We thank RC 1 for a detailed and helpful review. Please, see below our responses and proposed changes to specific review comments (Italic).

General Comments:

1.) Dependence of the production rate on target chemistry  

Is the production rate of 10Be in pyroxene dependent on the composition of the pyroxene? Unlike quartz, which is characterized by a tightly constrained target chemistry, pyroxene is not a single mineral, but rather a group of minerals of diverse compositions. I would argue that the production rate of 10Be in pyroxene is likely to vary with pyroxene composition.

To illustrate this with a “back-of-the-envelope” calculation, assume that, to a first order, all production of 10Be in pyroxene occurs through spallation on oxygen. In enstatite (with an endmember composition of Mg2Si2O6) oxygen accounts for 47.8% of the molar mass. Now, consider that in another common pyroxene, hypersthene (En50Fs50) (MgFeSi2O6), oxygen accounts for 41.3% of the molar mass. This implies that the production rate in enstatite is ca. 16% higher than in hypersthene. The actual difference in production rate is likely to be even larger when considering that 10Be production from Fe is lower than from Mg. Similar calculations can be made for other pyroxenes, for example the difference between enstatite and hedenbergite (CaFeSi2O6) should be greater than 24%.

Although comparisons between endmember compositions give a maximum range of variation, it seems likely that the variation in production rate due to compositional differences would very often be much greater than the ca. 2% analytical uncertainties on 10Be measurements. I wonder if such variation might be the source of the scatter between estimates of 10Be production rates in pyroxene from different studies (as shown in Figure 3). The Balter-Kennedy data, which you note agrees well with yours, was also obtained from pyroxenes from the Ferrar dolerite, which may have a similar composition to those you analyzed.   

Although this critique does not in any way invalidate the measurements presented in this study, I think that it would be useful to know to which pyroxene composition this production rate applies. I encourage the authors to provide some constraints on the composition of the pyroxenes that they have analyzed. At a minimum, these constraints could be literature values for pyroxene from the Ferrar dolerite, although direct measurements of the composition of the analyzed pyroxenes would be even more useful. Likewise, if the authors believe that compositional variation is not important, then I think that this argument should be made in the text.

It is true that the Be-10 production rate in pyroxene is theoretically predicted to be somewhat compositionally variable. In fact, as the reviewer points out, it has to be, because the dominant target is O, and the O content by weight in pyroxene is variable with the mineral composition. It is also true that this point has not been considered in detail in any of the production rate calibration studies for this nuclide-mineral pair. 

Masarik (2002) gives a formula for estimating the compositional dependence of the Be-10 production rate:

P(10Be) = 9.82 [O] + 1.74[Mg] + 0.89[Si] + 1.03[Al] + 0.35[Fe]

Although the absolute values of the coefficients are not expected to be accurate because of changes in Be–10 measurement standardization after 2007, this should give a good approximation for the relative variation. As suggested by the reviewer, this formula permits a 27% variation between extreme end member pyroxene compositions (enstatite vs. ferrosilite). However, the variation among compositions of pyroxene in which Be-10 concentrations have actually been measured is much less. The expected variation in production rates among the various pyroxenes present in the Ferrar Dolerite is < 6% (using compositions from Elliott and Fleming, 2021, and various unpublished data). As the mineral separation process used to prepare samples for Be-10 analysis does not select for individual pyroxenes, it is likely that the variation among aliquots analyzed in this study and that of Balter-Kennedy et al. (2023) is substantially smaller than 6%. Thus, although the possibility that the one outlier we observed is due to compositional variation cannot be rejected without compositional data, it is unlikely. As the reviewer also suggests, it is most likely the case that for analyses of bulk pyroxene exclusively from the Ferrar, the effect of compositional variation is most likely at the level of measurement uncertainty. 

That being said, we agree that it is desirable to report compositional data for pyroxenes used for Be-10 analysis. Unfortunately, although the samples in this study have already been submitted for XRF analysis, we don’t expect results for at least 4-6 weeks. We defer to the Geochronology editors as to whether to delay publication of the paper until these data can be reported. 

In addition, the reviewer is correct that this issue could be important when comparing results from Ferrar pyroxene to pyroxene from other lithologies. However, production rates predicted using the Masarik equation for all the samples from other calibration studies fall within the range predicted for Ferrar pyroxene compositions, and therefore <6% variation in the production rate. 

