This manuscript presents a unique dataset that required an impressive logistical and analytical effort to produce. It concludes that a glacier in the Amundsen Sea Embayment, West Antarctica, experienced fluctuations of its grounding line landward of the present position within the last several millennia. This history thus implies that the retreat of glaciers in the study area may not indeed be so-called ‘irreversible,’ since, simply put, its retreat apparently reversed prior to the 20^th century.

Extending a cosmogenic-nuclide ice-thickness dipstick transect to below present-day ice cover is not the only novel aspect of this work. Novel too is the OSL exposure dating application of sub-ice bedrock core tops, and its combination with CRN depth profile data in the same sub-ice cores. This is fantastic, and a first. The site selection at a hotspot of global glacier change makes this work particularly relevant, and it expands on important work in the region by extending it to samples from under the ice.  Topping all this off is an elegant treatment of uncertainty that highlights the most plausible solutions of ice thickness history at the site in a statistically robust way. The authors have crafted a very digestible description – in writing and illustration - of a complicated dataset. This paper will no doubt be a benchmark as the community is poised to apply this approach at additional sites.

For the above reasons this paper is a no brainer for publication in TC. I provide some comments that the authors may wish to consider; I would categorize these comments as minor, even if some question (or help to bolster) the paper’s major conclusion. Very important in my view is the novel methodology that the study provides.

1. The glacier thickness history most compatible with the data, according to the interpretations laid out in the paper, is one that I would characterize as actually rather stable. Following a period of rapid ice thinning between ~6000 and 8000 years ago of >200 m in <1000 years is a subsequent period 1000s of years in duration with a thinning of only “30-35 m relative to present.” One could interpret this amount of glacier thickness change across many millennia as minor, and maybe not a reason to question the irreversible retreat concept, as the title does. There is mention in the conclusion paragraph that 30-35 m of thinning “may have been associated with grounding line retreat of tens of kilometers upstream of present locations.” With the emphasis of the paper being on the reversable nature of marine glaciers in West Antarctica, I might suggest the addition of evidence/discussion backing up the inference of 10s of km of grounding line retreat associated with 35 m of thinning.

2. I can think of a few ways to bolster support for the interpretation laid out in the manuscript:

• I think that an underlying requirement for applying luminescence exposure dating in this situation is that a sub-glacial site of interest experiences(ed) non-erosive glaciation. If the base of the glacier is erosive, and the drill sites had been exposed in the middle Holocene, the glacier could have eroded the upper few of cm of the bed during late Holocene overriding. In this case, wouldn’t the luminescence results would be the same as if the drill sites were not exposed at all during the Holocene (the current interpretation)?

• The authors might therefore mention that the drill sites are cold-bedded (I didn’t find anywhere in the paper that mentions this, but I might have missed it). I believe Winke operations require a cold bed at the time of drilling? (not sure about the packer set-up, if that could still obtain bedrock cores with minor drill fluid loss at a warm ice-bed interface) Knowing the basal temperature would be best (but maybe not possible). If the bed is only slightly below pressure melting, then it may be difficult to know if it was always cold-bedded during the Holocene. It might come across as a surprise to some that this is a site of cold-bedded glaciation, given the marine-based, fast-flowing ice-steam nature of these glacial systems; literature suggests velocities on order 1 km/yr and beds nearby that are not frozen, although there must be sharp boundaries in a landscape like this.

• The authors could attempt to rule out another possibility for the OSL signal to be saturated at the surface during an ice-free period, which would be that the two drill core sites with the OSL data were covered by debris during a Holocene ice-free period. Such debris could shield underlying bedrock from being bleached. If this is unlikely, say why. Perhaps more information from the ice-free portion of the bedrock ridge would be useful – does it lacks debris, or is debris sparse? Similarly, back to the glacial erosion part, maybe some descriptions from this ridge would be useful here as well. Does it lack glacial molding, other glacial-erosional landforms and striations (particularly below the 1966 limit)?

• Given the two reasons above that could lead to a saturated OSL signal despite an ice-free middle Holocene, it could be worth mentioning whether the CRN results alone are or are not compatible with an ice-free period during the Holocene. If not, then great, and the interpretation in the present manuscript is further bolstered.

• The authors pioneered the 14C/10Be chronometer for Holocene ice burial. I might have missed it, can there be mention of this ratio in the bedrock cores and whether it or supports or excludes a scenario of ice-free conditions followed by ice burial? Are there any 10Be measurements from the ridge between today’s ice height and the 1966 limit? Having a C/Be ratio in this portion could be informative in constraining the pre-1966 duration of ice at this location.

