Review for “Global analysis of short- versus long-term drainage basin erosion rates“ by Chen et al.

General comments:

This paper by Chen et al. is the latest attempt to gain a better understanding on the controls of climate and tectonics on erosion from the comparison of modern river loads with longer-term cosmogenic nuclide-derived denudation rates. The authors have my respect for attempting this comparison, as it is time-consuming to do. Nevertheless, I find the approach too general to be useful. For example, no attempt has been made to quantify uncertainties for short-term erosion rates, but knowledge of which should be crucial for when comparing two independent methods. Short-term rates are erosion rates from suspended sediments, while rates from cosmogenic nuclides are denudation rates, thus integrating over erosion and weathering. Strictly speaking, the two cannot even be compared. One way out would be to include dissolved river fluxes in short-term rates. While for rates from cosmogenic nuclides the authors rely on a previous compilation which has been carefully quality-checked, a quality check for the compilation of short-term rates is missing (see below).

As such, this study does not provide in my view significant scientific advances over previous studies that have carried out this comparison, and it is missing several substantial characteristics of a solid scientific manuscript (like uncertainty assessment). I am therefore against the publication of this manuscript at it is now.

Specific/extended comments for each section

Intro: What makes this study unique over the previous studies that compared these two different methods? (Besides, maybe, a larger dataset now available?). Why do we need yet another comparison? Is the comparison actually leading anywhere, as both methods have different biases… and the uncertainties associated might be too large to say anything beyond something that is better than a factor of 2 comparison? That alone could result in differences that are beyond the uncertainties.

Methods:

What does “compiled from published literature” mean for suspended sediments? Was there some initial quality check performed? For the USGS data, 2 criteria were used to confine the data (monitoring time and a basin area threshold). But, were there similar criteria for the other station data? Often, data is published were sediment rating curves are really poor, or monitoring times are really short. Especially in remote terrains, suspended sediment data is very sparse due to inaccessibility (in glacially impacted terrains) or due to infrequent rainfall and low discharge in general (dry regions). Hence, a rigorous data quality control and resulting means to use only the best data is needed first. Otherwise, any comparison can only be qualitative in nature and a quantitative comparison that even includes statistical analysis, as attempted by the authors, is useless. A useful endeavor for making short-term erosion rates better comparable with cosmogenic nuclide denudation rates would be to associate an uncertainty to the former. Perhaps this could be done by MonteCarlo Simulation or so, but without having an uncertainty associated, the comparison remains qualitative. What does a factor of e.g. “1.4 higher” mean? Is this beyond uncertainty? As you may have guessed by now, in my view anything that this < factor of 2 between the two methods is actually a quite acceptable agreement. The problem is that not much more to be drawn if one of the methods does not have an uncertainty….

Results:

Another issue is that once datasets are compared to each other (short- vs. long-term rates), one should use the individual data from each basin/river only, meaning the data should be compared 1:1, i.e. only compare stations where there is actually short-term AND long-term data measured within an acceptable range of distance, or better even measured at the very same station). Only when trends with e.g. climate are analyzed for each short- or long-term dataset individually, the entire dataset might be used.

Section 3.4: This area-grouping makes sense and should have been done prior to the entire analysis. Otherwise, there is always the question of whether any trend observed may be due to the different number of observations within each bin….

Fig. 3: This trend found between the US-derived long-term erosion rates and MAP  - is this trend also present in the entire dataset? If not, why is it present only in this dataset and how can then a global general interpretation be drawn if the global dataset does not show the same trend? (In line 376, the usage of 3,074 datapoints is mentioned in this regard. I´m confused, as in Fig 3, only the US data is used…Is the red line in Fig. 9 now using the entire dataset, or only a US-subset?)

Fig. 4: glacially impacted denudation rates higher than non-glacially impacted rates: That is nothing new. See reviews by Dixon et al. (2018) and Delunel et al. (2020, ESR) for the European Alps and the study by Ganti et al. 2016 (Sci Adv) that shows that cosmogenic denudation rates are likely affected by a time scale averaging bias. It´s a pity that these studies were not cited.

