Review Reports

Round 1

Reviewer 1 Report

 

 

Presented work considers a number of Machine Learning models to predict precipitation type using satellite passive microwave observations over land. The study fits the scope of the Journal. Topic is of the interest to the community. The outline of the study is good. Delivering the results has likely required significant effort. Figures provide meaningful information. Unfortunately, 1) the work has some major flaws in methods, 2) manuscript suffers from structural issues and 3) most of the conclusions are not supported by findings. Below I provide extensive comments and suggestions on how this work can be “fixed” before it can be recommended for publication. In short, authors fail to identify current state of the field on this particular topic. Cited work may seem to be relatively published but with the fast pace the ML field progress, significant move in both the tools and goals has been made within last few years. This has been ignored. If authors check IEEE and JGR publications on this topic they will see that the ML models used here are obsolete. The problem of retrieving convective type class from PMW sensors has been more or less solved. What the community is currently missing is uncertainty information on ML output. The presented study does not tackle this problem (not mentions it). My recommendation at this time is reject, but I highly encourage authors to re-submit the study once the issues are addressed. Suggestions are not particularly hard to implement, but the necessary work will likely be time consuming. Please pay attention when stating the conclusions. In the current manuscript almost all of the conclusions are not supported by work (I provide paragraph-by-paragraph comments for the conclusion section).

 

GENERAL MAJOR COMMENTS

 

A)   Authors state that the goal of the study is to evaluate different ML models and different data augmentation techniques and training attributes (see lines 80-82). Still, they fail to identify what the literature reports on this topic. Authors only cite some pioneering work on this topic. There are publications in IEEE journals that tackle this same problem but at a higher level, using more complex architectures, with a goal to deliver a more complete result. Presented study reports somewhat obsolete methods with results that are not better than those already reported in the literature, falling short of dealing with uncertainties of any of the employed ML methods and datasets. All the applications authors list to motivate this work require information on uncertainty of the convective class output. None of the presented models delivers this information in a fully probabilistic manner. In fact, authors do not mention any. To make a true contribution to the field, one should perform this same exercise starting from the best available, proven to work, ML architecture. Do the literature review, implement the latest findings.

 

B)   My suggestion to the authors would be to consider incorporation of at least one ML architecture or technique that can deliver probabilistic quantitative uncertainty of the output and include it into the exercise presented in this manuscript. The exercise itself is well structured and requires not changes. Alternatively, authors should provide justification on why would community see the presented study as something new. The presented study is complete in the sense that covers global domain and performs meaningful, validation, testing, and to some extent comparison.

 

C)   Motivation for “mixed” type: Authors chose to define a new type of precipitation – a “mixed” class. One must provide a justification for such a decision, especially given that this new type, as defined here, accounts for almost the same amount of observed precipitating area as convective type. As presented, it appears that this new type is defined so that all “challenging” to predict FOV can be assigned to it, making the models performance on the rest of classes look good.

 

D)   Authors have to explain what’s the benefit of using convective area to define a convective scene. There is no guarantee that any of the DPR pixels are 100% convective or stratiform. Meaning, defining mono-type convective and mono-type stratiform GMI FOVs is always going to be “mixed” to some extent. Convective volume is widely used in the literature to separate convective from stratiform. Why not here? Explain. Justify.

 

E)    Some serious flaws in methodology description are present (see comments below). It takes a while to get to the point in text where important aspects of decision making in creating the training dataset are explained. This is easy, but necessary to fix.

 

F)    It is unclear how authors calculate the overall accuracy. This has to be explained. The new “mixed” type has a very low prediction accuracy (but large occurrence). It is confusing how exactly contributed to the overall accuracy.

 

 

Line-by-line comments (MAJOR):

 

Line 79: The statement seems to be misleading. The cited study reports low accuracy of convective flag, not convective rate (i.e. volume). According to the abstract of the cited work, the method captures more than 85% of rainfall volume correctly. [edited (after reading through the manuscript): This confusion between volume and is set right here and is misleading throughout the text. Everything presented in this study refers to convective area. How much rain volume is correctly classified is unknown.]

 

Lines 127-129: It appears that you use DPR flag(s) for training, not DPR precipitation type. This has to be clearly explained.

