Dear Dr Schaller and co-authors,

I have read both the reviewer reports and your paper carefully, and have recommended that some moderate revisions be undertaken. Some indication of the areas requiring attention is provided below; I have added some additional comments from my own perspective.

The two reviewers have provided some helpful and informative commentary on the manuscript, especially as regards the need to adopt a systematic nomenclature for the weathered materials being discussed. The authors' proposed revisions to the manuscript in light of these comments appear to be entirely appropriate, and should adequately address this issue.

Reviewer #2 also commented on the extent to which the work described goes beyond prior published work from the same field sites and using the same GPR methods. All of the soil chemical data analysed in the present paper were derived from prior work at these sites. I therefore think that a fundamental issue to be considered during revision of the manuscript is to make a clear demarcation of what is new and what is derived from prior published studies. For example, in lines 152-155, the paper reports that various soil locations were 'described, sampled, and analysed'. Yet all of this was done in previous studies, not for the current manuscript, as the text may tend to suggest. This needs to be more clearly acknowledged; this is not done until much later (lines 190-191).

I think that the prior published work could also be cited to avoid the repeated descriptions of methods, since they are in many cases not new. The procedural descriptions make the current manuscript rather long. For instance, in lines 222-22 there is no need to explain what LOI (loss on ignition) means; likewise, I suggest omitting the simple introductory description of GRP in lines 235-240. Readers can either refer to the literature or to a standard text to find this material if they are unfamiliar with GPR methods. Again, I think that you could omit lines 273-285, where the processing of the GPR signals is described, and merely cite the prior published studies from the field sites. At the least, it ought to be possible to greatly abbreviate this material.

Reviewer #2 also points to a concern over unmeasured water content in the weathered materials examined using GPR. Given that this can strongly influence GPR signals, I think that some further comment is required, especially in light of the likely site-to-site (especially N to S) differences in water content among the sites and at the various depths within the weathered material. In the absence of such data, unknown variation in water content may be confounded with other properties of the materials such as the chemical properties. Presumably, samples for water content determination could readily have been collected in sealed bags for later water content analysis.

I would like to raise some further issues for consideration, from my own reading of the manuscript.

First, I found there to be a lack of clear hypotheses or objectives, though two are listed in the Abstract but not enumerated in the body of the manuscript. Clearly, the study relates to the possible use of GPR methods to extend the available information on soil thickness that can be derived from pit sections. The reasons for seeking to do this are not immediately clear. Moreover, in line 141 (under '2. Study areas', rather than in the Introduction where it would be more appropriate) the manuscript refers to the issue of how climate and vegetation affect soil thickness and GPR observations. This might, for instance, have been listed as an objective in the Introduction. Was investigating this issue indeed an objective of the present work, or not? If it was an objective, then I felt that more information on the site conditions was needed, including for instance NDVI data or some comparable information on the vegetation, perhaps supplemented by aridity indexes, data on seasonality and seasonal variation in climate conditions, and so on. In this context, moisture content in the weathered materials would again have been informative. Later in the manuscript, the role of aspect (equator-facing or pole-facing slopes) is raised: was there also an hypothesis underlying this, in light of which the N and S faces were sampled separately? If so, this provides another subject that might be listed in the Introduction as an objective of the current work, if that was indeed the case. Regardless, the reason for sampling both N and S facing sites warrants some explanation, as does the denser sampling of pedon locations on the S-facing slopes than on the N-facing slopes, where only a single site was examined. Readers are likely be interested in the rationale behind such choices.

In relation to the field sites, I noted that the hillslope study sections are in some cases extremely short: apparently < 3 m in the N-facing site at Nahuelbuta, to judge from Figure 3. Extrapolation from the pedon to the hillslope scale over a distance of < 3 m amounts to only a very limited extension of the pedon data. Similarly, the S-facing slope at Pan de Azucar appears to be < 10 m long, raising similar issues. In general, I think that some additional commentary on the scale of the topography being studied would be helpful for readers. For instance, is the challenge of extrapolating from pedon to hillslope over such short hillslopes typical of the challenge faced more generally in such work? In other words, do these sites constitute an informative test case?

The manuscript touches on hillslope aspect and its relationship to soil thickness (lines 622-624). Here I felt that if this topic is to be discussed, then wider acknowledgment of the growing published literature on this topic was needed. I mention here a few studies that came to mind only as examples. The literature on this topic is now quite large.

