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Under review as a conference paper at ICLR 2027

DirectSR: Rethinking Zero-Origin Residual Flow via Observation-Guided Endpoint Prediction for Remote Sensing Super-Resolution

Abstract

Remote sensing super-resolution requires both fine-detail recovery and strict spatial consistency with the observed scene. We revisit a zero-origin deterministic residual flow with target and linear path , for which the analytical velocity target remains constant and equal to R along the trajectory. This motivates direct endpoint recovery without explicit time-dependent residual transport. We propose DirectSR, which predicts the target residual through a single endpoint-predictor evaluation, conditioned on frozen multi-scale DINOv2 features, pixel-aligned differential responses, and an LR-consistency correction. We further study an optional candidate-aware refinement stage, DirectSR+. On Potsdam and Toronto 2×, DirectSR improves over a matched four-step residual flow by 2.4442 and 3.2632 dB, respectively. Under our unified evaluation protocol, DirectSR achieves the best PSNR and SSIM on Toronto 4× and ranks first on all reported structural metrics, while DirectSR+ achieves the best PSNR and SSIM on Potsdam and Toronto 2×. Final-candidate experiments further show that Stage-2 refinement is dataset dependent, supporting DirectSR Stage-1 as the default model. These results support direct endpoint recovery as a simpler alternative to iterative integration in the deterministic paired residual formulation studied here, without extending this conclusion to stochastic flow, diffusion, or multimodal generative models.

Primary area:
applications to computer vision, audio, language, and other modalities
Keywords:
remote sensing, image super-resolution, high-fidelity reconstruction, structural fidelity

Reviews

Among:
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1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_rTJPOpenReview ↗
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Paper summary

This paper studies paired remote-sensing single-image super-resolution using a deterministic residual-flow formulation. Given a bicubic-upsampled observation B and the target residual R = x_{HR} − B, the linear path r_{t} = tR has a constant analytical velocity target. Motivated by this property, the authors propose DirectSR, which predicts the residual endpoint directly rather than learning its evolution along a trajectory. The default Stage-1 model combines a residual encoder–decoder with frozen multi-scale DINOv2 features, six fixed differential responses, bounded residual prediction, and an approximate low-resolution consistency correction. An optional Stage-2 refiner produces DirectSR+. Experiments cover Potsdam, Toronto, and AID at 2× and 4× scales, with Toronto used exclusively for cross-region evaluation of the Potsdam-trained model. The matched comparisons favor endpoint prediction over the tested Flow configurations. These findings are useful for the deterministic formulation considered here, but should not be interpreted as evidence against flow matching or diffusion models more broadly.