 

Note: Authors correctly present that DPR assigns a flag to each 5km FOV, but with multiple DPR FOVs falling into a single GMI FOV a decision has to be made whether GMI FOV is convective or stratiform. Keep in mind that given the GMI’s signal is affected by hydrometer content of the atmospheric content one should really focus on rain volume (not area) defined by DPR as convective or stratiform. For example, GMI FOV being 51% convective by area can be radiometrically very different from 51% convective by volume. Convective/stratiform is a microphysical property that doesn’t translate linearly to passive microwave signal. [edited (after reading through the manuscript): clearly, I was not aware at this point how you define FOV type; it will come latter. It has to come here.]

 

Lines 132-142: Move this text to the Methods section.

 

Lines 151-152: Authors use cloud liquid water path (CLWP), total column water vapor (TWV), and 2-meter temperature (T2m) to train the models. GMI frequencies are sensitive to all of these parameters. Given that pixel-scale emissivity is also provided on the input, the ML model(s) should be capable of extracting (or if not extracting, then accounting for) the TWV/CLWP/T2m information on their own from the GMI Tbs + emissivity alone (although it will be suppressing to see that even the emissivity adds anything to the information content). By using the reanalysis variables, which in the best-case scenario just smooth out the information that’s already in Tbs, you only introduce noise to the training dataset. If evidence gathered during the training process do not reflect this (e.g., you do see improvement when you add reanalysis data), then the ML architectures are not optimal for this particular task. I would like to hear authors’ thoughts on this.

The same applies to the PD, which introduces no new information content relative to raw Tbs. Being a derived form direct observations, the PD will help a less complex model (such as RF) to converge sooner (it reduces the learning time by directly linking to the microphysics relevant to C/S). In fact, I would expect that if PD is used as the only input feature to a ML model, the model would still have a decent accuracy.

 

Lines 182-187: I don’t see how is this paragraph relevant to this study?

 

Line 279: What do you mean by “sample-size weighted averaged accuracy rate”? Is the reported accuracy the overall accuracy (e.g. ratio of correct predictions to the sample size), or something else (e.g. individual class accuracies are “normalized” based on sample size(s) and averaged)? This has to be clearly explained.

 

Figure 7: Both plots need x-axis labels (or expand the caption to explain what’s on x-axis). Add to the caption info on which model this corresponds to. Explain negative probabilities shown in the right plot.

 

Line 321: last sentence of the paragraph is not of any interest to the reader. Remove.

 

Line 326-329:

a)     This is the first time I was able to understand how you define a GMI FOV (the label) class in the training process. If I am correct, GMI FOV is called convective only if all DPR FOVs that fall in are convective. Same for stratiform. The “mixed” class is if both convective and stratiform (as defined by DPR) appear, which explains the large sample size of this type (shown in Fig4). This information has to be communicated much earlier in the text. Also, you have to say which GMI channel FOV is used when creating the labels in the training dataset.

b)    Justify your choice to define the class by DPR area rather than volume type. It is quite unusual. How do you see applications (listed in the motivation) make a use of this information? You are essentially defining a new class (mixed) to reduce the challenge the ML models face. This might be OK, but the fact is that this new class is as large as convective (as shown in Fig4). The models presented here all fail to predict the “mixed” class.

DPR retrieval could have done the same for its 5km FOVs, but it did not, at least not in a large number of the cases. Users typically want to know whether a pixel is convective or stratiform. You have a large portion of the raining pixels defined as something else (mixed) which none of the models predicts well. What a user suppose to do with it?

 

Section 3.2

The exercise of removing the emissivity from the training, only proves that the model architecture is important, and that the models you chose are not perfect for this task. CNN is insensitive to the removal of the emissivity because it’s capable of extracting the same information from raw TBs. Under the “Mixed” type conditions, TBs are more ambiguous than under “regular” mono-type cases. Deeper models can resolve this, but simpler ones cannot. Meaning emissivity can help constrain this ambiguity only to the models that “don’t know what to do” with TBs alone, while in the CNN case emissivity simply presents additional noise on input. Longer training would likely (eventually) result in CNN reaching the original performance on “Mixed” type (i.e. 18%), but of course this would pose a problem of overfitting. This adds on the problem mentioned above: your model choice is obsolete. Literature suggests the use of more complex models (you fail not only to use them but to acknowledge them).

Your work would be of high interest to the community if you have used a more complex architecture that can provide uncertainty information with analyses similar to those you performed here. It is a bit of work, but you have all you need in place. What you presented here is not wrong, but I don’t see how it moves the field forward.

 

Line 409-410, starting at “it is temporarily concluded…”: remove this part of the sentence (or at lease rephrase into “confirms” instead of “concludes”). The emissivity model that delivers the product you use, relies on the same Tc’s you are using here. So, of course the information is redundant.

