Dear Floyd Khosa and Co-authors,

Thank you again for submitting a manuscript to our special issue. The reviewers highlighted a couple of issues and suggested that revisions are necessary before final acceptance to publication in HESS.

Having studied your manuscript, the reviews and your author comments, I feel very much in line with reviewer 2 to suggest to work out more clearly what degree of detail can be expected of the soil moisture estimates from the different sources:
What information can be expected from an averaged soil moisture (in lateral space, over depth and over time) in general?
What added information or reliable estimate can be derived from the respective sources? Or in other words what is the trivial part which can be gained by much simpler means like the water balance or distributed linear stores etc.?

Given your expertise and previous publications on the method, I suspect that allowing a slightly more clear focus of the manuscript towards the actual topic of the special issue would be beneficiary to both - the manuscript itself and the contribution to the special issue.
The following comments might appear rater fundamental in some respect. However, they are intended as constructive reflections guiding your revision process.

Further comments:
You summarise that the coherence of CCAM-CABLE and GLEAM results indicate “that the key physical processes that drive soil moisture in CCAM-CABLE and GLEAM, at the surface and root zone, lead to an appreciable degree of mutual information.” Since mutual information is well-defined in information theory, I would expect some more detailed reference and calculus what information is shared and conveyed in the different approaches. More importantly, having a strongly seasonal input signal, I would expect quite substantial shared information between monthly averages of soil moisture and rainfall. So what information is added by the models then?

As far as I understood, your reference data at Skukuza and Malopeni are both in sandy loamy soils. Your gridded soil map however, classifies the area near the stations as silty loam. If the soil types are important (as you claim), how does this affect your results? How does this relate to the covariance structures as estimate of uncertainty, when the covariance for the reference station sites is very low and other references are lacking? Are this topographic effects or patterns in the rainfall estimates or other compartments of the water balance?

Having a strongly seasonal signal and rather limited reference data, I am not quite sure that I understood the value of employing the cross-wavelet analysis. I do not find it very surprising to see a significant annual period and I would not expect any shift in this frequency. What can one learn about the validity of CCAM-CABLE or GLEAM-v3a if there is no ground truthing data involved? What is the frequency spectrum of the reference time series? Maybe even the mean annual soil moisture dynamics could serve as a reference when the inter-annual deviations are specified? Again, my question would link back to the information contained in the different sources under study.

Moreover I find it rather difficult to trace the respective reference data throughout the manuscript. Since you argue about using flux station data, I suspect that the water and energy balances can be closed with the available data. However, you only compare the most difficult to evaluate part of the water balance (soil moisture). Would there reside as much information about the respective states and processes in ET, P and Q? How do these compare to the downscaled GCM and GLEAM inputs?

I find it rather difficult to extract information from Figure 5 and 6. Since you are using an R2 for evaluation, maybe a respective Observed vs. Modelled dotty plot would be more insightful about the fit? How about further measures of correlation? Figure 6 is particularly difficult to evaluate. The lack of data appears to lead to overly positive rankings of correlation (in Fig. 7).

Coming back to the overall manuscript and the proposed major revisions, I also suggest to include the figures along the lines of argumentation. Fig. 1 might benefit from some topographic information instead of politic boundaries. Fig. 2 did not give me much insight, which might be due to my scepticism to the suitability of the employed method. Fig. 3 and 4 might be combined?...

With regard to your author comments to the reviews, I found it relatively difficult to grasp your intended lines of revision. I sincerely hope you will find my comments helpful in this respect. Please also note that both reviewers indicated room for improvement especially for scientific quality and scientific significance of the manuscript.

Since our special issue is an inter-journal one which opens the opportunity to publish related data in ESSD, I would like to encourage you to consider publication of the data and scripts either as appendix to your MS or as own data publication. As far I understood, the data you used is partly hosted on publicly available repositories already. However you like to see the HESS data policy for details: https://www.hydrology-and-earth-system-sciences.net/about/data_policy.html

Thank you again for your contribution. I am very much looking forward to receive your revised manuscript.