• The exposed bedrock below the 1966 limit is a playground and offers much. It is unknown when this portion of the ridge was re-occupied by ice, but I believe it is thought that the episode of thinning earlier in the Holocene led to the exposure of the portion of the ridge between the 1966 level and the present ice surface – and the 14C numbers reflect this. Does the recent ice cover (unknown period preceding 1966) need to be considered when interpreting the 14C ages of bedrock in this zone? I guess the 14C ages here are apparent ages? Also, is there any evidence of glacial abrasion in this zone? If so, I suppose some or all of it could date to the LGM. But if all of it doesn’t date to the LGM, could the 14C age scatter (in the paper explained by ‘locally derived snow and ice’) be explained by minor amounts of uneven late Holocene glacier erosion of the bedrock surface?

• Finally, are the CRN depth profile shapes themselves of any use in determining where in depth space the drill cores are – ie, has there been any surface truncation? Some of the profile data (H4 and H5) look remarkably flat, that is, fairly unchanging with depth (in Fig 7A-H5, the statistical profiles have a rather uncomfortable fit with the data). Perhaps this is a product of residing below meters of ice and a few cm of surface erosion would not be possible to detect.

A final thought on these points; if it turns out that a middle-Holocene ice-free period cannot be entirely ruled out, then this actually may support the title of the paper even more strongly. An ice-free period in the middle Holocene would only make the estimates for thinning and re-thickening all the more minimum.

3. As I wrote in my intro remarks, this manuscript does a remarkable job explaining a complicated dataset simply. The figures are outstanding. Yet, they are mostly highly technical. This is, of course a technical paper in a technical journal. Nevertheless, I wonder about a summary figure that shows the glacier history in a more cartoon fashion. A multi-panel cross section or something that shows the ice thickness history in several time slices through the Holocene. Something for the broader readership. Additionally, there seems to be some important interpretations that are rather nuanced and difficult to visualize without such a figure, such as the potential that the drill sites are slightly off ridge and could be covered by a ramp of glacier ice. This is rather important, as this point is used to suggest that the calculated ice thinning may be a minimum. Finally, some field pictures of sample sites could be really helpful, and what about any photographs of the cores themselves? For those of us who like to teach about very cool studies like this, these visualizations go a long way.

A list of minor things that the authors could choose to consider.

- page 2 line 9, could be useful not only to mention that people have modeled irreversible glacier retreat systems, but what they have found.

- page 2 line 20, here the authors are describing how OSL-ED and CRN systems work in the remote case of long-lived thin ice cover. Why not start by describing the more obvious case of an ice-free then ice-covered system. The text at present certainly foreshadows your interpretations, but sort of skips the basics first.

- figure 1, add legend of the ice velocity. Also, sometimes authors use hotter colors for high velocity (reds) instead of “colder” colors like blue.

- figure 2, I struggled a little bit here. The pink dots shown on the graph are fewer in number than the pink dots on the image - I'm guessing that the plot doesn’t encompass the entire transect shown in the image. But I had to stare and dig deep to conclude that. Also, there is mention of a sample at 171 m asl, but this plot doesn't seem to have a dot at that exact elevation.

- page 6 line 21, here it states that stable ice for millennia is unlikely; isn’t that more or less the interpretation that the manuscript goes with? The ice-thickness histories plotted in Fig 7C during the middle Holocene (the middle segments) appear flat and pretty unchanging.

- page 8 line 35 – could this “fragmented rock” be surface debris? Back to above comment about shielding the underlying bedrock surface during an ice-free period. This debris could theoretically be ephemeral, exist during an ice-free period but then be transported off a rock core site during subsequent overriding.

- figure 6, fantastic idea to re-occupy an older rock sampling divot. Could you model a profile that shows a plausible history alternative to the one this paper points to? - that is, middle Holocene exposure until something like 2 ka, and then subsequent burial to present?   It could be nice to see such a scenario stand in contrast to these data that were generated, much in the way that the null hypothesis is plotted in Figure 7A/B. Also, as an aside, it sure would be cool to have a core with OSL data from the above-1966 ridge just to see if you can match the 14C exposure ages – would be a nice proof of concept.

-page 12 line 11, not sure I entirely understand this sentence. It says that the 14C “concentrations are 2-3 times typical detection limits,” but then also “and are significantly lower than routinely measured.” Lower on line 25, it says these samples are “near detection limits.” Collectively, these statements leave me a little confused.

- figure 7C, is there a reason to choose the history ending with the present ice thickness at H5 in the scenario-modeling instead of a higher surface that could correspond to the “1966” thickness, which is 30 m higher?  I suppose all you could do is estimate. Perhaps it is of no real consequence.

