We would like to thank Christopher Halsted for the very helpful review. If the manuscript is accepted for revision, we would be pleased to implement the suggested reorganization as well as the minor and technical changes and improve the presentation of our statistical analysis. Our responses to specific questions raised by the review are recorded in italics. We do not comment on the minor and technical changes that we would like to implement in the revised manuscript directly as suggested in the review.

This preprint is remarkably well-written for being in the early stages of review. As a result, I have few purely technical corrections. The model construction and sample analysis procedures are in line with established practices and I see no flaws in their execution. There is a part of me that wonders about what uncertainties you take on by not knowing the original geometry of the Mt. Evans sample, but I think your approach of estimating sample thickness from measured mass is entirely reasonable. I have two general pieces of constructive criticism for the authors to consider, the first relates to the statistical analysis of the model/sample comparison and the second relates to the overall manuscript organization.

On the statistics side, I would like for more information to be provided about the chi-square goodness of fit test procedures and your interpretations. I provide more detailed feedback in the “Specific Comments” section of this review, but I found that I was reviewing section 4.1 several times to make sure I understood your results and interpretation correctly, and more information would help in my understanding of the test parameters and to ensure that your interpretations are reasonable.

On the organizational side of things, I have some suggestions for the authors to consider. This is not technical feedback, so the choice to adopt or ignore these suggestions is completely up to the authors, but I think they will help with the readability of the manuscript. Currently, the methods and results of your modeling is in the Methods section, while the methods and results for your calibration of nuclide production rates and scaling factors is in the Data Analysis and Results section. This made it a bit difficult on first read to directly compare your model results to your empirical results. I think some re-organization to put the methods for both modeling and empirical calculations in one section, and the results of both approaches in the other section, would help with readability. More detailed suggestions are provided in the Specific Comments.

Specific Comments

Introduction

• In the final line of the introduction, you mention how your results have implications for cosmogenic studies using Fe-rich rocks. This feels like an important outcome of this work but is not mentioned before or after. I think it would be worth expanding on this in the introduction, explaining that confident ³⁶Cl analysis in Fe-rich rocks could be valuable, particularly in quartz-poor areas.

The main motivation for studying this problem has been to understand ³⁶Cl systematics in magnetite in order to use detrital magnetite to infer basin-averaged erosion rates. We will add a sentence discussing this and reference some recent examples of this method from the literature. More accurately scaling ³⁶Cl production from Fe may also improve age estimates using ³⁶Cl in whole-rock basalt or silicate mineral separates in which Fe is important to total production. We will add a brief discussion of this.

Methods

• Section 2.1:
  • The final paragraph (lines 91 – 94) and Figure 2 are results, it might be worth creating a “Modeling Results” (or some other name) results section to house all of your results in one section, as readers might want to easily compare the model/empirical results.
• Section 2.2:
  • Is there any chance that substantial differences in time-integrated geomagnetic cutoff rigidities could exist between Mt. Evans and Owens Valley? If not, it would be worth explicitly stating this in section 2.2.

The time integrated cutoff rigidity is slightly lower at Mt. Evans than Owens Valley (i.e., ca. 4.9 GV vs. 6.3 GV). However, the scaling factor ratios are only weakly sensitive to cutoff rigidity, so this difference is not very significant. We will add some discussion of this in the text.   

• Again, the last sentence here (lines 107-108) sounds like results and could be relegated to a dedicated results section that would allow for easy model/measurement comparisons

• Section 2.3:
  • I do not see information in here or in the supplement about the ⁹Be carrier concentration

We report the amount of carrier added in terms of mass of beryllium, rather than mass of carrier solution, so the carrier concentration is not needed to recalculate the data. We will make this more explicit in the supplement.  