All the best and kind regards.
Conrad

Dear Floyd Vukosi Khosa and co-authors,

after studying your replies to the reviewers, the revised version of your manuscript and receiving two more reviews, I have to agree with reviewer #2 that many concerns of the original review have not been addressed. Although you worked through my suggestions, I cannot waive these concerns.

Since reviewers #1 and #3 were highly supportive to your study and I also see its potentials, I hereby open another round of major revisions.

All the best,
Conrad

Dear Floyd and co-authors,

thank you again for your contribution and the efforts you spend into your manuscript and the recent revisions. I had sent your last version to the second reviewer for evaluation and received a generally positive feedback.

To be honest, I have hoped for a more progressive iteration of your manuscript to increase the density, scientific quality and possible outreach above the current level. No reviewer scored your manuscript “excellent” in any of the quality aspects (scientific significance, scientific quality, presentation quality). Although reviewer #2 proposed to publish your manuscript, he/she scored the scientific quality only “fair”.

From my point of view as editor of the special issue “Linking landscape organisation and hydrological functioning: from hypotheses and observations to concepts, models and understanding” I have asked you before to relate more clearly to the topic of our special issue. In your case, I of cause see the relationship of landscape functioning, its modelling in terms of soil moisture products and your discussion of this products. However, I cannot find a synthesis towards the main goal of our special issue, which we formulated as the “link” between landscape organisation and hydrological functioning. Maybe it is a simple matter of the length of your manuscript that such important findings do not stand out more clearly?

To be more clear about our special issue, please allow me to stress once more that we see multiple examples of landscape organisation, the processes which shaped the landscape and the processes and state dynamics we are desperately trying to quantify. Your study has a very high potential to become a valuable contribution to this, as you are discussing satellite-based and model-based means to derive distributed soil moisture dynamics. However, the recent iterations of your manuscript did not convincingly address a condensation of your insights at the level of enhanced understanding neither of the systems nor of the data, nor of the models.

I have asked assistance of a more senior editor at HESS (Laurent Pfister) in the matter, as I see the extra work which is required to revise your manuscript. I also see the issue that I hereby ask yet another time for the mayor revisions, which have been demanded from the beginning. I regret to cause you more work. However, I hope you agree that manuscript is worth the efforts to become a concisely aggregated piece of scientific communication, which is really reaching out.

To get there, I propose to radically shorten the manuscript. 27 pages for basically an applied case study of already published tools is too long. Your messages are buried in too many details, which are of secondary importance. From my point of view, this is already the case in the abstract. What are your key points? With respect to the special issue you handed your manuscript to, there needs to be much more focus on the capabilities of your methods and the properties of the products and processes (i.e. the sources of the time lag, the uncertainties in the products, but also the strong correlations you found and their interpretation).

Moreover, I propose to radically reconsider how to structure your manuscript. In the current version you are repeating a lot of published details about the tools you use. As I pointed out in the initial request for technical corrections, your way of clarification that these tools are not specifically developed for your study but are a citation of the fundamentals of the R-packages or respective models, is not really convincing. Maybe I got it wrong, but to me, you “simply” applied the tools of several R-packages to publicly available GLEAM data and previously done CCAM-CABLE simulations. As reference, you have the two fluxnet station soil moisture time series. This is a fair setup, which should not take 11 pages to describe. Especially, there should be more room for the actual important things e.g. about the “de-trended and de-seasonalised (or decomposed) soil moisture time series signal” (L393, or is it only de-trended as in L389?, how is this done? what are the assumptions introduced by this? etc.). Moreover, there should be more room to motivate the capabilities of the respective applied techniques. E.g. you first compare the products on the basis of R2 (Fig. 3) and then in the cross-wavlet analysis (Fig. 4). To me this appears to relate to two opposite very far ends of a possible range of approaches with the first being highly aggregated assuming a normal distribution and the latter being very fancy with a focus on temporal patterns. But since the main pattern is the strong seasonality, both approaches could be criticised. The reasons why and how you seek to derive new insights from this combination did not become very clear to me. Instead, Fig. 5 takes on the seasonality by another means (timing of onset/offset), but the interpretability of this plot is limited. I also do not see, how your claim L630f. is corroborated by this plot, when the in-situ data time series of onset/offset presents some years with strong deviations (of several months!). I also find it disturbing that here is only one station with in-situ references, which raises several questions about your former claims (why can you calculate an R2 but no estimate about the seasonality? how does this relate to Fig. 2?).

