|I have reviewed the revised text of “Calibrating a long-term meteoric 10Be delivery rate into eroding Western US glacial deposits by comparing meteoric and in situ produced 10Be depth profiles”. The revised text is far clearer and better organized. However, as I now finally understand the methods employed, I have some new concerns to present.|
First, the final term of equation 4 must be dropped. The 10Be that does not sorb in the topsoil layer would normally sorb at depth as infiltration continues and become part of the inventory. Under the steady state assumptions behind equation 4, 10Be delivered to the soil at depth is already counted in the loss to decay term. If the authors believe that 10Be is genuinely lost to ground water and not sorbed to the soil at any depth, the loss to ground water must be in terms of the entire inventory, not merely the surface layer. However, it is hard to imagine loss to groundwater at depth in this context, given the pedogenic carbonate build up in the soil. In principle, there could be a surface runoff term. But you’d need to calculate the proportion of precipitation that exits the system as overland flow, which I imagine is fairly small even in this semiarid context.
Secondly, I don’t think it’s reasonable to blithely combine a transient erosion model with a steady state flux calculation. The period of highest erosion would have occurred before steady state was reached, while 10Be in the eroding topsoil was at significantly lower concentrations. The authors are therefore almost certainly overstating loss of 10Be to erosion and therefore overstating deposition. Furthermore, I doubt the 10Be profile in the Pinedale Moraine is anywhere close to steady state, even if erosion were steady (the Bull Lake may be). Depending on erosion rate and erosive depth, the time to steady state can potentially be hundreds of thousands of years (Graly et al., 2010). The authors need to create a transient model of 10Be development in the soil. I know they’d rather not, but there really isn’t any way around this.
Finally, the paleo-magnetic corrections remain poorly explained. No equations are provided nor is any data presented, save the final corrected numbers. A supplemental table that completely explains this is required.
Some line-by-line comments:
116: No justification is given here for why the industrial run is a reasonable upper bound on the paleo 10Be fallout. Nor is it explained why industrial processes would make 10Be flux nearly a factor of 2 higher in this location.
163-165: I find this statement deeply unsettling. Of course, you know where the mass loss occurred. That is the whole point of conservative tracer approaches. You know exactly, down to 10 cm scale, which elements leached out of the profile and in which abundances.
174: This still doesn’t clearly state that the two aliquots were combined. Maybe “combined and homogenized”.
Equation 3: In the previous round, I asked the authors to explicitly add inheritance to this equation. I don’t know why they haven’t. Explaining something in the text but omitting to include it in formal terms is not enough.
Equation 4: The first two terms do not need to be in parentheses. Neither does Iλ (also in eq. 2).
235: So instead of Gaussian, you assume the value is equally likely to fall anywhere within the confidence interval? This doesn’t seem justified. You should model the actual probability distribution of each of your values and randomly select from these (if you don’t want to solve it analytically).
243: Do you mean 20-40% less than current?
278: I don’t understand why the uncertainties are so lopsided (especially for Pinedale), when the Monte Carlo results are so flat.
282: As I mention above, these calculations are in error and need to be excised.
287: I am totally mystified as to why this correction is so large. The records presented in Christl et al., 2010 show very little in the way of variation over the past 25 ka. We need to see the data and equations behind this.
295: This is not true. A linear fit is significantly better for the Bull Lake data (if you exclude the inheritance-dominated samples).
308: Arguably, the bulge may have been missed in the Bull Lake profile, as no sample at equivalent depth was analyzed.
311-323: I would still like to see this subject treated in more depth. And, I still think that a preference for larger grain sizes in mixing (not downward transport, but mixing) is the most logical explanation.
Line 328: Since you linearly sampled at random from something that varies on an exponential scale, this result is expected. (Though as I mentioned above, I believe this whole term to be in error.)
Line 345: I don’t know why you took out the +20% paleo-precipitation from (Birkel et al., 2012). I thought that was a very useful point to bring in. My previous review stated only that you could not meaningfully use it as an upper bound when comparing the Graly et al. value to your results. Quoting the highest regional precipitation rate seems far less useful a fact than a paleo-precipitation model result.
Table 1: The final column should have inheritance subtracted.
Table 3: Uncertainties must be included for the Graly et al. (2011) line of this table. A root mean square error is provided in the publication.
I have no idea how the 0.83 value for the Graly et al. (2011) Holocene F term is derived. It is certainly not the first column divided by the third column, as the others seem to be. I am equally mystified as to how the Holocene correction factor for the Graly line is derived.
The Heikkilä line must also have uncertainties. These are provided in the publication. The industrial run is not an uncertainty. It is a different result.