To summarize, although it is true that some extreme pyroxene compositions could yield production rates varying by up to ~25%, typical compositional variation as expressed in the samples from this and other existing studies are expected to vary only at the ~5% level. However, we agree that discussing this more explicitly in this paper would be of value. We will add this discussion.

2.) Clarification of analytical methods

I think that in several places some of the methodological descriptions should be clarified, given that presentation and evaluation of the fusion approach for preparing pyroxene samples is a principal point of this study. In specific, I found the latter part of the fusion procedure description to be hard to follow (please see specific comments from lines 140-146).

Likewise, I think that the discussion of the 3He measurements and data analysis is pretty spartan. I understand that the 3He data may not be the focus of the manuscript, but the authors might consider developing this further for the benefit both of readers who are not familiar with 3He as well as for those readers interested in the details of the data analysis. For example, you might consider including some brief explanation of the nuances of 3He, such as capture of cosmogenic and radiogenic thermal neutrons by Li, recoil losses, mantle He etc., which are alluded to later in the manuscript but are never explained.

The reason that these procedures are not completely documented in this paper is that they are very well documented in other papers. The description of the fusion method by Stone (1998) is clear, comprehensive, and extremely detailed. The description of He-3 analysis at BGC by Balter-Kennedy et al. (2020) does not rise to the level of the Stone paper on the fusion method, but it does include all the needed information. As the He-3 analysis method is fairly routine, we decided that it was not necessary to repeat large sections of the Balter-Kennedy paper here. 

Specific Comments:

Line 17: Do you mean secular equilibrium here? To me, “production-erosion equilibrium” sounds like steady-state erosion, but in Eqn. 1 you do not consider erosion and at line 76 you give a statement of secular equilibrium. In a few places in the manuscript, you say “production-decay saturation,” which may also be a better way of phrasing this. I recommend changing “production-erosion equilibrium” to “production-decay saturation” or “secular equilibrium” throughout.  

This was careless usage on our part. Yes, because the erosion rates are very low, production-decay equilibrium is correct. We will change the wording.

Line 79: Isn’t the production rate weighted towards the younger portion of that time interval by radioactive decay? What is the actual averaging time?

Yes and no. In a simplified form, the “production rate” inferred from a single measurement is the value of P that satisfies N = (P/l)(1-exp(-lt)), where t is the exposure age and l is the decay constant. This yields what one might call a “decay-weighted,” or “effective” production rate, which is weighted toward the production rate at more recent times (when the resulting Be-10 has decayed less). 

However, this is not the case when these data are being used to calibrate a production rate scaling method (e.g., ‘St’, or ‘LSDn’). In this case, the scaling method accounts for time variability in the production rate, and the parameter being adjusted to match the data is either a “reference production rate” at a defined time and place, or a nondimensional correction factor. 

This is the case for Figure 3. The parameter values shown at the bottom are defined parameters in each scaling method. For St and Lm, these are a dimensional (atoms/g/yr) production rate at a defined time and place. For LSDn, this is a nondimensional correction factor. 

These calibration approaches are clearly laid out in many publications about cosmogenic-nuclide production rate calibration, for example Gosse and Phillips (2001) and Balco et al. (2008). In keeping with standard usage, we use ‘reference production rate’ when we are referring to this throughout the paper. 

Line 97: If the pyroxenes in the Ferrar dolerite have a range of compositions, does using a magnetic separator to separate the pyroxene mean that you end-up selecting the more Fe-rich pyroxene fraction? 

The magnetic separation is applied to separate pyroxene from the non-magnetic plagioclase, and minor grains of highly magnetic oxide which can be removed with a hand magnet. Even though the range of compositions in pyroxene has varying magnetic strengths, this variation is minor compared to the magnetic strength of plagioclase. We do not attempt to separate the pyroxene, and therefore keep any grains that are less magnetic than a hand magnet and more magnetic than plagioclase. This procedure is intended to retain all pyroxene in the rock, so, as noted above, the resulting composition is expected to be intermediate with respect to the possible compositional range. 

Line 102: Why do you begin this sentence by stating that a fine grain size reduces the amount of meteoric 10Be stored in the grain fractures, but then say that you do not need to powder the samples? Wouldn’t the first clause suggest that by powdering the samples you would decrease meteoric contamination?