If I am not mistaken, until here you are evaluating your model results against in-situ data and satellite-based estimates to prepare the next step: The extrapolation in space. Before I comment on this, I would like to mention that I am still confused, where the estimates/references to the two different depth zones in the soil enfold some explanatory power. Coming back to Fig. 3 there appears to be a standard deviation of about 10 vol.% for the top soil and all GLEAM models appear to have a positive bias again of about 10 vol. %. Your study is to my understanding also much about uncertainty with the different products, but this does not become clear here. Moreover, the lower depth zone appears to have a much smaller range of observed states (between 5 and 13 vol.%) which is not at all represented by any of the estimates? I did not find this as a conclusion in your manuscript, which I find rather disturbing. This is especially so, since there should be a problem with your water balance if you estimate more water in the top 10 cm AND the lower 10-100 cm. If we assume your mean soil moisture in the lower zone is estimated to be 15 vol.% higher than the observed, this accounts to 135 mm which is about one fourth of the annual water balance. Of cause, this can also be a problem with the soil moisture data. However, I am not quite sure, if this can be considered as “all the soil moisture products are able to capture the variability in the observed soil moisture” (L507)…

For the next step into spatial distributions, obviously there is no in-situ data reference. In the last step the ESA products performed ok for top soil moisture. Where are they now? As I said before, information about your general experimental setup appears to be obscured by too many details about the different techniques and side-tracked claims. And GLEAM did not convince me much in the first part. But you are left with GLEAM as reference for your CCAM-CABLE. How can you now evaluate the performance of your model against another model product which actually somewhat failed before? I appear to have missed this step.

Hence I am also not quite sure about the application of MI – especially for the spatially aggregated plot Fig. 9. Technically, there is a confusion about L389 and L392f., where it does not become clear, which exactly is the time series derivate you compare. In the results, you attribute the differences (Fig. 9) to the different forcing data, which appears a little strange to me if you seek to compare the information added by the respective model (or as Nearing et al. 2016 but it: “How much information do we have, and how well do we use it?” doi.org/10.1080/02626667.2016.1183009 2016). Anyways, if you now have deviations and agreement of spatial patterns between the models, and if these patterns are not caused by the input data or the landscape alone, what can we learn about specific process representations in the models? Or in other words, what can we learn about the representation of the landscape functioning in our models?

Please allow me to again raise questions about the seasonality and your claims about the strengths and “uncertainty” of the models under study. As you have introduced with the weather normals in Fig. 2, there is a quite strong seasonal pattern in rainfall. This seasonality is only weakly seen in the soil moisture data - mainly because the recorded in-situ values are really low. What is the water balance for the two sites? Do you at least find a majority of the water represented in the measurements? I am a little afraid, that there is quite an issue with this data. If the seasonality is a feature of your forcing data, why do you attribute the gains to the model? I would even claim that your seasonality appears to come with an error margin of several months - if I understand Fig. 5 correctly.
Your study area for Fig. 6 stretches over several climatic zones, land cover types, soil classes and altitudes. This opens many ways of first order estimates about indexes about hydrological functioning. For me it is almost impossible to evaluate the validity and meaning of your SSI. Is it an artefact of the input data or is it a new information which is worked out by the model? This would be another possible application of the MI, which for my understanding of the method is actually more in line with the idea of MI.
Both examples impose substantial questions about your claims with respect to the capabilities and uncertainties of your models. To be honest, I find them rather weakly supported. This is especially so, because your hypotheses and assumptions are very difficult to trace through the many steps and methods. Eventually, it appears to me that CCAM-CABLE and the GLEAM versions are compared without any references to landscape properties and first-order estimates (like a soil topographic index, budyko curve position, water balance estimate, etc.). Without such references, I do not see how you can make any justified statement about the model capability and uncertainty.

