Review Reports

Round 1

Reviewer 1 Report (New Reviewer)

Comments and Suggestions for Authors

The paper proposes DSConv+LR, an ultra-lightweight image super-resolution network derived from VDSR. The authors systematically evaluate three design choices: depthwise separable convolution (DSConv), a lightweight channel attention module (HAT), and a local residual connection (LR). The experiments show that HAT provides no performance gain in this setting (an honest negative result), while LR alone yields a 0.20 dB improvement without introducing any extra parameters. The final model contains only 49,217 parameters, achieving 35.21 dB on Set5, which is 99.7% of VDSR's performance. The paper emphasizes the effectiveness of minimalist design and honestly reports limitations in reconstructing fine textures.

My suggestions are as follows:

1、In Table2, the PSNR values for FSRCNN, CARN, and IMDN are taken from different papers with inconsistent training settings, data augmentations, and evaluation protocols. Direct comparison is therefore not rigorous. It is recommended to either re-implement these methods under the same training/test protocol, cite a unified benchmark, or explicitly state that "results under different protocols are for reference only."

2、The PSNR difference between DSConv+LR and VDSR is 0.12 dB, but no standard deviation or statistical significance test is reported. It is recommended to provide the mean and standard deviation over multiple runs and conduct a significance analysis to determine whether the difference is reliable.

3、The main results are evaluated only on Set5, lacking results on more general SR benchmarks such as Set14, BSD100, and particularly Urban100. It is recommended to report results on these datasets to assess the generalization capability of the model.

4、The design of the HAT module differs slightly from existing ones like ECA or SE, and it is not specified whether normalization is used, nor the order of activation functions. It is recommended to provide a detailed structure diagram, the mathematical formulation, and the activation functions used for HAT, and to explain why a lighter attention module (e.g., ECA) was not adopted.

5、The authors propose three hypotheses for why HAT is ineffective (insufficient training, too aggressive a reduction ratio, and DSConv already weakening cross-channel interactions), but no controlled experiments are conducted to validate these hypotheses. It is recommended to add experiments: (1) increase the number of training epochs; (2) use a reduction ratio of r=2; (3) apply HAT on top of standard convolutions (instead of DSConv) to verify whether HAT remains ineffective on a stronger baseline.

6、The number of LR blocks is fixed at N=10, but it is not verified whether more blocks (e.g., N=20) remain effective or lead to degradation. It is recommended to provide performance curves for different values of N (e.g., 5, 10, 15, 20) to verify that the local residual connection provides parameter-free improvement without causing overfitting.

7、The model is very small and prone to underfitting, but no regularization techniques (e.g., dropout, label smoothing, or advanced data augmentation like MixUp) are mentioned. It is recommended to either explain why regularization is unnecessary or to experiment with simple augmentations such as MixUp to see if PSNR can be further improved.

8、In Table 3, the NTIRE models are evaluated on a different dataset; therefore, direct PSNR comparison is not fair. Furthermore, the method for calculating FLOPs is not reported. It is recommended to re-implement or cite existing lightweight ×4 SR models on the same test set and provide detailed FLOPs calculation.

Author Response

Please see the attachment.

Author Response File: Author Response.pdf

Reviewer 2 Report (New Reviewer)

Comments and Suggestions for Authors

In this paper authors present an interesting study and proposal regarding application of deep learning for image super-resolution (SR) purposes, especially regrading significant challenges related to extremely high computationally expensive for resource-constrained devices (i.e. number of parameters and FLOPs needed). Authors here argue that by using and approach with the straightforward design competitive performance can be achieved with extreme parameter number reduction, in which classic VDSR (Very Deep Super-Resolution) architecture is used to evaluate three main design choices DSConv, HAT and  local residual connection (LR) with additional hybrid variants (some sort of ablative analysis). Thus chosen DSConv+LR architecture and designed VDSR architecture are compared with SOTA baselines. Based on the results authors advocates their minimalist approach with a honest reporting its strengths and limitations.

The paper is well conceived and written, with the strictly defined contributions (mostly supported by the presented numerical results), and with the high clarity and technical presentation level.

However authors are suggested to improve one important aspects of the paper:

• if the results provided in the referenced paper are not proper way to compare the performance of here proposed and baseline architectures, this should be provided in a more direct manner - by replicating prior work, followed by the transparent and correct performance comparison procedure. Current notice, which state that tree prior solutions have similar or in one case greatly superior performance but that this direct cross-paper comparison should be made with caution is not satisfying - especially when the experimental result are the sole guarantee or proof of the contribution.