Critical strengths
  1. Section 4.4 states that the two approaches share the backbone, observation conditions, data split, optimization budget, and loss family. Table 4 also tests several Flow step counts rather than relying on a single configuration. DirectSR achieves 41.8328 dB on Potsdam 2× and 37.1296 dB on Toronto 2×, exceeding the best tested Flow settings by approximately 2.09 and 3.03 dB, respectively. These are substantial differences within the evaluated setup.
  2. Table 13 includes three-seed Toronto 4× results, with a PSNR mean and standard deviation of 28.96672 ± 0.12341 dB. All three runs exceed the reported RCAN result of 28.71262 dB, although this alone does not establish statistical significance against RCAN. Tables 15 and 16 also show that refinement slightly reduces Potsdam PSNR while improving some perceptual metrics. Reporting these trade-offs gives a more balanced account of the method.
Critical weaknesses
  1. For the deterministic path r_{t} = tR, the analytical velocity target is constant along each training pair, making direct endpoint regression a natural baseline. Demonstrating its advantage in this setting does not establish that trajectory modeling is generally redundant, particularly for stochastic formulations intended to model conditional output distributions. The paper needs to distinguish more clearly between a finding about this particular construction and a broader methodological claim.
  2. Table 14 examines DINO conditioning, but comparable controls are missing for the six differential responses, residual bounding, and observation-consistency correction. Since these components are all part of the default model, the current results do not show which are necessary or how much each contributes. Matched ablations would also help distinguish the benefit of endpoint prediction from that of the surrounding architecture.
  3. Appendix A.6 states that Stage-1 losses are computed on the pre-correction image z, whereas evaluation uses the corrected output C = Q_{y} (z). This is not inherently problematic, but it leaves the contribution of the fixed correction unquantified. Results before and after correction are needed, along with an explanation of why the correction is excluded from the training objective.
  4. Table 13 reports Toronto PSNR and selected structural metrics across three seeds, but the full SSIM, LPIPS, DISTS, and FID comparisons remain based on seed 618. The paper identifies 618 as the default optimization seed, so there is no basis here to infer post-hoc selection. Nevertheless, the main tables should clearly distinguish single-run results from multi-seed estimates and prominently reference the available three-seed PSNR summary.
  5. Section 4.1 mentions the use of protocol-compatible official checkpoints for generative baselines, but readers are not given a concise per-method account of training data, degradation assumptions, external pretraining, checkpoint sources, and selection criteria. These details matter when interpreting differences between methods trained under different conditions. Table 5 reports latency and memory only for DirectSR and DirectSR+, which is insufficient to establish an efficiency advantage over the main baselines.
  6. Geographic non-overlap is verified for Potsdam, but the released Toronto and AID files lack sufficient coordinates or source-scene identifiers to establish the corresponding independence claims. This does not demonstrate overlap or leakage; it limits what can be verified. Likewise, the reported benchmarks do not establish robustness to other sensors or real-world degradation processes. These limitations should be stated explicitly.
Questions for authors
  1. Can you provide matched Stage-1 ablations for DINO conditioning, the six differential responses, residual bounding, and the observation-consistency correction, keeping the remaining architecture and training protocol fixed?
  2. How do the principal metrics change before and after applying Q_{y}? Why are the training losses computed before correction when the corrected image is used for evaluation?
  3. For the baselines in Tables 1–3, which were retrained and which used official checkpoints? Please summarize their training data, degradation assumptions, external pretraining, checkpoint sources, and checkpoint-selection rules. Same-hardware runtime and memory comparisons would also be useful.
  4. Can the main 4× tables include or clearly reference the three-seed Toronto PSNR results and label the metrics reported only for seed 618?
  5. Beyond the trajectory objective and number of model evaluations, what implementation differences remain between DirectSR and the matched Flow control? In particular, are conditioning inputs, residual bounding, correction, loss terms, parameter counts, and checkpoint-selection criteria identical?
  6. What geographic and sensor provenance is available for Toronto and AID? Please clarify which aspects of split independence can be verified and which remain uncertain because of missing metadata.
2 comments

Thank you for the questions. The completed controls address the following points.

Q1. Component ablations

The ×4 controls use seeds 618/2025/3407, fixed splits, global batch 8, 100k updates, and validation selection. Full-minus-control PSNR differences are:

ControlPotsdam, dBToronto, dB
DINO removed+0.09086±0.00751+0.08432±0.00109
Differential inputs zeroed+0.00220±0.00355+0.00114±0.00094
Residual bound removed−0.00035±0.00067−0.00735±0.00175
Gate fixed to 0.525+0.07780±0.00384+0.20014±0.00030

± denotes sample SD over three training seeds. No-differential retains the architecture/gradient loss. DINO improves all five principal metrics in every seed on both datasets. Differential effects are small; bounding has no consistent PSNR benefit. The gating control does not isolate spatial adaptivity from learning gate magnitude.

Q2. Correction and loss placement

For the three submitted checkpoints, mean pre→post PSNR is 34.1243→34.1273/28.9637→28.9667 dB on Potsdam/Toronto. LR-consistency L1 decreases 37.33%/48.33%. SSIM/DISTS/FID improve; LPIPS and some structural errors slightly worsen.

Pre-correction losses directly supervise the learned endpoint. Moving pixel, gradient, and LR image losses after correction/clipping, while retaining the residual loss, gives post-loss-minus-default PSNR −0.00035±0.00423/−0.01049±0.00414 dB across three seeds. The Potsdam effect is near zero and reverses in one seed; the default has higher PSNR in every Toronto seed. This supports retaining the default here without claiming optimal loss placement. Since DU≠IDU\ne I generally, QyQ_y is approximate back-projection.

