the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 09 Dec 2024
Paired 14C-10Be exposure ages from Mount Murphy, West Antarctica: Implications for accurate and precise deglacial chronologies
Abstract. Cosmogenic-nuclide surface exposure ages provide empirical data for testing the accuracy of models simulating the timing and pace of ice sheet response to a warming climate. Increasing emphasis is being placed on obtaining exposure ages that both accurately constrain Holocene deglaciation and are precise enough to capture ice sheet change at the sub-millennial scale. However, the accuracy of Holocene deglacial chronologies can be compromised by nuclide inheritance when measuring longer-lived nuclides, such as 10Be. Short-lived in situ-produced 14C is unique because it is largely insensitive to nuclide inheritance pre-dating the last glacial maximum (LGM), and when combined with longer-lived nuclides can be used to constrain complex ice sheet histories over Holocene timescales. Here, we present new in situ 14C exposure ages from Mt Murphy, West Antarctica. Many of the new in situ 14C ages are inconsistent with published 10Be ages, suggesting samples collected from the same elevation above the modern ice were exposed at different times. We investigate potential explanations for such conflicting exposure histories by analysing paired 14C-10Be data of Holocene age presently archived in the informal cosmogenic-nuclide exposure-age database (ICE-D, https://version2.ice-d.org/). Our analysis reveal that neither geologic sources of uncertainty due to variations in geologic setting nor modelled scenarios of subsurface nuclide production explain conflicting paired 14C-10Be exposure ages observed at Mt Murphy. Furthermore, we observe that repeat in situ 14C concentrations measured in 15 of 31 samples do not replicate within their nominal 6 % (2σ) analytical uncertainty and identify ~ 2 kyr of excess unquantified scatter from Mt Murphy in situ 14C exposure ages. Taken together, these results suggest analytical uncertainty for in situ 14C measurements may currently be underestimated. We provide recommendations for improving measurement precision that will benefit future Holocene deglaciation studies including analysis and publication of more replicate measurements, and the continuation of efforts to quantify and minimise sources of scatter in blank measurements.
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Status: final response (author comments only)
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RC1: 'Comment on gchron-2024-34', Anonymous Referee #1, 15 Feb 2025
GENERAL COMMENTS
This manuscript presents a dataset of paired in situ cosmogenic 14C (in situ 14C) and 10Be from glacial erratics collected along an altitude transect on the flanks of Mt Murphy in West Antarctica, to try to constrain Holocene thinning history of the margins of Thwaites Glacier. The in situ 14C was measured to assess whether previously measured and published 10Be data from those samples contained small amounts of 10Be inherited from previous exposures, as is common among long-lived cosmogenic radionuclides in many settings in Antarctica. However, the authors observe discrepancies in apparent exposure ages calculated from the in situ 14C and 10Be results and try to explore possible reasons for those discrepancies in most of the manuscript.
Unfortunately, this manuscript is fundamentally flawed in my opinion, due to incomplete data presentation and oversights and misinterpretations in its analysis that render most of the conclusions irrelevant for what should be the main question at hand – better understanding their dataset to enable refined constraints on the Holocene thinning history adjacent to Thwaites Glacier. It then proceeds to apply its flawed arguments to other labs without consideration for differences in procedures and equipment and potential effects of those differences on their analysis.
The paper is very poorly organized and does not flow logically. The authors make assumptions and arguments early on that there are issues broadly with in situ 14C reproducibility in general, without justification, before even describing the laboratory methods and presenting the new results specific to these samples. They present various data analytical and modeling arguments that they try to use to explain the 14C-10Be discrepancies in their data, again without first presenting the actual 14C data that could motivate the use of such techniques. The manuscript should have a simpler, more typically streamlined organization with 1) an introduction that provides background on the study motivation and geomorphic/glaciological setting (not assuming a priori that there is an issue with their results and those of other labs more broadly), 2) clearly stated laboratory methodological and analytical details and assumptions, 3) a presentation of the new results, and then 4) discussion of the results. If there was any justifiable motivation for the various data analyses and modeling done to attempt to explain observed discrepancies, then 4) would be the appropriate place to present those, not before. The authors have not presented such motivation in my view. Each paragraph and section should flow logically from the previous one instead of jumping back and forth from one topic to another without motivation, as the authors do in this manuscript.
I can’t speak to the discrepancies noted between apparent exposure ages for 10Be and 14C associated with the original system configuration at Tulane but in my experience with configurations similar to that of the new design at Tulane, the discrepancies between apparent exposure ages from four replicate 14C analyses and the corresponding 10Be results are likely due to the design and perhaps procedural changes, as well as the authors’ assumptions about how to interpret those 14C results. However, the authors present no data after those modifications to justify those assumptions about how to interpret the results – neither procedural blanks nor analyses of intercomparison materials such as CRONUS-A, CRONUS-R, or CoQtz-N. Instead, they gloss over those changes that likely have the biggest implications for their dataset, and instead raise what in my opinion are poorly justified, more generalized, and ultimately unsuccessful conjectures as to the potential “sources of uncertainty” focused broadly on in situ 14C. Thus, we are left with discrepant sample results without any basis to evaluate how they compare to the earlier results using a different system configuration. Stated more simply, to my mind this is largely a laboratory issue associated with Tulane’s system. It’s not relevant to compare the post-modification dataset to either the pre-modification dataset from Tulane in this study, nor to datasets from other laboratories, without considering their design and associated procedural differences and blank and intercomparison results. The authors would first need to present full analytical details of blanks and intercomparison results from the new Tulane system configuration before they can justify interpretations of the results from their unknowns and comparisons with results using earlier configurations/procedures at Tulane.
Intercomparison measurements before and after the modifications also have potential implications for what the correct production rate is to use in exposure age calculations. Goehring et al. (2019, Geology, 47(4), 291–294) and subsequent publications from that group argue that in situ 14C production rates derived from the pre-modification CRONUS-A concentrations from the Tulane system (reported as ca. 10-20% lower than other labs’ reported concentrations) are appropriate for calculating exposure ages from other samples measured in that lab. Without corresponding measurement details of blanks and CRONUS-A from the recently modified system, it is unclear if that assumption still holds, and all the modeling and analyses comparing this dataset to other datasets from Tulane and other labs are not supported here as a result. Based on the broad agreement of reported CRONUS-A measurements from most other labs, it’s clear that the 14C production rate derived from the Goehring et al. (2019) CRONUS-A measurements is not appropriate to apply to datasets generated from those other labs.
Furthermore, I feel VERY strongly the authors should limit their analyses to published datasets, and should not be using unpublished data posted to ICE-D, as that database only presents the final concentrations with no associated laboratory measurement or procedural details. Yes, as the authors note, unpublished datasets are posted there per funding agency requirements, but without the associated detailed information about lab results required to derive the posted concentrations, they should be considered preliminary at best and at worst, unreliable. For example, the 14C data in one of the references cited here, Johnson et al. (2020), are loaded into ICE-D, but the concentration values in ICE-D are listed in the supplement to that paper as the total 14C atoms measured for each sample, not the concentrations. That said, even the concentrations in the Johnson et al. (2020) supplement are apparently incorrect, if I assume that the total 14C values were correct – the original listed concentrations in the supplement are just the total 14C atoms for each sample shifted upward by one row, not total 14C atoms divided by sample mass in grams. The only way I know of this error is because Johnson et al. (2020) also presented those data in their supplement. I ended up finding a corrigendum to that paper (not referenced by these authors) with the correct total 14C atoms and concentrations properly listed, confirming the posted ICE-D values, but that was not included in the version I had previously downloaded. Yes, this is no doubt an exception rather than the rule in ICE-D, but without such published, publicly available and detailed analytical information, such errors might not be identified and corrected – therefore one could not be assured of the validity of unpublished values posted to ICE-D.