Author Response

Please see the attachment.

Author Response File: Author Response.pdf

Reviewer 3 Report (New Reviewer)

Comments and Suggestions for Authors

This manuscript proposes a minimalist lightweight image super-resolution network, DSConv+LR, which combines depthwise separable convolutions with local residual connections. Using only about 7.4% of VDSR's parameters (49,217 in total), it achieves 99.7% of VDSR's reconstruction performance. I think the authors' writing style is honest and transparent, and the parameter efficiency is outstanding. However, there are some issues with the training set, the HAT failure analysis, and the PSNR differences. Below are my revision suggestions, and I hope they will be helpful to the authors.

1. In the abstract you say "Starting from the classic VDSR architecture, we systematically evaluate three design choices... Our model contains only 49,217 parameters about 7.4% of VDSR yet attains a PSNR of 35.21 dB on Set5 (x2), which is 99.7% of VDSR's performance (35.33 dB)." Then in the first paragraph of the Introduction you say "yet many state-of-the-art models remain too computationally expensive for resource-constrained devices." The abstract uses "competitive performance" and "99.7% of VDSR's performance" to position the model, but VDSR itself is already an outdated and weak baseline by current standards (2016, with an original Set5 x2 performance of 37.53 dB), and modern lightweight networks like CARN and IMDN outperform this paper's model by 2 to 3 dB. Being close to VDSR does not mean "competitive." I would like you to revise this claim.

2. Set5 only contains 5 images. The abstract directly uses Set5 numbers to support its overall conclusions, and you should acknowledge this limitation. The experimental section also lacks results on standard test sets such as Set14, BSD100, and Urban100. Furthermore, the comparison with NTIRE models is already acknowledged in a footnote as "not strictly fair," but this is not reflected in the abstract at all, and I think you should fix that.

3. You list "HAT is ineffective" as one of your contributions, but the Introduction admits that this issue "remains unclear," and the subsequent analysis only offers three unverified guesses (insufficient training epochs, too aggressive a reduction ratio, and DSConv weakening cross-channel interactions). Without supporting controlled experiments, packaging a result that may stem from a training configuration flaw as a "valuable observation for the community" is, in my opinion, not convincing enough.

4. Please add a citation to: Frequency Regularization: Reducing Information Redundancy in Convolutional Neural Networks. Compared with your method, both works share the core goal of compressing neural network models by structurally reformulating convolution operations to drastically reduce parameter counts while keeping performance loss acceptable. Frequency Regularization achieves model compression by retaining parameters in the frequency domain and eliminating high-frequency components, while DSConv+LR achieves a similar goal by factorizing standard convolutions into depthwise and pointwise convolutions. Both works start from a lightweight restructuring of the convolution operation itself rather than a large-scale redesign of network topology. The two are highly aligned in research motivation, methodological logic, and evaluation framework.

5. In Section 4.6 you say "Although the test sets differ, DSConv+LR demonstrates superior parameter and computational efficiency." Meanwhile, in Table 3, DSConv+LR reports 32.26 dB on Set5, while NTIRE models only report 27.01 to 27.43 dB on DIV2K_LSDIR. Again, Set5 is a very small test set with only 5 images and naturally higher image quality, so its PSNR is inherently higher than that of large-scale diverse datasets like DIV2K_LSDIR. Dividing the 32.26 dB on Set5 by FLOPs to get PSNR/FLOPs = 25.05, and then comparing that against NTIRE models evaluated on a completely different dataset at roughly 0.45 and 2.74, is statistically meaningless. Even though the authors acknowledge in a footnote that it is "not strictly fair," Table 3 still presents these numbers side by side, which can seriously mislead readers.

6. I think your dB/K efficiency metric (Efficiency = PSNR/Params) has a fundamental flaw. PSNR/Params is a nonlinear mixed-unit indicator that is highly sensitive to the absolute value of PSNR. When models differ by 2 to 3 dB in performance, this creates enormous numerical differences in the efficiency ratio that do not reflect real engineering value. More importantly, FSRCNN has a dB/K as high as 3.083, far exceeding DSConv+LR's 0.715, yet this is glossed over in Section 4.5 with "offers a different trade-off," without directly explaining why FSRCNN, which uses fewer parameters and has higher efficiency, is not recommended. I think you should reconsider this more carefully.

7. In Table 2, the Reference column for IMDN is listed as "[13] (2025)," but reference [13] corresponds to "ECA-Net" (Wang et al., CVPR 2020), not IMDN. IMDN actually corresponds to reference [10] (Zhang et al., CVPR 2018, which is RDN).

