Improving the fine structure of intense rainfall forecast  by a designed generative adversarial network

Fang, Zuliang; Zhong, Qi; Chen, Haoming; Wang, Xiuming; Zhang, Zhicha; Liang, Hongli

doi:10.5194/gmd-18-9723-2025

Articles | Volume 18, issue 23

https://doi.org/10.5194/gmd-18-9723-2025

© Author(s) 2025. This work is distributed under
the Creative Commons Attribution 4.0 License.

https://doi.org/10.5194/gmd-18-9723-2025

© Author(s) 2025. This work is distributed under
the Creative Commons Attribution 4.0 License.

Articles | Volume 18, issue 23

Development and technical paper

|

08 Dec 2025

Development and technical paper |

| 08 Dec 2025

Improving the fine structure of intense rainfall forecast by a designed generative adversarial network

Zuliang Fang, Qi Zhong, Haoming Chen, Xiuming Wang, Zhicha Zhang, and Hongli Liang

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Final revised paper (published on 08 Dec 2025)
Preprint (discussion started on 27 Nov 2024)

Interactive discussion

Status: closed

CEC1:
'Comment on egusphere-2024-2888', Juan Antonio Añel, 27 Dec 2024

Dear authors,
I would like to point you out an issue regarding the code you have shared as part of your submitted work. I have seen in some pieces of code paths that point out to local systems, such as "/THL8/home/zhq/fzl/branch/forecast" that are not available in the assets that you have shared. I would kindly request you to double-check your code and fix these issues where they are relevant, paying special attention to share all the assets that are necessary to replicate your work (scripts, models, input and output data).
Thanks,
Juan A. Añel
Geosci. Model Dev. Executive Editor

Citation: https://doi.org/10.5194/egusphere-2024-2888-CEC1
- AC1: 'Code pipeline refinement', Zuliang Fang, 15 Jan 2025
  
  Dear Editor,
  
  Thank you very much for bringing this issue to my attention. Based on your valuable feedback and the journal's code requirements, I have reviewed and standardized the code format and supplemented the necessary information. You can find the updated materials at https://zenodo.org/records/14652556.
  If there are any further omissions or areas for improvement, please do not hesitate to let me know. I truly appreciate your guidance and will continue to make any necessary adjustments.
  Best regards
  
  Citation: https://doi.org/10.5194/egusphere-2024-2888-AC1
RC1:
'A review of "Improving the fine structure of intense rainfall forecast by a designed adversarial generation network"', Anonymous Referee #1, 08 Jan 2025

The paper presents an application of deep learning techniques, specifically U-Net and GAN-based models, to enhance short-term precipitation forecasting, with a focus on the fine-scale structure of intense rainfall events. The authors compare the accuracy of three numerical weather prediction (NWP) models against two deep learning techniques: a U-Net-based model (FRNet) and a GAN-based model (GFRNet). They use multiple evaluation metrics to assess the relative performances of these approaches. The goal is to evaluate the accuracy of predicting 3-hourly accumulated precipitation over the next 24 hours for a region in North China. The paper shows many metrics and concludes that GFRNet demonstrates significant operational value.

The paper deals with an interesting topic, related to improving the forecasting of the fine structure of intense rainfall. Moreover, it makes use of some current tools in deep learning, which seem promising for future operational use. However, I have two main concerns about the paper. The first one is the rationale of the model itself, as I do not understand how the fine structure of rainfall may be solely explained with the additional information (on top of the NWPs) provided to the GAN. The second one is related to the experimental design and the fairness of the comparisons and analyses provided. In my opinion, the paper requires an improvement of the rationale and the experimental design, as well as additional analyses before being considered for publication in a scientific journal.

Below, I provide more details about the issues that I observe with the work.

My main concern with the rationale of the paper is that it is not immediately evident how the information about Elevation, Latitude, Longitude, Cycle, and Lead Hour contributes independently to improving forecasts when much of this information may already be embedded in the NWPs. A mechanism should be presented or outlined to justify the gains in accuracy. If none exists, then all the required information about the fine structure of precipitation is already included in the original NWPs, and thus the methods presented are just extracting this information.

If this is the case, as I believe (although I may be wrong), there may be other alternative methods that could improve forecasting with reduced complexity. To verify this point, I suggest that the authors include additional models, such as SVMs or Random Forests, to test if simpler bagging methods with far fewer parameters could also improve forecasting accuracy. In my experience, basic machine learning methods tend to perform similarly to deep learning ones (in this kind of application) at a significantly reduced level of complexity. Including these additional comparisons may serve to justify whether a GAN is an optimal strategy and to show if the improvement in forecasting accuracy comes from the deep learning techniques or from the combination of different sources of information.