I still expect that much of my critique and confusion is due to the structure and length of your manuscript. Hence I hope that you will find my comments helpful to bring your paper to a very insightful and well-received contribution to the community.

As stated before, I suggest to really do a mayor revision, which should start with a reorganisation of the main lines of argumentation and a very clear presentation of the things YOU developed and adjusted (instead of repetitions of the toolbox descriptions your apply).
Eg. for MI, you could rather point out, why you use it and what it can (and cannot) reveal and simply cite the R package and the original reference (eg. Details can be found in the R package manual and in Kraskov et al. 2004…). Your eq. 12 to 14 are not helpful to understand your points. I would even claim that they obscure the understanding of your application where the time series pre-processing might be a fundamental step, which I could not really follow. Furthermore, you remain rather unclear about what you would describe as uncertain or certain. Did I get it correctly, that “low certainty” would mean large residuals in both model products? You might also like to double check for typos (L391: does it really mean “certainly” not “certainty”?)
This also holds for the other methods. Especially the different approaches to evaluate the models remain often very implicit. E.g. Fig. 5 appears to me to perfectly suggest quantitative measures of the “goodness of fit” (again toolboxes exist). But you expect the reader to follow your argument based on these graphs. I see that it is difficult to derive good estimates in the spatial comparisons later on. But there are nice examples in the literature, which really work out the uncertainty of the models.

Again, I sincerely hope that you find my comments plausible and helpful. Please let me remind you again to not to forget to relate to the scope of our special issue.

I am looking very much forward to a substantially revised version of your manuscript.
All the best and kind regards,

Conrad

Dear Floyd and co-workers,
First of all, thank you again for your work and submission to our special issue. Please accept my apologies for the recent delay. I have studied your last revision and sent it to one of the more critical reviewers. He/she acknowledged the substantial progress and was positive about a publication in the current form, despite some open issues. I agree with him/her in general.

The reviewer pointed out the following minor points:
l96 - missing endpoint
l102 - not sure if spatio needs to be lower case
l124 - I would prefer "...is one indication of how well ..." there are others as well!

I would be pleased if you could give some final thought about the following points:

1. The abstract could be a little closer to the actual emphases and findings of your study:
l23 - soil moisture organisation for different landscapes is not really assessed in your study as it does not approach any causes or functionality nor precise patterns. I would suggest to clarify the sentence to really point to spatio-temporal representation of regional differences by the products. I still find "partying" to be erroneous here - at least I cannot understand it.

l33f. - the variance might be "explained", but the (in some cases quite substantial) bias is not mentioned here nor reported in your linear models in Fig. 3. You point to this in the text though - especially in the later course of the manuscript. All deeper soil ("root zone") results turn out very weak in mean value and spanned range. Even the best fit (CCAM.CABLE) in this regard has more than +100% offset (observed mean around 7 vol.%, CCAM.CABLE mean around 15% at Skukuza). The GLEAM results are much further off. For the top soil a quite similar picture unfolds - just that the range of observed states is larger.
Just fitting a linear model and calculating the R2 cannot capture this. I consider it a methodological issue in this comparison to base it on R2 alone, so that the variance might apparently be better captured by GLEAM. But after all, GLEAM consistently and strongly overestimated soil moisture. The linear scaling factor appears to deviate much from 1, too. For an application in data scarce areas with little basis for ground evaluation, I think that your method should include this. Moreover, the comparison with R2 but datasets with different length is problematic, too. Maybe the reminder to this is not sufficient when the conclusions are not very self-critically presented? Please reconsider this in the respective parts of the manuscript.
To come back to l.33 and your abstract: Your conclusions are much more precise and informative on this issue. Maybe you could consider some sharper summary in the abstract as well?

l35. - in phase with the pronounced annual cycle in the semi-arid area?
l36. - Are the 20 days important? To what degree is this an effect of the temporal resolution of your data? I would omit this in the abstract.