Thus, in my opinion this manuscript should not be published in anything near its current form, if at all, as the conclusions are not supported by the authors’ data or analysis. I think that the manuscript would likely have benefitted had the authors included Drs. Ryan Venturelli and Brent Goehring as co-authors, instead of just in the acknowledgements, since they ran the in situ 14C samples for this study, and they are the two people who best understand the lab methods used for these analyses at Tulane University. That is a big red flag for me. Perhaps they could have helped to resolve what I argue are fundamental flaws in the authors’ approach to the manuscript and data analysis.
SPECIFIC COMMENTS
Title: Suggest changing title to ‘Paired in situ cosmogenic 14C-10Be exposure ages from Mount Murphy, West Antarctica: exploring potential sources of observed discrepancies’
Line 11:ice-sheet’ should be hyphenated throughout when it's acting as an adjective (modifies ‘response’ in this case).
Line 13: Define ‘nuclide inheritance’ for the reader
Line 14: Suggest changing ‘in situ-produced’ to ‘in situ cosmogenic (in situ 14C)’ then use in situ 14C throughout thereafter. In situ should typically be italicized since it’s Latin, although I know that’s also a style issue with Copernicus publications.
Line 17: Describe what is meant by ‘inconsistent’
Line 18: ‘exposed at different times’: Do the 10Be ages show evidence of inheritance? If so that's normal. If not, then succinctly describe the issue here for the reader. This wording is not particularly descriptive of the issue.
Line 20: Change ‘reveal’ to ‘reveals’
Line 24: I argue below that it’s inappropriate to generalize to other labs without detailed evidence from each – focus on uncertainties in the dataset here from the Tulane lab and try to understand that before adding unnecessary degrees of freedom.
Line 29: hyphenate ‘ice-surface’ – it modifies ‘change’
Line 31: hyphenate ‘ice-sheet models’
Line 32: Define in situ 14C here first before shortening – ‘in situ cosmogenic 14C, hereafter in situ 14C, and 10Be’
Line 36: Delete ‘of’: should read in situ 14C (5700 ± 30 yr), and no comma after parentheses.
Line 37: ‘the total inventory of in situ 14C in a sample decaying to below detectable levels in ~30 kyr’: This is only true if a sample is exposed for some time prior to 30 ka, then subsequently deeply shielded. Clarify.
Line 39: citations should also include also Lifton, N., Wilson, J., & Koester, A. (2023). Geochronology, 5, 361–375; Fülöp, R.-H., Fink, D., Yang, B., Codilean, A. T., Smith, A., Wacker, L., et al. (2019). Nuclear Inst. and Methods in Physics Research, B, 438, 207–213; and Lupker, M., Hippe, K., Wacker, L., Steinemann, O., Tikhomirov, D., Maden, C., et al. (2019). Nuclear Instruments and Methods in Physics Research Section B, 457, 30–36.
Line 40: Define what ‘inheritance’ is - probably best to do it a couple of sentences earlier when talking about 10Be inventories persisting over multiple cycles.
Line 41: Suggest changing to ‘combining analyses of short-lived in situ 14C with longer-lived 10Be…’
Line 47: Give a summary description of the site similar to that in earlier papers first, in this paragraph.
Line 55: ‘However…’: Sentence too long – split into two or more for clarity. Clarify that the 6% measurement uncertainty is being propagated into exposure age uncertainties per Table 1. The authors often seem to imply 6% exposure age uncertainties as opposed to concentrations (replicability of CRONUS-A measurements at Tulane). See comment on Line 400.
Line 62: Are these data the same as what you reference in the previous paragraph? Text should flow logically.
Line 65: As argued in General Comments - only use published data that fully describe all aspects of the analyses, particularly for in situ 14C.
Line 69: This whole intro discussion is premised on a poorly justified interpretation of the data from the Tulane in situ 14C lab. See General Comments.
Line 82: ‘Data producers’ – awkward phrasing – what are the authors trying to say? Clarify.
Line 90: ‘2-3%’: More like 2-3 permil for modern sample replicates - less so for older samples with lower ratios. In situ 14C is typically more on the percent uncertainty scale for AMS measurements, but again the precision is ratio-dependent. Clarify
Line 91: Cite the full list of in situ 14C studies from above including the most recent from each lab.
Line 94: Citing dead carbon as a contaminant reflects a misunderstanding of the Nichols and Goehring (2019) paper - dead carbon has no effect on the 14C measurement other than to lower the ratio that is measured. That paper argues that laurylamine, which is modern, not dead, can be a contaminant, and thus adds 14C to the in situ signal.
Line 97: Define for the reader what the ‘combustion’ step is. The authors can’t assume they will be familiar with it.
Line 112: ‘5% uncertainty’: If 14C muon production is ca. 20% of total production at the surface (SLHL) then 2-5% uncertainty on the total would be the uncertainty if 10-25% of total surface production by muons is valid. Clarify that 5% is the maximum estimate.
Line 120: Also cite Lifton et al. (2023).
Line 121: ‘In the following sections,…’: In my opinion, the authors are putting the cart before the horse. As noted in the General Comments, this should be pitched as a site study and then deal with the issues with the data in the discussion. Don't come out of the gate telling the reader the punch line and all the potential reasons for the punch line that may or may not be relevant. This section should just set the background to the site, etc., and motivation for exploring the dataset. Before making any arguments about other labs’ data, the authors first need to fully document the behavior of the Tulane system before and after the system modifications using intercomparison samples and process blanks. Again, see General Comments for further discussion.
Fig 1: Panel 1a is the only relevant figure here at this point in the manuscript. Panels b and c lack any motivation at this point and should be put in the discussion section if even needed at all, once the dataset is presented and lab-specific issues are addressed.
Line 148: The general geologic description of the sites should be summarized here for the reader.
‘Adams et al., 2022’ should be ‘Adams et al. (2022)’.Line 151: Why? What is the motivation for the replicates?
Line 152: Describe what is meant by ‘the in situ 14C extraction of NOT-103 failed’. How and why did it fail? These first sentences don’t flow logically with the rest of the paragraph.
Line 157: ‘in situ 14C’ should not be hyphenated.
Line 158: Delete comma after Goehring et al.
Line 160: in situ is not hyphenated.
The actual extraction procedure used here should be clarified. It appears from comparing the lab sequence numbers for these samples with the lab sequence numbers for the Balco et al. (2023) dataset that the procedure in place for Balco et al. (2023) (different from that of Goehring et al., 2019) applies here as well, but that needs to be confirmed.
The LiBO2 does not melt the sample, it dissolves it at 1100 C. Mentioning <1300 C is not relevant to this procedure.Line 163: Slota et al. (1987) is the wrong citation – it is for Zn reduction, not H2. Should be citing e.g., Santos, G. M., Southon, J. R., Druffel-Rodriguez, K., Griffin, S., & Mazon, M. (2004). Radiocarbon, 46(1), 165–174; and Southon, J. (2007). Nuclear Instruments and Methods in Physics Research Section B: Beam Interactions with Materials and Atoms, 259(1), 288–292.
