also prevents the model from reducing those penalties simply by lowering its predicted support. These choices provide a plausible approach to balancing detail enhancement and artifact suppression.

  2. Promising reconstruction performance with few inference steps. The method achieves a PSNR of 23.970 dB, compared with 23.592 dB for SelfRDB and 23.178 dB for RFlow, while reducing HFEN by approximately 4.4% relative to RFlow (Table 1). It uses five updates, and Table 5 reports lower inference time than SynDiff and SelfRDB under common hardware settings. The explicit subject-level separation of training and test data strengthens the evaluation.

Critical weaknesses
  1. The contributions of the proposed components are not sufficiently isolated. Table 2 only disables components at inference using the same trained checkpoint; neither variant is retrained. These interventions demonstrate the trained model’s dependence on its components, but do not establish their benefits over appropriately trained alternatives. There are no controlled retraining comparisons separating progressive scheduling, source-dependent gating, and endpoint supervision. Since these components jointly constitute the claimed methodological contribution, the current evidence leaves their individual added value unclear.

  2. Evidence for improved anatomical detail remains limited. Removing the detail branch improves HFEN from 0.666 to 0.655 and SSIM from 0.847 to 0.853, although LPIPS worsens (Table 2). The downstream study includes only two subjects: manual-reference Dice increases slightly from 0.6503 to 0.6589, while volume error increases from 35.26% to 40.43% (Table 3). Agreement with automated segmentation of real 7T images is useful, but does not independently establish anatomical correctness. The authors acknowledge these limitations; nevertheless, the results leave the central benefit of more faithful detail refinement insufficiently demonstrated.

Questions for authors
  1. Request for evidence on component contributions: Can the authors provide controlled, retrained comparisons isolating the effects of progressive scheduling, source-dependent gating, and endpoint supervision, with matched backbone initialization and training budget? A comparison with spatially constant attenuation would be particularly useful for establishing the value of source-specific guidance.

  2. Clarification and evidence on anatomical fidelity: Can the authors report paired subject-level differences or uncertainty estimates for the main reconstruction comparisons on the existing test set? How should the improved PSNR and LPIPS relative to the no-detail intervention be interpreted alongside its better HFEN/SSIM and the mixed manual-reference segmentation results?

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

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