This issue was discussed by Balter-Kennedy et al. (2023), who found that removal of meteoric Be-10 could be accomplished effectively with a fine grain size but without further powdering. We can clarify this section of the text.  

Line 105: What volume of acid was used vs. mass of sample? In other words, is the fraction dissolved limited by the acid volume (because the reaction goes to equilibrium) or by the reaction time?

Because the etching steps are relatively short, it is most likely controlled by the reaction time. A ballpark stoichiometry for silicate minerals is that 2-5 mL of 48% HF (the typical purchasable concentration) is required to dissolve 1 g of mineral. As we used 6 mL for 0.5 g of pyroxene, this is most likely well in excess of the stoichiometric amount needed for complete dissolution. Thus, we conclude that the dissolution was time-limited not acid-limited. 

Line 111: Does powdering after mineral separation and HF-leaching introduce the possibility for contamination? (Either from residual dust from previous samples processed in the shatterbox or from fragments of the material that the mill is made from?). It seems like this might be problematic if the shatterbox is routinely used to process soils or other high 10Be/9Be materials.

There is always a potential for dust contamination. However, between each sample, the shatterbox was cleaned. Further, in order to eliminate cross contamination between samples or material from prior use, we pre-cleaned the shatterbox by first crushing a small amount (<100 mg) of samples which was discharged and the shatterbox was cleaned again before the sample used for analysis was powdered. This limits cross contamination between samples. This ‘pre-contamination’ method is standard for shatterbox crushing and has been extensively tested for geochemical purposes. 

Line 123: At what temperature were these samples fused?

Stone (1998) indicated a target temperature of ~800° C.. However, the fusion takes place over an open flame, not in a controlled heating apparatus, and the temperature is not measured during the process. 

Line 136: Maybe it would be worthwhile to state here that BeF2 is soluble and most other fluorides are not? This is necessary to know to understand this method.  

Once again, the chemistry of this procedure is comprehensively explained in the Stone reference. 

Line 138: Do you remove the KClO4 by centrifugation?

Yes, HClO4 is added, which causes KClO4 to form as a precipitate and is discarded. See the Stone (1998) paper. 

Line 140-146: How you get from the KClO4 precipitate and a supernatant with the dissolved Be to a cathode that is ready to measure is not clear to me. Do you remove the KClO4 precipitate by centrifugation, evaporate the excess HClO4, and then redissolve the residues in 12 mL of HNO3? What concentration do you mean by “dilute”?

When do you precipitate the Be and at what pH?

For this and general comments regarding the lab procedure we refer to the Stone (1998) paper, which is comprehensive and describes the steps in great detail. Further, the precipitation of Be into a gel and packaged into cathode are general practice for cosmogenic analysis of Be and have been discussed in detail in prior literature.

Yes, the KClO4 precipitate is centrifuged and discarded. The excess HClO4 is evaporated and then redissolved in 12 mL of HNO3. Be is then precipitated into an oxide Be(OH)3 at a pH of 8. Once this happens, the sample is centrifuged forming a gel and the supernatant is discarded. The Be(OH)3 gel is dried into a small pellet, which is packed into a cathode for AMS analysis.

How do you determine Be yields? By ICP-OES measurements of aliquots? If so, when were these taken? Or do you determine the yield gravimetrically from the mass of the BeO product?

The Be yields were measured by ICP-OES at the CCF. We will include this detail in the revised text.

When you say “redissolving the precipitated sample” at line 141 to which precipitated sample do you refer (at the end of the last paragraph it sounded like your beryllium was dissolved in 12 mL HNO3) and in which acid do you redissolve in?

The supernatant is dried down to evaporate any remaining HClO4, and then redissolved in 12 mL of HNO3. We will make this clear in the paper. Once again, the procedure is discussed in great detail in the Stone reference.

When you say “these samples” are you referring to all your samples, or only to a subset? Earlier you mentioned that you changed your flux/Na2SO4 ratio at some point. Are you referring to something to do with this change?  

We are referring to the samples having low 10Be concentration. This will be made clear in the text.

Is the idea here that some K was present in the product, which led to a dilution effect in the ion source, reducing the beam currents? If you measured the beryllium yield by ICP-OES, then did you also look for other elements, such as K? Why would K co-precipitate with the Be? Isn’t K highly soluble at the mildly alkaline pH that you typically precipitate Be at?

We don’t think that K coprecipitated with the Be. We believe that we never completely got it into solution, because the solution was oversaturated. 