Using FRNet as a benchmark may not be entirely fair, as GFRNet is essentially an enhanced version of the same model with a more advanced training procedure. It would also be interesting to report training and inference times for all models used (I know that the authors have included part of this information in their manuscript).

Thus, with respect to my concern with the rationale of the paper, the authors should include additional simpler models to check if GANs are justified for their complexity level or if other simpler methods may work similarly. Additionally, they should provide some insight into why the improvement occurs. This point leads to my concerns with the experimental design.

My first concern with the experimental design is related to the limited amount of data used in the study. Using only four years of data may not be sufficient to fully verify the accuracy and robustness of the forecasting method. I understand that data limitations are difficult to overcome, but given the complexity of the models used, it is difficult to ensure that overfitting is not playing a role in the analysis. This concern is exacerbated by the fact that the original time series must be split into training, validation, and test sets.

Moreover, the initial data selection may bias the results. NWPs provide continuous forecasts, so alternative methods should ideally also deliver continuous predictions to ensure a fair comparison. If a heavy data selection procedure is implemented, the comparison may not be entirely fair to the NWPs.

A second concern with the experimental design is that I would have appreciated a clearer discussion in the methods' section about how the evaluation of accuracy was performed. Table 3 presents evaluation metrics and highlights the best and second-best performers. However, more attention should be paid to the differences. Are they significantly different? Or could all the methods (NWPs and nets) perform similarly given the amount of information used? What would be the expected distribution of the accuracy metrics? I am not fully convinced that part of the results are not an analysis of statistical fluctuations. Additionally, Table 4 seems to contradict the abstract, which states that "GFRNet outperforms all models in terms of Root Mean Square Error (RMSE)," but I may have missed something.

A third concern is related to the case studies, which I believe should be justified and presented in a more detailed way. This point may be related to my concern about the rationale of the paper: if a mechanism by which the GAN strategy improves the forecast is provided, then the case studies may focus on clear examples of this mechanism at play. Without this, I believe a general statistical evaluation would provide a clearer representation of the model's advantages. A detailed analysis of specific situations may not be as illuminating.

A fourth concern about the experimental design is related to the selection of three NWPs. If two models similar to ECMWF were available, would it make sense to include both? How would the results change? This raises questions about generalizability. In many machine learning applications, the data exert a closer control on accuracy than the algorithms themselves. I understand that a paper cannot address every concern, but some guidance from the authors would be appreciated.

My final concern relates to the generality of the conclusions and the reproducibility of the results in other locations. How robust are the results to the data selection procedure or the structure of the ANN? Would the same structure work well in other locations, or would changes be required? If a less intense data selection procedure were used, how would the results change? If 20 years of data were available, would GFRNet perform similarly? I believe the study would be much more robust if extended to other regions with more data available. Currently, the method seems to work, but the evidence may not yet be robust enough to fully support the claims made in the paper.

Finally, I present some comments about minor issues:

+ References should be enclosed in parentheses. The way they are written now complicates the reading of the paper.

+ Figures 4 and 5 are difficult to interpret, particularly due to their complex visual layout. A more intuitive representation could enhance their clarity. For the maps, since topography seems to play such an important role, residuals might provide better insights.

+ Some references to equations are incomplete.

+ A better discussion on ensemble forecasts and deterministic quantitative forecasts may be in order. In my opinion, ensemble forecasts may convey a much better idea of severe storm potential, especially when combined with synthetic generation, so focusing on deterministic forecasts may be a disadvantage.

Citation: https://doi.org/10.5194/egusphere-2024-2888-RC1
- AC2: 'Reply on RC1', Zuliang Fang, 17 Jan 2025
  
  Thank you very much for your thorough review and insightful comments and suggestions. Based on your feedback, I have identified and categorized nine specific issues, which I have addressed in detail and with focus. Please see the attached document for further information, where your questions are italicized, and my corresponding responses are provided in regular font.
  For the sections of the manuscript that require modifications based on your suggestions, I have already made the necessary revisions offline. These updates will be incorporated into the manuscript after the preprint public review period ends. I sincerely hope you will continue to provide your valuable comments and guidance during this process.
  Thank you again for your time and effort in reviewing my work.
  Best regards
  
  Citation: https://doi.org/10.5194/egusphere-2024-2888-AC2
RC2:
'Comment on egusphere-2024-2888', Anonymous Referee #2, 03 Apr 2025

Please refer to the PDF document for comments.