2. further text passages:
l95f. - the sentence appears fragmented. establishing what and with what purpose/capability? Could this be the place to somehow set the fact of the strong seasonality in the region into perspective?
l102ff. - the sentence consists of many. (i came across some rather long sentences before.) please try to simplify and clarify so that the repetition of the different estimate products is resolved too.
l148 - what is Clovelly?
l156 - what 80% threshold? are you aggregating to a 0.8 percentile instead of the mean? why? at what point in the study do you really calculate with daily data? in the wavelet analysis? how are e.g. the monthly aggregates derived? maybe table 1 could hold this temporal resolution and one or two sentences would help?
fig 2. - maybe a thinner line with dots at the reference points would be easier to read?
l423ff. - see remarks above.
fig 5. - I like the plot in general. what are we learning from the exposure (facing direction)? would this simplify the graph and enhance the comparability if this dimension is left out? given the many blanks, this is difficult to read. only N appears to deviate substantially. One could use violin plots to allow for two classes in one of the panels. Moreover, maybe a drought index or seasonal rain input sum could help understanding the temporal differences?
fig 6. - the contour lines refer to elevation I suppose. Please include in caption or legend. Would it be helpful to repeat some fig 1b-d as small prints on the right side as column over the legend? Is it maybe more honest to use a continuous colormap for this plot? The classes are difficult to evaluate like this.
l612f. - I would consider this discussion and I do not see why scale should be the foremost issue with this.
l613f. - Again, what is the explained variance of a strongly seasonal signal? The R2 assumes two gaussian distributions to explain one another, but at least the observed signal does not appear to be gaussian. I still do not see what I can learn from explained variance if offset and scaling factor in the linear model are the actual issue for any application.
l621 - Also again, I would not see much substance to the "root zone" values if all products deviate substantially from the ground observations. The time lag might really not be the issue here.

l663 - Please update your repository for the current state of the manuscript. To comply with the Copernicus data and code policy, this should also include a little more than the three short scripts. Is it possible to provide the data directly, so that your study can be directly reproduced with the scripts? At least this would be the aim of the data and code policy and it would be very helpful if we try to get as close to this as possible.

I hope these comments are helpful for the finalisation of the manuscript. HESS will also provide copy editing after finalisation. Thus I focused on the content. Thank you again for your work on this. I really think it makes great progress to become a nice paper.

All the best,
Conrad

Dear Floyd Khosa and co-workers,

Thank you again, for the efforts you invested into your manuscript. I am really confident that this manuscript has improved significantly during the review process and that you are constructively aiming to resolve the remaining issues in the manuscript.

However, I have to admit that I feel a little confused by some of the recent changes. The new Taylor plots and bias plot appear to me not only advantageous. My recent concerns have been with the interpretations rather than the presentations: I find it quite substantial for your study to point out that it remains difficult to predict the in-situ soil moisture dynamics by all presented models (with different strengths and weaknesses) and that especially the root-zone products suggest very little coherence with the observations. Your manuscript nicely points out what to expect and where to be careful. Admittedly, some of this weakness results from rather few data points in Malopeni. The new plots omit this situation and aggregate the data into single points with the three evaluation criteria. But it appears even more difficult to me, to actually evaluate the results in the Taylor plots.

You write "The disparity in the amplitude of variation at Skukuza, is indicative that there is a need for further investigation on the homogeneity assumptions for the site when it comes to the dominating drivers of soil moisture." L525ff. Judging from your old scatter plots, it appears to me that the "root zone" soil moisture is simply less dynamic (which is in line with most site observations) but that the models strongly overestimate the mean values and the amplitudes. To blame heterogeneity here, is maybe not very helpful nor does your study support this claim with data.? Or am I completely wrong with my reception of your results?

