The authors Mohren et al. describe the use of plutonium (Pu) measurements to trace loss of soil organic matter (SOM) from agricultural fields of three sites in South Africa, with experimental design based on fields with a span of 100 years of known times/histories of cultivation. Adjacent native grasslands are used as controls at each site. The soil samples were collected in 1998 as part of another project and archived samples were used by the present authors. The prior work found an exponential decline in SOM concentration with duration of cultivation, and previous researchers speculated that this was due to mineralization of SOM possibly caused by the disaggregration of soil aggregates by tilling.

The present work puts forth a hypothesis that wind erosion and process of deflation might instead contribute to a decline in SOM concentrations, based on regional importance of wind erosion impacts and some more local anecdotal observation. Because global bomb fallout ^239,240Pu isotopes (alone or in combination with Cs-137 or natural Pb-210) have a history of use for quantifying erosion, the authors are exploited a unique data set to add Pu measurements with intent to assess causes of SOM losses.

Overall the study is very well written and presented. I have one major criticism and some more minor suggestions. The serious scientific challenge to this study is the use of Pu and SOM concentrations rather than mass balance, since the latter is required to demonstrate mass redistribution as typically laid out by erosion studies based on fallout radionuclides (e.g. authors He, Walling, Wallbrink, Mabit, Alewell, Meusberger etc.). I recognize that the present authors are limited by the work of their predecessors but nonetheless this issue should require more direct and explicit treatment here. Else it sounds as though the attribution of declines in Pu and SOM concentrations with cultivation history to wind erosion is fait accompli, while there is otherwise no direct evidence of the process of wind erosion per se presented here.

There are alternative explanations for a change in SOM and Pu concentrations that may be challenged more directly by the authors. First, the foremost influence on SOM and Pu concentrations in soil upon first tilling will be the tilling itself, since in native soils the highest concentrations of both are at the soil surface. If the tilling process is anything but perfectly homogenizing in the 0-20 cm soil, and there were any bias in sampling depth relative to tilling depth (say, 20 cm and 30 cm respectively), would the appearance of the concentrations over time not be exactly what we see in Figure 2? I wonder what assurance the authors provide that the observed patterns are simply not an artifact of tilling and sampling?

Next, the authors should acknowledge that the lower boundary of the 0-20 cm soil depth is not closed. They do point this out with respect to one location that actually as higher Pu in 20-40 cm than 0-20 cm, but this is attributed to deeper tilling. While this actually speaks to my point (1) above, I also highlight the potential for leakage over time of both SOM and Pu below the 20 cm boundary. The normal migration of organometallic complex at just 0.2 mm y^-1 could export 1% of Pu and SOC to deeper soil, for example. Compounded with time this could easily explain the scale of Pu and SOC loss over decades.

However, it is interesting to observe that the two pulses have different time zeroes. Any SOC pulse from inherited O-horizon is necessarily timed with onset of cultivation, whereas the Pu pulse is independent of that. In fact the Pu pulse is centered at a cultivation time of approximately 40 years ... and there appears no obvious pattern in the data related to this (excepting the noted site with higher Pu >20 cm which I surmised is related to deep tilling near in time to peak Pu deposition). That the SOC and Pu patterns both reflect time since cultivation would seem therefore to be good corroboration that it is some extant property of the soil that is regulating retention of SOC and Pu that are introduced at the soil surface rather than any artifact of tilling.

It should also be noted that SOC and Pu differ in that there are continuous SOC inputs at the soil surface through ongoing plant growth, whereas there are no ongoing Pu inputs with possible exception of relatively minor remobilization through erosive process. I wonder if this difference explains the different long-term trajectories of SOC and Pu in Figure 2 ... Pu continues to decline due possibly to leakage out the bottom (point above), whereas SOC is at some steady state with respect to ongoing inputs.

Finally, the authors should make clear in this paper (and not through references), the handling of the samples to produce the <20 um fraction, and especially what % this represents of the whole sample. Otherwise it remains unclear how the <20 um fraction might relate to soil mass balance, and whether a decrease in SOC and Pu concentrations in this fraction is truly attributable to mass balance, or alternatively to a change in texture or other soil properties that regulate carbon and fallout metal retention. More details on the <20 um fraction are especially important since this fraction may now be interpreted as the ‘mineral associated organic carbon’ or MOAC fraction, which the author touch on tangentially as possibly related to changes in carbon sequestration over time.