Citation: https://doi.org/10.5194/egusphere-2024-2888-RC2
- AC3: 'Reply on RC2', Zuliang Fang, 08 Apr 2025
  
  I have done some ablation experiments and appropriate analysis according to your suggestions. Please see the attachment for the specific reply. Thank you very much
  
  Citation: https://doi.org/10.5194/egusphere-2024-2888-AC3

Peer review completion

AR – Author's response | RR – Referee report | ED – Editor decision | EF – Editorial file upload

AR by Zuliang Fang on behalf of the Authors (27 Apr 2025) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (29 Apr 2025) by Nicola Bodini

RR by Anonymous Referee #2 (06 May 2025)

Suggestions for revision or reasons for rejection

Based on the reviews of both reviewers and the author's responses, the quality of this manuscript has been significantly improved. However, further improvements are needed in the physical explanations, experimental rigor, and language expression. As a scientific paper on AI applications in meteorology, the "good results" need to be clearly explained, including the reasons why they are good, potential issues, and future development directions. The structure of the paper also needs to be very clear and well-organized. It is recommended that the author address the following issues to further improve the manuscript, especially strengthening the discussion on the physical validity of the model and the comprehensiveness of experimental comparisons to enhance the academic persuasiveness of the manuscript. I recommend that this manuscript undergo moderate to major revisions.
1. Model Explainability and Physical Reasoning
Issue: Although the author has verified the model’s performance through experiments, the physical mechanism explaining how the model improves precipitation forecasts via the GAN strategy is insufficient. The reviewers pointed out that the impact of terrain and meteorological features on precipitation needs more in-depth discussion, particularly on how the model captures these physical relationships.
Suggestion: Add an analysis of the physical validity of the model, such as visualizing feature importance or incorporating meteorological theories to explain the correlation between model outputs and terrain or meteorological conditions.
2. Comprehensiveness of Experimental Design
Issue: While the author has conducted ablation experiments to verify the role of key components (such as the SE module and weighted loss function), comparisons with other simple models (such as Random Forest or SVM) are lacking, making it difficult to fully prove whether the complexity of the GAN is necessary.
Suggestion: Supplement with comparisons to simple models, illustrating the irreplaceability of the GAN in improving forecasting accuracy and structural details, or discuss its cost-effectiveness.
3. Data Size and Generalization Ability
Issue: Using only 4 years of data may limit the model’s generalization ability, and the model's performance in other regions or over longer time series has not been verified. The reviewers suggested expanding the dataset or conducting cross-regional validation.
Suggestion: Clearly state the limitations of the data in the discussion and plan future work to validate the model in other regions or over longer time periods, or use cross-validation to enhance the credibility of the results.
4. Consistency Analysis of Results
Issue: Some results are contradictory (e.g., GFRNet has a lower TS than FRNet at the 40mm threshold), and the author attributes this to the conservativeness of the GAN but lacks statistical significance analysis.
Suggestion: Add statistical tests (e.g., t-tests) or error analysis to indicate whether the differences are significant, and discuss the pros and cons of the conservative strategy for practical applications.
5. Transparency of Technical Details
Issue: The selection of hyperparameters (e.g., gradient penalty coefficient γ, loss weights a/b) lacks a description of the systematic optimization process, with only grid search mentioned but no results provided.
Suggestion: Include detailed experimental data on hyperparameter selection in the Appendix or methods section to enhance reproducibility.
6. Language and Expression Standardization
Issue: Reviewers pointed out that some language expressions are not professional enough, and there is inconsistency in terminology and citation format, while the readability of charts and tables could be improved.
Suggestion: Thoroughly review the language throughout the manuscript to ensure consistency and standardization, including captions and table headings.
7. Specificity of Future Work
Issue: The discussion mentions directions like "integration of physical constraints" and "higher resolution," but lacks specific implementation plans.
Suggestion: Elaborate on future plans, such as how to incorporate physical equations into the model or specific data augmentation strategies.
[Please also refer to the uploaded attachment document.]

Referee Report: PDF

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RR by Anonymous Referee #1 (27 May 2025)

Suggestions for revision or reasons for rejection

General comments

The paper presents an application of deep learning techniques, specifically U-Net and GAN-based models, to enhance short-term precipitation forecasting, with a focus on the fine-scale structure of intense rainfall events. The authors compare the accuracy of three numerical weather prediction (NWP) models against two deep learning techniques: a U-Net-based model (FRNet) and a GAN-based model (GFRNet). Multiple evaluation metrics are used to assess their relative performance. The aim is to forecast 3-hourly accumulated precipitation over the next 24 hours in a region of North China. The manuscript reports extensive metrics and concludes that GFRNet demonstrates significant operational value.