Q3. Baselines and efficiency

SfmSR ×4 uses the protocol-compatible official λ=0.1\lambda=0.1 checkpoint; ×2 uses retraining. Full pretraining/resume histories and mappings to every submitted deterministic-baseline quality row remain unresolved. We will flag unavailable provenance.

Three-seed Potsdam-paired RCAN training matches data exposure and selection rules. Direct-minus-RCAN PSNR is +0.0272±0.0236/−0.0933±0.0373 dB on Potsdam/Toronto. Toronto reconstruction/structural metrics favor RCAN; mean perceptual metrics favor Direct. Their L1/Adam and composite-loss/AdamW recipes differ.

Same-hardware ×4 GPU-input-to-output measurements include conditioning, correction, and refinement:

MethodB1 msB1 peak MiBB16 images/s
DirectSR17.263508.106109.511
DirectSR+32.613528.05355.457
EDSR18.004301.17495.362
RCAN72.89293.774117.897
SwinIR30.279115.27056.152

Settings: one RTX 3090, 64→256, FP32 network computation, TF32/autocast off, 10 warmups/50 calls. Memory is peak allocated memory. Plus retains its FP16 candidate boundary and second DINO extraction. Loading, H2D, I/O, and metrics are excluded. The HAT-labelled snapshot is not certified as canonical HAT.

Q4. Multi-seed reporting

We will distinguish seed-618 entries from three-seed summaries. Unified evaluation of the submitted checkpoints gives:

Dataset ×4PSNRSSIMLPIPSDISTSFID
Potsdam34.1273±0.0581.86651±.00070.26808±.00178.17151±.0010452.3989±.1376
Toronto28.9667±0.1234.85873±.00236.20096±.00411.16632±.0017487.3862±.5769

FID is computed per complete per-seed test set before aggregation. This group is separate from matched controls; image bootstrap does not measure training-seed or geographic uncertainty.

Q5. Direct/Flow implementation

The controls share network, conditioning, bound, gate, optimizer, split, budget, and validation-PSNR rule: 91.851M total/5.269M trainable parameters. Direct trains at state/time zero; Flow uses target-derived tRtR and sampled times. Loss families/coefficients match, but zt−x=(1−t)(v−R)z_t-x=(1-t)(v-R) makes image supervision time-dependent. Training has no solver unrolling. Validation uses four Flow steps versus one Direct call.

One-step inference is identical for identical weights; compared models are independently trained. With 50% exact-zero supervision, Direct's ×2 advantage is 0.0841/0.1436 dB at one call and 0.0847/0.1748 dB against four-step final-only-corrected Flow. Starting-state exposure and correction placement affect the gap; this does not establish general trajectory redundancy.

Q6. Geographic/sensor provenance

Potsdam geographic non-overlap is verified. Toronto/AID lack patch coordinates/source-scene identifiers sufficient to certify independence. Duplicate checks cannot establish scene independence. Toronto is excluded from training, validation, and selection; missing geographic/sensor metadata remain a limitation. Single-seed noise/blur tests measure sensitivity, not real-degradation or cross-sensor robustness.

Overall, the authors have addressed several of my concerns through additional ablations and quantitative analyses. The new controls show that DINO conditioning is consistently beneficial, while differential inputs provide only marginal gains and residual bounding shows no consistent PSNR benefit. The pre- and post-correction results and loss-placement experiment largely clarify the contribution of the fixed correction and reduce my concern about the training-inference difference. However, the limited effects of some components leave their necessity insufficiently justified. The authors also clarify that DirectSR and the matched Flow control share the network, conditioning, residual bound, gate, optimizer, data split, training budget, parameter count, and checkpoint-selection rule. This makes the comparison easier to interpret. However, the two settings still differ in training-state exposure and time-dependent image supervision, while correction placement also affects the measured gap. Because the Direct-versus-Flow comparison is central to the paper, these remaining differences make it difficult to attribute the improvement entirely to endpoint prediction. The current evidence therefore supports the specific deterministic formulation studied here, but not a broader conclusion about trajectory learning. Finally, the multi-seed results, RCAN comparison, and same-hardware measurements improve the completeness of the evaluation. Nevertheless, baseline provenance remains incomplete, the HAT-labelled snapshot is not confirmed to be canonical, and the lack of geographic and sensor information for Toronto and AID still limits claims about cross-region, cross-sensor, and real-degradation generalization. Overall, while the rebuttal strengthens the paper and alleviates several of my concerns, the main methodological and comparability issues have not been fully resolved. Therefore, I have decided to maintain my original rating.