 

Figures 10 and 11: There are leftover comments in the captions. As stated in those comments, you do need to be address a number of points, especially the fact that Fig. 11 is missing wide-swath training

 

Line 433: 20 FOVs on each side of nadir or centered at nadir? Edit the sentence to clarify.

 

Section 3.4: Given that you dedicate one whole sub-section to study the effect of added noise in the input features, it would be expected to mention noise contribution introduced by slant vs. nadir looking sensors. I am not suggesting you should address it, but only mention it (perhaps in the Intro).

 

Line 561-562, the last sentence of the first paragraph: Remove the sentence. It is not a Conclusion section material and you have done nothing to prove the statement is true.

 

Line 572, last sentence of second paragraph, “Challenges are identified at the boundaries of transition of different precipitation types, as well as for mixed-class.”: Please point me to the text where those challenges are identified. I’d say you only speculate this is the case. If so, rephrase or remove the sentence.

 

Lines 574-580. The first sentence of the third paragraph: In the text you state that predicting raining vs non-raining pixel using PMW is not a particularly hard task. Meaning, that addition of non-precipitating type to the task does not make this work any different from the one you cite here.

The rest of the paragraph clearly indicates the importance of the balanced dataset, which is different from the cited work. However, the study does not demonstrate this importance. The only results shown are the ones when the balanced dataset is used, which is correct approach but does not provide grounds for the statement made in this sentence. Additionally, published work(s) that demonstrate the importance of the balanced training dataset in classification tasks already exist. Meaning, even from this perspective the work is not novel.  

 

Line 528-583: Using channel differences (e.g., PD) has been documented in published studies (see ABI-based precipitation type prediction). Expecting PD to be useful in ML training when all raw TBs are included as well, opposes the idea of ML methods. If positive contribution is made by inclusion of PD, that means the ML architecture is either not deep enough or non-suitable for the application. You confirmed this with your CNN model.

The use of Emissivity is novel, but as pointed above, without a more appropriate ML architecture for this task, it is hard to conclude if it brings any additional information to the input data. Repeat the study using models that can quantify uncertainty and this will become a very useful exercise.

 

Lines 588-590, sentence starting with “We demonstrate in this paper…”: this statement is not true. I don’t see how authors demonstrate this. They only speculate. Remove or rephrase the sentence.

 

Lines 592-596: Here authors state that Emissivity is important and the fact other PMW sensors currently do not have ready-to-use emissivity product is a challenge. In previous paragraph authors clearly state that CNN model, which is the best performing model in the study, does not benefit from Emissivity on input. Remove the paragraph.

 

Lines 597-607, last paragraph in the Conclusion section:

Second sentence: This is a strange thing to conclude. The DPR- view-angle artifact cannot propagate to the GMI because you do not train on it. The method you use physically prevents this to happen. ML model has no knowledge on DPR angle, hence it smooths out all the inputs (the resulting model “averages” this feature in). I would argue that the variability across DPR scan angle is seen from the ML model training as noise. And as such it has to affect the performance of the model. One cannot expect to see differences across the GMI scan, since the output is provided using FOV-position-independent model. That differences in the overall performance of the ML model exist when narrow vs. full DPR swath is used is evident from Figs. 10 and 11. I am confused with your statement here. You cannot conclude what you stated in this sentence.

The rest of the paragraph: Authors are concluding that conical scanning design is a better choice (over cross scanning) for the future missions. The goal of this study was not defined as “comparing cross vs. conical scanning design performance” (even if it was, the method and approach authors have used would be highly irrelevant to the problem; there is much more that goes to it than what’s shown in Figs. 10 and 11). Remove this “conical- vs. cross-track” conclusion from the paragraph. No bases for it, not supported by evidence (though likely correct) and not within the scope of the study.

 

 

 

 

MINOR

 

Line 31-32: If the environment is stable, it is unlikely to be any precipitation. Rephrase.

 

Line 79: “correction” or “correct”?

 

Line 94: “GMI and DPR are always collocated” - this is not correct (as indicated in the following sentence). Rephrase.

 

Line 102: consider removing word “current”

 

Line 113: “Nevertheless, …” remove this sentence. It is irrelevant to the presented study and of no use to the reader.

 

Line 130-132: “A further deep learning…” remove this sentence. It is irrelevant to the presented study and of no use to the reader.

 

Lines: 266-269: This sentence feels “disconnected” from the rest of the sub-section. It is more appropriate for the Introduction section. Consider moving it to the Intro.