Otherwise, yes, we believe it was a dilution issue in the ion source. 

We did not measure K in the final precipitate: this would have required redissolving the precipitate, and at the time we were expecting normal AMS performance based on the Be yields. The poor ion currents were a surprise. Thus, as the targets had been consumed, it was no longer possible to redissolve them and look for K. 

Table 2: Why do you think that a higher Be yield is not correlated with a higher beam current?

Our hypothesis is dilution by K, as noted above. In general, the fusion process applied to diverse geologic materials produces a much larger scatter in ion currents than a dissolution/chromatography process applied to quartz. See, for example, Balco et al. (2021) which discusses how contaminants in BeO targets impact beam currents. Some scatter in ion currents is therefore not surprising or unexpected: what was unexpected was the systematically low ion currents in the presence of relatively high yields in our second batch. 

Table 3: Please add the errors on the 10Be SLHL production rates. Also, I think that it might be worthwhile to include the Stone scaling factors in this table. This would make your production rates easier to recalculate.

We will include errors on the production rate in the table. With regard to including scaling factors, there is generally not a need for readers to individually recalculate these production rates. The data we have collected would typically be used for production rate calibration using a complete scaling algorithm, typically as implemented in one of the online exposure age calculators. 

One thing we could do here is provide the data in calculator input format so it can easily be pasted into the online production rate calibration calculator. That would most likely be more useful to readers  than giving the scaling factors.

Figure 1: Is it necessary to present both the “measured” and “corrected” 10Be production rates on the figure? Aren’t the “corrected” rates the actual rates after applying the thickness and shielding factors? Are the rates presented in Table 3 and that you state are calculated using Eqn. 1 the “corrected” or “measured” rates? If they are “corrected”, then I would recommend adding the thickness and shielding factors to Eqn. 1.

With respect to the outliers, are there two samples here, or is it like the others, where you present a “measured” and a “corrected” value? They are not distinguished by color.  

More generally, I would recommend sticking to presenting one set of rates, including the thickness and shielding factors (i.e., the “corrected” rates), in all tables and figures. I think this would avoid confusion between the two, and keep attention focused on the best estimate of the production rate.  

First, to clarify what is being plotted, Figure 1 shows concentrations, not production rates. We included the data as measured because, of course, the first basic requirement of a scientific paper is to clearly show the actual measurement results. The ‘corrected’ data are a model-dependent digest of the observations, and are not actual observations. 

Likewise, we view it as confusing and inappropriate to report corrected concentrations, which, again, are the result of a model-dependent calculation, rather than the actual measured data.  It’s important to clearly distinguish between the actual observations and model-dependent calculations based on the observations. As an aside, the reporting of ‘corrected’ concentrations that include various correction factors for scaling, sample thickness, shielding, etc. have proven to be a serious obstruction to reuse of data in some of the older literature on cosmogenic-nuclide dating. Happily, this practice is no longer current in the field. 

In regards to the outlier, we will distinguish these by color.

Line 198: How large is this subtraction?  

The contribution from muon production is < 1%. This will be included in the revised text.

Line 203-205: It seems to me that this outlier rejection could be justified more rigorously, perhaps using a statistical test, such as Chauvenet’s criterion. Moreover, why do you think it is an outlier? Could it be related to variations in the target chemistry between samples?

This is identifiable as an outlier based on a variety of statistical tests. As noted above in our discussion of compositional variation in production rates, we cannot reject the hypothesis that the outlier is due to a very different composition without an actual analysis of the sample, but this is highly unlikely to be the case. 

Line 205: Why quote the standard deviation here rather than the standard error of the mean?

This has been changed to the standard error in the revised text.

Line 209-212: Please explain this more clearly. Was this production rate cross-calibrated against 3He? Is the reason limiting assumptions are required that 10Be decays significantly over the relevant exposure timescales, but stable 3He does not?

As written, this section is unclear as to which study did which. We will rewrite to clarify. Regardless, the Balter-Kennedy study does in effect calibrate the Be-10 production rate by comparison to He-3. However, in the present study, our calibration is independent of the He-3 production rate because the samples have approached production-decay saturation. This is an important distinction and we will highlight it here in the revised text. 

Figure 2: What 3He production rate was used to calculate this figure and did you consider muon-production of 3He and 10Be? Which scaling model was used for the site-specific normalization? Did you use your production rate for 10Be or the average of your production rate and the Balter-Kennedy et al. data? Why are the error ellipses tilted?