Data Analysis and Results

• To be honest, I am a bit torn about the organization of this section. It is quite long, over 3 pages, and each subsection almost reads as its own mini paper, often including bits of what might be considered intro, background, methods, and results. While in some ways this works well, keeping the information about each aspect of the production rate calculation process contained in its own section, it did feel like I was jumping from topic to topic a bit as I was reading. This is not a technical critique, the information in all these sections seems sound, but more of an organizational consideration. If you are agreeable, one possible re-organizing to consider would be to take all the methods associated with production rate calculations (e.g., in sections 3.2, 3.3, 3.4, and 3.5) and bundle those together in a dedicated Methods section where they all fall under the heading of considerations for calculating and calibrating nuclide production rates and scaling factors. The results section can then be a lot shorter, simply stating (1) the results of your modeling efforts (which are now in the Methods section) and (2) the results of your sample analyses and calibrated nuclide-specific production rates and scaling factors. This would make the comparison of the two a bit easier to facilitate for the reader.

This is a good suggestion and is easy to implement. We will move 3.2, 3.3, 3.4, and 3.5 into the Methods section under a heading of “Calibrating production rates and scaling factors.”

• Table 2 needs a more informative caption. Specify that these are ³⁶Cl_Feproduction rates and scaling factor ratios. Additionally, it might be worth indicating somehow that sample OV19-1 was omitted from calculated scaling factors, and/or indicate that in the Figure 5 caption.

We will implement these corrections and add a footnote explaining that OV19-1 is omitted as an outlier and reference the section of the text where we explain this. We will also note this in the Figure 5 caption.  

Discussion

• Section 4.1:
  • I think a table to summarize your hypothesis tests and results would be a nice way to visualize this information

We will add this table.

• Some thoughts on the chi-square test procedures and interpretations (lines 311-317):
  • Some more explanation is needed about the chi-square goodness-of-fit test (perhaps also a reference to provide more information). I was a bit confused about this on my first read-through because you do not specify the null hypothesis for this test and do not specify how many degrees of freedom are present in each calculation (which is important for understanding how the MSWD values are calculated). Additionally, I at first interpreted this test as the calculation of a reducedchi-square statistic, which is commonly used in isotope geochemistry, and so I was extra confused when I saw reported MSWD values (aka, reduced chi-square statistic values) that sometimes agreed and sometimes did not agree with the reported chi-square values. Because of the lack of information, the MSWD and p-values confused me at first because I interpreted them as rejecting the alternative hypothesis that the reaction-specific models are better fits than the integral flux scaling model, which was contrary to your conclusions at the end of this paragraph. Additionally, because the degrees of freedom and calculation details are not provided, it took some time and inferring on my part to understand why the MSWD and chi-squared statistic values sometimes agreed and sometimes didn’t.
  • To help clarify all of this for other readers, you should identify what the null hypothesis is for these tests and provide needed information including how many degrees of freedom are present for each ratio pair and what your alpha level is. Granted, it is entirely possible that I am misunderstanding what is being reported, but this is all the more reason to expand your explanation for other readers and provide information about exactly which test(s) are being performed and how they should be interpreted.
  • While on the topic of the chi-square tests, I would also like some more detail about how you are interpreting the reported MSWD values. The reported MSWD values suggest that the reaction-specific models are overfitting the data (they are very low), while the integral flux Cl_Fe/Be_qtzscaling model actually has a decently good fit to the data (MSWD closest to 1), but you state in this section that “the data fit the reaction-specific scaling model more closely than the integral flux model”. Again, it is possible I am misinterpreting the reported values, but more explanation about your own interpretations of these values would help clarify this.

The chi-square test is useful for evaluating model goodness-of-fit. In our case, what we seek to test is whether the data are consistent with a particular scaling model, either the integral flux model or the reaction specific model. To clarify this, we will add some explanation of how we are using the chi-square test and reference "Data Reduction and Error Analysis for the Physical Sciences" by Bevington and Robinson (1992).

We will also add the degrees of freedom for the chi-square statistic in each case to the text. When there is only one degree of freedom, the MSWD and chi-square statistic are the same. In our study, this is the case when comparing between only two sites (e.g., feldspar-normalized data from Owens Valley and Mt. Evans).

Currently, we present the p-values for the hypothesis that the model correctly describes the scaling behavior. We can also add alpha values and accept/reject results.    