Long story short: To get your manuscript to a publishable state quickly and to avoid any further problems, I would suggest to combine Fig 3 and 4 into one, so that the bias plot can be seen as a third column (separated by some space but aligned to the regions and using the same marker colours) and reporting the old scatter as appendix with a respective reference in the main text. Content-wise, I simply ask you to honestly stick to the main story and data in your study. This includes to avoid speculations (i.e. about heterogeneity) and that statements as in L636 about ESA to capture within acceptable certainty might be rephrased to simply state that correlation for top-soil in Skukuza was 0.7 with few bias and that this is acceptable for you. The more general statement does not clarify, what is acceptable and that the root zone is not captured…

Unfortunately, also Fig. 5 (now 6) did not improve. My suggestion to use violins aimed at reducing the number of panels and combining the respective differences in one panel by plotting the two halfs of the violins with respect to the categories. Right now, there appears even a strange issue with the ESA-combined violins (violet) in row/subregion a and d (why very wide?). Moreover, you omitted to include information about the median and quartiles and confidence intervals. So the plot got even more difficult to interpret.
You argue that the plot is important to understand the organisation of soil moisture across the landscapes. I fully understand this notion but I find it very much left to the reader to draw conclusions from this plot. Hence, I suggested to reduce the number of panels (as 10 of 24 are empty anyways and make cross-comparisons rather difficult) and to really work out the important messages. Form my understanding, the difficulty which stands in your way is that the categorisation is somewhat arbitrarily chosen and hence may not reflect the organisation of soil moisture patterns (in the models and which probably may exist in nature or not) but may only try to look at model results which might be coherent or incoherent within a class due to many possible reasons. Frankly spoken, I would expect some sort of reduction of dimensionality and potential clustering of the data into the proposed classes. Given the fancy cross-wavelet transform on the one hand (where we basically learn that the data resembles the annual data pattern which comes at no surprise to me, given a semi-arid strongly seasonal climate), this approach appears rather imbalanced.
Another thing which striked me is that there is no reference about the respective number of sample points in each box/violin. Nor can I judge if a deviance in one category (e.g. higher CCAM-CABLE values in south facing e and f) is actually a problematic and consistent feature of the model as there is no reference to the overall distribution…

Again long story short and to conclude the issue asap: I would suggest to return to the boxplots and to revise the clustering of categories. One possible option could be to use the years as columns and allow for grouped boxes after the respective slope exposition. This would at least help to read the plot. With respect to the spatial differences, one could also imagine to group the boxes always after the landscape classes, the models as rows and the years as columns… Moreover, I would suggest to give the plots a background grid for easier reading.

Fig. 7 is much better now. Although you again tried to follow a suggestion of mine, a simple repeating of fig 1b-d is not really an appropriate solution.
Tab. 2: I am a little confused by the reported elevation ranges of the zones. From fig. 1c I would not expect them to fall into the reported classes without overlap and with exact match of the range bounds. Either I misinterpret Fig. 1c or there might be another issue which could resolve several problems:
Am I correct, that the sub-regions a-f consist of 16 cells each and that all analyses in section 3.2 are based on the respective monthly time series of the three models? So basically one box or violin in Fig 5/6 consists of the 12 annual data points of at maximum 16 at minimum 1 cell? Given the seasonal pattern, maybe it would be easier to look at the data from a different perspective, i.e. the time series or even monthly aggregates over the years? Why should the distribution of the whole year be more justified?
I would be very pleased if you could work out this aspect of the reference pixels much more clearly. Maybe this could also resolve the difficulties with fig. 7, when the sub-regions could be marked instead of the elevations or the national borders? I am very confident that a clarification of this issue will really improve the manuscript. Please also check, if these steps are appropriately explained in the methods section. For me, I still find it difficult to follow these steps in the methods section

This issue also may lead to an improved fig. 1: First of all, please remove all not used eco-climatic types from the legend. If the regions are plotted in each figure, there might be an easier reading of the respective classes, too? Alternatively, fig. 1 b-d could come into fig. 7 and a simpler version of the localisation of the sites and region is used in Fig. 1?