Fig. 5: I don´t think that an increase of 1.4 has any significance without analyzing uncertainties.

Fig. 6: What kind of figure is this? What does the bar legend indicate? Number of observations???

Discussion:

Section 4.1: A key point for the relation between long-term erosion and MAP is the LOWESS smoothing method. However, there is no reference nor any other further information given how this smoothing works (averaging window?). Given that the resulting shape of the pattern is so much different than that found by others, I would encourage these authors to provide more information on it. See also my comments to Fig. 3 that are relevant here.

Section 4.2: What are the actual apparent ages (integration time scales) of the long-term data? Given that denudation rates are typically high (>0.5 mm/yr or so) in glacially- impacted regions, the resulting integration time scale are low (<1200 yrs), and do therefore not integrate over the last 25-15 ka. Same problem for Section 3.2.

Section 4.3: Same here as for Fig. 5.

Section 4.4: Sorry, I don´t get where this leads to. I find the section too general to be useful. Why make such a fuss about an absent relation between erosion and drainage area? Usually people use such an absent relation to show that there data is NOT influenced by sampling location… This section jumps from one topic to another without any clear red thread….The second para is ok for what the first-order observation is… (the fact that the larger the basin, the better the agreement between short- and long-term erosion rates). Last para: An R² value of 0.24 or 0.29 does not describe a significant relationship.

The manuscript by Shiuan-An Chen et al. describes a compilation of cosmogenically derived denudation rates and a compilation of short-term erosion rates from gauging data and couples these together to ask/answer questions about long- and short-term controls on erosion rates.  I commend the grad student, first-author on a lot of work done in getting these datasets put together but I think the paper could be radically improved. I like the general idea of the paper but I found a couple of issues that I just can't get past in order to believe the results. First, denudation from cosmogenic nuclides is a combination of weathering products and erosion fluxes, but there is no mention of this in the paper or accounting for it by combining solute fluxes, or alternatively, convincing me that these data don't require this. Second, the paper reads like a choose-your-own topic where the authors pursue, in my opinion, too many different avenues. I would have preferred if they had decided, after doing all the background analyses that appear in the MS currently, which is the most interesting of the findings and then focusing the MS around that idea. Sadly(?), sometimes science involves doing work behind the scenes that doesn't need to appear in print anywhere. Personally, I find it really interesting that the analysis shows something very different from the Kemp et al., 2020 Nat. Comm. paper and would focus on that aspect given the strengths of the methods here and the flaws in that Kemp paper. Then, all the information/figures would be circling around this single topic.  So I recommend a substantial revision to make the MS more readable/interesting to the reader.  Currently, it has a PhD dissertation-chapter style, but not the style of a MS that tells a story or makes a compelling point through several lines of evidence. 

Abstract comments

    

"Measuring erosion rates, analysing their temporal variations, and exploring environmental controls are crucial in the field of geomorphology because erosion through sediment transport in drainage basins shapes landforms and landscapes." <-- This is a confusing first sentence because it seems to imply that erosion is important but then that sediment transport is important. Erosion of sediment and transport of sediment are different things when viewed through the cosmogenic lens. 

"unpicking" <-- perhaps use 'unpacking' or better 'unraveling' instead? In any case, are they really controls or are they simply correlations?  I'm guilty of doing this leaping myself so I know it is tempting.   

 

Introduction

I think the authors should take another try at creating a compelling abstract. This current abstract goes into details that are both irrelevant and either incorrect or imprecise. Fortunately, the authors don't need to correct each statement necessarily. It should be tightened up to focus on the paper and analysis done and conclusions drawn.  I suggest writing papers backward: i.e. write the conclusions, then the discussion necessary to support them, then the results, methods, only parts of the intro necessary to tell the story at hand and then the abstract. This paper seems to be written the opposite way. It should really help rewrite the paper a bit more logically. Missing from the analysis are the other ways long and short-term data can be different including aliasing and the likehood of rare events (a la Kirchner, 2001 already cited) as well as the likely timescales of sediment storage and purging, which are relevant for sediment gauging data.   