The default He-3 production rate in the online exposure age calculators, which is based on the ‘primary’ production rate calibration data set of Borchers et al. (2016). We will add this info to the revised text.

This uses the ‘St’ scaling model and the production rate calibration data from the present study. Construction of multiple-nuclide diagrams using time-dependent scaling is complex and requires a number of assumptions. 

The uncertainty ellipses are tilted because the quantities plotted on the X and Y axes both include the Be-10 concentration, so their uncertainties are correlated. This situation is common in isotope ratio diagrams used in many areas of geochronology and is discussed in detail in many textbooks, as well as, for example, the documentation for the commonly used ‘Isoplot’ and ‘Isoplot-R’ software. 

Lines 224-229: What production rates do these studies give?

The reference production rates they state in the paper can’t be directly compared to ours because different scaling algorithms were used. Thus, we structure this part of the paper around the question of whether or not their actual measured concentrations, not the derived production rates, can be reconciled with ours, using several scaling algorithms.

In general, it is an important principle that stated values of the reference production rate cannot be compared between studies, because calculation methods are slightly different. Thus, Figures 2 and 3 with accompanying discussion are focused on comparing the direct observations, not parameters derived from the observations. 

Lines 230-240: The LSDn scaling model may be time-dependent, but doesn’t that not really matter at high latitudes where the cutoff rigidity is 0? Isn’t it that LSDn takes into consideration the softening of the energy spectrum with decreasing altitude and the dependence of each production reaction on different cosmic ray energies?

Yes, in general this is true. The time-dependence of the production rate scaling is important in Figure 3, where data from low and high latitudes are being compared. The difference in the elevation dependence of the production rate between St/Lm and LSDn is a separate issue from the time-dependence. 

How are you calculating the LSDn scaling factors? LSDn is reaction-specific in the sense that it takes into consideration the excitation functions for each production reaction (e.g., neutron and proton spallation on Si and O for quartz). Do you just use the LSDn factors for quartz, or do you also consider the other elements that are present in pyroxene (e.g., Ca, Mg, Fe) and the different relative proportions of Si and O?  

We assume that the dominant production reaction is spallation on oxygen, as it is for quartz, and we use the scaling for this reaction. Thus, yes, the scaling is the same as for quartz. We did some calculations of the possible compositional effects, and in addition discussed the subject with Nat Lifton, and concluded that the compositional effect is minor and most likely below the resolution of real data that could reasonably be collected. 

Also, to what extent is the modern elevation and air pressure of these samples’ representative of the average air pressure that they have experienced over the multi-million-year integration time of the cosmogenic nuclide signal, given glacio-isostatic fluctuations and glacial-interglacial climate change (which might affect local air pressure)?

This question is unanswerable because of lack of data. However, because these parameters vary on a much shorter scale than the exposure time of these samples, we can most likely assume that the resulting production rate estimate is accurate for periods spanning multiple glacial-interglacial cycles. It is possible that this could translate into inaccuracy in an exposure age computed for a much shorter period of time, e.g., during the present interglacial. Note that the issue of long-term changes in elevation/air pressure are addressed in detail by Balter-Kennedy et al. (2020) as well as others. In addition, there has been extensive discussion of the effect of glacial-interglacial air pressure/elevation change in other cosmogenic-nuclide-related literature (Jones et al., 2019). Thus, this is a potentially important issue but has been well addressed externally to this paper. 

Line 236: Can you quantify this agreement? Perhaps using a goodness of fit metric, such as the MSWD?

The easiest way to demonstrate this is to use the St and LSDn scaling methods to derive a value of the fitting parameter (a reference production rate with units of atoms/g/yr for St, a nondimensional correction factor for LSDn) for each of the samples described in the present study, and regress these values against sample elevation. If the scaling method is correctly describing the elevation dependence of the production rate, the regression should have zero slope. In other words, a correct scaling method should generate the same value of the fitting parameter no matter what the elevation of the sample. As shown in the attached figure, carrying out this exercise yields a smaller regression slope for LSDn than for St, which implies that the LSDn method is more accurately describing the elevation dependence of the production rate. On the other hand, it is true that neither slope is distinguishable from zero (see the confidence bounds in the figure) at high confidence, so it is likewise not possible to demonstrate at high confidence that LSDn scaling performs better with these data alone. Keeping this in perspective, however, this issue is marginal to the main point of the present paper. The point of the paper is to estimate Be-10 production rates in pyroxene, not do a comparative evaluation of scaling methods, and there are much better data sets for comparative evaluation anyway. Thus, in the revised text we propose simply to de-emphasize this point in the text and the caption to Figure 3.