I am sorry if this review process is causing you more work than initially expected. At least it is very exhaustive for me. Maybe we both should have been more strict in the beginning of the review phase. If you like to switch to a more direct communication or in case of any questions, please contact me. I am very confident that you can and will resolve the issues and bring your manuscript to a state where it meets the high standards of HESS.

All the best.
Conrad

Dear Floyd Khosa and co-workers.

Again many thanks for the work you put into revising your manuscript. I think, it is now in a shape that we can all agree on worth publishing.
Your last revisions have made a huge impact from what I could judge during quick reading.

Unfortunately, I still spotted some issues I would ask you to address before final approval:
L371f.: You state the intention of the regional reference groups very briefly. But it is now only in L888ff that the zone are described. I did not see any references to Fig. 6 b-d. Please revise the presentation of the selected subregions. I see the dilemma of referencing fig. 6 before fig. 2 and table 2. I could imagine that table 2 is not really a result but a methodological prerequisite. As such this could be nicely placed in the methods description of your “pattern analysis”. I would not consider it problematic if you simply state that the map is given with the results in fig. 6 b-d for comparison. Another path could be to make fig 6 b-d a separate figure in sec. 2.4.3? You might wonder about this forth and back suggestion. However, these are simply reactive suggestions, because in the current form it is not solved consistently.
Please also check for a consistent referencing of the subregions’ attributes. With consistent I mean that a more general climate type is given in table 2, but in fig. 6d the Köppen-Geiger classes are reported. If I am not mistaken Cfb would be oceanic but the subregion resembles Cfa pixels. Moreover, the legend of fig 6d is still not easy to understand. It is not common practise of all of the audience of HESS to know the classes short names by heart. Nor is it reasonable to have BWk (arid desert cold) hardly discernible from Cfa (warm temperate fully humid summer hot). I suggest to use the colormap of the cited source (they have provided the colour definitions in their R-script) and I suggest to include the long names in the caption. Moreover, I still cannot see Cwc, Csc, Cfc and BWk in the map. This might be due to the chosen colormap. Please remove the classes, which are not in the map from the legend.
Subregion B is the only one, which consists of two KG climate types. Cwa and BSh. Why is it classified as humid (Cwa) if it could equally be semi-arid (BSh)? Maybe a brief statement would be helpful?

Moreover, the soil texture map suffers similar issues of readability. I see another issue with your classification. You report in table 2 a-c as clay, d-f as silt loam. I can imagine to discern a and d from the rest (based on your given map). But I do not see how you argue for the two main classes. From a functional point of view, maybe there could be a better way of classifying? Maybe it is just a matter of the awkward colormap? I feel a little uneasy that I have to point out such flaws in this very late state of the manuscript. Obviously, the view for such important details has been obscured by bigger issues before. Please make sure that your subregion attributes are reported correctly and consistently with the data you base the classes on.

Unfortunately, also your chosen characters for marking the subregions are not plotted in the same size. As such, also the appearance is difficult to understand.
Maybe you give the subregions more intuitive names? Like lowland silt-loam humid savanna for A. This could follow the different main classes and lead to a more intuitive code like LSHS compared to lowland clay humid savanna (B) as LCHS and so on. But maybe you have even better ideas.

Fig 3. The dot colour of ESA combined is not the same in the two plots. Moreover it is difficult to discern the respective dots. You might like to orientate on some sources for colourblind friendly palettes for your purpose (e.g. https://davidmathlogic.com/colorblind/#%23648FFF-%23785EF0-%23DC267F-%23FE6100-%23FFB000 , the link includes the 5 HEX codes).

Fig 5. Unlike your statement in the replies, I do not find your caption to be updated. Please carefully revise according to your reply (incl. the explanation of the data points behind each box). Given the discrimination into aspects, each box can host between 90*1 or 90*16 points, or am I mistaken (daily soil moisture on 90 days at 1 to 16 pixels respective to the distribution of aspects)?