Line 165: The coil trap does not change how gas is extracted from the sample - it’s just a different design. All traps on these types of systems use liquid nitrogen to freeze CO2 evolved from the sample.
Line 166: Pigati et al. (2010) is not an appropriate reference for this. Only Goehring et al. (2014) and (2019) talk about this effect but only Goehring et al. (2019) suggests it may be associated with the mullite. The authors need to specify that this is the interpretation of Goehring et al. (2019), not some general finding.
Line 172: ‘production within a mineral lattice’: Poorly stated. Hippe and Lifton (2014) basically just removes any corrections that are typically made for organic 14C in AMS reporting.
‘Long-term average’: What time period is this based on? The long-term mean blank and standard deviation from Balco et al. (2023, The Cryosphere, 17(4), 1787–1801) Table S5 is 56,300 ± 34,800 atoms. The mean blank for the time period spanning the initial set of analyses in this manuscript is 74,400 ± 41,600 atoms based on the lab sequence numbers. The latter is the defensible, representative value to use, in my opinion - even if one is using the long-term mean, one has to justify the difference in the value quoted and the value from the data presented in Balco et al. (2023). If the value is based on some other set of blanks, then those blank data should be fully presented in this paper similar to Balco et al. (2023).
For the replicate samples, all blank data underlying the value quoted here should also be fully detailed and presented, and explain why the authors need to use a different value. See General Comments.Line 184: The primary production rate calibration dataset of Borchers et al. (2016) works for 10Be in the University of Washington v3 online calculator but is not implemented by default for 14C. The default 14C production rate in that calculator is based only on Tulane measurements of CRONUS-A reported in Goehring et al. (2019) - not the Borchers et al. (2016) dataset (presented in Koester and Lifton (2023)). At present, the default production rate in the online calculator should only be used for measurements at Tulane prior to the design changes. As noted in the General Comments, all CRONUS-A measurements from Tulane after the modifications should be presented here if they have been made - then the appropriate production rate for those analyses can be assessed. It should also be noted that the mean value for CRONUS-A in Goehring et al. (2019) is not consistent with the data presented in Balco et al. (2023) Table S5 – the source of the discrepancy is unclear.
Line 192: See General Comments - present the analytical methods first, then results, then discussion of results. The narrative should all flow logically – Sections 2.2-2.4 should be in the discussion if they are even still relevant to the observed discrepancies at that point once baseline post-modification measurements (i.e., blanks and CRONUS-A) are presented if available. This paper struggles with logical flow as written – topics jump around without presenting an underlying motivation.
Line 195: 10Be exposure ages <11.7 ka can also have small amounts of inheritance. Clarify that here and in Line 197.
Line 204: The Type 3 scenario can also arise from normalization by incorrect production rates at the site (per discussion in General Comments). For example, the curves on the plot reflect the assumed production rates for each nuclide. If those production rates are not directly applicable to the dataset of interest, then the data can plot above the continuous exposure line. State what production rate (or calibration dataset) is used to generate the curves and which is used to normalize each data point. In particular, this could apply to datasets not from Tulane if the Tulane Goerhing et al. (2019) CRONUS-A production rate is used to generate the curves. Also, the units on the x-axis in all two-isotope plots in this manuscript should be years, not atoms/g. The concentrations of each nuclide for each data point are normalized by the sample site production rate (indicated by [14C]* or [10Be]*): atoms/g divided by atoms/g/yr = yr. This should be corrected on all such plots throughout.
Line 212: ‘local nuclide production’ – is this time-dependent? Are the continuous exposure and steady erosion curves generated using the same assumptions? Specify.
Line 217: ‘Sources of geological uncertainty’: This is putting the cart before the horse. See comment on Line 192. The authors should try to focus on understanding and describing the lab (and associated production rate) issues at play at Tulane – doing so I believe will at least explain some of the discrepancies. This paper in my opinion should focus only on explaining this dataset – much of the effort to incorporate analyses from other datasets around the globe is poorly motivated, and adds additional degrees of freedom without shedding any light on the question at hand in the end.
Line 224: The potential for 10Be inheritance needs to be included as well in such an analysis
Line 227: I have not seen any adequate justification at this point as to why this is something that needs to be investigated more broadly than just for this dataset. The authors ignore the significant change in system configuration before the replicate analyses, and provide no documentation as to the effect of that change (procedural blanks and CRONUS-A or other intercomparison material measurements before and after). Those data are critical for any subsequent interpretations in this paper. There is also no discussion of whether extraction procedures were modified after the coil trap installation. Once those supporting data have been presented in full and discussed in detail, then perhaps one can justify a broader search for sources of uncertainty – as things stand, in my opinion, none of the approaches investigating uncertainties in this dataset are adequately justified in the manuscript.
Line 231: See above comment. I also think that to pull in situ 14C analytical data from ICE-D without accounting for, or at least acknowledging potential lab procedural differences/biases/offsets/etc. serves to confuse the apparently lab-sourced issue here. Bringing other labs into the analysis brings in additional data complexities that can make comparisons to this particular study unreliable.
See General Comments above regarding using unpublished data from ICE-D – that is a really bad idea, even though funding agencies require the data to be placed in such a repository. Without the associated detailed information with all the data and procedural details that go into calculating a concentration for a sample, any such detailed comparisons are unreliable in my opinion.Line 240: This is where the authors should start - present the sampling and extraction methods in the previous section and then present the data here, then explore any issues in the discussion associated with the lab measurements. They should not a priori assume (at least from the reader’s perspective) that there are major issues generally with the techniques. Focus only on the lab that made the measurements, where there was a significant change in the system captured in this dataset.
Line 243: ‘When examining in situ 14C reproducibility’: This appears to be approaching the whole dataset with a level of suspicion that is not justified at this point. Just say all uncertainties are presented at 1 sigma unless otherwise indicated and be done. Present the results first, then discuss. Each paragraph should flow logically from the end of the previous paragraph.
Line 245: Seems like Scoria Cone is a place name (colloquial?) and should be capitalized throughout when discussed as such. Or if it is simple a description of the feature, then it should be referenced as ‘the scoria cone’.
Line 251: ‘Repeat in situ 14C measurements…’: Why were they made? Describe the reasoning. The authors only discuss the replicate results relative to the initial measurements on a significantly different system configuration, without appearing concerned with the significant system modification that has not been characterized in terms of any data that's been published or presented subsequently. See General Comments.
Line 266: As noted in the General Comments, applying a single production rate to all data here ignores the potential significance of the change in system configuration between the initial analyses and the replicates. Again, if the authors want to better understand the source(s) of any discrepancies, it is critical to present all supporting data (blanks and intercomparison measurements) from both before and after the system modifications, so that fully informed judgments about the appropriate production rate(s) to use can be made.
Line 273: Statement about concordant 14C and 10Be ages: The pattern noted here may be due to the choice of production rate used for 14C before and after the system change. See General Comments
Line 285: TUR-138 should plot on the continuous exposure line, if the authors normalize by the appropriate 14C production rate (e.g., LDEO CRONUS-A, per Johnson et al., 2020, or similar).
Line 293: Fig 4 caption: As above, these ages need to be calculated with the appropriate production rates - those for the replicates after the system modification need to be documented first. You don't need two panes - they could be combined into one with appropriate easily distinguishes symbols.
Line 313: 68% confidence is 1 sigma. So, at 2 sigma the ellipses not in the burial field overlap with the continuous exposure line.
