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- 2
- Confidence
- 3
- Informativeness
- 2
- Presentation
- 3
- Soundness
- 2
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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
- 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.
- 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
- 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.
- 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.
- 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.
- 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.
- 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.
- 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
- 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?
- 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?
- 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.
- Can the main 4× tables include or clearly reference the three-seed Toronto PSNR results and label the metrics reported only for seed 618?
- 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?
- 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
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.
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:
± 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=I generally, Qy is approximate back-projection.
Q3. Baselines and efficiency
SfmSR ×4 uses the protocol-compatible official λ=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:
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:
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 tR and sampled times. Loss families/coefficients match, but zt−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.