Here are some things that should be fixed and in some cases removed especially if irrelevant in a revision: 

  

"The erosion rate of a drainage basin is an important geomorphic quantity because it reflects the net flux of sediment from source to sink in drainage basin and correspondingly, the rate and spatial pattern of landscape evolution." <-- There are a lot of concepts mashed together without regard for precise language or concepts here in this first sentence, which paints a negative first impression of the work, unfortunately. 

Line 50: I take issue with these statements. There are many indications that sediment storage can be on the order of millennia in floodplains. Also, it's unclear exactly what timescale they are thinking is negligible. There are very few cases where bedload and suspended sediment have both been quantified to a degree that one could actually say this. I would feel uneasy making this statement for the whole world from just a handful of studies.  

Line 65: This whole paragraph is riddled with incorrect statements about the basin-wide cosmogenic method and missing are some critical parts that should be included. Cosmogenic nuclides don't assume no sediment storage. This is another example of imprecise language. If that was the case, no one would ever publish any cosmogenic nuclide data, because there's obviously sediment storage in watersheds. Cosmogenic nuclide basin-wide erosion rates do not assume no decay. It is often negligible but it fact we *know* that decay exists and is ongoing. Also, there is a lot of data to show that in many cases there *are* discrepancies with 10Be-derived erosion rate with differing grain size. In fact the earliest paper (Brown et al., 1995 that the authors cite) showed that this was the case. No erosion–deposition cycle? No, that's not how I understand it.  Those papers don't say cyclicity doesn't exist anywhere that I remember.  Quartz is not assumed to be equally present throughout the catchments - that is something that is checked, and if it isn't the case, it is corrected for or we don't use the method if it cannot be accounted for. 

Cosmogenic nuclide analyses do actually need to assume that catchments have been receiving cosmic radiation throughout the entirety of the time they have been eroding the layer that has moved through the production zone and that the eroded sediment is coming from the surface. So, if a catchment has been glaciated - especially if only part of it has been glaciated - the concentration generally can't be used as reliable indicator of the erosion rate. Unless(!), the erosion rate was so high that the timescale of averaging is less then the glacier retreat age and it is only scraping off the very surface - not below the attenuation length. This is maybe the case in a couple places (New Zealand?) but it also creates circular reasoning given that the averaging timescale is determined from the erosion rate that might be too high owing to the glaciation itself. What a pickle! Another strategy is to not assume that t->infinity (in steady state) and to assign a deglaciation age to the "t" (time) in the erosion rate equation. Unfortunately, these conditions for "ok cosmo erosion rate data" from glaciated catchments are not met in the OCTOPUS database to the extent that you should trust them to make a definitive statement about glacial vs. non-glacial erosion rates. Any small difference you find in the two datasets could easily just be due to violation of the 10Be method. If the rates are lower for the glacial catchments, then you could maybe qualitatively infer something (I don't know how it would be quantified) since the glacial bias would cause the observed rates to be too high - not too low.      

Line 80: The authors go from 'global' to 'nation' a little too quickly. (Also, I know this wasn't the intent but it sounds like the authors are saying the US is the only nation in the world.) 

Line 84: Typo: "of sediment yield" not "on sediment yield" but also saying non-linear here evokes the wrong concept.  At mid-MAPs, the erosion rates are highest and are lower for very high MAPs and very low MAPs.  Non-linear is a very vague way to say this.  It is also non-exponential. You might say, there's a mid-MAP maximum or something like that. A similar fit is described much better in the later section that talks about the Misra et al., paper. 

Line 95: "Global analyses of short-term erosion rates from suspended sediment records

suggest that a change to agricultural land cover has enhanced erosion rates by one to two orders of magnitude (Dedkov and Mozzherin, 1996; Montgomery, 2007; Wilkinson and McElroy, 2007; Kemp et al., 2020)." I don't think this is exactly right since these authors don't show a timeseries with agriculture imposed at some point. They simply show that agricultural rates are higher than different areas with other rates - sometimes at discrepant timescales, which is a fraught topic. Of the places currently in the literature (before this paper) where long term and short term rates are compared, in Covault et al 2013, which the authors cite, >50% of the long-term rates are higher than the short term rates.   