 

Line 294: “by warmer…”. Make sure this reads well.

 

Line 371, “does not present”: consider rewording.

 

Line 377-378: this sentence reads as that you are suggesting the redundancy exists in information of 89 and 166 GHz channels. Consider rewording so it’s clear you refer to emissivity.

 

Lines 385-386, starting at “the precipitation type is more closely related to the  cloud regime (frozen or liquid) above rather than surface precipitation characteristics.“:  What you state here is given by definition of the Convective and Stratiform regimes. One does not need to go through the ML input/output analyses to draw such a conclusion. You did not find anything new here. Consider rephrasing this sentence to say that your finding confirms the definition. (This is a nice result to see).

 

Line 396: You meant 183, not 190, right?

 

Line 416: make sure these read degrees, not 170.

 

Figure 10 and 11: add y-axes variable labels and units.

 

Line 437: remove word “Luckily”. It is changing the meaning of the sentence (in a non-favorable direction).

 

Line 474-476: Rephrase this sentence to be clear that you only speculate there is an anvil head associate precipitation. There is not proof this exists (though it’s likely true).

 

Figure 12: Mapped features appear blurry, while labels and legend are not.

 

Line 528: Reword the beginning of the sentence, it is too colloquial.

 

Figures 16 and 17: color bars need variable units.

 

Line 564: Reword: “precipitation types are trained”. Models are trained, not types.

 

Author Response

We are grateful to your reading and comments, especially the detailed line-by-line suggestions. Please see our responses in the attached word document. Thanks.

Author Response File: Author Response.docx

Reviewer 2 Report

The manuscript compares multiple ML approaches to classify precipitation types over land using GMI observations. In this study, one year of data has been used to train the ML models and the DPR rain classification is considered as truth. This study is certainly an interesting application of the popular ML techniques. The manuscript is well organized and mostly easy to follow. The manuscript fits into the scope of Remote Sensing, and I would recommend its publication after the following comments have been addressed.

 

 

1. Section 1: The introduction motivates nicely on the importance of precipitation classification, but I find the review of existing studies a bit lacking. Maybe it will be good to point out in what aspects the previous studies mentioned in the manuscript were lacking or if they had any limiting aspects.

 

2. Section 2.1 : I find the description of finding DPR and GMI collocations lacking. It is not clear how GMI channels with two different swath widths are taken into account. It is mentioned that collocation process is loosened to allow “fuzzy logic learning”. But not explained how?

 

3. Line 143: DPR is used as a “truth” but it has its own limitations. You mention the viewing angle dependent artifact, but the other factors affecting its accuracy should also be mentioned. It will be good to have some statistics on the general accuracy of DPR classification. 

 

4. The methodology explains the training and validation dataset, but what about the testing dataset which is used during the training process?

 

5. You use 6 ML models, out of which only two are compared in detail citing their good performance. This is OK, but using five simple ML models seems like overkill. This also prevents you from describing the details of e.g. CNN algorithm (how it was implemented for your dataset, what you describe is a bit generic). Think about if the simple ML models could be moved to an Appendix while focussing only on 2/3 main models in the main text?

 

6. The most noticeable accuracy is for non-precipitating cases. This is not unexpected, however, did you consider that cases with light precipitation are beyond the sensitivity of GMI. Is it possible to quantify how well the cases below the detection threshold can be classified?

 

7. The impact of emissivity on the accuracy is found to be quite small, and as mentioned by the authors, a thorough investigation is required to understand whether emissivity can be a useful parameter. Such an investigation will add significant value to the continuation of the study. Though understandably out of the scope of the present manuscript, it will be good to discuss the future approaches in the Conclusions.The future work/under-development work is mentioned in the text, but conclusions should also be updated. 

 

Minor comments:

 

1. Abstract: Line 12: You miss mentioning Logistic Regression .

2. Line 52: typo in Microwave

3. Line 146: typo in conical

4. x/y Labels missing in Fig. 3, Fig 7, Fig 10, Fig 11, Fig 12, Fig 14, , 15, 16, 17

5. Fig 2, 5, 8, and 9 are figures or tables?

6. Fig 10, 11, please update the text.

Author Response

We are grateful to your comments and acknowledgement of our work. Please see our responses in the attached word document. Thanks.

Author Response File: Author Response.docx

Reviewer 3 Report

see attahed.

Comments for author File: Comments.pdf

Author Response

We are grateful to your comments and acknowledgement of our work. Please see our responses in the attached word document. Thanks.

