Before the manuscript is sent back to review, I would like the author to make some simple modifications to better justify some of his assumptions.

Dear John

I believe your manuscript still requires to be improved before I send it back to the reviewers. I acknowledge that you have tried very hard to respond in a constructive way to the criticisms that were made. However I feel that a few minor but critical points need to be addressed. I believe that these would strongly improve the likelihood of satisfying the reviewers (and me). Follows my appreciation of your improved manuscript as well as a set of recommendations. I am totally committed to providing you with a fair and honest review and appraisal of your paper, but you will understand that the criticism it has raised among the reviewers require a well crafted response from your part.

Jean

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One of the main issues concerns the computation of what Pelletier calls residuals and is referred to as “computing multiple intercepts” from a single regression by several of the reviewers. Although I see what the author has been trying to do, I also appreciate the point made by the reviewers that the value of P0 obtained by regression depends of course on the assumed value for h0 used in equation (1). Pelletier should call his residuals P’ or Pr, to avoid confusion and refrain from making the assertion that by analysing the residuals, he is providing further constraints on what controls P0, as defined by Heimsath.

Pelletier argues now that the main factor controlling the residuals is tectonic stress. He shows that a simple relation obtained by Savage and Swolfs to predict stress can be used to predict the residuals. I note that in his revised version Pelletier makes references to Figure 2 whereas he means 3, I think. Pelletier also claims that there is an additional climatic control which he assesses by comparing the already corrected residuals with those further corrected by a climate correction factor. I am still somewhat confused on how that coefficient is determined.

In the first version of the paper submitted to EsurfD, Pelletier argued for a control by fracture density which he estimated by introducing a damage index. He has revised not only the definition of the damage index, but also lessened his conclusion concerning the importance of damage/fracture density, arguing now for a control by topographic stresses alone. In this way, he has responded constructively to many of the reviewers criticisms.

Another major point of disagreement with the reviewer(s) is the measure of fit to data used by the authors (regression coefficient), whereas one of the reviewers argues for another, more appropriate measure, based on so-called Nash-Sutcliffe statistics. Pelletier argues that the measure proposed by the reviewer is inappropriate for assessing regressions. I am not an expert on this, but interestingly, the two methods yields the same fitness measure and Pelletier argues that it is appropriate.

All reviewers wonder why Pelletier has not performed a more classical multi variate analysis of the residuals, rather than privileging a step-by-step reduction of the residuals by incrementally incorporating potential processes through a simple mathematical description of the process. The main reason, I believe, of Pelletier’s choice is that the relationships between variables (such as slope, climate, etc.) and residuals may not be linear at all and/or depend on thresholds which would be difficultly extracted from a simple cluster or multi variate analysis. I dont think, however, that this is clearly stated in the revised manuscript and it should (if my interpretation is correct) or an alternate explanation should be given.

There a few (unfortunate) comments by one of the reviewers that almost suggest that the author may have not properly reported the data (difference between a table and a diagram); the author has verified and confirmed that this is not the case. I checked a few points and saw no difference between table and plot. I will specifically ask the reviewers to refrain from making such comments in further reviews.

Several reviewers argue that the physical processes invoked to explain the residuals are unwarranted or difficult to justify. Pelletier has revised his arguments that there is a significant control on P0 from slope aspect. He has refocused the paper to argue that topographic stress and, to a lesser degree, climate, are the main controls on explaining the residuals from the “simple” soil thickness control relationship of Heimsath et al.

Pelletier has addressed most of the reviewers' other concerns in his responses and in the modifications he has brought to the manuscript. It is, however, important that the manuscript be re-assessed by the reviewers before it is considered for publication in ESurfD.

My recommendation is to ask Pelletier to further improve his revised version before we send it back to the reviewers by:
- changing the symbol from P0 to something else to clearly express that he is talking about residuals from a first order control/fit to soil thickness, not P0 as defined by Heimsath. He should also refrain from directly referring to P0 (as defined by Heimsath et al) in the discussion and conclusion parts of the manuscript. Rigorously, his findings concern P, the production rate, not P0, the maximum production rate at 0 soil thickness, although they might be strongly related, of course;
- verify the numbering of the figures in the revised version of the text;
- explain in the text of the article and in more detail why a “classical” multi-variate analysis of the data is not appropriate here;

Following the first set of contrasted reviews and the extensively revised version of the manuscript that you resubmitted, I sent it for an additional round of review. One of the first reviewers was contacted and accepted to provide a review, as well as two new and independent reviewers. All three of them recognize that your contribution is important and should be published but they also all recommend that revisions be made before publication. I read these reviews very carefully and I am of the opinion that the manuscript has been greatly improved but still requires further modifications. In particular, parts needs to be clarify so that the reader understands all the details of what you have done to interpret the soil production rate dataset of Heimsath et al. All reviewers also question parts of your approach, and make suggestions to improve the relevance of your findings and, in my opinion, the impact of your manuscript. My recommendation is that you carefully consider the suggestions made by the reviewers and, using them, prepare a revised version of your manuscript. Where you do not agree with the reviewers suggestions, please indicate and justify why.

I would like you to pay attention to the following important points:
- Please explain what the “average slope” as defined by Heimsath means, i.e. how it is calculated and whether this is an appropriate measure to relate to local stress intensity (all three reviewers comment on that point);
- Please respond or take into account the second point made by Reviewer 1 who disputes your argument that the relationship between slope and production rate is due to extensional stress fracturing;
- Could you easily check whether hill orientation with respect to the regional steps field direction plays (or not) a role in setting production rate (through stress fracturing) as suggested by Reviewer 2; this is a good test of your hypothesis and, in my opinion, would not require much work to verify;
- Please pay attention to the various remarks concerning the applicability of the Savage and Swolfs relationship to the study area, as well as the use of a correct measure of slope (see my first point);
- Reviewer 3 makes very constructive points concerning the way you have analyzed the data; the Reviewer’s suggestions should help clarify your approach and help supporting your interpretation;
- Reviewer 3 also makes a very interesting suggestion concerning the important section 2.2 of your manuscript; I urge you to consider this point carefully and, if possible, implement his suggestion(s) in your revised manuscript.

Upon reception of your revised manuscript, I will decide whether it is appropriate to recommend publication or send the manuscript for an additional round of review. However, in view of the nature of the concerns expressed by the reviewers, I do not think that this will be a priori necessary. Let me also apologize for the delay in making a decision on your manuscript but the last month has been extremely busy for me and I found it difficult to isolate a few hours of my time to carefully read your revised manuscript and the comments made by the reviewers. I hope you will understand.

Many thanks for the thorough revisions and clear response to all reviewers' comments and suggestions. As it is, I believe the manuscript has been greatly improved and made clearer for ESURF readership.

I am pleased to accept this manuscript after its extended and thorough review and revision process. Thanks to the author, associate editor, and reviewers for the time and effort to see this through, and I hope the paper stimulates further debate and additional targeted studies on this topic.