Reviewer_VTJJOpenReview ↗
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Paper summary

DirectSR studies paired remote-sensing super-resolution through a deterministic residual path, r_t = tR, where R is the HR image minus a bicubic reconstruction. It replaces trajectory integration with an independently trained endpoint predictor. The three-scale residual network combines frozen DINOv2 features, six observation-derived differential channels, a bounded/gated output, and approximate LR back-projection. DirectSR+ optionally refines a frozen Stage-1 candidate. Experiments cover separately trained 2x and 4x settings on Potsdam and AID, with Toronto used exclusively for cross-region testing of Potsdam-trained models. The strongest result is Toronto 4x; performance elsewhere is competitive rather than consistently best.

Critical strengths
  • A clearly delimited empirical comparison. The paper acknowledges that residual regression and single-pass inference are established ideas and restricts its flow conclusion to the deterministic zero-origin formulation. Table 4 compares independently trained endpoint prediction against 1/2/4/8-step flow inference with the stated matched backbone, conditioning, optimization budget, and loss family. DirectSR improves over the best tested flow setting by 2.0892 dB on Potsdam 2x and 3.0332 dB on Toronto 2x. Full-pipeline comparisons give smaller gaps: the reported DirectSR+ means exceed flow plus refinement by approximately 0.27 and 0.44 dB, respectively (p.24, Table 18). These controls provide useful evidence of the endpoint model's performance within the studied formulation.

  • Positive cross-region and semantic-conditioning evidence. Toronto 4x PSNR is 28.96672 ± 0.12341 dB across three optimization seeds, and all three runs exceed the reported RCAN result of 28.71262 dB (Table 13). The default seed also leads every structural metric in Table 2. Table 14 supplies three-seed DINO ablations: average gains are 0.03557 dB on AID 2x and 0.13892 dB on Potsdam 4x, with all six paired-image bootstrap intervals above zero. These intervals quantify image-level variation for fixed trained model pairs.

  • Useful experimental transparency. Evaluation uses saved uint8 RGB outputs without border cropping; Appendix B.1 distinguishes pixel-duplicate checks from geographic-overlap verification. Appendix A.5 documents DirectSR's optimization and validation-based checkpoint selection. On the final Potsdam 4x candidate, both refiners lower PSNR despite improving perceptual distances (Tables 15–16). The manuscript appropriately distinguishes this experiment from the separate ablation candidate.

Critical weaknesses
  1. The matched-flow comparison leaves the source of the gap only partly resolved. As the paper acknowledges, intermediate states used in flow training contain target information, whereas inference begins from a zero residual (p.3, Section 3.1). The matched controls establish a performance advantage, and the one-step flow result shows that the gap cannot be attributed solely to error accumulation over multiple steps (p.9, Table 4). However, the relative contributions of training-state information, supervision near the starting state and trajectory-based inference remain unclear. Giving greater emphasis to training near the inference starting state, with other settings fixed, would help assess this explanation.

  2. The architectural explanation is only partly tested. The DINO ablation supports semantic conditioning (p.21, Table 14), but separate ablations are not reported for differential inputs, back-projection, residual bounds, or spatial gating. Removing these components would help assess their contributions. Appendix A.4 specifies the resizing operator used in the loss and correction; what remains unclear is how the fixed Potsdam/Toronto LR pairs were generated and how that process relates to the reported operator. Clarifying this relationship and testing sensitivity to degradation would strengthen the evidence for observation consistency.

  3. Baseline reproducibility and uncertainty limit the ranking claims. The main-table differences from strong deterministic baselines are often small, while Toronto's advantage is supported by three seeds (Tables 1, 3, and 13). However, the individual training configurations, checkpoint provenance and seed variability of deterministic baselines such as EDSR, RCAN, SwinIR and HAT are not documented at the same level as DirectSR's recipe in Appendix A.5. These details would help assess the comparisons. Potsdam already has three-seed results in Table 14; summarizing those existing runs under the main comparison evaluator would make their relationship to the headline results clearer.