Author Response File: Author Response.docx

Reviewer 4 Report

General comments

Accurate precipitation type classification retraveled from remote sensing measurements is benefit for cloud-precipitation interaction understanding. The manuscript used GMI and DPR dataset and 6 ML models to predict 5 types of precipitation globally, and the prediction accuracy is much more robust than previous similar study. Also, the impaction of polarization difference and surface emissivity features were detailed evaluated to improve the physical understanding of the ML model results. The manuscript was well structed with plenty scientific and technical information, so I suggested to accept it with minor revision.

Specific comments

1. The similar previous study (Petkovic et al., 2019, J. Atm. and Ocn. Tech.) was mentioned and compared in this manuscript, especially in conclusion section. But only unbalance training dataset (non-precipitation data were used in this study) and data augmentation were emphasized. Other differences such as model structure and input features and their influence on the prediction results need to be discussed further.
2. The title declared “An Ice Microphysics-based Machine Learning Approach”, which is arguable due to 6 ML models were used and no one can be identified as Ice Microphysics-based.
3. In abstract, “One novelty of this work is to introduce data augmentation 16 (subsampling and bootstrapping) to handle extremely unbalanced samples in each category”. Data augmentation is a normally used technology for ML and is not so novelty.
4. The manuscript claimed that GB and CNN are two highest accuracy score models and were selected for further statistics for comparison (line 286-288). But in case study section 4, only RF and CNN results were provided.
5. In Figure 3, x and y axis labels are missing.
6. Figure 5, 8, 9 should be changed as tables.
7. Figure 10 and 11 need to be improved and keep same format (both plotting wide and narrow swath results).
8. Figure 16 and 17, sub-plot (a) has no y label.

Author Response

We are grateful to your comments and acknowledgement of our work. Please see our responses in the attached word document. Thanks.

Author Response File: Author Response.docx

Round 2

Reviewer 1 Report

Authors did acknowledge all of my major comments, but have addressed very few of them (all of the minor comments have been addressed). Authors did invest time and put effort in explaining their point of view (which is appreciated). However, the same major issues still stand. In short, the manuscript describers the work which is very meaningful and needed, but it’s being presented in a misleading way. Listed conclusions are questionable and not of the interest to the community. The greatest value of this work lies in the analyses of the retrieved convective class. Instead of focusing on it, authors insist on ML aspect of the study, which is behind the currently available literature. I strongly encourage the authors to rephrase their conclusions and focus on the results (which are good and useful to the community) and stay away of drawing conclusions from the ML findings. What is currently presented on the ML methods does not provide results that are anywhere near existing models. See more details below.

 

 

Title: Remove words “An Ice Microphysics-consistent”. You do not focus on ice microphysics in the study. It is only the findings of the study that are consistent with the ice microphysics properties. No need to have this in the title. If the method is chosen in a correct way, one should not expect anything else but to see “ice microphysics-consistent” result. Authors are stating the obvious, which can easily become is misleading. A reader may expect ML methods that seek consistency in ice microphysics. Title will read better and relate correctly to the content of the presented study if it starts by “Machine Leaning Approach…”

 

 

Existing literature: At minimum, authors should include the following citations (which are not easy to miss when searching on this topic).

 

-   "Bayesian Deep Learning for Passive Microwave Precipitation Type Detection," in IEEE Geoscience and Remote Sensing Letters, vol. 19, pp. 1-5, 2022, Art no. 4500705, doi: 10.1109/LGRS.2021.3090743.

 

-   Classifying precipitation from GEO satellite observations: Prognostic model. Q J R Meteorol Soc, 147(739), 3394– 3409. Available from: https://doi.org/10.1002/qj.4134

 

-   Classifying precipitation from GEO satellite observations:Diagnostic model. Q J R Meteorol Soc, 147(739), 3318– 3334. Available from: https://doi.org/10.1002/qj.4130

 

-   "Decomposing Satellite-Based Classification Uncertainties in Large Earth Science Datasets," in IEEE Transactions on Geoscience and Remote Sensing,vol. 60, pp. 1-11, 2022, Art no. 4106211, doi:10.1109/TGRS.2022.3152516.