TUR-138: As noted above, what production rate and 14C concentration are the authors using for this? The original Johnson et al. (2020) paper used the LDEO CRONUS-A measurements for the production rate, which are in line with other labs' measurements, and its apparent exposure age agrees within 1 sigma with the corresponding 10Bemeasurement.Line 316: I still am not clear as to the motivation or need for this, given the potential effect of the system change. The motivation should flow logically from the dataset discussion, which has not really occurred yet – this is again putting the cart before the horse.
What production rate datasets are the authors using to a) construct the exposure and erosion curves, and b) normalize the concentrations? Do both a) and b) use the Tulane Goehring et al. (2019) CRONUS-A dataset?Line 328: There are no 14C data in the Balco and Schaefer paper. This needs a different (or additional) citation if they are published somewhere with all analytical details, other than only ICE-D. On the other hand, Table 2 only lists ICE-D as the source - as argued in the General Comments, no unpublished 14C data from ICE-D should be included without full extraction and analytical details for each dataset. In that case, this dataset should be deleted throughout.
Line 334: See comment for Line 328.
Line 335: I’m not sure what the age of the exposure has to do with anything, other than the concentrations being low? More to the point, there are no significant details about the extraction procedures in that paper. Also, what is a non-uniform ellipse - I've never heard of such a thing. If it's an ellipse, it's elliptical and thus uniform - maybe not centered on the data point is what you're referring to, i.e., asymmetric uncertainties? Clarify
Line 341: See above comments on the Sjögren glacier samples – Line 328
Line 342: Specify which production rates were used for which samples. As noted earlier, applying the same production rate across all samples may be incorrect here. And again – only published datasets should be included, regardless of whether or not they are in ICE-D.
Line 346: Should be moved to the discussion – this does not flow logically. Citation needed if published - Balco et al. (2019)? If not published, then the data should be excluded
Line 348: This all needs better motivation - first document Tulane system behavior after the modifications, then make thorough comparisons to the pre-modification dataset. Also, why do the authors have search criteria if they then ignore them? Explain why Tucker Glacier is included. How do the authors define ‘relatively large degree of scatter’? Be precise in the wording. Maybe there are similar issues to this dataset, but one can’t just pool them together and expect to understand what might be causing those differences without understanding any potential differences in extraction systems/procedures (and subsequent discussion below, Line 353, suggest they are not particularly useful in that comparison).
Line 352: Explain what Shark Fin is and how it relates to Tucker Glacier.
Line 353: If the ratios are consistent with simple exposure histories then why include this? If there is a ‘large degree of scatter’ similar to the current dataset then why wouldn’t they plot similarly on the two-isotope diagram. I assume the ellipses on that diagram are also 1 sigma (68%)? And again, x-axis units are years. What purpose does it serve to present this and then just leave it be for the reader to ponder?
Line 361: As before, this is poorly motivated and should be moved to the discussion or deleted. Each of these sections is just presented without adequate motivation. And I would argue that these plots don’t support the hypothesis being proposed anyway. In each panel of Fig 8 only one sample overlaps the steady erosion or continuous exposure line at 1 sigma, regardless of what is being modeled. Furthermore, the 14C data from that Sjögren glacier are apparently not published, so without full description of analytical details they should be excluded, and this section can be removed.
Line 390: Move to discussion and limit to published Tulane measurements focusing on this site.
Line 400: It is not clear where the 6% number is coming from. Provide details as to how the 6% number is calculated, or better yet use the full CRONUS-A data in Balco et al. (2023). The mean in that publication is 5.78±0.50 e5 at/g for the Goehring et al. (2019) data - that's 8.7% std deviation, which is the appropriate uncertainty measure here. If one includes the rest of the data in that table gives 5.88±0.59 e5 at/g (10.0%). Subsequent measurements associated with the new system configuration should also be detailed here.
Also, it should be clarified throughout that the 6% number (or 8% or 10%) applies to 14C concentrations only, not ages.Line 405: Again, unpublished 14C data from ICE-D should not be included without full analytical details. Per the General Comments, this is an area where the people who know the most about operation of that lab would be REALLY useful to have as co-authors.
Line 422: See comment Line 348.
Line 425: As I’ve said earlier, to try to understand differences in the measurements one needs all the extraction details, not just the final concentrations that are presented in ICE-D. And again – no unpublished data from ICE-D should be included per the General Comments. Any such analysis should be restricted to published data from Tulane at the most to minimize the number of variables affecting the various datasets. Adding in data from other labs using other extraction techniques or system configurations only makes understanding the variability harder. Keep the analytical framework as simple as possible.
Table 2: At most, only include published 14C datasets sourced from the Tulane lab. Simplify the framework.
Line 432: I think that the authors’ approach to this entire discussion should be re-evaluated with the system change at Tulane as the starting point. I have a lot of thoughts about the discussion as written, but am holding them back because they mostly depend on the authors’ assumptions that have been made without those underlying basic data about the effects of the changes to the Tulane system on 14C measurements. Without the details of the blanks and intercomparison measurements both before and after the system change, one can’t make informed assessments of system performance, much less instructive comparisons with other datasets from Tulane or other labs.
Line 486: I would not expect a geological explanation for what appears to me to be likely a laboratory issue.
Line 495: It’s best not to speculate without data.
Line 590: I don’t find that this analysis sheds any light on the Mt Murphy dataset so would just remove it. A lot of effort has gone into trying to explain this unpublished, undocumented dataset that is not particularly relevant to the Mt Murphy data - focus the paper just on understanding that dataset.
Line 626: I don’t think this sort of high-altitude view of the dataset is helpful for understanding what’s going on. If the authors really want to try to figure out what is going on, then I think they need to explore similarities and differences in each dataset in granular detail.
Line 645: It isn’t correct to just change the measured value - the measured value is what it is. However, as noted what IS different between the two labs are the CRONUS-A measurements - Balco et al. (2019) use the CRONUS-A value from LDEO for the production rate for that sample - that is the correct approach. If the normalization of that sample 14C concentration uses the Tulane production rate (too low for that sample), then that is why it plots above the continuous erosion curve. If it was normalized by the correct production rate it should plot correctly.
Line 653: The background improvement is not attributed to the extraction technique but to the AMS technique that doesn't require graphitization.
As noted previously, one can calculate the long-term mean blank from the data in Table S5 of Balco et al (2023). Also, the CRONUS-A data from the Tulane lab are in that spreadsheet. The blank from the period during which the initial Mt Murphy samples were extracted for this study exhibits a mean blank of 74.4k ± 42.2k atoms (1 sigma std dev). That is the appropriate value to use.Table 3: I'd label the blank column 'representative blank' - not all are 'long-term' - and the blank is in units of atoms, not at/g.
Tulane CRONUS-A measurements – see comment Line 628. Unclear where that value in the table comes from based on the Balco et al. (2023) table.
The extraction laboratory for Lifton et al. (2023) is PRIME Lab, not the University of Arizona.Line 660: There are subsequent analyses from a number of labs not in that paper that should be considered as well.
Line 664: Best not to speculate about any potential role of impurities – just state that no link was found between low levels of impurities in the samples and reproducibility and move on. Koester and Lifton (2023) indicate typical levels of impurities would not likely have any significant effect on 14C results from quartz samples.
Line 670: Blanks and reproducibility: The authors need to present the blank data representative of their samples that reflects the blanks run during each time frame when the samples were run (pre-coil trap is in Balco et al. 2023, Table S5) - especially the post-modification time span for which there are no published data.