I have read the authors' responses to my original review and would like to thank them for their efforts in revising the manuscript. However, I believe that several of my key concerns have not been fully addressed. While the revised version shows improvements, I still find that significant issues remain, and I cannot recommend the paper for publication in its current form. I outline these concerns in more detail below.

1. Justification of the model's rationale

My concern regarding the rationale of the paper has been partially addressed, and I appreciate the analysis on the relative importance of the input features. However, the manuscript still lacks a concrete explanation or experimental support for the mechanism by which the GAN architecture improves performance over simpler or non-generative alternatives. I think my point here will become more clear with the explanation on the need of simpler methods for the comparison.

2. Lack of comparison with simpler methods

This concern remains unaddressed. In your response, you acknowledge that such comparisons would add value but state that "primary focus of our study is to address the limitations of non-generative models and evaluate the advantages of GAN-based
techniques". However, such advantages can only be meaningfully evaluated through comparison with classical alternatives—especially those that might yield similar results with significantly lower complexity and higher interpretability.

If the primary contribution lies in deep learning architectures, and precipitation serves primarily as a benchmark, a journal more focused on artificial intelligence might be a more suitable venue.

The lack of comparison with simpler methods is not a minor point. For instance, the "blurriness" of NWP model outputs may result, at least in part, from the bilinear interpolation applied. What if elevation or forecast cycle were used to locally adjust the interpolation? What if a local regression approach was used to estimate rainfall as a function of elevation in each subregion? Such strategies might outperform bilinear interpolation without the need for complex machine learning models.

Similarly, forecasting methods such as the analogue method—a well-established baseline in meteorology—could be implemented via K-nearest neighbors, even avoiding interpolation altogether. Dimensionality reduction techniques could also be applied to simplify the input space before using such methods.

Without at least exploring these simpler alternatives, the comparison is incomplete and the added value of GFRNet remains unclear. Deep learning and AI are undeniably powerful, but I believe they should be applied where their added accuracy justifies the associated cost in complexity and loss of interpretability.

In summary, without a fair comparison with classical methods, the paper's core value proposition is not convincingly demonstrated.

3. Experimental design and statistical significance

I remain concerned about the experimental design. Most critically, the manuscript does not include any statistical hypothesis tests to determine whether observed differences are significant or due to random variability. Table 4, for instance, is difficult to interpret without such tests—particularly considering the limited dataset. This should be a central concern for the authors.

This issue is exacerbated by the heavy filtering applied to the original dataset. I still do not understand the motivation behind defining “valid samples,” nor do I fully understand Figure 2. If samples are filtered based on precipitation criteria, how is it possible that the resulting dataset still contains a mix of valid and invalid samples? Could the authors clarify this?

Moreover, I question how Figure 2b demonstrates a fat-tailed distribution. What is the metric or evidence supporting this claim? Based on this assumption, a custom weighted loss function is designed. But this chain of reasoning—and the corresponding design choices—seems to hinge on multiple small decisions that are not fully justified. I am concerned that these steps may unintentionally lead to overfitting—not necessarily through the model itself, but through tuning the data processing to the specific characteristics of the dataset.

In this context, I find particularly problematic the statement in line 136: “This increase in the proportion of valid samples improved the stability and efficiency of the model training.” This suggests that the validity criteria were defined a posteriori to improve performance, which undermines the generalizability of the results.

All these comments should also be understood in the context of a somehow limited dataset.

4. MS-SSIM vs. RMSE

Another methodological point that requires further justification is the choice of MS-SSIM over RMSE as a primary evaluation metric. First, given its central role in the analysis, the MS-SSIM metric should be defined mathematically so that readers can judge its appropriateness. Second, the manuscript should offer a clear argument as to why spatial structure should be prioritized over magnitude in evaluating model performance.

As shown in Table 5, ECMWF achieves the best RMSE. Without knowing how ECMWF would perform spatially using a better interpolation method (e.g., structure-aware or topography-guided), it is difficult to accept that GFRNet clearly outperforms it overall. The manuscript would benefit from a more explicit discussion of the tradeoffs involved.

5. Additional minor comments

I believe my original comment on the case studies still holds: their selection and interpretation could be more clearly justified.

Figures 4, 5, and 6 remain difficult to interpret. Improvements in visual clarity and labeling would greatly enhance their value.

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ED: Reconsider after major revisions (27 May 2025) by Nicola Bodini

AR by Zuliang Fang on behalf of the Authors (02 Aug 2025) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (04 Aug 2025) by Nicola Bodini

RR by Anonymous Referee #2 (06 Aug 2025)

Suggestions for revision or reasons for rejection

The manuscript has undergone several rounds of review and revision, significantly improving in quality. In my opinion, the manuscript may be ready for acceptance based on the publication requirements of GMD after a minor revision. I believe this paper contributes meaningfully to AI-based precipitation forecast correction research, though operational implementation may still require further development.