8. You say "The loss function is the mean squared error (MSE) between the network output and the ground-truth HR image." MSE (i.e., L2 loss) tends to produce overly smooth reconstructions, which is directly related to the "inability to fully capture complex texture patterns" that you mention in Section 5.4. You could discuss whether you tried alternatives such as L1 loss or perceptual loss, or at least connect this design choice to the texture reconstruction weakness of your model.

9. Set5 has 5 images in total, yet the authors only show the "butterfly" image, which has the smallest visual difference, while images with more discriminative results such as "woman" (a gap of 0.08 dB) are not visualized. I suggest showing a few more images.

Based on the above, I think while the manuscript does make contributions, there are still shortcomings that need to be addressed. I therefore recommend major revisions at this stage.

Author Response

Please see the attachment.

Author Response File: Author Response.pdf

Reviewer 4 Report (Previous Reviewer 3)

Comments and Suggestions for Authors

1. The author only used Set5 as the quantitative test set (5 images) in the experiment. This dataset has been widely considered to be too simple and performance-saturated, unable to reflect the true performance of the model in complex textures and multi-scale scenarios. It is suggested that the author supplement the PSNR/SSIM results of Set14, Urban109, or Manga109.

2. In model evaluation, only PSNR is reported, lacking SSIM, LPIPS, or subjective user evaluation. Modern SR research emphasizes the balance between fidelity and perceptual quality, and a single PSNR is insufficient to support conclusions of "competitive performance". The conclusion section lists Set14/Urban109 as "future work", but as a complete study, the lack of cross-dataset validation severely limits the academic value of the paper. It is recommended that the author add perceptual metrics such as LPIPS or NIQE to evaluate high-frequency texture restoration capabilities; provide a Pareto frontier plot of Params/FLOPs vs PSNR to visually demonstrate the efficiency trade-off. 

3. Table 1 only presents HAT with a single configuration (reduction ratio r=4), yet it acknowledges in Section 5.1 that "r=4 may be too aggressive, and attempting r=2 might be more appropriate." The conclusion that "attention is ineffective" is drawn without conducting a sensitivity analysis of hyperparameters, which is not methodologically rigorous. The impact of training strategies on the attention module (such as the attention module typically requiring a longer warm-up period or a smaller initial learning rate) is not discussed, and using only 80 rounds of fixed scheduling may not provide sufficient optimization space for HAT. It is recommended that the author add comparative experiments with HAT at r=2, 4, and 8 in the experiment, and attempt to adjust the learning rate scheduling (such as linear warm-up + cosine decay) or increase the number of training rounds to 120 to observe whether HAT is activated.

Author Response

Please see the attachment.

Author Response File: Author Response.pdf

Round 2

Reviewer 1 Report (New Reviewer)

Comments and Suggestions for Authors

1、Although LR and HAT were evaluated separately, it has not been verified whether LR can consistently improve performance across different depths. Please add a subsection or a supplementary figure/table to show the performance difference with and without LR under varying N, thereby validating its robustness.

2、The presentation format of the tables can be appropriately optimized.

Author Response

Please see the attachment.

Author Response File: Author Response.pdf

Reviewer 3 Report (New Reviewer)

Comments and Suggestions for Authors

I have carefully reviewed the authors' response letter and the corresponding modifications in the revised manuscript. The authors have significantly improved the quality of their work by clarifying the outdated baseline claims and extending their evaluation to include multiple standard datasets. They also improved the evaluation fairness by removing the misleading cross dataset comparisons and replacing the flawed efficiency metric with a clear Pareto frontier plot. Additionally, they successfully resolved the issues regarding the HAT mechanism by providing controlled ablation experiments, corrected the loss function details and provided more comprehensive visual examples.

I highly appreciate the authors' serious and thorough approach to these revisions. They have successfully addressed all of my previous concerns. I believe the current version of the manuscript has reached the standard required for publication. Therefore, I recommend this paper for acceptance.

I hope the authors continue their great work and keep making valuable contributions to this field! Finally, I would like to sincerely thank the Editor in Chief and the Associate Editor for their excellent support and guidance throughout the review process of this manuscript!

Author Response

Dear Reviewer,

Thank you very much for your thorough and constructive review, and for your positive recommendation of our manuscript. We greatly appreciate your valuable suggestions and the time you dedicated to evaluating our work. We are delighted that the revisions have met the required standard.