Line 679: Why is the blank correction higher? Present all the underlying data and describe the basis for the calculation.
Line 681: I argue that in typical system operation, the blanks associated temporally with the sample runs should be representative for the samples. I would not expect one normally to need to use a lognormal distribution - there are periods during the Tulane lab operation (Balco et al., 2023, Table S5) that have high blanks with increased variability, and some that have low blanks with more typical variability. Samples run during those times should reflect the coeval blanks in my opinion - an approach used in 10Be and 26Al analyses, for example. Not an exact parallel with 14C blanks but similar. At any rate, Balco et al. (2022) state that their lognormal approach applies to low-level, blank-dominated datasets at Tulane, which is not the case for this dataset, and there is no evidence that I know of to justify applying it to other labs or all 14C samples in general.
As such, I argue that the most appropriate blank value to use for the samples here (and generally) is the mean blank bracketing the times during which the analyses in question took place - the mean value (and 1 SD) for the pre-coil trap samples is 7.44 ± 4.16 e4 atoms, from the Balco et al. (2023) dataset. The authors need to include corresponding blank measurements (full details) for the time spanning the post-coil trap replicates to support the value they use here. Applying the pre-coil trap blank values to those is not appropriate without documentation.Line 695: Again, this behavior with mullite tubes has only been noted at Tulane. Clarify.
Line 698: See argument above about temporal variability in the Tulane blanks pre-coil trap - the lognormal distribution would only apply to pre-coil-trap data, for very low-level samples, but should not be used beyond that unless there is experimental evidence of that after the coil trap addition. Even then I would argue the blank distribution during the sample extraction time period is more relevant. Suggesting that it be applied to all 14C data generated by all labs is completely unjustified.
Line 707: Use the full Tulane CRONUS-A dataset in Balco et al. (2023) (Table S5) for comparison – the mean from that is significantly lower than the value quoted here and for the samples listed in Goehring et al. (2019). As noted earlier, it’s not clear from the data what the source of the Tulane discrepancy is. At any rate, the difference between the LDEO value and the Tulane reported value is ca. 50-60k at/g, not 6k.
Line 712: Sample ‘combustion’ should instead be sample ‘extraction’.
Line 714: Include Lifton et al. (2023) – blanks are typically < 50k atoms – comparable to many non-flux-based systems. Should also include Lamp et al. (2019) (and perhaps Young et al., 2021, as well) as a flux-based system.
Line 717: The CRONUS-A value in the Young et al. paper is 662,132 ± 9849: 0.09 should be rounded to 0.10 at two decimal places. Again, this is not consistent with the stated Tulane concentration nor the mean of the concentrations in Balco et al. 2023, which is MUCH lower - 5.88e5 at/g, including analyses after those in Goehring et al. (2019).
Line 720: The authors are comparing results from systems with different designs from that of the Tulane system, and the effects of which add degrees of freedom to the analysis that are not being considered in this discussion.
Line 732: These findings only apply to results from the Tulane lab, and again, that conclusion depends on post-modification measurements of CRONUS-A and blanks. Don't cast a wider net than is warranted. Also this section should be folded into the conclusions, in my opinion.
Line 744: Absolutely run replicates, and intercomparison materials of various concentrations in addition to CRONUS-A - e.g., CRONUS-R and CoQtz-N. As noted above – such information is needed to evaluate the effects of system modifications to enable informed assessment of the observed discrepancies in exposure ages.
Line 745: There is no justification that I know of to apply the lognormal blank correction for the low-level Tulane data of Balco et al. (2023) to any other laboratory or higher-concentration datasets from Tulane. This recommendation should be removed as a result. I would argue that it is more important to understand the sources of the blank and to minimize uncertainties from those. See comment for Line 681.
Line 750: That’s fine to consider impurities but they would have to be WAY more significant than what the authors measured (and which is probably reasonably typical for normal quartz separates for cosmogenic work) to have any reasonably measurable effect on production.
Line 754: This section should be refocused pending comparisons of process blank and CRONUS-A measurements before and after the system design change.
Also, I only count n=13 analyses here from Mt Murphy area, not 20. Where are the other 7 coming from? Are the authors including the measurements from Johnson et al. (2020), and if so, which ones? Not to mention the potential change in relevant production rate for the pre- vs post-modification analyses, pending post-modification CRONUS-A measurements if available.Line 760: As noted previously, I would not expect any geological sources for the discrepancy - this appears clearly to be a lab issue. Perhaps Drs. Goehring and Venturelli could have shed some light on that as co-authors.
Line 762: The 6% value is supposedly derived from the concentrations of CRONUS-A measured at Tulane in Goehring et al. (2019), even though the data in Balco et al. (2023) indicate a scatter of the longer-term dataset more on the order of 10% (nearly 9% for just the Goehring et al. samples).
Line 764: Post-modification CRONUS-A and blank values are critical before one can make informed comments.
Line 765: See General Comments about using unpublished ICE-D datasets
Line 766: First compare pre- and post-modification CRONUS-A and blank values for the Tulane system. In my opinion, the exploration of other potential sources of variability is not relevant without those data, diverting the focus from first understanding the potential laboratory sources of such discrepancies.
Line 772: Again - this is specific to Tulane. Not generally applicable without a more in-depth analysis of techniques from other labs.
Line 776: Quartz impurities at the typical level measured for cosmogenic quartz separates are not likely to affect reproducibility (see magnitudes predicted by Koester and Lifton, 2022) - what is the proposed mechanism? This is weak and speculative at best currently, without any evidence as you note. I recommend leaving this out of the conclusions.
Line 778: This broad conclusion is not justified based on the data here. Again, avoid broad generalizations - this specifically applies to this dataset only. Most of what the authors describe can perhaps be ascribed to laboratory issues at the Tulane lab.
Line 798: Yes, the data are available in ICE-D but often the details of the analyses are not – no unpublished data without those details should be included. See General Comments.
Line 816: As noted previously this is concerning that Drs. Venturelli and Goehring are not co-authors. A red flag in my eyes....
Supplement
Line 21: I appreciate the documentation of lithology and interpretation of relationship to potential nearby sources (i.e, local erratics).
Line 60: What does ‘See Chapter 4’ refer to? Clarify.
Table S3: If any of these data from ICE-D are unpublished they should removed as noted in earlier comments
Line 104: Are the Kay Peak data pulled from ICE-D or elsewhere? If the authors are using the LDEO 14C analysis from Turtle Rock they should not be using the Tulane-derived production rate but the LDEO CRONUS-A-derived production rate in Johnson et al. (2020) for that sample. Specify which Kay Peak samples are included – also Kay Peak Ridge? Only erratics? Bedrock 14C details are not presented in Johnson et al. 2020 but are included in their Fig 5 and results are in ICE-D – Should not include those.
Also check that all the ages used here have been recalculated using the current UWv3 calculator and LSDn as is described – the ‘LSDn-derived’ values in Johnson et al. (2020) are not consistent with LSDn, but seem more like St was used.Line 114: It appears that the bedrock analyses from Kay Peak were excluded. Clarify.
Line 122: ‘analytical uncertainty’: Should be using external uncertainties for comparing different nuclides – LSDn scales them differently and the production rate uncertainties are distinct and should be included. Clarify
Line 135: See comment above.
Line 259: Suggest CRONUS-R as perhaps a better material for 14C. See e.g., Fülöp et al. (2019).
