Review of King et al.: Ice core nitrogen isotopes archive dramatic changes in West Antarctic Ice Sheet thinning

King et al present new nitrogen and argon isotope data from the Skytrain Ice Rise (SIR) ice core, centered around a 8 ka warming event observed in the water stable isotope ratios. That warming event was the topic of an earlier study (Grieman et al., 2024), that argued that it represents a rapid ice thinning event, followed by a retreat of the Ronne ice shelf margin. The nitrogen (d15N)) and argon (d40Ar) isotope data provide an opportunity to investigate the firn evolution during this time period, and to further test the hypothesis of rapid ice thinning.

Abrupt deglacial changes in d15N are seen in most (all?) coastal cores where such data are available (Siple Dome, Berkner Island, Roosevelt Island, arguably James Ross Island, and now SIR). Understanding the drivers of such behaviors is indeed an important objective. The authors argue that the signal represents an episode of ice sheet thinning, that drives horizontal ice flow divergence thereby compacting the firn vertically. From what I understand (though this is not made explicit), they do this via the continuity equation only (Divergence in v being zero), and do not consider more non-linear effect such as strain softening.

Overall the study is interesting and mostly easy to follow. In balance, the analysis they provide is somewhat unsatisfactory. It does not thoroughly assess all possible scenarios, and the solution that is chosen is not assessed in enough detail to allow us to really learn something new. Their solution is also unable to fit the 15N excess data that they present. I would recommend publication of the paper after the authors have addressed the concerns listed below.

First, I think their section “Comparison to other ice core records” (line 313) is rather inadequate. As mentioned earlier, multiple coastal cores in prior studies (Siple Dome, Berkner Island, Roosevelt Island, arguably James Ross Island) show abrupt d15N signals. This literature is not well incorporated. These studies should be mentioned in the introduction, perhaps as part of the motivation of the study. It is notable that prior authors have opted for different mechanisms to explain their d15N signals, and so these alternative mechanisms should be discussed, compared, and explored for SIR.  

At Siple Dome, Severinghaus et al. (2003) identify two abrupt d15N changes. The one 21 ka resembles the one at SIR in that there is an abrupt warming event in the water isotope ratios, as confirmed with 15N excess. The one at 15 ka (mentioned by the authors) was explained as a possible ablation event that removed part of the firn-notably, it has a similar 15N excess signal as seen by the authors.

At Roosevelt Island, Lee et al. (2020) explain the abrupt d15N signal as an accumulation change. Those authors explicitly note that some aspects of their data cannot be explained via thinning (Page 1703, Left column, item 2). At a coastal/margin location like SIR I have no expectation that accumulation should follow temperature on shorter timescales, see for example (Fudge et al., 2016; van Ommen et al., 2004). So the authors could be more creative in exploring accumulation changes.

Capron et al. (2013) do not really address the abrupt d15N variations at Berkner and JRI, but there is quite some overlap between the authors of that paper and the present one,

Strongly negative 15N excess was more recently explained via a rectifier effect at South Pole (Morgan et al., 2022). Since it is also seen (even more strongly) at SIR, could a rectifier be part of the solution? The SP rectifier is maintained by wintertime firn cracking. An interval of strong horizontal divergence could also drive firn cracking, which could both explain the low d15N and very negative 15N excess (via rectifier). In retrospect, could that explain the Siple Dome data also?

The above, prior work on deglacial d15N anomalies and 15N excess, suggests other mechanisms that should be discussed and compared. At the very least accumulation anomalies (that do NOT scale with d18O), ablation, and deep cracking should be considered more seriously as alternative explanations. Though I suspect that only deep cracking can explain *both* the d15N and the strong thermal signal (via a rectifier) – unfortunately purely in a qualitative way. Of course multiple methods could contribute.

Second, with d15N, the gas age-ice age difference is an equally important constraint on firn dynamics. It would particularly be helpful in constraining the T and Acc changes proposed (before and after the event). The authors do not really address the Delta-age or its importance. What is the modern-day Delta-age, and are you able to empirically assess the Delta-age back in time? For example, by combining volcanic and CH4 ties (e.g., the 8.2 ka event) it could be calculated. Alternatively, by comparing the abrupt signals in the ice (d18Oice) and gas (d15, TAC) phases it can be estimated.