We are also grateful to the Editor in Chief and the Associate Editor for their excellent support and guidance throughout the review process. We will continue our efforts to make further contributions to this field.

Sincerely,
The Authors

This manuscript is a resubmission of an earlier submission. The following is a list of the peer review reports and author responses from that submission.

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

This manuscript proposes a method for early detection of apple Marssonina disease using hyperspectral imaging combined with a super-resolution reconstruction network (DGRCN) and transfer learning. The research is relevant and meaningful for precision agriculture and non-destructive disease detection. However, the manuscript suffers from limited novelty, insufficient experimental validation, and weak methodological justification. Several key components of the proposed framework are not rigorously evaluated, and the dataset is relatively small, which raises concerns about the robustness and generalization ability of the model.

1). Irregular spaces in the Abstract.

2). The introduction lists many applications of hyperspectral imaging technology in disease detection but does not specify the existing problems of existing research and cannot highlight the advantages of the proposed method.

3). Section 2.3 and Section 3.1 are both hyperspectral image preprocessing, and it is recommended to integrate them.

4). The spectral image range of the study is 900-1700nm, and only the spectral data of 1350-1650nm is retained. Whether it can prove the representativeness of the experimental results.

5). It is proposed to add some comparative analysis of existing studies to the discussion.

6). The serial number (1) does not appear in the conclusion.

7). The chart is not bolded in the article.

8). Figure 4, Figure 5, and Figure 6 have formatting problems.

9). It is recommended to add comparison experiments; The paper does not provide ablation experiments, how to demonstrate the contribution of each module.

10). The dataset has only 168 samples, and the categories are severely unbalanced (e.g., only 1 in Level 4). How can Level 4 be correctly classified, unbelievable.

 

In all, this manuscript lacks in scientific soundness. The writing, and formatting are disasters. The organization is quite poor. And I doubt the results.

Reviewer 2 Report

Comments and Suggestions for Authors

The document requires a complete review of grammar and formatting. Please review the underlined sentences in the attached document; ensure that there is a space between the word and the reference number in the citations. 

Please review the abstract, as it contains grammatical errors that make it difficult to understand.

Please review the sentences in lines 31 through 34, as they contradict each other. 

Hyperspectral systems are very expensive; review the statement in lines 36 and 37. 

Section 2.3.3 needs to be expanded; it is unclear how lesions are extracted from the leaves. 

Please include a justification for using PCA in section 2.3.4. The advantage of hyperspectral images over multispectral and RGB images lies precisely in their spectral resolution; when PCA is applied, this wealth of information is lost. This raises the question of why use hyperspectral data if, in the end, only four principal components. 

Check the formatting of the equations in sections 2.4.3 and 2.4.5 

Section 2 must include details of the implementation (model training and testing) to ensure the reproducibility of the results. For example: How was the data split into training and testing sets? What hyperparameters were used for the model? How was the optimization method selected? What was the learning rate? Among other details. 

In section 3.1.3, explain why only four components were considered.

Comments for author File: Comments.pdf

Reviewer 3 Report

Comments and Suggestions for Authors

The authors propose a method combining hyperspectral imaging with super-resolution reconstruction and transfer learning for early detection of apple brown spot disease, demonstrating significant application value, particularly in the field of agricultural intelligent sensing. However, the manuscript has several shortcomings that require discussion.

1. The core technologies used are simple combinations of existing methods: PCA (classical dimensionality reduction), VDSR/DnCNN (existing models), and transfer learning (conventional strategy), lacking clear structural or theoretical innovation. It is recommended that the authors clarify the "essential innovation" of DGRCN compared to VDSR/DnCNN, and add a network structure diagram (detailed to each layer) for comparison with state-of-the-art methods (such as ESRGAN and SwinIR).

2. The dataset is too small, containing only 168 samples, and the training/testing partitioning and cross-validation are not specified. The results (94% accuracy) lack statistical credibility. Validation with public datasets is lacking; all data is self-built, making it impossible to verify generalization ability. It is recommended that the authors add more data samples and open-source datasets to validate the model's generalization ability.

3. The comparison method is too basic, only comparing Bicubic, VDSR, and LapSRN. It lacks comparative experiments with current mainstream methods. It is recommended that the authors add mainstream models for comparison, such as EDSR, RCAN, and SwinIR.

4. The model evaluation metrics are not comprehensive enough, only using PSNR and SSIM. These metrics cannot demonstrate improvements in detection performance. It is recommended that the authors add classification evaluation metrics, as well as ROC curves/AUC, Precision, Recall, and F1-score.