  4. Comparative efficiency remains unquantified. Table 5 provides parameters, latency, memory, and throughput for DirectSR and DirectSR+, and Section 4.5 specifies the measurement protocol. The remaining need is a complete-pipeline comparison with deterministic baselines and matched flow. Table 5 measures 4x SR, whereas Table 4's flow comparison is at 2x; each timing comparison should therefore match input/output sizes and scale factors, as well as hardware, precision, and timing procedure. Conditioning, correction, and any refinement should be included.

Questions for authors
  1. Does giving the matched flow more training examples at or near its inference starting state change the performance gap when the backbone, loss family, and optimization budget are held fixed?
  2. Can you specify the deterministic baselines' configurations, training/checkpoint provenance, and seed variability, and summarize the existing Potsdam seeds from Table 14 under the main comparison evaluator?
  3. How were the fixed Potsdam/Toronto LR pairs generated relative to the specified bicubic operator? What changes when differential inputs, back-projection, residual bounds, and spatial gating are removed separately?
  4. Using Table 5's hardware, precision and timing procedure, can you report end-to-end latency, peak memory and throughput against the deterministic baselines and matched flow, at matched input/output sizes and scale factors? Please include conditioning, correction and any refinement used in each comparison.
1 comment

Thank you for the specific suggestions. We have completed controls on starting-state supervision, component attribution, baseline uncertainty, and inference cost.

Q1. Does starting-state supervision change the gap?

Yes, substantially. Uniform Flow, Zero-mixture Flow, and Direct share the backbone, observation conditions, split, global batch 8, 100k updates, and seeds 618/2025/3407. Zero-mixture uses 50% exact-zero and 50% uniform times. These controls use BF16 network evaluation and FP32 losses. Toronto is test-only.

At ×2, within-seed Direct-minus-Zero-mixture PSNR differences are:

Flow protocolPotsdam, dBToronto, dB
One call, one correction+0.0841±0.0051+0.1436±0.0082
Four calls, every-step correction+0.6625±0.0038+0.7551±0.0044
Four calls, final-only correction+0.0847±0.0051+0.1748±0.0080

All ± values denote sample SD across three training seeds. Correction-placement tests use fixed validation-selected weights and retain per-step clipping; no test-set reselection occurs.

Starting-state supervision and correction placement both materially affect the gap. It cannot be attributed solely to integration. Since zt−x=(1−t)(v−R)z_t-x=(1-t)(v-R), time sampling also changes effective image supervision; these effects are not fully causally separated. We will make this qualification central to the interpretation.

Q2. Baseline provenance and multi-seed evaluation

We completed Potsdam-paired RCAN training with the same split, global batch 8, 100k updates, three seeds, and validation-selection rule. Direct-minus-RCAN PSNR is +0.0272±0.0236 dB on Potsdam and −0.0933±0.0373 dB on Toronto. Toronto PSNR/SSIM and structural metrics favor RCAN; mean LPIPS/DISTS/FID favor Direct, although FID reverses in one seed. RCAN uses L1/Adam and Direct composite loss/AdamW, so this compares training recipes rather than architecture alone.

Unified full-test evaluation of the three submitted DirectSR checkpoints gives ×4 PSNR 34.1273±0.0581/28.9667±0.1234 dB on Potsdam/Toronto. SSIM/LPIPS/DISTS/FID have also been evaluated across these seeds. FID is computed per complete per-seed output set before aggregation. These checkpoints remain separate from the matched-control group.

The full pretraining/resume history and quality-row mapping of every submitted baseline remain unresolved. We will report verified configurations and flag unavailable provenance; seed uncertainty remains incomplete for baselines other than the documented RCAN comparison.