Line 100: To my knowledge, nobody has definitively shown with data that vegetation actually plays a role like the authors are suggesting here (except perhaps Vanacker et al., 2007), it is a hypothesis.   

Line 110: Similar comment to that above: 'higher rates are *associated* with glaciated terranes' might be a defendable statement (but not using cosmogenic nuclides, since they actually don't show this.) Are the authors actually saying that the decreased infiltration that fires create in soil surface geochemistry (that last for only ~1 week to months at the most) are responsible for higher long-term rates of erosion?  There's really no good way (with cosmogenic nuclide data) to show which areas are burned more or less over the millennia of averaging. 

Line 118: Good paragraph! 

Line 136: topology? I don't know that this is actually achieved.

Line 210: "To extract river profiles from the database for comparing topographic parameters with erosion rates, we chose a subjective distance threshold as 150 m between river profiles and erosion rate sampling points (i.e. selecting river profiles which are within 150 m to the closest erosion rate points), and calculated the mean slope gradient and total relief of river longitudinal profiles." 

I don't see why such a large window was used here. Usually, people sample for 10Be right on the river itself and this highlights a potential problem with the geoid or projection used, if the points are this far away from the actual river on the map. The OCTOPUS sites have made sure that the sites are approximately on river sites.  

Line 225: To a reader not familiar with kruskalwallis, could you describe the method and why it was chosen?  This is fairly important because so many variables here interact so the authors could be/are conditioning on a collider.  I think the kruskalwallis function does not help to eliminate this issue. I hope another reviewer covers some suggestions for stats that would be helpful to the author because I don't know what to use with so much nonlinearity and dependencies in the data. For example, higher precipitation and lower temps are actually *created* by mountain ranges. So how would one disentangle slope and elevation from those climatic effects. This is not the way to account for that. 

Discussion and conclusions: 

I assume these will radically change in scope/focus with submission of a major overhaul revision.  

‘Global analysis of short- vs long-term drainage basin erosion rates’

General comments

Chen et al. present a global meta-analysis of previously published data on denudation (erosion) rates from a wide selection of drainage basins. The data draw on two approaches to quantifying basin-scale erosion: suspended sediment (SS) yield and cosmogenic Be10 measured in fluvial sediments. Key findings are that short- and long-term erosion rates tend to differ significantly, and that this disparity is largely due to i) human activities, and ii) climate-related factors involving the role of plants, glacial history, topography, and scale effects associated with sediment storage in fluvial systems.

How timescale affects the quantification of erosion rates is a primary question in geomorphology that has received plenty of attention. Making use of large datasets to explore the problem is not novel, but to my knowledge the suspended sediment (SS) yield data has not been previously examined specifically in this way.

In my view the study would gain from some restructuring that clarifies the rationale behind each step of the analysis and leads to a more logical unfolding. At present the MS gives a jumbled impression, some passages are difficult to follow and several loose threads detract from the main arguments. The conclusions are mostly compatible with previous work, but my main concern is with a number of oversights that seriously weaken the standing of the work.

I have 5 main points that require some consideration (my other comments are keyed to line #).

(1) Treating Be10-derived erosion rates as long-term in comparison to the SS records is a valid approach, but it’s also important to note that the Be10 integration timescale is a function of erosion rate. The integration timescale is conventionally calculated at one absorption depth scale ~ the time taken to remove ~ 0.6 m of rock under long-term steady erosion. This means Be10 integrates a continuum of timescales spanning 3 order of magnitude (10³ to 10⁶ y), and this may have implications for how the erosion rates are interpreted, as noted below in my comments on Fig. 3a.

(2) There is a striking omission here of the time-dependence of the distribution of hiatuses in the sedimentary record known as the Sadler Effect. This issue lies at the heart of comparisons of erosion and deposition rates over different timescales and cannot simply be passed over without comment. There is a stack of recent papers, but Schumer & Jerolmack (2009, JGR) would be a good start.