The Delta-age is also the characteristic timescale of the firn response. Comparing Delta-age to the duration of the various anomalies is probably very insightful in my view.

 Third, I think the authors should provide more details on the thinning scenario, and how realistic it is. The horizontal divergence is based on a model simulation, but we are not shown many details:

• Can you plot the details of the model run? How much thinning is simulated?
• How does the horizontal divergence translate to vertical compression / strain rates? Are you just using the continuity equation? Are you assuming divergence in one direction? Or is this the sum of the x and y components?
• How does the divergence vary with depth in the model? Are we looking at surface values, or does this change with depth? I think that question is important when thinking about vertical strain in the entire ice column.
• What is the total strain when integrating over the strain rate, and what does this number represent?

The authors suggest that the PISM-based strain-rate forced model run is “only a guide”, but it needs to be realistic if we want to draw any meaningful conclusions (such as, for example, whether or not strain softening is needed to explain the observations). Naively, integrating the strain rate should give the total strain/deformation. The proposed strain rate integrates to around -2, which means that there is no ice left! (is that interpretation correct?!) So it seems to me that the rates may be overestimated quite a bit. Again, knowing this is key to assessing whether the proposed mechanism can actually work.

Can you give more details on how the strain rates are implemented in the CFM? I imagine there is a negative feedback at play, than when you thin the firn via horizontal divergence it reduces the overburden pressure experienced by the deeper layers, and reduces the densification rates (which then counteracts the flow thinning). Do you observe this?

Last, this may be a detail, but I am puzzled by the fact that the temperature change comes earlier, and is of shorter duration, than the proposed thinning. In my mind the thinning and elevation change (and related lapse-rate warming) are linked. You cannot have one without the other. So how do you envision these two processes to be de-coupled in time like that?

I have a few shorter comments as well for the authors to consider:

Order of figures: I think it makes more sense for figure 3 (data) to come before figure 2 (model runs). Just a suggestion.

The reader needs more details on the CFM. What is the depth domain, spatial resolution, and time step? What is the geothermal heat used in the firn modeling? Surface density? How do you determine the lock-in depth?

The warming appears to precede thinning by ~200 years in the optimal scenario. How does that work conceptually?

Be clear throughout whether you plot things on the gas age or ice age. Particularly for the interpretation of TAC this is important.

Should you consider strain heating in the case of such extreme strain rates?

I am curious about the fact that TAC overshoots, and then undershoots. Could this be some transient effect of speeding up, and then slowing down, bubble trapping?

Line-by-line:

Line 43, 74:  “just 200 years”: the TAC anomalies show an adjustment time of closer to 2000 years (Fig. 1C, authors’ markings), while sodium stabilizes ~1k after onset of event. Would this not suggest that the regional readjustment is much longer than 200 years?

Line 79: “first time”: What about Siple Dome, wouldn’t that one be first?

Line 99-100: aren’t most of our cores frozen to the bed? In all cores thinning is proportional to its depth. Is the thinning profile unusual in any way? If not, please remove this sentence.

Line 114: d15N is not defined as the 15N/14N ratio, but as the 15N/14N ratio relative to its standard (here: the atmosphere)

Line 145-146: I don’t understand this argument. What does the 1-sigma uncertainty represent here? From the text, it appears that this is the dual inlet standard deviation when comparing over many sample-standard cycles. Once the air is extracted from the sample, the variations on the spatial scale become irrelevant. Or is this the std dev of replicate samples? Please clarify. If it’s the former, it would imply the IRMS is not running optimally, if it’s the latter it makes more sense.

Line 147: The better reference here is Severinghaus 2003, who developed the method, or Morgan 2022 who perfected it. Kobashi and Orsi also did quite some work on this.

Line 168: Do you mean Supplement figure 1 here? Can you explain what the implication is of the observation you refer to?

Line 184: This is a complicated sentence, can you rewrite?

Line 187: Is uniform strain the same as the Nye model? What would your thinning function look like - does this imply a linearly thinning function (1 and surface, 0 at bottom?).  

Line 189-190: what borehole model? This has not been introduced. Can you not just use the Lliboutry strain rates in your firn model? That seems straightforward, no?

Line 199: please give a reference or justification for the 0.8 permil/K. The number is fine of course, just good practice.

