Review of Wang et al.
This paper contains a clear comparison of the chi and S-A methods for extracting information such as the channel steepness and concavity index from river profiles. The paper is timely since these two methods are being used in parallel and a comparison of their strengths yet to be performed in such detail. I ask for revisions as I am not quite prepared for this to be published; I believe there are some elements that could be improved and will hopefully increase the impact of the paper. The original AE was unable to continue handling the paper, and thus I have looked at this paper after the first round of revisions, so this does constitute a second round of review that the authors were not expecting. Hopefully the authors find my comments constructive. I have spent some time making editorial comments in order to improve the readability of the manuscript. In addition, I still feel the authors have missed a few relevant papers, although they have done a good job of addressing the comments relating to landscape transience and the papers cited by one of the referees.
Referee 1 had three main comments. Firstly, they felt changes in concavity might have been caused by transience and suggested an inversion of the uplift rates from the channel profiles. The authors have done this to show there is only minimal evidence for transience in the studied catchments, and in addition cite previous work that suggests a low degree of transience. In chi space, the best fit concavity index, based on collinearity, tends to lead to concave channels (e.g., figs 10, 12 and 14). If the channels were all incising into spatially homogenous bedrock, and the uplift rate was spatially homogenous, this would suggest a slowing of uplift. This is seen in the inversion results, but is subtle. It is not really clear how the inversion might deal with changing transport processes: the authors suggest the change in concavity is due to alluviation rather than changing uplift rates, and thus represents a change from detachment to transport limited conditions. Overall, I feel the first two comments from this referee are addressed but I do feel the methodology could be clearer. In my lined comments below I make specific suggestions about where more detail is needed.
Referee #2 had further methodological questions. The authors have answered some of the comments but again I feel there is more scope for making their methods clearer. Again, I will suggest changes in my lined comments below.
My recommendation is that the paper be accepted subject to revisions. I think there are some interesting and timely results here, but the paper could use some further edits to help readers understand what the authors have done. Since I am not calling for additional analysis, I will say these required revisions are minor.
Lined comments:
P1 line 8: Delete “one” after “former”. Also what are “deviated concavities”? I don’t see a discussion of this in the paper. It seems the concavity indices identified by the S-A method are similar to the ones determined by the chi method, but with higher uncertainties. I would just delete the phrase “and deviated concavities” from this sentence.
P1. Line 9: “False knickpoints”: again, I don’t see much discussion of this in the text. How is one more likely to find a “false knickpoint” using chi analysis vs S-A analysis? S-A analysis, done with intensive smoothing, might only pick up the largest knickpoints, but this isn’t discussed in the text. The main focus of the text is that the S-A method is better at identifying changes in concavity than the chi method. So why not write that in the abstract instead?
P1. Line 11: Delete “manage to”.
P1, line 13: Add a sentence explaining why serial correlation of residuals is important to eliminate.
P2, line 10: This section is not as clear as it should be. There is a very important point that belongs here and that the authors imply but do not state explicitly. The concavity index can change. In the S-A approach, the plots are simply data reflecting topography and the concavity index can be extracted from regression. This regression is subject to the noise of S-A data and the details of profile smoothing, but it is a reflection of data. The chi transformation, on the other hand, contains an assumption about concavity. Thus if a chi profile is used one must use some discriminatory technique to separate areas of different concavity: such a method has not, to my knowledge, been suggested. There are a number of suggestions for determining concavity of a river network using chi analysis but none for determining spatially varying concavities. In S-A analysis the concavity can be extracted directly from a regression of the data. This point is extremely important! I believe this point is what the authors wanted to highlight in the paper so it needs to be stated very, very clearly. S-A analysis is very noisy compared to chi analysis, so this property, that S-A analysis is a more direct measure of concavity, is really the main reason to continue using S-A analysis. The authors would do well to emphasize this point.
P2, line 10: I do suggest rewriting this section, as outlined above, but “for its need to estimate slope” is awkward and needs to be rewritten.
P2 line 12-13: Awkward sentence. Rewrite to: “In addition, the derived channel steepness suffers from high uncertainty due to…”. Also Perron and Royden need to be re-cited here.
P2 lines 19-21: This section needs some rewriting. Say “Thus, the chi method provides…”. Then the reason the uncertainty will be underestimated should be explained. Finally the last sentence (“false concavities and knickpoints”) needs to be rewritten into my suggestions stated above: because chi analysis is based on the assumption of a single concavity, in places where there is spatially varying concavities (because channels may go from bedrock to alluvial) the chi method may show a break in the chi-elevation profile that is spurious.
P3 Line 1: say “is debris flow dominated and therefore will not display the typical fluvial scaling in Equaiton (1)” and then cite the Stock and Dietrich 2003 paper:
Stock, J., and W. E. Dietrich (2003), Valley incision by debris flows: Evidence of a topographic signature, Water Resour. Res., 39(4), 1089, doi:10.1029/2001WR001057.
P3 Line 3: the sentence ending in “scaling” needs a citation. The Whipple and Tucker 1999 paper might be appropriate here, or perhaps the 1994 willgoose paper:
Willgoose, G. (1994), A physical explanation for an observed area-slope-elevation relationship for catchments with declining relief, Water Resour. Res., 30(2), 151–159, doi:10.1029/93WR01810.
P3, line 5. Replace “could get” with “derive”.
P3, line 7: This sentence is unclear. How exactly is the channel subject to lower uncertainties? You can restate that the chi analysis of the channel can be derived from the bedrock section that is suggested by the varying concavities in S-A space.