- page 16 line 26, interesting interpretation of the basal debris-rich ice. It sort of seems that erosive ice during the Holocene is ruled out, therefore this debris must relate to the LGM. But I didn’t find anywhere in the paper where this is stated. Ruling out more firmly a Holocene origin could help to bolster the interpretation in the paper.

- page 20 line 6, here there is a lot packaged into one sentence. This amount of grounding line retreat is somewhat critical for justifying the paper’s title which challenges the irreversible glacier concept. I’m not against the authors’ choice to not include a lengthy “implications” portion to this paper, but they could add some supporting discussion here.

- page 20 line 9, similarly, a lot is packaged into the sentence on the RSL-rebound control on the grounding line in this system, readers might find bit more on this useful.

- page 20 line 12, I generally try to avoid making stylistic/subjective comments about writing, but I’ll make one here – sentence beginning with “Thus” is lengthy and I found it a little difficult to follow.

-Jason Briner

GENERAL COMMENTS

This manuscript presents new cosmogenic nuclide and luminescence results from three subglacial bedrock cores at a site between the Pope and Thwaites Glaciers in West Antarctica that indicate that the ice over the cores experienced thinning during the Holocene, with subsequent thickening to the present. The luminescence results from the uppermost core tops are consistent with continuous burial over the last 200-280 ka, precluding Holocene surface exposure. On the other hand, measured 10Be and 14C depth profiles from each core are broadly consistent with a few thousand years of exposure under thinner ice than present during the Holocene, based on forward modeling of cosmogenic nuclide concentrations under plausible ice thickness histories. The authors argue that mass loss from the Holocene thinning could have led to subsequent isostatic rebound and relative sea-level fall at the site, thus stabilizing the ice sheet due to readvance of the grounding line.

I found this manuscript to be timely and well written, presenting an interesting albeit noisy dataset and solid modeling that supports a conclusion that may shed light on future West Antarctic Ice Sheet behavior in a warming climate. That said, I think that there are some significant aspects of the data analysis and presentation that need to be addressed before the paper would be ready for publication. In particular, I think that the treatment of the 14C data would benefit from additional supporting data, analysis, and clarification in order to strengthen their interpretation.

First, I think the authors are overinterpreting their 14C blank data, particularly with regard to the core results. The lognormal fit to the 49 blanks (those presented in supplement S5 – not 50 samples as cited in the supplement text S2) is a novel approach but I’m not convinced it’s necessary or even appropriate because most of the actual sample analyses presented here (cores + surface samples) take place at each end of the overall time span considered. Depending on how one splits them up, somewhere around half of the blanks in that analysis have no direct bearing on the samples presented. I would argue that rather than lumping all the blanks together over the two-year period, it would be more appropriate to separately consider only the blanks being analyzed that span each set of analyses - TUCNL 465-490 (so maybe blanks 461-491) and TUCNL 663-780 (so maybe blanks 656-782). The blanks bracketing the first batch of samples (461-491) are uniformly low, so a simple average and standard deviation would be a reasonable and conservative estimate in my opinion for those initial surface samples from Kay Ridge. The blanks associated with the last batch of analyses are more scattered, but one could argue either for a straight average and standard deviation covering blanks 656-782, or for perhaps for breaking that set into one or two (or three?) straight averages or even time-dependent linear fits (656-696 increase approximately monotonically, while subsequent blanks tend to decrease approximately linearly, particularly from 715 onward). With fully propagated uncertainties in resulting fitting parameters or averages, I think it would be informative regarding any assessment of detection limits for given samples, given the low concentrations. 

This leads to my second concern – the authors claim that all 14C analyses are above detection limits without specifying how that detection limit is assessed. Typically, the detection limit reflects some multiple of a conservative measure of uncertainty in the blank measurements. Given that many of the core samples have concentrations nearer to the asserted detection limit of the Tulane system than are typically analyzed at that lab, it is important to present how that limit is evaluated – probably best accomplished with blank measurements from the periods of sample analyses. With the observed variations in the blanks noted above, perhaps the detection limit is also time dependent, which would be fine in my view, but that should be clarified in the text and accommodated in their analysis. Based on the data in supplement S5, I agree with the authors’ assertion that many, if not most, of the core analyses’ uncorrected 14C atom inventories are above coeval background levels, but several are also comparable to the coeval backgrounds, depending on how the detection limit is evaluated. A more rigorous assessment of detection limits here would thus be useful for putting the dataset on firmer ground. 