Line 201: this is a very low sensitivity, just Clausius-Clapeyron is more like 7%. The estimates from (Nicola et al., 2023) are nowhere near that low at SIR – to say that they are at the lower bound is a misrepresentation of that study I think (the low values in Nicola are all along the Siple coast. For example, the high-res RACMO estimate in the Nicola study is more like 10% at SIR. Did you explore higher values?

Line 214: Is there a plot somewhere of this modeled thinning history? The timing, duration, elevation drop, strain rates and there depth dependence, etc?

Line 216: underconstrained (one word, or add hyphen)

Line 220: I cannot really understand what this means, and what the generic cosine is: “The parameter is tuned to the time-resolution and length of the input data such that the spline produced is at half height of a generic cosine function, which is a good balance point between preserving signals in the record while not being overly influenced by record variability”.

Line 225: In the results section, I would expect to see the data first, so I know what the models are trying to fit. Can you swap figures 2 and 3? Can you also add subsection numbering (3.1, 3.2 etc.?)

Line 225: in all the modeling, how do you conceptualize the changes to the deposition site? Do assume you maintain the local isolated dome and deposition site, or did it get overrun and does some of the ice originate upstream? So for example, in the warming scenario, is the dome thinning throughout and is the lapse rate giving you  the warming? Or is the deposition site moving downstream, giving you the warming?

Line 239: what is the duration of the signals? It appears to be around 300 years, or one Delta-age? Compare this to the duration of the d15N signal (1000 years) or the TAC signal (1500 years).

Line 240: I would remove the “all else being equal”. You’re using rather ad hoc assumptions. I would rewrite: This suggests that under our assumptions of what the d18O increase represents, we would…..

Line 243: I think this divergence reconstruction needs to be explained better, e.g. in the supplement with a figure. I don’t fully understand what was done, and how realistic the imposed forcing is.

Line 249: Are the data in Fig. 3 plotted on gas age or ice age?

Line 281: ‘strain is larger in upper layers’ – since you’re basing this on existing ice flow models, can’t you test this easily? Do you mean strain *rates*?

Line 282: If you integrate the applied divergence (red) over the duration of the signal, what do you get? My back-of-the-envelope gives -4E-3 (peak) multiplied by 500 years (duration at half peak), or around -2. To me that seems unphysical, as it would imply there is less than no ice left? I would expect a number between 0 (no thinning) and -1 (fully thinned), but perhaps my understanding is naïve? Please explain.

In this regard, the depth-dependence is actually very critical. If this rate is constant over the full ice column, does one get a realistic result? Or if it needs to decline with depth, by how much? The duration of the strain rate pulse relative to Delta-age is also key here.

Line 293: what is this “observed rise in site T” based on? Water isotopes? Water isotopes are complex, and the shift can also reflect a change in circulation, accumulation, etc. I would call it a “likely rise”, or something similar. Warming is the most likely explanation, but not the only one.

294: Should this be supplementary Fig 3 or 4 perhaps? Not 2. Based on the geothermal flux, what DT and 15N-excess would you expect?

Line 308: check supplementary figure number

Line 312: another potential driver of the 15N-excess is a seasonal rectifier, as explored by Morgan et al. (2022). Could that be at play here? Vertical cracking would contribute to such rectification, which may be induced by horizontal divergence.

Line 313: this section is incomplete and misses other coastal core d15N (Berkner, RICE), and incompletely discusses Siple Dome. This should give a more thorough discussion of existing literature and ideas.

Line 319: there are multiple things going on at Siple Dome. The authors refer to a situation around 15 ka where there is suspected abrupt deep cracking/ablation in the firn, causing gravitational enrichment to go to zero. However, the more relevant comparison to Siple Dome, in my view, occurs around 21 ka (725 m), where there is an abrupt thinning and warming event (as evidenced by 15N excess). This 21 ka event is a much closer analogue to what is discussed here. That event is commonly interpreted as a rapid thinning of the ice sheet. The data are in Severinghaus et al. (2003). The Siple 21 ka event has a 15N excess signal consistent with surface warming. The Siple 15 ka event actually has the 15N excess signal that is similar to SIR. Please discuss.

Roosevelt Island likely has abrupt d15N signals during the deglaciation, that are interpreted as accumulation changes. That should be referenced in this section too (Lee et al., 2020).

Berkner Island also has abrupt changes during the deglaciation (Capron et al., 2013), with one event that is close in timing to the 8ka event discussed here.