Line 269: Again –should not include any unpublished ICE-D data.
Citation: https://doi.org/10.5194/gchron-2024-34-RC1 -
AC1: 'Reply on RC1', Jonathan R Adams, 27 Feb 2025
We thank the reviewer for taking the time to provide a very detailed and thoughtful review. We note they express potential issues with the manuscript in its present form, primarily 1) the motivation for the manuscript and replicate measurements, 2) the need for additional reporting of in situ 14C replicate CRONUS-A and blank data from the Tulane laboratory, 3) the use of in situ 14C data publicly accessible in the ICE-D database from another part of West Antarctica, and 4) the general structure of the manuscript. We respond to these points in brief here and will include a detailed point-by-point response if we are invited to revise the manuscript.
First, thanks to dedicated efforts and recent developments by a relatively small group of technical experts, the application of in situ 14C cosmogenic nuclide exposure dating is becoming an increasingly common technique. Accordingly, the number of in situ 14C end-users is growing rapidly, demonstrating the value and need for the technique within the Quaternary research community. A paper such as ours that examines in situ 14C data from the end-user perspective is therefore useful, relevant, and timely. The value of our manuscript to the broader community is partly to serve as a cautionary tale to end-users of cosmogenic nuclide data; specifically, that datasets with apparent inconsistencies and conflicting results should be rigorously investigated and fully interrogated. For example, in our manuscript, the motivation for measuring replicate in situ 14C measurements is that the majority of initial in situ 14C concentrations led to exposure ages suggesting deglaciation at 5–3 ka – results that were inconsistent with previously-measured 10Be ages at the same site and that contradicted all published literature on the timing of Holocene ice thinning in the Amundsen Sea Embayment (ASE). If we had just taken the initial in situ 14C measurements at face value, we could have concluded deglaciation occurred from 5–3 ka, which would have radically and spuriously altered the current consensus on the timing of deglaciation in the ASE, which occurred 9–6 ka, and West Antarctica more widely. The reason we include examination of potential geological solutions to our dataset is because we first tried to explain the concordant-discordant exposure ages prior to measurement of the in situ 14C replicates and believe these efforts to understand the data are generally useful, uniquely rigorous, and should be documented. Our manuscript is particularly valuable because it provides a conceptual framework with which the growing end-user community may better critically test, diagnose, and improve the accuracy and precision of future in situ 14C cosmogenic exposure ages using multinuclide (e.g., in situ 14C-10Be) methods.
Second, we agree that an expanded treatment of replicate CRONUS-A and blank data, especially following modification of the in situ 14C extraction line at Tulane, is a reasonable request that will strengthen the manuscript, and we thank the reviewer for indicating where we should source additional information on the blanks and CRONUS-A. Furthermore, we would like to point out that Dr. Brent Goehring and Dr. Ryan Venturelli are co-authors on the accompanying in situ 14C data set submitted to the UK Polar Data Centre (PDC) (https://doi.org/10.5285/dbb30962-bbf3-434a-9f27-6de2f61a86e2) and were consulted in the production and submission of this dataset to the UK PDC.
Third, the reviewer raises a point about the inclusion of an in situ 14C dataset from Sjogren Glacier that was sourced from the “ICE-D Antarctica” database. Table 2 in our manuscript demonstrates the comprehensive approach we undertook to credit the sources of the data we use in our study, and we believe the inclusion of the unpublished in situ 14C dataset from Sjogren Glacier dataset is necessary and appropriate for two reasons: 1) the close geomorphic resemblance of the Sjogren Glacier, Site C to our study site, and 2) the high number of replicate in situ 14C measurements from this site.
Finally, we also acknowledge that structurally the paper has many moving parts and there are perhaps alternative ways to present these ideas; therefore, we will consider the reviewer’s helpful recommendations on how to restructure the manuscript in our revision.
Citation: https://doi.org/10.5194/gchron-2024-34-AC1 -
CC1: 'Reply on AC1', Greg Balco, 13 Mar 2025
The aim of adding a comment here is to try to provide some broader context on what I think this paper is trying to do and why it comes into conflict with some of the views in this extremely thorough and comprehensive review. Although I have some connection with this paper as noted in the acknowledgements, this was limited to providing code for the 2-nuclide diagrams and making some comments on early drafts.This is an unusual paper for a couple of reasons. One, it's an attempt to analyze a lot of C-14-in-quartz data that is written by a set of authors who do not themselves operate a C-14-in-quartz analytical facility and did not themselves collect the data being analyzed. This acts to draw criticism on the basis that the authors do not have enough expertise in the details of C-14 analysis to correctly interpret these data. Two, it basically concludes that there is a lot of unexplained scatter and irreproducibility in the C-14 data available for Antarctica. As the authors are, in fact, associated with a lab specializing in cosmogenic Be-10 analysis, there is a risk that this paper will be read as a self-serving screed about how C-14 data are much worse in some way than Be-10 data.
I'll address the second of these aspects of the paper first. It's important to keep in perspective, and this paper could do a better job of reminding readers of this, that the reason we want to measure C-14 in Antarctic rock samples is not because it is more accurate, or more precise, or easier to measure than Be-10 or Al-26. In fact it is probably none of these things, because C-14-in-quartz measurements are very difficult. We still want to measure it, though, because it provides unambiguous information on LGM ice cover that we can't get from measurements of any longer-lived cosmogenic nuclides subject to inheritance from previous ice-free periods, no matter how precise they are. It's unfortunate that this paper kind of gives the impression that it is setting up a competition between Be-10 and C-14 data, because that's not the point that should be understood here. The point that should be taken from this paper is that the authors are trying really hard to understand the properties of the C-14 data set so they can use it in the way it should be used. It can certainly be argued that this paper isn't doing a perfect job of this, possibly far from it in many areas suggested by both reviewers, but the fact that researchers who did not collect these data are trying really hard to use it is a major success of the overall C-14 data collection enterprise. This is a good thing.
The first issue then comes up when this reviewer correctly points out that there are some serious obstacles to looking at these data as a whole, the main one being that, in general, not enough background laboratory information and quality control data are available to disprove the hypothesis that all the inaccuracies and inconsistencies noted by the authors are laboratory errors (errors in this case meaning atoms of C-14 spuriously being added to or lost from the sample) or mis-standardizations (meaning incorrect application of blank corrections or interlaboratory normalizations). Basically, this reviewer takes the position that if you can't fully document all of the laboratory procedures with substantial amounts of QC data, you shouldn't use the results.
Certainly it is true that there could be more documentation for many of these data. However, this is the situation we have at the moment. A significant majority of C-14 data from Antarctica were collected in the Tulane laboratory. The Tulane laboratory is no longer in operation. It is no longer possible to collect additional QC data from this facility. The suggestions in this review that the authors of the present paper obtain new QC data from Tulane, or enlist Tulane lab staff as authors, are most likely not actionable. In fact, it could reasonably be argued that NOT having Tulane-associated authors might be more likely to lead to an unbiased analysis.