P3, Line 9: Here the authors say that the coupled process provides a better way to perform stream profile analysis. As I mention earlier, this has not been well demonstrated because the different advantages of the two methods have not been sufficiently highlighted in previous sections. Modification of the text earlier in the paper should fix this problem.
Page 3, Line 9: While it may be true that “little has been done” on the statistics of S-A or the integral method, there are some papers that investigate this topic that are strangely not cited here. In fact there is a paper with the title “A statistical framework to quantify spatial variation in channel gradients using the integral method of channel profile analysis” which I am familiar with because I wrote it! The entire purpose of that paper was to explore statistical ways to constrain channel steepness and m/n. So I cannot understand why that paper is not even mentioned.
Mudd, S. M., M. Attal, D. T. Milodowski, S. W. D. Grieve, and D. A. Valters (2014), A statistical framework to quantify spatial variation in channel gradients using the integral method of channel profile analysis, J. Geophys. Res. Earth Surf., 119(2), 2013JF002981, doi:10.1002/2013JF002981.
As a historical note, our original version of that paper included calculation of the D-W statistic, but we found it did not yield information that was better than other tests. However, if you use our code that was released along with the 2014 paper you will see that it still spits out the Durbin-Watson statistics for all chi analysis (https://csdms.colorado.edu/wiki/Model:Chi_analysis_tools).
P3, line 14: What I think is missing from this section is a clear description of why these statistical tests are necessary. I only think a few sentences are necessary but an explanation of the benefit of these statistics would help keep the attention of the reader.
P.3, line 16: The authors need to state if these tests are performed on the entire profile or only for the sections identified as bedrock using the S-A analysis.
P4, line 11: Again, an additional sentence or two is needed here to explain why these statistics are needed and useful.
P4, line 17: The Harkins et al is an excellent paper, but they do not present any evidence that chi and S-A methods produce the same results. To my knowledge, the first paper to actually compare the methods was the paper by Scherler et al (2014), which should be cited here:
Scherler, D., B. Bookhagen, and M. R. Strecker (2014), Tectonic control on 10Be-derived erosion rates in the Garhwal Himalaya, India, J. Geophys. Res. Earth Surf., 119(2), 2013JF002955, doi:10.1002/2013JF002955.
P4, line 19: How was the dividing point determined? Was it done by eye or some other method? This needs to be explained. There are a number of ways to do this rigorously. I’ve done it with multiple segments in the Mudd et al. 2014 JGR-ES paper and we also used a 2 segment method for 1st order channels to find the area of the process transition in this paper:
Clubb, F. J., S. M. Mudd, D. T. Milodowski, M. D. Hurst, and L. J. Slater (2014), Objective extraction of channel heads from high-resolution topographic data, Water Resour. Res., 50(5), 4283–4304, doi:10.1002/2013WR015167.
P4, line 23: The difference in the results between this paper and the Perron and Royden paper is curious. If you use the 10m DEM that they used do you get the same result they did? I note that a previous review has asked for such an analysis and it has not been performed. I now see that higher resolution data has been downloaded and analysed so it seems not too much work to report the results with higher resolution data.
P4. Line 24: Delete “with each other”. Then later in the sentence you can say the “there are large uncertainties in channel steepness of approximately 40%. Also I think there should be a sentence saying how the uncertainty is computed.
P4, line 30: This is an important result and I feel it should be stated in the abstract.
P5, line 3, 4: Again, how was this transition point identified? The method needs to be stated.
P5, lines 13-15: These sentences could be clearer. Please rewrite.
P5, lines 20-24: Again, there is a need for some text explaining why the D-W statistic and t statistics are useful. What are the implications of these tests?
p.6, line 3: Here is another chance for the authors to highlight why the S-A approach is useful even though they have shown that it gives highly uncertain channel steepness values. They need to reiterate here that S-A data makes no assumptions about m/n and therefore is more sensitive than chi analysis in detecting spatially varying concavities.
P6, line 8-9: Awkward sentence. Rewrite.
P6, line 13: In the Mudd et al., 2014 paper we included an extensive discussion of selecting m/n based on the main stem vs the collinearity and I feel that paper should be cited here.
P6, line 15: I suggest writing Theta_co is the concavity from the collinearity test, and theta_mR is the concavity derived from averaging. Also, there should be some more detail as to how theta_mR is calculated: what, exactly, is being averaged?
P6, line 30: It needs to be stated here if these results are based on all of the profile data or just the data that has been determined to be bedrock using S-A analysis.
Page 8, line 6: Replace “various” with “variable”. Do you mean “calculate”? This sentence doesn’t make sense, please check.
P.8 Line 22: Add sentence explaining why this is the case.
P. 8 line 33: Unclear what is meant by “composited”. Reword.
P.9 line 10: This is an interesting result, but brings me back to the question of why your estimated concavity of the bedrock sections is so different from that estimated by Perron and Royden (2013); see comment on p4, line 23.
P. 9, line 19: Say “The knickpoint is located at an elevation of…”
P.9, line 24: replace “it” before “suggests” with “these steepness indices suggest”.
P.9, line 32: I don’t feel the sentences starting with “thus” is supported. Why would you trust the S_A analysis more than the chi analysis when you have already shown that estimates of k_sn from S-A analysis are highly uncertain. I believe your results show that when the S-A analysis differs from the chi analysis it should be the chi analysis that should be trusted due to its lower uncertainties. Either explain or delete this sentence.
P. 10 line 22: Does “Amanda” have a surname?

S. Mudd

I have a few minor edits that should make the text clearer. Hopefully it takes no more than half an hour. My comments are attached in an annotated pdf.
I look forward to seeing this paper in ESURF.

This paper is ready for publication and I thank the authors for their attention to reviewers' comments.

Thank you for taking the time to thoroughly address the comments of the reviewers and the AE.