How close an MSWD must be to 1 to qualify as a good fit depends on the sample size. For the small sample size, the low MSWDs do not necessarily indicate that the data is badly overfit, rather, my understanding is that the p-values indicate that the reaction-specific model is somewhat overfitting (p = 0.88) and the uniform flux model somewhat underfitting (p = 0.19) the data, but that neither model can be rejected at the 95% confidence level. However, for the ³⁶Cl in feldspar normalized data, the integral flux model (p = 0.03) can be rejected at that confidence level.  

We will add some discussion of this to the text.

• Finally, if you decide to adopt my re-org suggestions and directly report the model scaling factor ratios and calibrated values together in the results section, Section 4.1 could also be moved to the results section, as it reads like what might be traditionally considered “results” rather than a discussion point.

We will implement this reorganization, which we agree would help improve the structure of the paper.

Technical Corrections (indicated by preprint line number)

32: Consider changing “show” to “suggest”, as this is based on modeling and not empirical evidence

72-73: Should provide citations to show examples of irradiation experiments and cosmic ray cascade modeling

267: As written, “and low-levels of pore water by increasing neutron…” sounds like it needs a grammatical fix to improve readability.

We would like to thank Irene Schimmelpfennig for the very useful comments on the manuscript and thorough review of the tables, figures, and supplement. If this manuscript is accepted for revision, we would be pleased to implement the suggested changes. Our responses to specific questions are recorded italics. No comment is provided following the technical corrections that we would like to implement directly as suggested in the review.

In this paper, reaction-specific altitude scaling of 36Cl production rates from Fe is investigated by cross-calibrating the production rate of this reaction against those of 36Cl from K in feldspar and 10Be in quartz in the same samples at three different altitudes. I find the majority of the manuscript easy to read (except for a few parts, which I commented on below), the physics very well explained and the approaches well designed. The study is very useful in the light of using 36Cl analyses in magnetite.

I have arbitrarily checked the calculations of 2 samples from the AMS results to the 36Cl production contributions of the various reactions using my excel spreadsheet, and obtain broadly the same results (see one question about this below at the end). I don’t have the expertise to evaluate the Polynomial parameterization.

I have one general question: As far as I understand, you scale the production rates of all reactions by default with the reaction-specific scaling factors of Lifton et al. (2014). By doing so, isn’t there a circular component in your approach? Did you check the effect of using non-reaction-specific scaling factors?

This is an excellent question. We believe that it is unlikely that the results would differ significantly using integral flux scaling factors because the reaction-specific effect for all reactions apart from spallation on Fe and Ti is quite small. The reaction-specific ³⁶Cl_K­/¹⁰Be_Qtz ratio changes by only ca. 3% across the elevation transect, as compared with 18% predicted for the ³⁶Cl_Fe/¹⁰Be_Qtz ratio. We will include some discussion of this in the revised manuscript.

In a broader sense, our view is that if we are going to attempt to evaluate a reaction-specific scaling model, all elements of the model should be reaction-specific for the comparison to be internally consistent.

Here I provide detailed comments, suggestions and minor corrections:

Introduction:

Paragraph starting with line 35 (or the one starting with line 48): please note that in Schimmelpfennig et al (2011) (doi:10.1016/j.quageo.2011.05.002), we have measured 36Cl/3He/21Ne on an altitude transect of Kilimanjaro. It is to my knowledge the only other altitude transect including 36Cl on a similar altitude range as your samples, and might therefore be considered to be mentioned (although 36Cl was measured in Ca-pyroxene and -plagioclase).

We will add this reference here.

Line 40: as you consider the high-energy reactions, and to avoid confusion, maybe better something like “because these reactions are sensitive to the lower end of the high-energy spectrum”?

We will adopt this wording.

Line 105: regarding the estimated thickness of the Mt Evans sample add the reference to Table 1. Also, 25 cm is quite deep. I recommend to clarify whether or not other thicknesses would have an impact on the results. What is the reason of approximating the boulder geometry as a cube? In contrast to the other sites, the exposure history of this boulder is not mentioned here - in Table 1 and later in the text it says “steady state erosion”, please give according information here in the text.