1. Major strengths of the manuscript
- The proposed GFRNet model combines GANs with multi-source NWP data fusion, demonstrating significant improvements in heavy rainfall forecasting (e.g., TS, FSS scores), particularly at 20–40 mm/3h thresholds, outperforming traditional NWP and baseline models (FRNet/MSEM).
- Adversarial training and the weighted loss function effectively mitigate the common "over-smoothing" issue in deep learning models.
- Comprehensive experimental design, including validation on three independent rainy seasons (2022–2024), multi-threshold evaluation (0.1–40 mm/3h), case studies, and statistical significance tests (e.g., Top 10% subset analysis).
- Ablation studies confirm the necessity of the SE block and weighted loss function.
- The model achieves high-resolution (5 km) precipitation forecasts within operational time constraints (3-hour training/2-minute inference on an A100 GPU), showing clear potential for disaster prevention.

2. Outstanding reviewer comments
- Code/Data Availability. The appendix declares access to code/data, but authors must confirm their actual functionality (I did not test them, though future users in the field may verify reproducibility).
- Language/formatting. The authors should carefully proofread the entire manuscript for grammar and spelling errors. I have already identified a few issues. (e.g., “contrained” should be “constrained” in the Line 25; “Table ??” in Line 136).

Referee Report: PDF

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RR by Anonymous Referee #1 (12 Nov 2025)

Suggestions for revision or reasons for rejection

General assessment

The authors have thoroughly revised the manuscript and addressed most of the comments raised in the previous review round. The overall structure is clearer, the methodology is better justified, and the presentation of results has improved substantially. The new version reflects a careful and constructive response to the reviewers’ suggestions, and I appreciate the effort invested in strengthening both the clarity and the scientific rigor of the paper.

Specific improvements

Sampling and dataset definition – The description of the sampling procedure has been rewritten with quantitative detail, eliminating the ambiguities previously associated with “valid samples.” The revised figures and tables make the dataset composition much clearer.

Weighted loss and long-tail justification – The rationale for the weighted loss is now explicitly linked to the pixel-level long-tail distribution, and its impact is supported by a well-structured ablation experiment (Appendix B1). This substantially improves the methodological transparency.

Statistical significance testing – Section 3.4 introduces a comprehensive significance analysis using paired t-tests across multiple thresholds and stratified subsets. This addition directly addresses a major methodological concern and reinforces the robustness of the conclusions.

Evaluation metrics (MS-SSIM) – The definition and role of MS-SSIM are now properly introduced, including the mathematical formulation and appropriate references. This clarifies the interpretation of the results and enhances reproducibility.

Figures and case studies – The graphical presentation has improved considerably, with more readable legends and a clearer narrative linking qualitative and quantitative results.

Comparison baselines – The inclusion of MSEM as an operational and interpretable baseline is a valuable addition that grounds the performance comparison in a realistic context.

Remaining concern

Despite these important improvements, the comparison with simpler and more classical methods remains limited. While MSEM is an appropriate baseline within operational ensemble post-processing, it does not fully represent the family of low-complexity statistical or physically informed approaches that could serve as alternative benchmarks (e.g., locally weighted regression, analogue methods, or elevation-adjusted interpolation). The justification for adopting a GAN-based framework therefore still rests primarily on empirical performance rather than on a clear demonstration that simpler, transparent models would fail under similar conditions.

I recognize, however, that the authors have made a sincere and substantial effort to strengthen the paper, and that the present version is technically sound and clearly written. My remaining comment should therefore be understood as a recommendation for future work rather than a condition for acceptance.

Recommendation

The manuscript can be accepted after minor editorial polishing. Nevertheless, I would encourage the authors to explicitly acknowledge in the discussion that a more systematic comparison with classical statistical or regression-based methods could further consolidate the argument for using GANs in this context.

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ED: Publish subject to minor revisions (review by editor) (13 Nov 2025) by Nicola Bodini

AR by Zuliang Fang on behalf of the Authors (17 Nov 2025) Author's response Author's tracked changes Manuscript

ED: Publish as is (17 Nov 2025) by Nicola Bodini

AR by Zuliang Fang on behalf of the Authors (18 Nov 2025) Manuscript

Short summary

We developed a deep learning model based on Generative Adversarial Networks (GANs) to improve rainfall forecasts in northern China. Traditional models struggle with accuracy, especially for heavy rain. Our model merges data from multiple forecasts, capturing detailed rainfall patterns and offering more reliable short-term predictions.