Summary: This paper is very much of value because the relatively newly available method of subglacial bedrock exposure dating is really the only available means of obtaining data on what the Antarctic ice sheets looked like during past periods of warm climate when they were smaller. As we live in a warm period, understanding how and when ice sheets become smaller than they are now is, obviously, of critical importance for sea-level prediction. This paper is an important contribution in this area. Its main conclusion, that cosmogenic carbon-14 measurements on subglacial bedrock require a period of thinner ice in the middle Holocene, appears to be correct as far as I can tell. Overall this is a very good paper. However, the paper needs some attention in several technical areas having to do with the C-14 and luminescence measurements before I think it'll be suitable for publication. 

I'm checking 'major revision' because I think publication requires (i) review by a luminescence specialist, and (ii) expanded reporting of process blank data for the C-14 measurements. See below for details. 

Details: 

The main conclusion of this paper is that the C-14 measurements on subglacial bedrock require a period of thinner ice in the mid-Holocene. As this is consistent with other indirect geological evidence that somewhere between permits and suggests a Holocene lowstand (really we probably shouldn't use 'lowstand' for this because of the confusion with sea level...maybe 'thinstand'?), this conclusion isn't unexpected, but it's extremely valuable to be able to show this with direct evidence and put some limits on the extent and timing. Starting from the reported blank-corrected C-14 concentrations, I repeated the ice-thickness-history fitting calculations with a similar random search optimization code and came to a similar conclusion as the authors, so, given the assumption that the reported C-14 concentrations are accurate, I agree with their conclusions. 

There are some technical areas of the paper that need attention, as follows. 

1. Luminescence measurements. Although I am not a specialist in luminescence measurements, I'm reasonably knowledgeable on the subject and I see several parts of this section of the paper that either don't make sense or seem incorrect. It should be noted, of course, that the luminescence data aren't involved in the main conclusion of the paper that there was a mid-Holocene thin period -- this conclusion rests completely on the C-14 data, so any issues with the luminescence measurements don't affect this main result. However, there seem to be some issues here. 

First, the protocol used appears to be intended for quartz and is not, I think, able to  differentiate between quartz and non-quartz signals. Thus, the later discussion that makes it appear likely that a lot of the signal is actually from feldspar would seem to have the implication that a lot of these results are pretty hard to interpret. Was a quartz protocol used simply because the rock is basically a quartzite in hand specimen scale, and it was not envisioned that significant feldspar would be present? 

Second, again, I am not really a specialist in this, but to me Figure 5 shows essentially no evidence of an exposure profile/bleaching front. I imagine this is a fairly clean quartzite, and the photos show a fairly light color, so it's probably a relatively translucent rock as rocks go, so I think we would expect a bleaching front > 1 cm deep, even for only a few years of exposure, no? The suggestion that there is a bleaching front present in the upper 3.5 mm therefore seems unlikely. Frankly, it would seem more feasible (or, I guess, less unfeasible) to argue that if there is a bleaching front, it is > 1 cm in thickness and manifested by the approximately linear increase in apparent age with depth (of course, that still leads to an impossible LGM apparent age). Note: there is some discussion of opacity in the paper and supplement, but there does not appear to be an actual measurement of the opacity that could be, e.g., compared with other rock types. 

Third, the measured fading rate is extremely high, which would tend to indicate that we are looking at a saturation profile. Furthermore, the statement in line 243 that fading will result in a higher apparent burial age appears to be backwards -- fading should yield a younger apparent burial age, no? 

In any case, I should point out again that I am not a luminescence specialist, but many parts of this discussion seemed incompletly thought out. It seems to me that really the only conclusion that you can get from the luminescence data is that it's not possible to reject the null hypothesis that both profiles are just saturated. This is basically the conclusion that the authors get to in the end -- the luminescence data provide no evidence for a completely ice-free surface in the Holocene -- but this section appears weak to me. I don't want to be discouraging of including these data: obviously we are all very new at collecting luminescence data from subglacial bedrock surfaces and I think it's extremely important to report all the available results, even if confusing, for the benefit of future work. However, I strongly suggest review of this section by a specialist in this field. 

2. C-14 measurement. Basically, the review process for the Balco et al. 2023 paper that is obviously very familiar to these authors included a painfully long correspondence about exactly how to deal with analytical blank corrections for C-14 measurements, that eventually led to a large amount of reporting of process blank data for the Tulane C-14 laboratory where the measurements were made. The present authors have clearly absorbed some of this review correspondence (e.g., Figure 6), which is good. However, the authors have not provided the full set of process blank measurements as were eventually included in the Balco paper, which leaves the reader wondering a lot about the blue curve in Figure 6. Although the sense is that this value, which is described as a 'global' or 'long-term' blank, is probably a digest of multiple process blanks measured in the UoW lab, these constituent blanks aren't reported and there's no info about what the 'global' value actually is (mean and SD? Weighed mean?). Just as in the Balco paper, really the whole point of this paper hinges on whether C-14 has been detected above background and how you correct for that background. More importantly, the credibility of all our efforts at subglacial bedrock exposure dating using C-14 completely relies on this being right. False-positive detections of ice thinning using C-14 measurements would be extremely damaging to not only the credibility of the method itself, but also the credibility of the entire enterprise of ice-sheet and sea-level change studies. We can't have false positives. 