Line 334: The disadvantage of selecting time periods further apart is that insolation starts to impact TAC potentially. Thoughts?

Line 337: *relatively* well constrained at best, in my view. Why/how does temperature change TAC?

Line 353: I think more nuance is needed here. Eicher hypothesized that the acc increase was responsible, but ultimately it is unclear whether it is the Acc increase, the T increase, or the temperature gradient across the firn driving anomalous grain metamorphosis or vapor movement. During DO events a lot of things change all at once.

Line 362: Do you mean physical properties analyses? Or grain-size analyses?

Line 366: the more cynical part of me would say that both proxies together are not very insightful either, unfortunately, given the complexities of TAC!

Figure 1: Throughout you use SIR, this figure uses ST as the acronym. Can you make this consistent by updating the figure labels? In panel B, do you have a vertical scalebar?

Figure 2: why plot the horizontal divergence – isn’t it the vertical strain rate that we care about? Is this the divergence at the surface, or at depth?

Figure 3. I like the temperature scaling that is in Supplemental Fig 2. Why not just use that figure as the bottom panel of Fig 3?

Figure 4. Why do you place the onset of the divergence several centuries after the increase in temperature? If I understand the concept, isn’t it the divergence that drives the temperature, so shouldn’t it lead? I understand that this is better for the model fit, but it makes less sense conceptually.

Figure 5: Please specify what timescale you use for Siple Dome. There have been many, and some of the older ones are somewhat outdated. The most recent one is probably from (Seltzer et al., 2017) – but there may be more recent ones. Also consider the 21 ka event, that may be more similar in dynamics to what you’re trying to argue for here.

Supplement 1D borehole model: This is fine in the supplement, but it needs to be referenced better in the main text.

Supplementary Fig 4, upper: why is there a constant offset? Does the CFM not include a geothermal heat flux?

Capron, E., Landais, A., Buiron, D., Cauquoin, A., Chappellaz, J., Debret, M., et al. (2013). Glacial–interglacial dynamics of Antarctic firn columns: comparison between simulations and ice core air-δ15N measurements. Clim. Past, 9(3), 983-999. http://www.clim-past.net/9/983/2013/

Fudge, T. J., Markle, B. R., Cuffey, K. M., Buizert, C., Taylor, K. C., Steig, E. J., et al. (2016). Variable relationship between accumulation and temperature in West Antarctica for the past 31,000 years. Geophysical Research Letters, 43(8), 2016GL068356. http://dx.doi.org/10.1002/2016GL068356

Grieman, M. M., Nehrbass-Ahles, C., Hoffmann, H. M., Bauska, T. K., King, A. C. F., Mulvaney, R., et al. (2024). Abrupt Holocene ice loss due to thinning and ungrounding in the Weddell Sea Embayment. Nature Geoscience. https://doi.org/10.1038/s41561-024-01375-8

Lee, J. E., Brook, E. J., Bertler, N. A. N., Buizert, C., Baisden, T., Blunier, T., et al. (2020). An 83,000-year-old ice core from Roosevelt Island, Ross Sea, Antarctica.Clim. Past, 16(5), 1691-1713. https://cp.copernicus.org/articles/16/1691/2020/

Morgan, J. D., Buizert, C., Fudge, T. J., Kawamura, K., Severinghaus, J. P., & Trudinger, C. M. (2022). Gas isotope thermometry in the South Pole and Dome Fuji ice cores provides evidence for seasonal rectification of ice core gas records. The Cryosphere, 16(7), 2947-2966. https://tc.copernicus.org/articles/16/2947/2022/

Nicola, L., Notz, D., & Winkelmann, R. (2023). Revisiting temperature sensitivity: how does Antarctic precipitation change with temperature? The Cryosphere, 17(7), 2563-2583. https://tc.copernicus.org/articles/17/2563/2023/

Seltzer, A. M., Buizert, C., Baggenstos, D., Brook, E. J., Ahn, J., Yang, J. W., & Severinghaus, J. P. (2017). Does δ18O of O2 record meridional shifts in tropical rainfall? Clim. Past, 13(10), 1323-1338. https://www.clim-past.net/13/1323/2017/

van Ommen, T. D., Morgan, V., & Curran, M. A. J. (2004). Deglacial and Holocene changes in accumulation at Law Dome, East Antarctica. Annals of Glaciology, 39(1), 359-365.