However, even though it is not possible to collect additional QC data, one important thing about the Tulane lab is that it has already produced an enormous amount of QC data compared to other C-14 analysis facilities. No other lab, to my knowledge, has published anything like the 50 process blanks and 24 replicates in the 2023 paper cited in the review,, or the substantial set of replicate analyses in the present paper. Even if the documentation of background information such as changes to the extraction line, etc., is incomplete, I am not aware of any other lab making C-14 measurements that has published anywhere near this amount of blank/replicate data. Of course, the result of measuring all these replicates is that they show a lot of unexplained scatter - the collection of large amounts of QC data have revealed problems that would never have been known about if fewer data were collected. Certainly this may be a public relations disservice to the Tulane lab, and possibly by extension to the entire C-14 analysis community, but, again, these data were collected, they exist, we're stuck with them, and they are of value in showing that there appear to be significant and poorly understood reproducibility issues with at least some C-14 data. As other labs have mostly not reported these numbers of blanks and replicates, it remains mostly unknown whether or not they have the same problems as the Tulane lab. It is certainly a reasonable hypothesis that other labs with other extraction systems and procedures have better reproducibility and blank control than the Tulane lab. However, this can't be established unless/until other labs generate the same amount of QC data.
Thus, I disagree with the reviewer here. If we can't evaluate the Tulane data with the relatively huge pile of blanks and replicates that are available from this lab, how are we going to even start evaluating the data from any other lab? Even though there are some obstacles to looking synoptically at a data set primarily composed of Tulane-generated data, that isn't a reason not to do it. I agree that is is nearly certain that there are undocumented errors and mis-standardizations in both the published and unpublished data in the ICE-D compilation. However, that doesn't mean we shouldn't try to use it, as long as we are trying to use it in an error-tolerant way. This is what the present authors are trying to do, even if they may not have perfectly accomplished it. For example, this review points out that there were likely some changes to the Tulane extraction procedure that may have caused systematic offsets between C-14 concentrations measured before and after the changes. If we have a large data set of replicates measured before and after such a change and identified by consecutive analysis numbers, which the reviewer implies that we do, it ought to be possible to clearly identify an offset. Of course, the present authors have not tried to do this, but it ought to be possible. From this perspective, therefore, I think the authors should be given every opportunity to try to interpret these data, rather than being asked to remove them from the paper.
To summarize, this review correctly points out numerous examples in which apparent irreproducibility or inconsistency in poorly documented data could simply be the result of measurement errors or mis-standardizations, and argues that this can't be established one way or the other without process data that don't exist. The conclusion of the review is that all the poorly documented data should be discarded. I disagree with this: these are the data that are available, in actual fact there are an exceptionally large amount of QC data from the Tulane lab that can be used to evaluate data quality, and the authors are trying to do exactly what they should be trying to do with these data. I do agree with this reviewer that it is not totally clear whether the authors have succeeded in doing this, and some of the material towards the end of the paper having to do with possible explanations and fixes for various inconsistencies is very speculative. However, I think the authors should be given the opportunity to work with all the data that are available.
On a separate topic, as one of the ICE-D project developers, I have a couple of comments about the ICE-D system in response to some of the comments in this review. Mainly, this reviewer correctly points out that all the exposure-age calculations for C-14 in the ICE-D system use a production rate based on Tulane analyses of CRONUS-A, which could cause some distortions in the 2-nuclide diagrams and their interpretation. There is a reason for this, which is that most of the C-14 data in the ICE-D database were measured at Tulane (60% of data worldwide; 86% for Antarctica). We fully appreciate that it is highly likely that there are systematic interlab offsets, and concentrations and production rates should therefore be normalized to a common value for calculation of exposure ages. The system already does this for cosmogenic noble gas data, which have well-characterized interlab offsets. However, this cannot be fixed for C-14 exposure ages until C-14 labs show that apparent offsets based on CRONUS-A measurements are not specific to CRONUS-A and can be replicated on other samples. Lacking this information, renormalizing everything to a common value of CRONUS-A is only slightly less sketchy than not normalizing at all. We strongly encourage C-14 lab operators to do this experiment.
Note that the authors of this paper could try to correct this issue for the present paper by renormalizing data from labs other than Tulane using the data in their Table 3, although most of the data they show/discuss are from Tulane, so it's not clear that this would have a huge effect on any of the discussion. Also, many of the C-14 data in the ICE-D database do include a reported value of CRONUS-A for the period in which the analyses were done, which could also be used for normalization.
A final ICE-D-related comment is that the 28,000 in line 322 appears to have too many zeros. There are about 17,000 Be-10 measurements worldwide. In Antarctica, there are about 2700 Be-10 data and 1000 Al-26 data.
Citation: https://doi.org/10.5194/gchron-2024-34-CC1
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CC1: 'Reply on AC1', Greg Balco, 13 Mar 2025
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AC1: 'Reply on RC1', Jonathan R Adams, 27 Feb 2025
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RC2: 'Comment on gchron-2024-34', Anonymous Referee #2, 28 Feb 2025
General comments
The manuscript is trying to analyze in-situ 14C paired with previously published or analyzed in-situ 10Be and/or 14C results near the Thwaites Glacier, West Antarctica to reveal the deglacial history. However, many of datasets appeared out of the “constant exposure” zones and trying to reveal several effects which made them “underestimated”. As a result, the authors missed both “revealing true deglacial history” and “strengths of in-situ 14C/10Be paring analysis”.
I’m not sure whether the authors are aiming to reveal glacial responses to climate changes with paring isotopes or discussing about the limit and problems (without clear conclusion) of less-precise results with low reproducibility. The whole manuscript is concentrating on the in-situ 14C works and discussion about the limits, somewhat irrelevant with the title of the manuscript. Please clarify the main theme of your work and make the structural changes through whole manuscript.
Authors are trying to compare previously published 10Be data with newly analyzed 14C data. If the chemical pre-treatment with HF, HNO3, and frothing (maybe only performed during 10Be pre-treatment?) were carried out contemporary, the qz grains could be highly homogeneous. If not, especially the repetitions of purifications, additional crushing, difference of grain size, and due to other many reasons, can make the samples to be highly inhomogeneous. Since the authors are not suggesting any detail information about whole procedures, I cannot assure the accuracy of the 10Be-14C compare result (not about the difference between replicate measurements).
I’m not sure that the authors are providing enough information to calculate from the chemical and physical treatment to the calculated age (in situ 14C) data. I think the author must suggest the “collected mass of gases after combustion (also need to explain how you liberated C in the form of CO2. With flowing oxygen or just oxidized in chamber without flow?)”, “collected mass of purified CO2 after cryogenic purification”, and so on. Some information and datasets are lack in the manuscript and supplementary.
The treatment system uses LiBO2 flux. As author commented, it makes many problems such as corrosive effect of mullite tube or other Qz containing parts of the system. And the system must have many contaminants from the expandable parts. If the authors want to consider about all the possibilities of the contaminations which can affect the high error range between the replicate measurement, especially in Blank samples in 4.5.2. Please suggest the AMS ratios of diluted CO2 (low level 14C CO2) and system or process blank (whole process without Qz) and their repeated data.
Since the authors are trying to overcome the discordance of parings, I’d like to suggest additional repetition of analyzing CRONUS-R or N samples with full data to make sure the treatments are reliable. I cannot talk about the reliability of the Tulane CEGS system with this work, but at least the authors should have suggested more than 2 standard samples (not the oxalic acid in AMS measurement, but which were co-treated through the CEGS system).
I have a great concern and confuse with using ICE-D database. it is a really great database for cosmogenic nuclides exposure dating studies, but there are too many unpublished data with many lack of information and difference. Please check the specific comments.
There are too many results and discussions with unkind explanations. In-situ 14C studies need many explanations about terminology, procedures, results, and so on. Please explain not only the geochronological words but details in in-situ 14C for readers in the introduction or methods part.