Thus, the point of all this is that, just as in the other paper, we need to see all the process blank data before I think this is acceptable for publication. This will allow readers to see whether it's appropriate to use the proposed long-term blank or something more complicated than a normal distribution. The needed data here include the UoW lab and AMS data on all the process blanks that were used to assemble the 'global' value cited here, the dates they were run, and the dates that the samples were measured. 

3. Optimization calculations. This is technical, and as noted above doesn't affect the overall conclusion, but I think the discussion of model fitting needs some attention. First, we see (line 295) that we are discussing the best 5% of the random search models by RMSE, but we don't get any information about whether they actually fit in the sense of whether the actual value of the RMSE has a low rejection probability. As it happens, having redone the calculations, I know that it is possible to find lots of thinning histories that do have acceptable RMSE by the usual criteria (that is, they're close to 1), which is what you would expect from the fact that the fact that the downcore measurements basically overlap at quoted uncertainties. Specifically, what I found here is that for BH03 there are lots of histories that can't be rejected at 95% confidence, but for BH03 there aren't very many - there are lots at 98% but few at 95%. But for both cores you can find thinning histories that "fit" in a chi-squared/RMSE type sense. However, there's no information in this section of the paper about what the relationship is between the top 5% by RMSE and the ones that actually fit based on a RMSE rejection criterion. Are the 5% a small subset of the ones that fit the data (probably true for BH02)? Or are there histories in the 5% that don't fit the data (probably true for BH03)? I strongly suggest revising this discussion to focus on the histories that fit the data based on a statistical criterion and not just on the top 5%. [Note: this wasn't done in the Balco et al. paper because you can't fit the Be-10 data at high confidence -- there is a systematic misfit at the core bottoms that probably has to do with processes not included in the model -- but that issue doesn't apply here because there are no Be-10 data.] Adjusting this discussion won't have a significant impact on any of the conclusions, but it'll be a lot clearer as regards whether the models actually fit the data. In fact, as noted, they do fit the data according to usual metrics, but you can't tell that from this discussion.  

4. I think the statement in line 321-ish that the fitting calculations slightly favor the thinner ice/longer time models has a good chance of just being a random consequence of measurement uncertainty. Basically what that is saying is that the optimizer favors models that have a larger downcore decrease in concentration (because exposure happened closer to the surface) over models that have a smaller downcore decrease in concentration (because exposure happened deeper). What I found in redoing the calculations (with a piecewise-linear thickness change history as in Balco et al., not a piecewise-constant history as used in this paper) is that this effect is only present for BH03. This basically agrees with Fig. 6 in the present paper. I think this has a good chance of just being random, because the top 3 concentration measurements in BH03, although they are consistent with a surface spallation profile within their uncertainties, randomly happen to decrease faster than possible with a spallation profile. The optimizer is trying to fit this, even though it can't because the model can't get any steeper than a spallation profile, by making the ice thickness as thin as possible. Regardless, random or not, this effect does appear to be present in BH03. On the other hand, it's not present for BH02 -- the BH02 data do not favor the thinner/shorter solutions (or the opposite).  So, this conclusion isn't super well supported. This is not to say that it isn't true that the lowstand ice thickness was on the thin side, just  that it's tough to really prove it conclusively with these data. In the Balco et al. paper much of the leverage on this comes from the more precisely measured Be-10 data, and, of course, there are more C-14 data, so there is a bit more constraint on the slope. 

Anyway, the conclusion, that the thin/short solutions might be favored, correctly isn't really strongly emphasized in the section of the text near line 321, so I think that part is fine. However, this needs some clarification in line 335-ish -- I am not sure what 'total exposure' means, but it would appear that the luminescence data preclude the rock surface actually being totally ice-free, so 'total' is misleading. It seems like really the most simple and specific way to state the constraint is that thinning has to be more than about 25 meters, period. And, also, it is worth noting that you could have more thinning -- you could easily have a situation, as is common now, where the rock surface is covered with permanent snow or thin ice (look at the big wind tail on Plummer Nunatak) but the outcrop as a whole is well above the regional ice surface. 

5. There's a lot of 'while we cannot exclude' and 'while being mindful that...' towards the end of the paper, which is fine, and correct because at a site like this the real relationship between dynamic thinning, blue-ice ablation, and the ice thickness is mostly unknown, but really the important point here is not that the data in this paper are ambiguous with respect to grounding line position, but instead that this type of data can only ever be collected in certain places where there is rock to drill into. We can't ever go to the exactly perfect place that has the perfectly unambiguous relation to grounding line position, because that (probably) doesn't exist. So I would be clear, as the authors have, that nothing is perfectly unambiguous because nothing is in exactly the right place, but also point out that this is something that needs to be figured out! If we are serious about understanding sea level impacts of ice sheet change during past warm periods, glaciologists have to get to work on making the relationship between this type of data and grounding line positions less ambiguous. So it's fine to have all the caveats in the conclusions of this paper, but it is not good to give the sense that the authors are apologizing for the fact that they collected data from the best possible place closest to the grounding line that actually exists. Don't apologize! I would also point out that there is also an important challenge here -- the sites where we can collect this type of data are imposed by geology/topography, but we need to be able to quantitatively use this type of data, and even though that's not in scope for this paper, people need to get to work on figuring this out. 