In the absence of direct constraints, a cube is a relatively straightforward and simple option. It is unlikely that deviation of the actual geometry from a perfect cube would have a significant impact on the results of the analysis. This is because we are considering only production ratios (i.e., the ³⁶Cl production rate from Fe is cross calibrated against ¹⁰Be in quartz and ³⁶Cl in feldspar). In this case, the sample geometry only matters to the extent that the different production mechanisms have different attenuation lengths or that radioactive decay is important. We will include a brief discussion of this in the revised manuscript.

We will also add at line 103 that the Mt. Evans blockfield is likely eroding in steady state and support this with reference to Fig. 4, where we make this argument.

Lines 161-169: is there a specific reason why bulk rock is treated differently for the major element analysis?

We used a fusion approach for bulk rock so that we could determine the Si concentration, which forms a volatile fluoride. We will make a note of this in the text.

If you have the measurements of all major elements in the target fraction, I recommend to add them in your supplement table, as these data are included in and necessary for the calculation of the negative muon capture yield in other calculators (Greg’s calculator, GREp 36Cl, and an updated version of my 36Cl spreadsheet published in 2009).

Unfortunately, we do not have all major elements in the target fraction but believe that this is likely not a major source of error in the analysis.  

This is because negative muon capture is likely a minor source of ³⁶Cl, accounting for ca. 1.5% of total production in the Owens Valley feldspar, and only slightly more in the Mt. Evans sample, even under steady-state erosion, because at higher elevation muons become proportionately less important to total production relative to nucleons.  

Furthermore, there is likely little to no production of ³⁶Cl by slow-negative muon capture on Fe because the average ca. 20 MeV nuclear excitation of a muon capture is insufficient to produce ³⁶Cl from Fe.   

Lines 188-192: I recommend to add here a reference to Supp Table “Computed Parameters” (Sub-table “Fraction of 36Cl production in feldspar by target element”).

Line 199: I guess this should be changed to “In the constant exposure model”

Line 200: for completeness, I guess you should add “…feldspar, multiplied by the total 36Cl production rate in feldspar, minus production…”

From section 3.2 on, it would be very helpful for readers if the “types” of production rates or scaling factors were better specified each time, even if this means repetitions. E.g. in line 201 “…derive the Fe production rate at the sample site.” – If I understand correctly, in line 203, P_36,i are the local production rates, right?

That is correct. We will try to clarify this in the revised manuscript.

Line 203: as these concentrations are corrected for the radiogenic component, I would not call them “measured” here. Maybe “cosmogenic”.

Line 225: this correction is not included in Eq. 3. Shouldn’t it?

We will add this to the equation.

Line 258 “…in the subsurface, i.e. with increasing pressure, than 10Be in quartz (as modeled in Figure 2)…”?

We will improve this wording.

Line 265 “…36Cl by low-energy neutron capture by Cl…”

Lines 271-272: please specify if following this analysis, was a correction done for low-energy neutron fluxes on the Owens Valley magnetite samples.

Yes, for the subsequent calculations we used the adjusted low-energy neutron fluxes. We will state this in the revised manuscript.

Lines 275-286: Things become quite complicated here. To allow readers to better follow the approach, I recommend to be more specific about which rates or scaling factors come from your measured data, from modelling or from published LSD-scaled SLHL production rates. E.g. line 276: “…normalized by the LSD-scaled SLHL production rates (Borchers et al., 2016) of either 10Be in quartz…” (if that’s correct). Line 180: “…PFe,cal is the calibrated production rate of 36Cl from Fe at the calibration site (as calculated in section 3.2)“. Are S_K,Be, S_K,Be,0 and most importantly S_Fe,0 LSD scaling factors or where do they come from? Also, it would be helpful to add in Eq. 4 the calculation where the SLHL production rates of 36ClK or 10Beqtz are shown in both the numerator and denominator  (in addition to the calculation where both are canceled).

We will revise this section to differentiate more clearly between what is modeled, measured, or taken from the literature by including this explicitly in the variable descriptions. Yes, the S_0 variables are scaling factors at sea level at the samples’ latitude and longitude, which serve the purpose of normalizing for the geomagnetic effects. We will revise the equation accordingly.

BTW, in supp table “Computed Parameters”, Marrero et al 2016” are cited for the SLHL production rates. The rates are very similar, but the citation should be consistent.