Specific comments
L13: please explain what “inheritance” means for readers (just shortly in this abstract paragraph).
L14: please use “Shorter-lived”, since Fig. 2 and other sections are using “longer” and “shorter” word.
L17: please consider about the sentence “many of the new in situ 14C ages…”. unnecessary in abstract part and makes your work confusing. What made the different times and the reason? Because of the mixed erratics and/or inheritance? And I also suggest what sample you took and analyzed in this part. Erratics or bedrocks.
L42: if the author wants to comment the “(26Al)”, please cite reference.
L84: first letters of the full name of “ICP-OES” is using capital letter. Please make the AMS in same format.
L104: need space between “%” and “(Borchers…)”
L125: Fig.1 I think the panel labelings (a), (b), (c) are unnecessarily large. And also, I cannot find the groundling line and coastline in fig. 1(a) which are described in legend.
L149: need a space between “S1,” and “and”
L153: need “.” After (2016)
And also the citing formats are different. “A general geological description of these sites (see Fig. 1a) is provided in Johnson et al (2020) and Adams et al., 2022. “ “We performed quartz mineral separation for in situ 14C samples at Imperial College London largely following Corbett et al., (2016) “
L160: please explain the supplying method of oxygen from first heating step.
L165: you mean SOx and NOx removing with copper? Please explain the detailed alterations because present manuscript has too little information.
L168: already used AMS acronym from L84.
L169: delta 13C is not stable isotope analysis.
L173: authors explained blank level in “atoms/g”. please suggest the what mass (g) is used here. Does it mean “per total CO2 gas mass” or “per total C mass”?
L181: there is no unit of CRONUS-A long-term value in the sentence.
L186: maybe the 1 sigma after 6 % is unnecessary or should be in parenthesis.
L196: it doesn’t make sense because your sentence seems to mean “the older ages than Holocene have inheritances risks”. Younger ages also can have inheritances and also vice versa.
L199 & 210: I understand the types of the paring results. But authors would better explain the types with “sectors” not the “ellipses” in Fig 2. And also, please separate a line down the “[14C]/[10Be]” label on the y-axis.
L290: for the replicate samples, authors used “-R” in samples names, but the sample names on figure 3 and 4 seems quite complicated and hard to discern. How about using parenthesis on the label instead using “-R”?
L355: please explain what does the “* (asterisk)” mean on the x and y-axis label.
L393: one of “1 sigma” and “6%” would be better in parenthesis. Same as in L400, L410, and so on.
L404: Fig 9 and the paragraphs about the “ICE-D” data would have quite large risks.
L428: Table 2 also have high risks since each reference (their extraction system, method, blank level, reference material, normalization material, calculation method (14C/13C & 13C/12C or 14C/13C & total C…)) are totally different.
L535: I think the fig. 10(a) would be more proper on fig. 1, showing the study area. And also, the color ramp of the ice velocity seems not clearly on the satellite image
L538: please make a label legend on the figure about the groundling line (black lines). And unify the thickness of the lines. They seem quite different on (a) and (b).
L551: delete a space between “in this case to” and “10Be”. And also, unify the decimal place of the age with other age data (to one).
L554: authors already used the full name and acronym of “LDEO” in Table 2.
L706: format of the 14C atoms are different through the manuscript. Please ignore the no superscript applied values, but just take a look at the orders and words in following examples from your manuscript. “1.19 ± 0.37 x 105 atoms g-1 14C” “7.14 ± 0.30 x 105 14C atoms g-1” “1.28 ± 0.20 105 at g-1” “6.93 ± 0.44 x 105”
Supplementary Fig S2-S4: What is the topographic transect profile based on? I think they are too low resolution. How about using Reference Elevation Model of Antarctica (REMA) with 8 or 2 m resolution. The satellite image and elevation profile seem too much different.
Citation: https://doi.org/10.5194/gchron-2024-34-RC2 -
AC2: 'Reply on RC2', Jonathan R Adams, 18 Mar 2025
We thank Reviewer 2 for their constructive feedback on our manuscript. If invited to submit a revision, we will address specific comments point-by-point alongside a revised version of the manuscript, but here reply to the main points raised by the reviewer. These points include 1) clarification of the main research theme and structural changes, which is similar to Reviewer 1’s comments, and 2) the need for additional detail about both the quartz purification and in situ 14C extraction procedures.
First, we previously clarified the motivation and main research theme of our manuscript in our response to Reviewer 1’s comments. To briefly reiterate, our paper aims to examine in situ 14C data from the end-user perspective, and to illustrate that datasets with apparent inconsistencies and conflicting results should be rigorously investigated and fully interrogated. The recent community comment by Greg Balco echoes our intended message by stating that “The point that should be taken from this paper is that the authors are trying really hard to understand the properties of the C-14 data set so they can use it in the way it should be used". To address both reviewers’ comments on this similar point, we will include further clarification in our revised manuscript. Both reviewers also provided helpful suggestions on paper structure, which we will consider in our revisions, and we are happy to make necessary structural changes to improve manuscript readability.
Second, the reviewer raises a point about the homogeneity of the quartz samples. We will supply more detail on the laboratory procedure in the revised manuscript, but, for clarity, we outline the main relevant details here. Each of the 13 in situ 14C concentrations in our study (initial n = 9; replicate n = 4) was measured in a ~3-5 g aliquot of the same homogenised batch of purified quartz that was separated from the same whole rock sample at Imperial College London before shipment to Tulane for 14C extraction. For samples from the scoria cone site, ~10-35 g aliquot of the same batch of purified quartz was measured for 10Be as was measured for 14C. For samples from the Notebook Cliffs and Turtle Rock sites, 10Be concentrations were determined in a previous study (Johnson et al., 2020) and in situ 14C concentrations were measured in a different batch of purified quartz than was previously measured for 10Be; both batches of quartz, however, were separated from the same original whole rock sample. Paired in situ 14C-10Be measurements from the scoria cone (same quartz batch) and Turtle Rock and Notebook Cliffs (different quartz batches) exhibit several discordant 14C-10Be ages, yet there is no observed systematic correlation between concordance-discordance of situ 14C-10Be pairs and the batch of quartz from which they were measured. Therefore, there is no evidence that our results and conclusions can be attributed to inhomogeneous quartz samples. We also acknowledge the reviewer’s request for more detail on the specifics of the in situ 14C extraction procedure and will provide this information in the revised methods section as much as possible.
Finally, we appreciate the due diligence the reviewer has paid to highlight minor typographical inconsistencies in our manuscript and suggest improvements to specific figures, all of which we will incorporate during revisions.
Citation: https://doi.org/10.5194/gchron-2024-34-AC2
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AC2: 'Reply on RC2', Jonathan R Adams, 18 Mar 2025
Data sets
Cosmogenic in situ 14C data and calculated surface exposure ages for 9 erratic cobbles collected from Mount Murphy, West Antarctica J. A. Adams et al. https://doi.org/10.5285/dbb30962-bbf3-434a-9f27-6de2f61a86e2
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|---|---|---|---|---|---|---|
| 341 | 64 | 14 | 419 | 30 | 9 | 9 |
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- Total: 419
- Supplement: 30
- BibTeX: 9
- EndNote: 9
Viewed (geographical distribution)
| Country | # | Views | % |
|---|
| Total: | 0 |
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| PDF: | 0 |
| XML: | 0 |
- 1