Q3. Components and fixed LR generation

Matched ×4 full-minus-control PSNR differences are:

ControlPotsdam, dBToronto, dB
Differential inputs zeroed+0.00220±0.00355+0.00114±0.00094
Residual bound removed−0.00035±0.00067−0.00735±0.00175
Gate fixed to 0.525+0.07780±0.00384+0.20014±0.00030
DINO removed+0.09086±0.00751+0.08432±0.00109

Differential inputs and bounding are not supported as necessary. Learned gating helps relative to the constant reference, without isolating spatial adaptivity from gate magnitude. Same-checkpoint correction adds about 0.003 dB while reducing LR-consistency L1 by 37.33%/48.33%.

The fixed Potsdam/Toronto LR-generation script/version remains unverified; the internal bicubic operator does not establish its provenance. In a single-seed synthetic test, LR noise SD 2/255 and 5/255 reduces PSNR by 1.561/5.532 dB on Potsdam and 1.092/3.906 dB on Toronto. These quantify sensitivity, not real-degradation robustness.

Q4. Complete-pipeline efficiency

The ×4 group uses one RTX 3090, 64→256 inputs/outputs, FP32 network computation, TF32/autocast off, 10 warmups and 50 timed calls. GPU-input-to-output timing includes conditioning, resizing, correction, and refinement:

MethodB1 msB1 peak MiBB16 images/s
DirectSR17.263508.106109.511
DirectSR+32.613528.05355.457
EDSR18.004301.17495.362
RCAN72.89293.774117.897
SwinIR30.279115.27056.152

Memory is peak allocated GPU memory. Plus includes its FP16 candidate boundary and second DINO extraction. Loading, H2D transfer, I/O, and metrics are excluded. The HAT-labelled audited snapshot is not certified as canonical HAT.

In the separate ×2 128→256 group, three independent process repeats give 64.216±0.286 ms for four-step Zero-mixture, 43.317±0.409 ms with within-call observation-feature caching, and 16.251±0.080 ms for Direct. Here SD is over process means. Cached Flow retains every-step correction; its timing is not assigned to final-only quality. Direct has a latency advantage over this multistep path, while RCAN's throughput and memory show that efficiency is metric-dependent. These two timing groups do not cover every method at both scales.

Reviewer_shNnOpenReview ↗
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Paper summary

This is a paper that looks at the direct endpoint residual prediction as an alternative to the specific deterministic residual-flow formulation for the remote-sensing super-resolution. The method named DirectSR combines a residual encoder decoder with the frozen DinoV2 features, and observation-derived cues, and an LR-consistency correction. It is also a second stage that is optional that refines the reconstruction. Using Potsdam, Toronto and AID at 2x and 4x for evaluation.

Critical strengths

First strength: They have a controlled comparison of the recovery formulation by matching the backbone, conditioning, and training-budget for comparisons and they also show substantial gains over the tested residual-flow variants, which then supports useful simplification within the studied setting. Second strength: They use a somewhat credible cross-region evaluation. Potsdam trained models outperforms the strongest reported conventional baseline on the Toronto 4x case across 3 training seeds, with the complementary structural metrics supporting the improved reconstruction fidelity.

Critical weaknesses

First weakness: They have a limited advance beyond the conventional direct SR, the large gains concern a very specific zero-origin flow control, while the improvements over the standard direct SR methods are very dataset dependent. Leaving the significance of the endpoint formulation uncertain. Second weakness: There is a lack of a complete component validation. The differential conditioning and LR-consistency correction lack isolated ablations, leaving their individual contributions to the observation-guided design unclear.

Questions for authors
  1. How does the zero-origin residual flow relate to the published flow based SR? Would be nice to specify it complete training objective and then the numerical integration scheme?
  2. Can you also separately ablate the differential conditioning and LR consistency correction under the settings to establish their individual contributions?
1 comment

Thank you for recognizing the controlled comparison and for identifying the questions about contribution scope and component attribution. We have completed additional controls addressing both.

1. Scope and relationship to flow-based SR

Direct residual regression is established. We will position our contribution as a controlled empirical study of endpoint prediction in a specified deterministic paired residual formulation. Let B=U(y)B=U(y) and R=x−BR=x-B. The path rt=tRr_t=tR is the residual-coordinate form of B+t(x−B)B+t(x-B), with pair-specific analytical velocity target RR. This does not imply a constant learned field or general trajectory redundancy. Our matched control studies this construction with shared architecture and budget; it does not reproduce the entire pipeline of a published flow-SR system. The conclusion does not extend to stochastic flow or diffusion.