Yetemen, O., E. Istanbulluoglu, J. H. Flores-Cervantes, E. R. Vivoni, and R. L. Bras (2015), Ecohydrologic role of solar radiation on landscape evolution, Water Resour. Res., 51, 1127–1157, doi:10.1002/2014WR016169.

Yetemen, O., E. Istanbulluoglu, and A. R. Duvall (2015), Solar radiation as a global driver of hillslope asymmetry: Insights from an ecogeomorphic landscape evolution model, Water Resour. Res., 51, 9843–9861, doi:10.1002/2015WR017103.

Srivastava, A. et al. (2019). Aspect-controlled spatial and temporal soil moisture patterns across three different latitudes. 23rd International Congress on Modelling and Simulation, Canberra, ACT, Australia, 1 to 6 December 2019 mssanz.org.au/modsim2019.

Inbar, A. et al. (2018). Climate dictates magnitude of asymmetry in soil depth and hillslope gradient. Geophysical Research Letters 45, 6514-6522.


In the Discussion section, I think that there is much speculative material that would likewise benefit from additional supporting references. For example, there is the unreferenced claim that

"From the top- to toe-slope position along a catena the potential for physical erosion decreases downslope due to decreasing physical potential whereas the potential for deposition increases".

There are certainly many situations where this does not apply; in drier climates the volume of overland flow may increase downslope, and whilst hillslope gradients might decrease there, the surface roughness may decline such that the surface runoff becomes faster and more erosive. Rilling and gullying are consequently often characteristic of footslopes, not the steeper upper slopes. The more general point is that, in order to interpret soil thickness and the variables that influence it, some knowledge of the erosional and geomorphic processes that operate at the site concerned is really needed. None is provided in the current manuscript, and it would be helpful if something could be said. Similarly, in discussing the different patterns of soil thickness on N and S-facing slopes (lines 624-642) the manuscript is almost entirely speculative. The authors hypothesise that some differences might perhaps relate to aspect-related differences in soil moisture (lines 624-625) or vegetation cover (line 627) or subtle lithological changes (line 630) or local heterogeneities in erosion (lines 634-635) or even other processes such as differences in evaporation (line 641). Given that the manuscript presents no evidence bearing on these issues, I think that this discussion might be curtailed somewhat. Reference to prior published work on this topic (see suggestions above) would support some brief comments. The authors also raise some issues in passing, that are not given further attention in the manuscript. For instance, they mention possible site-to-site differences in bedrock joint spacing (line 165), but do not discuss how important such variation might be in affecting their results. In this context, I was conscious of the recent work of Leone et al. (reference below) in Arizona where regolith thickness was influenced not primarily by aspect but by the orientation of the foliation in the underlying bedrock, in relation to the topography. This is an instance that reminds us that weathering and soil production can be influenced by much more than surface climate, vegetation, or three-dimensional hillslope curvature.

Leone JD, et al. (2020). Strong slope-aspect control of regolith thickness by bedrock foliation. Earth Surface Processes and Landforms. Available in Early View.

Finally, I think that the Pearson correlation analysis that is set out in section 3.3 ('statistical correlation and principal components analysis') is poorly utilised in the paper. This is suggested as one of the new contributions of the manuscript (lines 37-39). No correlations are actually presented in the paper; rather, these are only briefly qualitatively referred to, and the actual data are relegated to the Supplementary information. Little appears to be said about the correlations, and therefore perhaps the long methods description relating to this work (lines 296-311) could be abbreviated. Alternatively, if the correlations are regarded as important, then perhaps more analysis of these results could be incorporated.

Dear Dr Schaller and co-authors,

Many thanks for making the various revisions to your manuscript, "Comparison of regolith physical and chemical characteristics with geophysical data along a climate and ecological gradient, Chilean Coastal Cordillera (26° to 38° S)".

Having read the revised version, I can report that it has adequately addressed the issues raised by the reviewers and in my own editorial comments. I think that the paper is now is a condition suitable for publication, which I will now recommend.

Congratulations.We appreciate your submission of research work for publication in 'Soil'.

kind regards,
David Dunkerley

Dear authors, I am glad to inform you that your manuscript has been now accepted for publication in SOIL.

Congratulations and thanks for consider SOIL as the journal to publish your research results.

Sincerely

Jorge