(3) In order to reflect short-term denudation, the SS data should be limited to specific sediment yields within the upland source zone only. In the transfer zone, downstream SS load is chiefly driven by sediment exchange between floodplains and channels: a function of sediment availability, not denudation (see Dunn et al. 1998, GSAB). If on the other hand, direct efflux from agricultural lands and plantation forestry is the driver then the authors need to make their case accordingly.

(4) I am not convinced the median is a legitimate choice of parameter for comparing datasets that overlap across several orders of magnitude. In such variable data, the median has no specific value other than being roughly in the middle. I would like to see a justification for the use of the median as the basis for comparing relative erosion rates.

(5) The topographic indices do not include mean hillslope gradient despite it being the strongest of all parameters tested by Portenga and Bierman (2011). The local river slope used here has practically no bearing on Be10-derived basin-scale erosion rate and there is no reason to expect it would either. Channel relief is not an effective substitute. The physical basis of the alternative approach presented here needs to be justified.

Specific comments [keyed to line #]

Intro

35- Perhaps add that SS flux records also reflect the availability of fine sediment, and to some extent the production of fines via weathering and transport; e.g. some lithologies like NZ greywackes break down remarkably fast.

36- ‘…basin-averaged exposure ages’, is not the correct phrase. As used here, Be10 abundances are modelled to yield surface erosion rates, not exposure ages, which generally impose a zero-erosion constraint—it’s a different equation. Please correct this error throughout the MS.

52-3. This assumption of uniform bulk density seems reasonable for the purposes here but should probably be propagated through the uncertainty analysis. I didn’t find any evidence of that.

58-59 Good point. I agree the SS records are likely to yield transient rates in light of widespread riparian zone destruction and the global expansion of river bank revetment over recent decades.

63- Usually described as ‘secondary cosmic rays’—mainly neutrons and muons by the time they get to ground level.

63- The integration timescale of cosmogenic nuclides varies with erosion rate.

68-73. I appreciate seeing an explicit statement of the method assumptions; however, I can suggest a few amendments. Sediment storage is not strictly a problem (reworking can be). Most important is that the sampled grains have been subject to long term steady erosion and continuous exposure to cosmic rays. Those two assumptions are violated by abrupt and deep erosion (e.g., landsliding), or long-term burial followed by erosion. Landscape-scale equilibrium is not really necessary (see Willenbring et al. 2013, Geol); if it were, practically all of the OCTOPUS dataset would be invalid. The key is that the erosional processes acting are more or less steady and there is a minimum of deeply shielded grains (e.g., from landsliding) in the sample collected. Please clarify the meaning of ‘no erosion-deposition cycle’.

74-76. See note above on the integration timescale of Be10. This statement is valid only for the longer-lived nuclides such as Cl36, Al26 and Be10 (not C14). It is not clear what is meant by ‘stochastic events’, but perturbations such as landsliding and extreme floods that erode old sediment storages can potentially affect Be10 abundances, and certainly will affect abundances of in situ C14.

107- ‘…stripping of rock underneath basal ice’ is not how it is usually described.  Perhaps rephrase to something like ‘Glaciers erode bedrock via quarrying and abrasion wherever subglacial conditions allow basal sliding.’ The legacy of deep and steep walled glacial troughs prone to mass failure is another key reason why glaciated landscapes yield high sediment load.

129- True, but deconvolving the effects of tectonics and climate is not really one of the aims of this MS. Perhaps confine the scope of this literature survey to the issues that are specifically addressed in the MS.

134- … glacial and periglacial processes.

Methods

147- Was the Ray and Adam (2001) study used here because it classifies vegetation distributions at the LGM? Are there more up to date alternatives?

164- ‘…published literature’ seems a bit general—perhaps refer to the Supp data here.

166-67. One of the strengths of the OCTOPUS dataset is that the nuclide data are recalculated from scratch with uniform methods and propagation of uncertainties. Has the same been done with the SS data including uncertainty analysis? e.g., the bulk density assumption? It would be good to see an effort in favour of reproducibility.

182- It is a bit unclear whether the original K-G zones or the new modified versions were used. Fig. 4 is not clear to me. What is the purple representing? I cannot determine clearly where the previously ‘glacial and proglacial zones’ are exactly. Is the map indicating that the Tibetan Plateau was ice covered during the LGM? That idea has long been discredited (e.g. Heyman 2014, QSR), giving the impression that these glacial extents are a bit outdated.