Third, I’m concerned about the reproducibility of the 14C data from both surface and core samples, particularly the latter. It would be useful to see if updated blank corrections as suggested above have any influence on the reproducibility of at least the core samples – I would expect less effect from the blank corrections for the surface samples. It’s not clear from the data in S5 if any of the surface sample analyses are replicates (it doesn’t appear so), but the authors state that multiple quartz aliquots were analyzed for nearly all samples – if that only applies to the core samples then that should be clarified. While it’s true that some (or even all) of the scatter in the surface results could be due to variability of time-integrated shielding by ice fields, etc., on the landscape, I think it would still be worth considering other potential procedural sources of scatter, particularly for the low-level core samples. For example, were analyses of higher-concentration surface samples (either from this study or from other studies) interspersed with analyses of the core samples, thus perhaps leading to some low-level sample memory in the extraction system that might have affected some of the core results? Gaps in the TUCNL numbering in supplement S5 raise that question.

Along these same lines, and for the additional reasons below, I think it is vital to present in situ 14C results for the CRONUS-A intercomparison material from the time frames of the sample analyses – TUCNL 465-490 and TUCNL 663-780. Although the concentrations from this material are several times higher than those in the samples measured as part of this study, it would be instructive to demonstrate reproducibility in the extractions at that level at least. An evaluation of reproducibility using surface replicates and CRONUS-A analyses for 10Be and 26Al is already included with the supplemental dataset, so it seems reasonable to include a similar evaluation for 14C analyses for data comparison between the nuclides, particularly since replicate analyses are available for many of the core samples. Analyses of other available intercomparison materials with lower concentrations would also be useful, if those data are in hand.

The CRONUS-A 14C data would also be useful for assessing the modified extraction procedures cited in the supplement S2 text. The procedures cited here differ substantially from those cited in Goehring et al. (2019) – half the 500°C combustion dwell time and 2/3 of the dwell time at 1100°C of Goehring et al. (2019). It appears from scanning subsequent publications from the Tulane group that the changes in duration at each temperature step were made at different times after Goehring et al. (2019). Given that each of these changes has the potential to affect the final measured in situ 14C concentrations, I think that it’s very important to present comparisons of CRONUS-A replicates from before and after each of these procedural modifications (whenever they occurred), to demonstrate that no significant shift in measured CRONUS-A concentrations was observed in either case. As noted above, additional CRONUS-A analyses during this study’s time frame would also help the reader evaluate possible magnitudes of procedural and perhaps other contributions to the scatter (e.g., Balco et al., 2019, American Journal of Science, 319(4), 255–286).

Furthermore, the authors state that they calibrated the spallogenic in situ 14C production rate using CRONUS-A measurements. From the references cited, it appears that those measurements are the ones presented in Goehring et al. (2019). It would be helpful to state that here if that is the case. Goehring et al. (2019) note that the mean of those measurements is ca. 10% below that of the consensus value of Jull et al. (2015). Deriving production rates from the Goehring et al. (2019) CRONUS-A measurements on the same extraction system used here should in principle yield an internally consistent basis for calculating exposure histories for in situ 14C, since any systematic offset should affect both similarly. However, comparison of those original values to more recent CRONUS-A measurements at Tulane using the modified procedures during the measurement intervals for this study would allow for a more quantitative assessment of potential systematic impacts on measured concentrations and/or exposure ages.

Finally, I note that while 10Be in the cores does tend to decrease with depth in each, as stated by the authors, I’d like to see some mention that in two of the cores (H4 and H5) the profile deviates from an exponential (at least the preferred ones in green in Fig 7) on the high side below about 50 cm. The 10Be profile shapes in those two cores actually appear more similar to the 14C profiles in those cores than to the fitted 10Be exponentials; the steeper 14C profiles presumably reflecting their greater proportion of muogenic production. I would like to hear the authors’ thoughts on assessing the source of the deviations.

All that said, my impression is that the main conclusions of this manuscript are probably reasonably robust, and that they would largely still stand once these comments are addressed, although key details and inferences may change. As such I think this will ultimately be an important contribution to our knowledge of West Antarctic Ice Sheet behavior.

Minor comments

P. 6, Line 4: The currently accepted half-life for 14C is 5700 ± 30 yr (www.nndc.bnl.gov) – see Hippe and Lifton (2014)

P. 12, Line 6:  In the flux-based extraction of in situ 14C, the quartz does not melt, but rather dissolves in the flux. One could also replace “melting the quartz” with “fusing the quartz in a lithium metaborate flux”

P. 14, Line 9:  Suggest that “rejected” would be better than “falsified” – the latter sounds like the results were made up.

P. 16, Line 16: “calculation” is misspelled

P. 17, Lines 7-12:       As noted above I’m not convinced the 14C measurement uncertainties are correctly characterized.