Figure 3: Is the number in the bottom left corner of panels b.) St and Lm the mean production rate considering all the data in the plot? What is the error on this value?

It’s the fitting parameter used when fitting the scaling method to the data. For St and Lm it’s a dimensional reference production rate (atoms/g/yr). For LSDn it’s a nondimensional correction factor. Again, these are all properties of the scaling methods and the fitting approaches, which are described in detail elsewhere and are not new elements of this paper.  

What is the meaning of P in the LSDn panels? What do you mean by a non-dimensional correction factor in this context? How was the correction factor determined?  What are you correcting? Is it that you are correcting the production rate inferred from a non-reaction specific scaling model?

This issue has been discussed elsewhere and is not a new contribution of this paper. Basically, the LSDn scaling method directly calculates production rates by multiplying neutron fluxes and reaction cross-sections. The nondimensional correction factor is then chosen to bring those predictions into best agreement with the calibration data. 

I would recommend distinguishing the data from Blard and Eaves from those of your study using color or symbology. Right now, each scaling model is colored differently, but this is probably not necessary because each has its own plot. Instead, you could give each sample set (i.e., Blard, Eaves, yours) a color that is consistent across all three plots.

We considered this and decided to leave it as is. 

Finally, I think that it would be worthwhile to remind the reader in the caption where the samples from Blard and Eaves were collected.

The details about the samples and sites is discussed in the paragraph directly before (line 228-231) the reference to Fig. 3.

Line 246: This one sentence paragraph seems “tacked-on” to me and doesn’t really follow from your previous two paragraphs or the adjacent figure. I would consider deleting it. It doesn’t seem to further your argument and I think that it disrupts the flow of the text. Alternatively, you could develop this sentence into a full paragraph summarizing this section and perhaps bring in some comparison with the Blard and Eaves studies.

As mentioned in a previous comment, the reference production rates that Blard et al. and Eaves et al. state in the paper can’t be directly compared to ours because different scaling algorithms were used. We therefore reconcile the measured concentrations with ours, using several scaling algorithms, all which is discussed in the previous paragraph and Fig. 3.

This sentence simply states that previously published data and productions rate calibrations from Balter-kennedy et al. (2023), Blard et al. (2008), and Eaves et al. (2018) as discussed in the previously three paragraphs, are all in agreement with the production rate determined from the present study and therefore conclude the section.

Line 248: Is this the production rate from Balter-Kennedy? I find this confusing because you were just discussing Blard and Eaves, and this value seems to differ from those in your figure. Would it be worthwhile to add the data from Balter-Kennedy to Figure 3?

We agree this is unclear and will revise the text to limit confusion.

It is not feasible to add the data from Balter-Kennedy et al. to Figure 3, as their production rate is not directly constrained by the exposure age and the data set can therefore not be used for calibration without reference to their He-3 data, whereas the data shown here can be used independently. We discuss this in the text and instead compare their measured Be-10 and He-3 concentrations with our measured results to evaluate if they are internally consistent when applying the production determined in the present study.

Line 259: I recommend developing this assumption a bit. Thus far, I do not think that you have discussed non-cosmogenic sources of 3He in your samples.

These are very simple assumptions and we are not sure how to make them any more clear. The source of noncosmogenic He-3 (e.g., magmatic vs. nucleogenic) is not relevant here; we are just assuming that whatever it is, it is constant among samples. 

Line 266: Which regression technique do you use to fit this slope?

We use a York regression and will include this detail in the caption.

Line 294: It is unclear to me here what you are normalizing by, please explain. Why is the range in normalized residual for the high-concentration samples (ca. -2 to 6) almost as great as for the low-concentration samples (ca. -2 to 8)?

The normalized residual is the difference between the measured and predicted Be-10 concentrations, divided by the uncertainty in the measured concentrations. The high-concentration samples range between -2 to 2, with the outlier having a value of 6. We have updated the figure to highlight the outlier for clarity.