The paper by King et al. reports new measurements of δ¹⁵N of N₂, δO₂/N₂, and δ⁴⁰Ar performed on the gas phase of the Skytrain Ice Core (SIR) over a well-defined interval characterized by a complex and still unexplained oscillation in the previously published Total Air Content (TAC) profile by Grieman et al. (2024). This TAC fluctuation occurs just after the large decrease in elevation (about 450 m) inferred from the δ¹⁸O record during the early Holocene.

The study aims to improve our understanding of the anomalous TAC profile in terms of changes in firn properties during this rapid ice loss, by analyzing the nitrogen isotopic profile in combination with a firn densification model. The authors interpret the observed isotopic and TAC profiles in the context of ice dynamics at the Skytrain Ice Rise, following elevation changes and thinning that preceded the ice-shelf breakup indicated by the Na record.

The paper is original and innovative in that it uses the nitrogen isotopic profile to constrain ice-dynamic changes in ice-sheet models.

I found the paper generally easy to read, although some sections could be clarified further (see comments below) to make it more accessible to the broader Climate of the Past audience. I recommend publication after the authors have addressed the following comments.Line 79: please, change climate record into paleoclimate record.

Line 81: These situations are not limited to the West Antarctic Ice Sheet. Perhaps the authors could add a sentence about other coastal regions of East Antarctica (e.g. Wilkes Sub Glacial Basin).

Line 85: change into Fig. 1c

Line 111: what do you mean by modest accumulation rate?

Line 120: “ ….. the disrupted TAC gas archive…”: This is something that is further elaborated but how you can exclude that the mechanisms behind are not also affecting the d15N record?

Line 134: Is the -25°C enough cold for avoiding gas loss fractionation effects? I suppose that this can be checked with the dO2/N2 record…..

Lines 145-146: It is not clear why the uncertainties for the SIR samples are so much larger than usual. How are the uncertainties calculated and to what are referred? Which are the implications for your interpretation? How much is the uncertainty of the calculated N excess values? Are these uncertainties considered in the figures?

Line 168: This should be Supplement Figure 1.

Lines 198-205: If I understood well the accumulation is derived from the isotopic profile but there are several processes that could change the snow accumulation rate and not only temperatures particularly at centennial scale. May you comment on this.

Line 215: “his” should be “this”.

Lines 217-223: are these smoothing splines considering also the 0.14 per mil uncertainty in d15N measurements? This uncertainty seems quite a lot considering the observed variability …. At least looking at the records reported in the figures.

Line 238: see comment above: you are looking at a change of 0.04 per mil….. quite small compared to the uncertainty.

Line 251:  “ …. 500 years after the initiation of ice mass changes….” as suggests by the d18O record. I would add.

Line 257: “Predicted values … “ not shown or reported in figure S3?

Line 262-263: which are the implications for the d15N record of the mechanisms causing the disruption of the signals?

Lines 275-276: you are suggesting that the ice shelf breakup could have increased the accumulation rate, but this could have also affected the d18O profile. May you further comment on this?

Line 279: accumulation-to-sensitivity ….. do you mean sensitivity to temperature?

Line 293: This should be Supplement Figure 2.

Line 295: this should be supplementary Fig. 4.

Lines 291-294: Could the unexpected cooling suggested by N excess be a result of a climatic effect superimposed on the elevation change effect? What is reflecting the N excess record?

Line 307: Is this Supplement figure 4??

Lines 310-312: It is not clear why you did not use the most optimised methodology. See also my comments above regarding uncertainties.

Lines 314-323: are there other records to compare with?

Line 321: is this interpretation (diffusion column height to zero) in agreement with Severinghaus et al., 2003? Are the processes similar? You are looking at a quite different period of the last deglaciation for the Ross Sea…. Not sure that they are comparable.

Figure 1 and figure caption: may you use SIR instead that ST?

Figure 3: May you check the legend and the y axis title regarding Ar? Is Ar/4 or is Ar? Check also the figure caption.

Figure 4: may you add a legend to this figure? Are the vertical segments referring to uncertainties (0.14 per mil)? They seem less…

In general, please, check all the figures, figure legends, figure captions and citations in the text. There are several errors (see my comments above).