Minor items:

What is a 'sub-aerial controlled moraine' (line 385)? 

The paper entitled, “A thinner-than-present West Antarctic Ice Sheet in the southern Weddell Sea Embayment during the Holocene” by Small and colleagues presents new cosmogenic nuclide inventories from subglacial bedrock cores that elucidates Holocene ice sheet history in the Weddell Sea Sector. This work is very timely as grounding line retreat and re-advance in the Holocene has been found in both Amundsen (Balco et al., 2023; Nichols et al., 2024) and Ross (Venturelli et al., 2020, 2023;  Kingslake et al., 2018) sectors of West Antarctica. Thus, the results presented in this paper are important because they prove the hypothesis of retreat and re-advance in the Weddell Sector originally posed by  Bradley et al (2015) and demonstrates that this phenomenon occurred in every sector of West Antarctica. As a result, I believe this paper should be published with very minor revisions and I provide some minor comments and questions below that I hope will help to clarify what is already a very excellent contribution to the literature.

1. The feat of drilling and recovering 4 subglacial cores is really impressive. I found this to be a bit underplayed in the manuscript and suggest including a bit of context to highlight (a) how impressive/important this is and (b) how targeting blue-ice areas might be advantageous in future subglacial drilling areas given the results and successes herein. It could also be useful to add some context about the conditions at the ice-bed interface, given past challenges with sediment-laden basal ice in non-blue-ice-areas described in Braddock et al. (2025).

2. I realize that some of this information is in the supplement, but can you provide a bit more information about quartz preparation for in situ ¹⁴C samples? With the work of Nichols & Goehring (2019) showing that quartz isolation/preparation methods may impact the validity of the in situ ¹⁴C result, adding some specific details about how long successive leaches were carried out, if any other separation techniques were used (e.g., frothing or magnetic separation), etc. would be useful for the interpretation of these results into the future.

3. In addition to quartz preparation: I do have some specific questions about the in situ ¹⁴C data:

• Can you provide some more information about the long-term blank value and how that is derived? With the methods paper being cited coming from ~6 years ago, I do think more information is needed here. Specifically, I would like to see the values of individual blanks analyzed during the measurement window of the core samples presented herein. This would help to not only understand the long-term blank value, but also blank variability during the measurement of these samples.
• I am curious about the very low CRONUS-A concentration (5.85 x 10⁵¹⁴C atoms g⁻¹) presented in the supplement. The consensus value for CRONUS-A is 6.93 ± 0.44 ×10⁵¹⁴C atoms g⁻¹ (Jull et al., 2015), which has been maintained in the literature as new laboratories come online (Lupker et al., 2019; Fulop et al., 2019; Lamp et al., 2019; Lifton et al., 2023; with the exception of similarly low values from Goehring et al (2019)). The authors state that an in vacuo cleaning step at 600°C was used to remove meteoric ¹⁴C—how long was this step carried out? Lifton et al (2023) showed that holding a sample at 600°C for >1 hr has the potential to remove higher temperature/in situ ¹⁴C, so it is possible that this step is removing some of the in situ component here too.These methodological details are important as they have implications for the interpretation of ice history from the core samples, because concentrations presented might not reflect the full period of exposure, but rather a concentration accumulated during exposure minus the removal during the 600°C step. If this explanation can not be used to justify why the CRONUS-A value is so much lower than the consensus value, I do think some justification and details on the value presented are needed (How many measurements of CA were done? Was there any variability? Why doesn’t the value presented here match previous values from this lab (e.g., Fulop et al., 2019).
• The slightly higher value at depth in BH02 and BH03 is a pretty cool observation, and it’s interesting that the increase in concentration occurs at different depths. I think this is a bit overlooked in the text, and some context about how much muogenic production would be needed to produce the concentrations observed would be of value to the in situ ¹⁴C community.

4. The authors invoke dynamic thinning to explain that grounding line retreat would be expected alongside the magnitude of thinning observed from this work. This argument could really be strengthened by the addition of some simple calculations to demonstrate the likely magnitude of grounding line retreat associated with the thinning observed at the site. Such a constraint would be a valuable addition for constraining ice sheet models, and provide constraints on future sub-ice drilling efforts for grounding line retreat signals (e.g., Venturelli et al., 2020). 

Again, I believe this paper is a valuable contribution to the literature and the suggestions and requests above should be viewed only as minor suggestions. I really enjoyed reading the submitted manuscript, and I commend the authors on the excellent work presented herein.