Line 288: correct to 36Cl_Fe/10Be_Qtz

Fig. 1:

• In my opinion, figure captions should have a general title and not start with the description of individual panels. Here maybe something like “Comparison of high-energy particle flux energy spectra (grey curves, left y-axis) with excitation functions (dashed curves, right y-axis). A. …”
• Reading of the figure would be easier/faster if you could somehow visually relate the energy spectra with the left y-axis and the excitation functions with the right y-axis, or at least give the information early in the caption (maybe similar to my suggestion above).
• In the legend: either add or remove the masses of the target elements for all reactions
• Millibarns is a unit, therefore better label the right y-axis “reaction cross section (millibarns)”

Table 1: Please add the names of the locations (Owens Valley etc) above each batch of samples

Fig. 3: The caption says that all sites have similar exposure ages (no erosion etc.), however, in Table 1 steady-state erosion is given for the exposure model of the Mt Evans sample. Please correct this in the caption (or in Table 1?).

Fig. 5:

• Please add the site names on the figure.
• Legend: next to the blue mean correct “Site mean, Fe/Qtz”, or even better be consistent with the labels next to the blue and orange lines in the legend.
• The same should be corrected for the grey circle and diamond in the legend

Table 2:

• Make sure that the table is easier to read in the printed paper, i.e. two columns belong to one header
• Specify somewhere (in the caption or in the headers of the columns) that these are 36Cl production rates from Fe
• Here and in all supp tables, I would clarify that you exclude OV19-1 from your results

Supp Table “AMS Data”:

• In the columns with the rare/stable isotope ratios, the order of magnitude is missing (I guess it must be x10^-15)
• For 36Cl Blank-3, two measured ratios are given for 36Cl/Cl and 35/37, respectively. So, are there actually 2 blanks? Only one mass of spike Cl mass is listed, though? Is the other mass missing? If there are different blanks (one with the felspars and one with the magnetite), wouldn’t it be easier to call them the differently? Why give them the same name?

Yes, there are two blanks, and the spike mass is missing. We will correct this and revise the naming scheme.

• In general, I find this table hard to read. It would be easier if you’d just list the different minerals for each sample one below the other and make one column per spike mass and measured ratio.

Supp Tables “Nuclide Concentrations”, “Target Chemistry” and “Rock Chemistry”:

• Would it be possible to add the concentrations for BL and LL here, for completeness, even if they have been published earlier?

Supp Table “Computed parameters”:

• In the uppermost sub-table (and in the sub-table “Production Rates”), please be consistent in the headers of your columns: in the scaling factor columns you mix target elements (for 36Cl) and the produced nuclide (Be). Ideally put both, e.g. 36Cl_Fe etc and 10Be_qtz.
• Please explain what “Scaling factors to site at sea level” is. I’m confused to what this corresponds in your calculations and in the manuscript.

These are the S_0 values used to normalize for geomagnetic variability between sites.

• It’s unclear to me why you differentiate superscripts 2 and 3 (i.e. “production rate of 36Cl in magnetite by pathways other than spallation on Fe (Owens Valley only, used for Fe calibration)” and “production rate of 36Cl in magnetite by spallation on K, Ca, and Ti (Mt. Evans only).”)
• I would simplify the values in column M (radiogenic 36Cl…) to “atoms 36Cl g-1”, as that’s the number that you probably use to correct your measured 36Cl concentration.
• I recommend adding the nuclide after “atoms” in columns O, Q etc (in all sub-tables); i.e. atoms 36Cl g-1 yr-1 etc.
• Sub-table “Fraction of 36Cl production in feldspar by target element”: Please clarify whether or not the fraction of 36Cl produced from Cl includes the radiogenic component. If yes, I get similar results for sample OV19-13 (the only one I tested that far); if not, the spallation component becomes more dominant by 15% according to my calculations.

This calculation does not include the radiogenic component but does include the higher thermal neutron production estimated due to snow cover, which may account for the discrepancy (section 3.4).

Many thanks for the thorough review of the tables and figures. All comments and corrections will be implemented as suggested in the revised manuscript.