For the low-concentration samples, we are computing the normalized residual against an expectation derived from the Eaves/Collins data set, not from our data set. Thus, all the residuals are positive, except for sample HB-TC-12. These range from 3 to 8 with no clear relationship with mass loss as one would expect if the excess concentration of Be-10 were solely from meteoric Be-10. 

Line 308-312: I think that your experiment may be fundamentally different from a leaching series experiment performed on an individual sample. I think that you might not see a decline in meteoric 10Be with increasing loss fraction if each sample is weathered to a different degree and contains a different fraction of secondary minerals, grain size distribution, fracture density, etc. that may give each sample a different initial amount of meteoric 10Be.

Possibly true, but it’s all the data we have. 

Lines 314-321: Alright, but what if you were to take the alternative approach and subtract the blank associated with the batch rather than the average of all blanks? Might this be more representative of the contamination associated with that batch? Would this change your results?

Moreover, would a different blank subtraction be sufficient to fully explain your results if the samples are higher by 394,000 and 840,000 atoms and your max blank is only 288,000 atoms? Isn’t it true that you could not account for this much 10Be unless there was more contamination than indicated by your blanks? If so, this would seem to support the meteoric 10Be hypothesis. 

As mentioned in line 318 and shown in Table 2, the highest and the lowest blank are measured in the same batch with the low concentration samples and account for 10-60 % of the measured total in that same batch. Depending on how you correct for the blanks it certainly changes the result, but it wouldn’t change the conclusion that how you handle the blank has a large effect on the results, which is the important point here.

Line 366: The final paragraph seems underdeveloped to me. I recommend adding some discussion of what these “new opportunities” are and reiterating that analyzing 10Be in pyroxene opens quartz-poor landscapes.

We considered this and decided to leave it as to highlight a potential without providing further details, as this is beyond the scope of the paper.

Technical Corrections:

All corrections have been made in the document where appropriate, or a response has been provided below.

Is there a typographical error in the units on the 10Be conc.? Should these be 107 atoms g-1? Likewise, the 3He conc. units are missing a -1 superscript on the g. Also, the 10 on “10Be” in the caption should be in superscript.

I see the confusion here. The units are correct. We measured 34.89 Matoms in a sample of ~0.5g pyroxene. After black correction this results in a Be-10 concentration of 70.5 Matoms/g, which is Matoms per 1 g of pyroxene sample. 

Summary

To summarize, proposed changes to the text in response to this review are:

1. Discussion on the variation in pyroxene composition and how this could affect the production rate. Unfortunately, we do not yet have results for the pyroxene composition for the samples used in this study, and we, therefore, defer to the Geochronology editors as to whether to delay publication of the paper until we receive XRF analysis that could be included in this discussion.
2. Clarification of the analytical methods and discussions where needed as noted in the review.
3. Include supplementary files that contain formatted input data that can easily be pasted into the online production rate calibration.
4. De-emphasize the statement in line 236 and the caption in Figure 3.
5. Errors and technical corrections as noted in the review.

Thank you for your comments and helpful review. Please find our responses and proposed changes to specific review comments (Italic). 

Specific comments: (numbers refer to line numbers in the manuscript) 

All specific corrections will be made in the revised text where appropriate, or a response has been provided below.

45 Niedermann et al. (1994) is an inappropriate reference for production rate  determinations based on another production rate. Although these authors compared the cosmogenic 21Ne to 26Al and 10Be in the same quartz samples, their production rate determination was indeed based on the (presumed) radiocarbon age of the studied glacially polished rock surfaces. Better references for production rate determination by  comparison with another production rate are e.g. Niedermann et al. (EPSL 257, 596- 608, 2007) or Luna et al. (EPSL 500, 242-253, 2018). 

We will correct the reference in the revised text

76 Symbols used in the equation (N10, P10, λ10) should be explained.  

149-151 What about the uncertainty of the standard? If this isn’t included it should at least be  mentioned here. Also, please indicate whether stated uncertainties are 1σ or 2σ. 

For historical reasons, the Be-10 measurement standard to which data are normalized is generally considered as a defined parameter (thus lacking a formal uncertainty) rather than a measured value with uncertainty.  Thus, it is conventional to not propagate an error in the assumed standard ratio. 

All stated uncertainties in the paper are at 1 standard error/standard deviation. As this is the default usage by convention, we leave it to the editors to determine whether a blanket statement of this is required. 

