Soilscape evolution of aeolian-dominated hillslopes during the Holocene: investigation of sediment transport mechanisms and climatic–anthropogenic drivers

Cohen, Sagy; Svoray, Tal; Sela, Shai; Hancock, Greg; Willgoose, Garry

doi:https://doi.org/10.5194/esurf-5-101-2017

Articles | Volume 5, issue 1

https://doi.org/10.5194/esurf-5-101-2017

© Author(s) 2017. This work is distributed under
the Creative Commons Attribution 3.0 License.

https://doi.org/10.5194/esurf-5-101-2017

© Author(s) 2017. This work is distributed under
the Creative Commons Attribution 3.0 License.

Articles | Volume 5, issue 1

Research article

|

30 Jan 2017

Research article |

| 30 Jan 2017

Soilscape evolution of aeolian-dominated hillslopes during the Holocene: investigation of sediment transport mechanisms and climatic–anthropogenic drivers

Sagy Cohen, Tal Svoray, Shai Sela, Greg Hancock, and Garry Willgoose

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Final revised paper (published on 30 Jan 2017)
Preprint (discussion started on 01 Feb 2016)

Interactive discussion

Status: closed

AC: Author comment | RC: Referee comment | SC: Short comment | EC: Editor comment

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- Supplement

RC1: 'review of Cohen et al.', Anonymous Referee #1, 06 Feb 2016
- AC2: 'Responce to Reviewer #1', Sagy Cohen, 11 Apr 2016
RC2: 'paper review', Anonymous Referee #2, 24 Feb 2016
- AC3: 'Responce to Reviewer #2', Sagy Cohen, 11 Apr 2016
AC1: 'Responce to Reviewer #1', Sagy Cohen, 11 Apr 2016

Peer-review completion

AR: Author's response | RR: Referee report | ED: Editor decision

AR by Sagy Cohen on behalf of the Authors (11 Apr 2016) Author's response Manuscript

ED: Referee Nomination & Report Request started (02 May 2016) by Arnaud Temme

RR by Anonymous Referee #1 (02 May 2016)

Suggestions for revision or reasons for rejection

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.

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RR by Anonymous Referee #2 (09 May 2016)

ED: Reconsider after major revisions (10 May 2016) by Arnaud Temme

AR by Sagy Cohen on behalf of the Authors (24 Jun 2016) Author's response Manuscript

ED: Reconsider after major revisions (25 Aug 2016) by Arnaud Temme

I thank the authors for their second revision of this manuscript. Some of the issues that the reviewers flagged after the first revision have been solved, and this is to be commended. However, as the associate editor, I feel that not all issues and in fact few of the major issues have been dealt with to the extent that was expected. In some cases, I have the impression that no answer is given to reviewers' questions or criticism, and that instead merely a different point of view is presented. From my role safeguarding the process, I feel that it is therefore best to send the manuscript back to you without consulting the reviewers again. Below, I have attempted to provide more detailed guidance about a few points that I think you should focus on for a subsequent revision. However, I think that your entire response needs to be reconsidered. Given the importance of changes that I feel that you should consider, I see this as a "reconsider after major revisions" decision.

The first issue where I think no full justice has yet been done to a valid point of criticism, is reviewer 1's criticism of the value of parameters n4 and beta. You refer to an extensive sensitivity analysis and discharge data, but I believe these are not shown in the paper. Even if you insist on not showing them in the paper, it is a good idea to show them in your response to the reviewers, to convince them that this has been done successfully. When you show that, make clear what your criterion was for the ' best approximation' that you refer to on page 3 of your response document. I can imagine that it is worthwhile to pull into this response your intention with the two figures of diffusivity versus slope. You state that beta = 0.1 is needed to reproduce the observed topography, but is this topography a result of the aeolian setting? Is the current aeolian activity and diffusion in the landscape in equilibrium with the shape of the landscape? It seems you are making that argument, and if so, I would disagree with that just like reviewer 1.

There is heated discussion between you and reviewer 1 about how to model diffusion. There appears to be mutual misunderstanding or difference of opinion regarding the definitions of concepts such as routing, but I think the main point that the reviewer makes about diffusion modelling is that the results you show in the various figures have 45 and 90 degree angle elements that are likely model artifacts. I find that you should answer this point rather than go into a heated discussion about the modelling itself. As editor, I can live with differences in opinion about how the modelling is best done and best described, but results should be at the very least plausible. Please comment extensively on whether you agree that some of your figures show unrealistic patterns (I tend to agree here with the reviewer), and consider whether this should lead to an adaptation and rerun of your model - or to acknowledging to the future reader that this is unrealistic, but does not affect the main results of your study, which remain interesting. (As a scientist in your field, may I suggest that the apparent disagreement over routing may be resolved by adopting Dinf ' routing' with p=0? If I follow along correctly, then that that is functionally equivalent to the diffusion equation in your case.)

Thirdly, the basic form of two equations has been criticized, and I think the criticism has not been taken to heart. For Equation 4, the unit problem persists. After your small change in the manuscript in Eq 4, the units read: [m/y] =not [-/-][m/y][y]. This must be improved rather than defended, it seems to me. If you have a more elaborate algorithm that you summarize for readers' comfort, that is to be commended - but it should be correct. I did value the addition of Eq 5 in this context. (The changes to Equation 4 should be made in context of the discussion about diffusion above).

The other example of criticism of the basic form of a function comes from reviewer 2 who to my mind correctly points out that also your version of the humped equation is not correct in terms of units. Your response is not understandable to me, and appears to duplicate an earlier answer to reviewer 1 - which would indicate that the problem persists. Please provide responses and actual improvements for the next round of revisions.

As you consider whether you want to submit a further revision, please take into consideration that a novel answer to the reviewers' comments after your first revision is expected. They will not have received your current response.

I think the paper remains very interesting and deserves ultimately to be published - but that it requires a substantial amount of work to get there. I hope you have the opportunity and the continuing interest to make this happen. I wish you all the best with the revisions.

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AR by Sagy Cohen on behalf of the Authors (21 Nov 2016) Author's response Manuscript

ED: Publish as is (04 Jan 2017) by Arnaud Temme

ED: Publish as is (04 Jan 2017) by Tom Coulthard (Editor)

AR by Sagy Cohen on behalf of the Authors (04 Jan 2017)

Short summary

Soil-depleted hillslopes across the Mediterranean and Europe are thought to be the result of human activity in the last 2–5 millennia. We study a site on the margin between Mediterranean and desert climates which was subject to intense wind-borne soil accumulation for tens of thousands of years but is now mostly bare. Using a numerical simulator we investigated the processes that may have led to this landscape and identified the specific signatures of different processes and drivers.