188-194. Some repetition could be cut here.

191- In addition to the regions directly covered by Plio-Pleistocene glaciers, it is worth considering the widespread distribution of frost weathering associated with periglacial activity. At high latitudes, this is a far more extensive and more persistent control on sediment production and transport than ice sheets per se. The direct affects of glaciation extend far beyond those regions directly covered by Plio-Pleistocene glaciers. The great northern ice sheets fed prodigious amounts of sediment into surrounding glaciofluvial landscapes, which were in turn surrounded by a vast periglacial domain. Even today, about 18% of the ice-free terrestrial surface has a mean annual temperature <0°C and of course this expanded greatly during the LGM.

196- Perhaps ‘glacial-interglacial cycles’ rather than ‘ice ages’ which is a bit general; ‘last ice age’ presumably means the coldest part of the last glacial cycle, the global LGM (~27–19 ka). This is important in the context of the Be10 integration timescale noted elsewhere.

207-11. Owing to its scale dependence, estimates of ‘mean slope gradient’ i.e., hillslope gradient, have created some difficulties in previous meta-analyses (e.g., Willenbring et al. 2014, ESurf). I suggest you be specific about how this is calculated; expand on Chen et al. (2019).

A bit puzzling. The topographic data presented here include river profile concavity but not river slope, or some normalised version of steepness such as ksn. That seems a bit odd given that river slope is one of the main drivers of fluvial incision (via bed shear stress). Is this saying that it was local river slope that was measured within 150 m of the Be10 samples, not mean catchment hillslope gradient? Local river slope has practically no bearing on a Be10-derived erosion rate. In any case, I suggest the term ‘reach-scale channel slope’ be used instead of ‘mean slope gradient’.

226- Please expand on the description of the Kruskal-Wallis test. I understand the K-W is an old school ANOVA based method, but it needs to be justified here. Why is K-W the most appropriate tool to use among so many others?

Results

Fig. 2 is a nice and clear representation of the data. My first impression was that all these erosion rates overlap at the interquartile range and so demonstrate remarkable similarity despite spanning such different timescales! Fig. 2 shows that most sample sets span an order of magnitude in the interquartile range and 2–4 orders for the 5–95 percentile (I presume the whiskers are 5–95, though I could not find it stated anywhere). I have several concerns.

(i) How were those outliers defined? Is there a physical basis for excluding those data? In my view a solely statistical reasoning for defining the outliers is not justifiable because these are simply descriptive classes; they do not imply a model distribution that would dictate the shape of the tail, for instance. Excluding outliers implies that there is a problem with those data. But what would that problem be other than they are in the tail of the distribution? This is important because excluding data naturally affects the shape of the distributions—possibly a lot (the Portenga & Bierman 2011 study does the same).

Given that the outliers are all at the upper end of the data range, I would guess that the distributions are close to log normal. If so, then it probably also means they could benefit from log-transformation before plotting. Out of curiosity, I plotted the SS data provided in the Supplement using violin plots rather than the standard box-whisker. The violins have obvious advantages and I suggest the authors try these out.

(ii) If one includes the outliers for a moment, most of the classes span >4 orders of magnitude in erosion rate, which suggests a severely undetermined problem. In my view these climate classes are simply not discriminating enough—there are too many other factors at play.

(iii) I find it difficult to understand why the median is a legitimate choice of parameter for comparing datasets that overlap across several orders of magnitude. In such distributions, which are potentially polymodal, the median has no specific value other than being roughly in the middle. Further, the median ignores the magnitude-frequency of events that drive sediment yield. For instance, a good proportion of the sediment yield in the tropics is the result of tropical cyclones and another large fraction is related to seasonal burning which has been practiced by indigenous people over ~10⁴ timescales. My guess is that the median would fall in between those two. Is that a good model? In my view, the authors need to work a bit harder to convince the reader here and especially argue why the K-W is the best and most appropriate tool to use.