 

These studies show that models similar to those presented hare have already been consider for this task (on geostationary satellite input and passive microwave low Earth orbiting sensors input) and that more complex models provide by far higher accuracies than the ones reported here (when using passive microwave observations). Additionally, the literature lists the use of high frequency channels. This taken into account, the “novelty” of the presented study is down to (quoting authors response): “suggested a general data augmentation approach (data rebalance) that can be useful for any types of unbalanced sample training”, which is not really a novelty. Simply, the way the results are presented is such that does not offer any new contribution to the field and as such it is hard to justify recommendation for publication. However, the analyses of the retrieved/predicted convective class as valid and interesting and in my opinion worth publishing. Authors could easily re-state the conclusions and focus on those, and have the manuscript reach the publication level.

 

Several notes on authors responses:

 

- On providing uncertainties: Probability, that authors state presents the measure of uncertainty, is not a complete information on the uncertainty of the ML output. First (as authors correctly state), it does not come as a single-number metric (there is a probability for each class), which is very hard to interpret and requires an arbitrary cutoff. And second, the probability does not provide information on how far [you believe] the ML model is from the correct solution, which is what the uncertainty is.

 

 

If the authors choose to pursue improving the ML aspect of the study, my suggestion remains the same: consider incorporation of at least one ML architecture or technique that can deliver probabilistic quantitative uncertainty of the output and include it into the exercise presented in this manuscript. The exercise itself is well structured and requires not changes.

 

 

- On the interpretation of the overall accuracy: After providing the clarification on the overall accuracy calculation method, and using the information given in Fig 4, it becomes clear that if the ‘no-precipitation’ category is to be eliminated, the overall accuracy of the model(s) would be well under 40%. In other words, the accuracy of the three convective classes, as defined in this study (convective, stratiform and “mixed”) is under 40%. This is hardly comparable to the results of the currently published literature. Note: The high accuracy reported in the study is driven by the high accuracy of the non-precipitating class (which is by far most represented class). Yes, the models presented here were not trained for raining pixels only, but the authors correctly state that retrieving rain vs. no-rain class from passive microwave observations is an easy task (a simple regression can probably provide a decent accuracy). Once again, from the ML perspective, the methodology authors use in this study is obsolete.

 

 

- Authors state (referring to TPW, CLWP, T2m): “We believe including these parameters will help the ML model to learn their contributions to TBs for different channel frequencies and hence the residual signal is relatively clean.” Yes, it will help the models, but only those that are simple enough (i.e., “shallow”) to not be able to extract this same information from the TBs alone. Simply, from the ML field perspective the models the authors use in this study are very simple models. Given the published literature, if the scope of the study was to compare multiple models, I would expect that the simplest model to start with is the CNN one. If this would be the case, the findings on the ML training contributors as currently reported in the study would be significantly different.

 

- On the PD features: It is true that Random Forest cannot learn the Polarization Differences (PDs). But deep NNs can (e.g. CNN model used in this study). PDs are nothing else but the differences of already provided input parameters. By definition, NNs are universal function approximations. Simple features learning are gradients (i.e. differences). The study shows that CNN model has no benefit of added PDs on the input. Why? Because it was able to learn this information using the “raw” input. If the authors believe that CNN cannot learn the differences (i.e. PDs) of the existing features, perhaps they should perform analyses of Fisher Information and prove me wrong.

 

Figure 7: Authors still did not explain negative probabilities shown in the right plot.

 

 

 

MINOR

 

The authors have addressed all of my previous minor comments. Still, I encourage them to re-visit several:

 

Line 204-210: The paragraph on GPM still feels disconnected. Consider adding “For example,” in front of the “GPM team currently…”

 

Original comment: Line 130-132: “A further deep learning…” remove this sentence. It is irrelevant to the presented study and of no use to the reader.

 

- Authors response: Some of the readers might have the similar concern as you to whether we are manipulating the “mixed” class. As we shown in the response here, deep learning including image learning does help improve the “mixed” class accuracy rate in the preliminary study. It’s beyond the scope of this work, but we’d like to clarify that we are working on it.

Comment: Then say: “It is beyond the scope of this study…”

 

 

Original comment: Line 294: “by warmer…”. Make sure this reads well.

 

- Authors response: Clear-sky TB is warmer at high-freq channels but colder over ocean at low-freq channels. So the description here is accurate, we believe. Non-precip scenes are roughly separated by half clear-sky and half cloudy-sky with LWC or IWC > 0. This is analyzed from our other parallel study using collocated CloudSat-GMI samples.

 

- Comment: The statement is correct, I only thing that the part/phrase “that reflect by” sounds odd.

 

Line 412: Change “proves” into “suggests”

 

Line 567: The statement in the sentence “Another merit of this…”: Add reference to support this statement.

 

Author Response

Please see the attached word file for responses (in blue).

Author Response File: Author Response.docx