2. Training objective and numerical integration

Define v=vθ(tR,B,t)v=v_\theta(tR,B,t) and zt=B+tR+(1−t)vz_t=B+tR+(1-t)v. The Flow objective is

LF=E[ρ(v−R)+0.5ρ(zt−x)+0.15G(zt,x)+0.20∥D(zt)−y∥1].\mathcal L_F=\mathbb E\left[\rho(v-R)+0.5\rho(z_t-x)+0.15\mathcal G(z_t,x)+0.20\lVert D(z_t)-y\rVert_1\right].

Here ρ(e)=mean⁡e2+10−6\rho(e)=\operatorname{mean}\sqrt{e^2+10^{-6}}; G\mathcal G averages L1 differences of normalized Sobel-X/Y and Laplacian responses. All L1 terms use mean reduction. Training uses one sampled time and one network evaluation per example, without solver unrolling. Uniform Flow samples tt uniformly on [0,1)[0,1).

Inference starts at r0=0r_0=0. For k=0,…,K−1k=0,\ldots,K-1:

r~k+1=rk+K−1vθ(rk,B,k/K),rk+1=Qy(B+r~k+1)−B,\widetilde r_{k+1}=r_k+K^{-1}v_\theta(r_k,B,k/K),\qquad r_{k+1}=Q_y(B+\widetilde r_{k+1})-B,

where

Qy(z)=clip⁡[0,1][z+U(y−D(z))].Q_y(z)=\operatorname{clip}_{[0,1]}\left[z+U(y-D(z))\right].

Thus, Euler updates are followed by approximate back-projection and clipping. Direct is independently trained at state/time zero. With z=B+R^z=B+\widehat R, its pre-correction loss is 1.5ρ(z−x)+0.15G(z,x)+0.20∥D(z)−y∥11.5\rho(z-x)+0.15\mathcal G(z,x)+0.20\lVert D(z)-y\rVert_1.

We also trained Zero-mixture Flow with 50% exact-zero and 50% uniform times, keeping the budget fixed. Across three matched seeds, Direct's ×2 PSNR advantage is 0.0841±0.0051/0.1436±0.0082 dB on Potsdam/Toronto at equal single-call inference. Against four-step Flow with final-only correction, it is 0.0847±0.0051/0.1748±0.0080 dB. These results show that starting-state supervision and correction placement materially affect the gap. Time sampling also changes effective image supervision because zt−x=(1−t)(v−R)z_t-x=(1-t)(v-R).

3. Isolated differential-conditioning and correction controls

Full and no-differential models use seeds 618/2025/3407, the same split, global batch 8, 100k updates, and validation-based selection. The latter zeros the six input channels while retaining the architecture and gradient loss. Each checkpoint is evaluated with correction disabled/enabled:

Differential inputsCorrectionPotsdam ×4 PSNRToronto ×4 PSNR
EnabledDisabled34.1885±0.005229.1029±0.0027
DisabledDisabled34.1862±0.001729.1016±0.0026
EnabledEnabled34.1913±0.005229.1059±0.0028
DisabledEnabled34.1891±0.001729.1047±0.0027

All ± values denote sample SD across three training seeds. Differential conditioning has a small effect here and is not supported as necessary for the observed advantage.

Separately, pre/post evaluation of the three submitted checkpoints reduces mean LR-consistency L1 by 37.33%/48.33% on Potsdam/Toronto, with approximately 0.003 dB PSNR gains. SSIM/DISTS/FID improve, while LPIPS and some structural errors slightly worsen. Correction is therefore a modest consistency adjustment, with metric trade-offs.

Finally, the matched three-seed ×4 comparison gives Direct-minus-RCAN PSNR of +0.0272±0.0236/−0.0933±0.0373 dB on Potsdam/Toronto. Toronto PSNR/SSIM and structural metrics favor RCAN; mean perceptual metrics favor Direct. Their loss/optimizer recipes differ. We will report this trade-off and limit the claim to competitive, protocol-dependent performance.

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

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