Table 1. Tables are never a nice way to present an argument. To clarify, the ‘erosion rates between climate zones’ are merely the median erosion rates, not the full distributions. Is that correct?

Fig. 3. Interesting plot; I like the LOWESS approach. Where are the uncertainties on the erosion rates?

Fig. 3a. Combining present-day precip rates with Be10-derived erosion rates, which integrate a range of timescales, might have some implications worth considering. Two related issues that come to mind with regard to the bump in the data at MAP <1000 mm: the higher erosion rates (~1000 mm/kyr) are integrated over a timeframe of ~600 y while the slower rates (~20 mm/kyr) are integrated over a timeframe of ~30 kyr. It is well established that presently arid parts of the American West experienced much wetter conditions over the transition from full glacial to the present-day interglacial (REF), and this is the same timescale spanned by the Be10 samples. The changes in MAP are sufficient to move these data to the right (possibly forming a cluster alongside the ‘humid trough shown now). I’m just speculating here …

274-275. This is good idea to exploit the region between the former maximum ice margins and the non-glaciated temperate zone but this is not well executed, in my view. A couple of things require clarification given that the glaciated and non-glaciated zones seem to overlap to a great extent:

(i) What is the purple zone in Fig. 4?

(ii) Note that the LGM ice limits were visited only very briefly; ice cover for most of the Pleistocene was a small fraction of the LGM max. In other words, how useful is the LGM limit as an index of glacial erosion given that most of the glacial forefield is mantled with drift in places hundred of metres thick.

(iii) Not all glaciers are alike. Polar ice masses erode slowly (<10-100 mm/kyr) owing to their frozen-beds. It is true that the ice sheets complicate the quantification of large-scale erosion rates, but short-term rates linked specifically to glaciers have been quantified (see Hallet et al., 1996, GPC; Koppes & Montgomery 2009, Nat.Geo).

277- I don’t think it is reasonable to characterise this comparison as 5-fold discrepancy without mentioning that it is merely the medians being compared (as stated in the Fig. 4 caption). Most of the data (5–95) overlap across 2 orders of magnitude.

279- As noted above, this effect is not just driven by glaciers but the full range of cold climate processes.

290- Puzzling why so little difference! It suggests the classes are not effective. Can this be improved somehow—there must be a stack of global datasets describing anthrogenic activities nowadays.

304-305. Finding that R_S/L > 1 is a predicted outcome of the time-dependence observed in the sedimentary record known as the Sadler Effect.

Fig. 7. Aside from the issue that these histograms obscure the enormous spread of these data, I’m interested to understand what causes the differential between the tropical and arid datasets. Could these trends be the magnitude-frequency factors emerging? For instance, the flood frequency curves in the tropics are characteristically flat whereas those in arid regions are steep.   

Fig. 8. Not well conceived in my view. I cannot grasp what the right panel is aiming to show. In (c) no river slopes exceed about 0.05, unlike in (a), because SS load derives mainly from reworking of fine sediment fills found predominantly in the transfer and sink zone at low channel slopes. At higher slopes there is little availability of SS load, so I expect that this plot is largely reflecting landscapes with argillaceous lithologies or glacial settings–not an effective way of exploring how slope affects erosion rates.

Discussion

336- Given that this study is based upon comparing short- and long-term erosion rates, this part of the Discussion ought to include some consideration of the effects of the time-dependence observed in the sedimentary record known as the Sadler Effect. I suggest a brief outlining of how it has been recognised by previous workers, followed by some analysis demonstrating that the observed findings of R_S/L > 1 are not a simple outcome of the Sadler Effect.

It is my understanding that Be10-derived basin-scale erosion rates are not subject to this bias for the reason that they incorporate the erosional-depositional dynamics across a wide range of ground surfaces in the basin, some eroding some not, and this effectively neutralises the time-dependence. Whether or not the SS load data reported here is subject to a time-dependent bias is for the authors to demonstrate.

346- This could be rephrased to be less general. As it reads now, this conveys very little information and reports findings that more or less echo those of previous work. A major part of the analysis is not global, it is restricted to the USA.

352- Perhaps a bit too generalised. The non-linearity in this relationship is most likely a function of the response of plants (soils reinforced by roots, rainfall interception, weathering etc.).