Please make sure you have high quality graphics ready for the final typesetting. This includes a consistent font of the annotations and axes format (fig. 6b-d differ in size and formatting). You may consult the HESS guidelines again: https://www.hydrology-and-earth-system-sciences.net/for_authors/manuscript_preparation.html

Furthermore, I am not convinced that your reported "analysis script" is really coherent with the paper. The data and code availability statement is intended to make research reproducible. To be honest, I would need extraordinary effort to recollect all bits and pieces of your study and the scripts would not help me because I have no idea what is in "SSM-comparison-all-products-skukuza-monthly-imputed.csv” or in the moisture comparison grid tiles. A brief check also reveals that the scripts are not complete as e.g. the package “varrank” is not loaded but mi.data is called in your MI script. Please make sure to comply with the data policy of HESS: https://www.hydrology-and-earth-system-sciences.net/about/data_policy.html
For the ESA and Gleam data, this requires to follow the citation policy of the data source and HESS (including the version number and potential parameter subsets). For the data of your institution you might ask for permission to publish the data along with the manuscript to follow the HESS standards. This can be in a preprocessed form. Maybe the data behind fig. 5 would already make a great step? Your code should at least be complete.

Again, I am sorry to cause you work. This is not what I intend. However, handling your manuscript dramatically exceeds the regular processing efforts in the role of an editor. You had very supportive reviews and yet, flaws surface (like the elevation classes in the last version) which weaken my trust in your analysis. I hope that you can appreciate the efforts we take to get your manuscript published. I would be very pleased, if this is the last round of corrections. Please double-check all scientific details, the consistency and readability of your figures, as well as compliance with the HESS standards with your co-authors before submission of the revisions. I am confident in receiving a final manuscript next time. Otherwise I will have to step back as handling editor of your manuscript and forward it to another editor for further processing.

All the best. Kind regards,
Conrad

Dear Floyd Khosa and co-workers,

Thank you again for the work you invested in revising your manuscript. Again, the improvements have been worth it.

I also thank you for preparing the data alongside, although I cannot access the dataset yet. Could you please update the data availability statement accordingly? Does the dataset on Mendeley include your r-notebooks? The pdf print is just for the review process, right? I would not see it as a valid supplement for final publication. You could also simply upload your r-notebook and the data to your GitHub repository. There you can use their publication scheme with a doi through zenodo. Either way, the data availability statement needs to be updated.

For the data from other sources, please also include the version reference and citations in the data availability statement.

Fig. 2c: Fig. 2 improved. In 2c you still have the locations of the flux sites, but they are not included in the legend. I still find the colormap of 2c very difficult to discern. The sizes of the subplots is not the same...

Fig 6: First of all, you did not update the subregion "a-f" in the caption and the long name HuSuSa-HoSeSa is cut off as label on the right side.
Sorry to push this minor issue so much. But I either do not understand correctly or the number of data points in one box is not 16*3*30*4. I can follow that each set of boxes refers to this number. But since you chose to present the aspects, it could happen that in one box only a single pixel (1*3*30*4) is included. I also see that this will be consistent for all 5 models. Although I still find it difficult to interpret your data based on aspect but without consideration of slope (only implicit as range of altitude), soil water storage, topographic wetness index or something more explanatory... For now, I would not change the plot any more but the caption should be correct and self-descriptive. Maybe a simple statement that the data basis is daily 3-month data at 16 points of the subregions for 4 years (2011-2014) for each data product would be helpful?

Appendix A: I am generally very happy about seeing this data. However, I am also a little surprised and lost. If you report the data in the repository, maybe this could be simply referred to? Otherwise, the linewidth needs to be reduced and the style should match with your other figures. Moreover, the axes lack their labels.

Figure B1: I would see Skukuza as black (not blue). R2 of the upper left panel is covered by data points. The caption does not only allow to guess that the figures in the panels are the R2.

Could you please carefully check your manuscript accordingly.
Sorry for appearing picky, but finding such flaws that quickly should actually not happen in this late phase.
All the best.
Conrad

Dear Floyd Khosa and co-workers.
Thank you for your corrections.
All the best.
Conrad