Table 3 The error shown for the 3He concentration and exposure age of 15-OTW-58 is  obviously much too small, at least by a factor of 10. Other 3He errors are around 1%,  which looks rather small also. Do these errors include the uncertainty of the mass  spectrometer sensitivity calibration? And in case of exposure ages, what about  production rate or scaling errors? If they are not included that must at least be  mentioned. Also, how have uncertainties been calculated for data where there is more  than one measurement per sample in the ICE-D database?

The low uncertainty for sample 15-OTW-58 is a mistake and has been corrected in the revised text.

Yes, the calculated concentration error includes the uncertainty in the mass spectrometry sensitivity. The uncertainty in the age is the internal uncertainty using the online exposure calculator and does not not include the production rate uncertainty.

The samples where multiple aliquot has been analyzed for He-3 the concentration and uncertainty is calculated based on the error weighted mean and standard error.

We will include the mentioned details in the table caption.

214 Also give the assumed 3He production rate!  

220 “the 68% confidence interval in the measured uncertainty”: Strange wording.  Uncertainties are nor measured but derived from measurement statistics or propagated 

from other error sources, and it’s not an interval in the uncertainty but just an  uncertainty or perhaps uncertainty range.  

247 Two other scaling models have just been mentioned, but the only production rate value  given is for St scaling. What production rate values would be obtained for Lm or LSDn  scaling?  

The ‘St’ scaling model assumes that the production rate does not vary over time, whereas the other two are time-dependent. In addition, because the ‘St’ scaling model is quite simple, most studies use the same algorithm to compute scaling factors and therefore reference production rates are comparable between studies. Thus, it is simple to compute a reference production rate for ‘St’ scaling directly from the observations, and this procedure is commonly used as a simple way to compare the results of different production rate calibration studies. On the other hand, the much more complex, time-dependent ‘Lm’ and ‘LSDn’ scaling models typically have differences in implementation between studies, so reduced reference production rates are not directly comparable. Although we discuss reference production rates briefly here as a simple comparison, the preferred way to compare different calibration data sets is to ask whether or not the measurements, not the reference production rate derived from the measurements, are consistent with each other for a particular scaling method. We use this approach for all three scaling models later in the paper. 

276-277 What is meant by measurement background? Only later in the manuscript it  becomes clear that this is about blanks; please use clear and consistent terms.

We will make this clear in the revised text 

Fig. 4 Similar issue, what is called “measured concentrations” here has been called “blank corrected concentrations” in Table 2. There, the “measured concentrations” are not  blank-corrected. Such inconsistent wording is confusing. Also, are uncertainties 1σ or  2σ? 2σ would be consistent with the confidence bound of the regression line.  

This inconsistency has been fixed in the revised text.

293-296 and Fig. 5 Please give a clear definition of the “normalized residual”. Normalized to  what? And what are the units of the y axis in Fig. 5? Percent?  

302-303 Here again, you need to give a better explanation of what you did. What are the  “replicated samples”? The low concentration samples shown in Table 4? And did you  assume that the measurement with the least 10Be was free of meteoric 10Be?  

The “replicated samples” are samples that have been measured both in this study and by Eaves et al. (2018) as indicated in Fig. 4 and Table 4. Yes, we assume that the 10Be concentrations measured by Eaves are free of meteoric 10Be, and this assumption is supported by their linear relationship with the He-3 data. We will include these details in the revised text.

314-323 If blanks are so much variable, the blank correction should take account of the whole variation, which is achieved by assuming realistic error limits. This will of course  increase the uncertainty of the blank-corrected 10Be concentrations. Anyway, if variable blanks are the reason for variable 10Be concentrations I would expect values that are both too high and too low. So I doubt this can explain why 10Be concentrations are mostly higher than expected. Again, take care not to confuse blank and background  (again in line 364).  

Yes, which is why we also discuss the potential for insufficient removal of meteoric 10Be as  a source of this increased 10Be concentration as well. However, we can not exclude the fact that a variable blank will have an effect on the overall results. 

Technical comments: (numbers refer to line numbers in the manuscript)  

This review includes a number of technical corrections, all of which will be dealt with in the revised text, with one exception. The exception is that the units of years in the X-axis label in Figure 2 are correct. The quantity plotted here is the nuclide concentration (atoms/g) divided by the production rate (atoms/g/yr), which results in units of yr.