I recognize the authors have alternative explanations to some of data patterns and interpretations above, but I think it may be constructive for them to consider these lines of reasoning.

In arguing for wind erosion to the authors do conclude with some observations on a possible gradient in Pu concentrations along wind fetch. If this were the case, could this also be correlated with changes in soil texture or % fines due to deflation? Such a correlation would make a fine figure and would provide some independent evidence for wind erosion that is otherwise lacking.

Finally, the peculiar problem of a Pu point source some 40 years prior to soil sampling might be countered if the authors were able to use Pb-210 which was likely measured concurrently with their Cs-137 measurements. Similar to Cs it may be that the Pb-210 half-life precluded robust measurement from old archive samples, but even in this case it would be worth including a statement to this effect since otherwise Pb-210 could be quite valuable to the study. It would powerful to show for example that Pb-210 more precisely mirrors SOC due to continuous input to both through the history of the experiment ... or not!

Overall, the demonstration of a strong link between Pu and SOC is the studies soils is a nice contribution, but it remains to be better understand what processes are truly responsible for changes in Pu and SOC concentrations in a particular sample fraction.

c.r. line 426: for additional evidence for wind erosion, examine residuals from exponential fits of SOM and Pu along wind direction ... do concentrations (residuals) for both SOM and Pu covary tightly?

line 346: please clarify, aggregate size increases with time since cultivation?

line 384: excellent point

Figure 2: both Pu (panel a) and SOM (panel b) show exponential declines with cultivation time, but the dropoff appears much more steep for Pu than for SOC. I wonder about the significance of this, or is it simply a result of intersite variability? It may be due to different pulse input histories?

Figure 3: this is a methods figure and I would recommend placing in supplemental materials, or simply omitting it while replacing with relevant summary statistics in the methods section.

Figure 4: it would be nice to indicate the Pu:Cs fallout ratio decay-corrected to 2012. The correlation here is impressive, but this does not necessarily indicate that both Pu and Cs are retained to same degree, only that the fraction that IS retained is retained to same degree. This occurs in lake sediments for example where Pu and Cs are similarly strongly correlated with depth, but by mass balance as much as half of Cs depositional flux is missing presumably due to higher solubility in the water column.

Figure 5: high Pu in 40-50 year cultivated sites... did first plowing quickly follow period of peak Pu deposition, and mix Pu into subsurface 20-40 cm soils thereby minimizing susceptibility to erosion? What would this mean for mass balance and assumption that Pu is lost to wind erosion at the soil surface?

General:

Generally, the writing is clear and nicely framed. However, I have some serious points which need to be addressed before publishing. One minor point is that the introduction is to much on climate change, CO2 release etc. which is not the topic of this paper. On the other hand, nearly nothing is said on FRN use to assess wind erosion, methods to accomplish this or how to quantify erosion. The loss in SOC and FRN is attributed to wind erosion, just from visual assessment of the site. Could you please give exact slopes in the table for all sites? I find it hard to believe that at these altitudes you have so many sites completely flat. If this is true, this needs at least be identified. If it is not true, please consider that even small slopes will induce significant water erosion even on grasslands whenever you have rain events. In some parts it is not clear to me, what the authors did with the data. They talk of „normalisation“ but report data in percentages. Or was there really any normalisation done? Why not presenting the SOC concentrations and the FRN inventories over time? Much more interesting to soil scientists.

To apply the FRN approach to assess soil erosion you need at least 3 if not more reference sites. You cannot assume, just because SOC and FRN is highest in your “natural” site, this would be a site without soil erosion. What you could do, however, is compare your arable sites to the one natural grassland and discuss if you have higher or lower erosion. Can you really guarantee that the natural sites were never ploughed since 1950s?

All in all, I cannot really see how the data and the interpretation justify the conclusions. Please revise considerably (see more comments below).

Abstract:

26          the sampled plots did not show signs of fluvial erosion? How do you assess this? And even if they do not show this today, how do you know for 100 years back?

31          how do you know that 6% of the FRN inventory is lost in the first year?