362-64. The question is, why does Mishra et al. (2019) differ from the curve produced here? Perhaps the authors could raise some explanations here.

376-77. This statement does not accurately reflect the results. Note something like a 10-fold increase in MAP from hyper-arid to arid to semi-arid is accompanied by <2-fold increase in median erosion rates. Why is that? Across this range, ground surfaces typically go from being totally bare to having complete seasonal vegetation cover.

388- This statement needs some rethinking. I do not follow why erosion ‘rates might not be expected to change much’ after glacial retreat. What is that based on? I expect rather the opposite as bare sediment and bedrock surfaces are colonised by vegetation over the postglacial period and large areas in North America and Scandinavia are uplifted isostatically. The paraglacial regime is associated with a well studied trajectory of sediment flux over the postglacial period.

389-90. This also ignores that high erosion rates are integrated over short periods…

397-98. Please clarify.

413-414. But according to Fig. 1, it seems that few data are available for boreal regions. The regions for which data are available are some of the most agriculturally exploited on Earth. Could the low SS loads be the result of generally low relief and the intensively modified lowland riverbank revetment?

429-36. This is a reasonable deduction, but not a satisfactory resolution. Why not recompute the data using a range of different thresholds to evaluate the problem thoroughly? As for the second point, I don’t follow the logic. How does this explain the discrepancy? You find an 8 vs 3.5-fold increase in the smaller basins but then point to the conservation efforts in upland (smaller) basins?

438-41. Yes, slope forms part of stream power law, but slope was not part of your evaluation of the influence of drainage area. It's difficult to see the point of this statement.

442- Be10 derived erosion rates are rarely affected by floodplain storage—the sediment would need to be buried deeply for a long time (>10⁵ y), then large volumes would need to be somehow reworked into the channel. As for ‘…violating the detachment limited assumption within area-erosion relationships’, it's hard to follow what this is getting at—certainly not the effects of sediment storage on Be10 erosion rates. Further, the Whipple et al. (1999) reference cited here makes no mention of cosmo.

438-52. A paragraph of confused thinking. E.g. 442-446, this is not an argument that accounts for differential erosion rates in large vs small basins. 447, What evidence is there that active plate margins have steeper relief than passive margins? The steepness of hillslopes is set essentially by rock strength such that mass failure occurs beyond a certain threshold of internal friction within the slope (Schmidt & Montgomery 1995, Science). Elsewhere in the MS, 126, it is stated that tectonic uplift lowers rock strength via increased fracturing (also not true as a rule: the tallest hillslopes commonly occur in tectonically active terrain, e.g., Nanga Parbat).

449- It is clearly true that lithology strongly influences erosion rates, but this analysis did not assess lithology. Why is this being raised here?

461- It is not clear whether this statement refers to short-term or long-term erosion rates but in the case of Be10 derived rates the sediment buffering is not very effective. Several studies by Wittman have shown this.

466-73. One of the most striking aspects of Fig. 7 is that tropical basins have much higher R_S/L combined with a greater sensitivity to drainage area. I would expect to find some Discussion of that point but I can find no explanation for why R_S/L ratios are notably higher, nor why such regions are more sensitive to drainage area.

487- Good to see mention of landsliding: the main driver of high erosion rates in mountain belts.

489- As noted above, the representation of local channel gradient in Fig. 8 conflates the Be10 derived basin-scale erosion rates with reach-scale fluvial incision rate. Be10 abundances measured in fluvial sediment are not closely related to basin-scale erosion rates.

492-499. Clearly true; agriculture is highly concentrated in lowland settings. But its effect in terms of soil loss is likely to be most destructive in steep terrain. This study sets out to compare erosion rates. And yet, the last few sentences reveal the failure of SS load data to capture soil loss where it actually occurs on hillslopes—due to sediment trapping in reservoirs and perhaps post hoc soil conservation efforts. Recent advances in isotope-based approaches (e.g., cosmogenic C14) mean that soil depletion can be quantified without the source-to-sink assumptions inherent with conventional sediment yield estimates.

John Jansen, Prague