Below are my point-by-point responses to the authors.
1) In my previous review I commented that the fact that a model with both fluvial and diffusive processes works better than one with just diffusive or just fluvial processes is not a significant conclusion. In their response the authors state that this is not a conclusion of their study (i.e., “the conclusion of this study is NOT that both transport mechanisms are in play…”). In fact, the text of the paper makes clear that this is major conclusion of their paper. Their conclusion section states “Only by simulating both fluvial and diffusive transport mechanisms can the model correctly simulate the observed soil distribution.” However, I accept the fact that the authors are also examining how the relative importance of diffusive versus fluvial processes varies with topographic position.
However, the authors do not provide any reason why the addition of mass in the form of aeolian deposition would fundamentally alter the relative importance of fluvial versus diffusive processes as a function of topographic position, which was considered in Cohen et al. (2015) for what the authors call "bedrock (normal) landscapes". Instead, they simply modify the values of key parameters (n4 and beta especially) without calibration to data, then conclude that aeolian soilscapes lead to a completely different ratio of fluvial to diffusive processes as a function of topographic position than bedrock landscapes. I would be completely in support of this result if there was actual evidence presented that n4 and beta should be 0.1 for this field site or any other aeolian soilscape, but there is simply no data presented to demonstrate that these are the correct values. I continue to believe that any difference between the results of this paper and that of Cohen et al. (2015) for bedrock landscapes results not from the fact that one is a “bedrock (normal)” landscape and the other an “aeolian soilscape” but rather that this study has chosen very different and ad hoc values for n4 and beta that have no justification and no clear connection to this our any other aeolian-dominated landscape. In their rebuttal the authors present two figures of soil diffusivity versus slope that purport to show a calibration, but there is no data in these figures. They appear to be simply graphs of S^1 and S^0.1. A more minor but related issue is that I don't think that bedrock (normal) landscapes and aeolian soilscapes are fundamentally different kinds of landforms. They exist on a continuum, since soils everywhere in the world contain some fraction of material derived from in situ weathering and some from aeolian deposition. This was my point when I recommended to the authors that they obtain some data (using immobile element ratios or similar geochemical techniques) on the relative fraction of the soil derived from aeolian input versus in situ weathering. The authors countered that they don't need data because the aeolian-dominated nature is clear from "walking the site." I don't know what this means.
2) I agree that some type of power-law relationship with depth and slope is correct for fluvial transport, so I am not going to harp on the fact that there is little clarity in how the authors have modified Engelund and Hansen (1967) to arrive at their eqn. (1). The fact remains that, if the reader looks at p. 42 of Engelund and Hansen (actually p. 41) there is an expression for the Shields stress as a function of the mean dune height and other parameters. How these equations relates to equation (1) of Cohen et al. remains unclear. Referring me to TOPOG or some other model does not answer the question of how one goes, step by step, from one or more of Engelund and Hansen’s equations to eqn. (1) of Cohen et al., which is what I think readers need (in an appendix would be fine, if the authors consider this to be ancillary).
3) Yair and Kossovsky (2012) may provide a basis for using a value of n4 that is lower than 1. However, the authors have provided no justification for the specific value they used (0.1) either in the paper or in their rebuttal. This value still seems to be pulled from thin air. Why not 0.3 or 0.5? This is a major issue, since the value of n4 directly controls the strength of the fluvial term in the model, and its variation with topographic position.
4) I am very disturbed by the author’s statement that “Diffusion absolutely involved routing, how else does the model transport the sediment down the slope?” This seems to indicate that the authors do not know how to model diffusion. Diffusion is the divergence of a flux. The divergence of a flux is defined as the derivative of the x component of the flux in the x direction plus the derivative of the y component of the flux in the y direction. Flow routing such as D8 do not appear anywhere in the definition of divergence and SHOULD NOT be used for diffusion on hillslopes. There is certainly no reason why flow routing methods are REQUIRED to model diffusion. The fact that D8 is being incorrectly used leads directly to the unrealistic “striping” seen in the results. Obviously, any model result that shows large variations in model results along 45 or 90 degrees is a model artifact that needs to be minimized. I don’t see any of this kind of striping in other aeolian soilscape models that have been used in the literature to model soil depth or aeolian soil fraction (which are not referenced). This is a major issue that simply must be fixed.
5) In my review I noted that D8 cannot be used for hillslopes, where the flow of water and fluvial sediment is divergent (D8 assumes strong convergence everywhere). The authors counter that they have developed a fast model and so any inaccuracies should be acceptable in the name of speed. I disagree. I think the model needs to be accurate first. Again, this is a major issue that must be addressed.
6) As with the value of n4, no calibration is performed to show that beta = 0.1 for this field site, either in the paper or in the rebuttal. To do this calibration, the authors would need data. There is no data in the two figures provided in the rebuttal, which appear to simply be plots of S^1 and S^0.1. The authors may be correct that beta = 0.1 is an interesting result, but the authors need to show the readers (via some type of least-squares or other fit to DATA) why beta = 0.1 at this location.
7) Equation (4) continues to have a units problem. In their rebuttal the authors state that equation (4) does not have a time step but I am looking at eqn. (4) right now and the last term is “delta t”. Since diffusivity is always L^2/T and the only other term with units is delta t then D must have units of L^2. However, the reported units are L/T. The authors may think that “In practice it makes not difference” but I think it will matter to readers trying to replicate their work. The authors have indicated that their diffusivity has units of L (no units were reported in the paper so I was guessing that diffusivity had units of L^2/T, which is always the proper unit of diffusivity), but this still leads to a units problem since if I use units of L for diffusivity, then according to eqn. (4) D should have units of L*T, not L/T.
8) I am not going to comment on the author’s response to my concerns about the weathering portion of their model, since I don’t find it acceptable for the authors to refer me to older papers and send me code rather than simply answering my question.
9) I don’t see how “walking the site” allows one to conclude that the fine grained component of the soil cannot be from weathering of bedrock. Again, data is needed.
10) I asked for a table of parameters. The authors refer me to the last 4 papers on this model. Including a table is a very simple request and I am disappointed that the authors refuse to do even that much to assist the reader.
I can see how the authors might view my review as an attack on their paper. However, I am really trying to help them meet common standards for accuracy and transparency. |

The same two anonymous reviewers have read the resubmitted version of your manuscript, along with the response to reviewers that you provided. They reach differing conclusions (reject vs minor revisions). It is my opinion that many of the points that reviewer 1 raises, are fair. Indeed there appears to be insufficient consideration of the concerns that this reviewer raised based on the first version of the paper. More changes are clearly required. Reviewer 2, although less critical, agrees at least on one point: that one of your most important formulae has wrong units. To my mind, this means that adaptation is required, and that model reruns with reconsideration of results are necessary. I translate this into a request for resubmission after major revisions.

Should you decide to resubmit an improved manuscript, please make sure to provide a detailed response that reflects the importance of reviewer 1's concerns.