Introduction

37          subtitles is misleading.... this is not about the release of CO2 (which is not the focus of your manuscript) but about the role of SOM in soils and how it is connected to erosion processes

79-83    the discussion on the potential CO2 of African soils is not very convincing. You already have strong arguments why SOC loss is important: because of general soil degradation. I would suggest to leave that out.

93-96    I cannot follow your rational, why the molecular compound analysis will indicate SOM loss with increasing periods of cultivation

Section 1.3. literature of how caesium or plutonium is used to estimate wind erosion is lacking. Web of science lists over 80 studies for caesium and 14 studies for plutonium. Also, no literature is discussed, how inventories are converted to soil erosion rates. As you obviously had a transition from natural grasslands (e.g., distinct depth profiles with FRN declining with depth) to ploughed arable soils (mixed plough layer) this is not a trivial task.

Methods

Table 1: could you please give exact slopes in the table for all sites? I find it hard to believe that at these altitudes you have so many sites completely flat. If this is true, this needs at least be identified.

127-129               this is a crude oversimplification. As FRN is deposited with wet and dry deposition, you have substantial heterogeneity. This needs to be considered in taking a adequate number of reference cores. These reference cores should have a CV < 30%. See Sutherland et al.....

Section 2.1 belongs to introduction. Together with a discussion on the use of FRN to estimate wind erosion.

153        how flat is flat? Already very slight slopes will induce water erosion in African soils. If you have heavy rain events after dry periods, slopes of <2° might already induce water erosion.

174        why <20 μm? In Africa, you can expect to have winds which blow out larger grains.....?

Did you not do any decay correction for the caesium to a reference year? Why not? How do you then relate to the year of deposition?

Results

Table 2: this table looks like a working table from the lab. Could you please make it reader friendly with a column for site name, sampling depth etc???

240 – 255 most of this is redundant if you format Table 2 properly, make suitable headings and explain some of this in the methods. This has nothing to do with results.

260 -163 sentences incomprehensible

264 sentences like “Figure 2A shows…” are unnecessary… please give adequate figure headings and delete these kind of sentences

Figure 2: what do you mean by “normalised”? What you did is, setting the site you defined as natural to 100% and calculated percentages from that. But this is not normalised? Why do you give percentages and not the original concentrations? Or did you any other normalisation with the data?

275        what do you mean by “internally consistent”?

290 even higher

Section 3.3         It is not unusual that Pu migrates down to 20-30 cm or even 35. But this might also indicate deposition of soil material. As such, you need reference soil profiles to compare you original FRN deposition to erosional or depositional sites.

323        to apply the FRN approach to assess soil erosion you need at least 3 if not more reference sites. You can not assume, just because SOC and FRN is highest, this would be a site without soil erosion. What you could do, however, is compare your arable sites to the one natural grassland and discuss if you have higher or lower erosion.

336 I can not follow this assumption nor the conclusion

341 do not understand why exponential decline indicates higher adsorption and the conclusion to aggregation seems far fetched (or explain and constrain it better)

Section 4.3 I do not agree with this discussion. Of course, using FRN in Southern Hemisphere means you can only assess the period from 1950ties to now. However, soils which were already ploughed during that time, are the only ones where you could quantify soil erosion, as you do not need any reference site depth profile but only a total inventory of the reference site and can then apply the proportional model. For all other sites, e.g. the sites changing from natural to ploughed in between, you would have to assume an (unknown) depth profile first and then a mixed plough layer after to quantify erosion.

402        What do you mean “deflation processes rather than turnover rates”?

Figure 5: I am generally puzzled by this Figure. If you see this strong decline in Pu concentrations over time and attribute this to erosion process, this means that what you measure today as 0-20 cm depth was 20-40 cm depth 100 years ago, right? But why don’t you see any changes in 20-40 cm depth? This should for sure decline to zero 60 years after cultivation. I think there is something else going on and you should for sure calculate your inventories considering your mass depth of soil and may be even assess erosion rates comparing it to you natural site. These simulated erosion rates (which, strictly speaking would not be absolute erosion rates but rates above the natural site values) would then give you some confidence about possible processes going on. However, you clearly need depth profiles of FRN from your natural site and the time of conversion from natural to arable land.

Conclusion

Sorry to say, but from the above, I can not really see that these conclusions are justified by your data.