Dear Authors

I have now received the second round of review and reviewers are still concerned about the interpretation and data correction.

I have pasted below the second round of comments. I may accept the manuscript only after these new comments are taken into account. Thus I will reconsider your manuscript after these major revisions.

Referee 1
The authors have taken on board most of the comments I made on the earlier version, and although I don’t always agree with the conclusions they reach (for example about nitrate as a fertiliser), most of them are now reasonable. The conclusion about the cause of the increasing concentration at S100 needs further work. Apart from that, the remaining issues with the paper are mainly to do with readability as the changes made are quite rambling and confusing and I suspect many readers will not be able to follow the arguments. In particular:

Section 3.4 and Table 4 should be deleted. The authors have agreed that the pit data cannot be used because they do not represent even a full year. This means that now they are trying to regress 4 data points against 4 variables which obviously cannot be done in any meaningful way. Even where you find significance it looks spurious: for example sulfate is significantly related to latitude because S100 and KM are higher values than the other two sites, but the latitude difference between them is a matter of minutes and it is not credible that this is actually what is causing the difference in sulfate. Simply state that you cannot see any significant relationship between chemistry and the variables assessed, although sea salt is clearly lowest at KC, which is further inland than the other sites.

You have now added a lot of SI about the snowpits, which are not used in the text. I appreciate you probably put work into them and are attached to them, but they add nothing to the paper and complicate it for the reader. I propose removing Table S1, S3, and Figs S2 and S3, plus any mention of them in the text.

The new tables 2, 5, 6 and 7 are unreadably complicated because of the way that different statistics are piled vertically on top of each other. I propose that the authors present these tables with only the mean values (or the medians if they prefer) in the main text. If they really want to show off the other statistics (which are really thesis material and not needed in the paper), then place them in the supplement.
Sections 3.5 and 3.6 are very long and confusing. They need carefully evaluating by all authors who should then try and express the concepts more concisely, pointing carefully to the reduced Tables 5 and 7.

The conclusion about the increase at S100 after 1950 is now more credible, but still ignores what seems the obvious answer, and the authors still did not address what I asked about. While it could be that the loss of the ice tongue somehow influenced sea ice formation and caused the change it is not obvious to me why this would affect S100 so strongly but not KC or KM. What I asked is whether the authors are sure that the ice shelf immediately in front of S100 has not retreated over the last 50 years, putting S100 much closer to the sea (something that cannot affect the fixed points at KM and KC). Although the authors point me to glaciological data there is nothing I can see that answers this question, because there is no information about the ice front position, but I can make a guess. S100 is apparently 3 km from the sea today. I would guess the ice front position is almost fixed relative to the ice rise adjacent to it, with regular calving events keeping up with the ice velocity behind it (high resolution images seem to show crevassing near the ice front so this seems likely). The authors say that the ice velocity is “10s-100s of m/a”, but if one blows up the Rignot map the velocity in the free-running parts of Fimbul all appear to be in blue shades, ie at least 100 m/a. Then over 50 years the site S100 has moved at least 5km, and is now that much closer to the ice front, and out of any “shadow” from the unnamed ice rise next to it. A move from eg 8 km to 3 km from the sea might well be enough to explain the data. (As an example a paper by Gorlach et al (FRISP report 2, page 48) shows sea salt concentration increasing by a factor 4 over about 10 km near Neumayer, moving from what I estimate to be about 13 to 3 km from the ice edge). This suggests that this section of the paper needs a further iteration as this seems a much simpler explanation than yours. I know that you are trying to explain a change in the nss-sulfate contribution as well, but this is actually poorly constrained. The nss sulfate is very obviously negative in the last 50 years because the sea salt is so high in concentration and dominates. In the pre-1950 period, the partitioning of sulfate between ss and nss is much less safe, and it remains plausible that the sea salt part may still be depleted. In any case whatever you choose to say, you cannot just ignore the likelihood that S100 is just a much more coastal site as time progresses.

Referee 2
I’m happy to see that Authors made almost all the changes I suggested and the text was improved accordingly. For this reason, I think that the manuscript is now ready to be published on The Cryosphere journal.
However, I have to note a potentially relevant error in calculating the ss- and nss-fractions of Na and Ca. If I have well understood, Authors used totCa as a marker of the crustal source and calculated nss-Na by the Ca/Na ratio in the Earth crust. This is not correct because also Ca can have two main sources: mineral dust and sea spray. This is particularly true for coastal sites, where the ssCa contribution could be relevant or even dominant. In order to calculate more reliable ss- and nss-fractions of Na and Ca, Authors should use the following 4-equation system:
totNa = ssNa + nssNa
totCa = ssCa + nssCa
ssNa = totNa - 0.562 nssCa
nssCa = totCa - 0.038 ssNa
where 0.562 = Na+/Ca2+ (w/w) in the crust (Bowen, 1979), and 0.038 = Ca2+/Na+ (w/w) in seawater (Nozaki, 1997).

Bowen, H.J.M., 1979. Environmental Chemistry of the Elements. Academic Press, London.
Nozaki, Y., 1997. A fresh look at element distribution in the North Pacific. http:/www.agu.org/eos_elec/97025e.html.

By solving the equation system (4 equations, 4 unknown variables), a more correct evaluation of ss-Na can be obtained.
If Authors consider that all the Ca comes from the crustal sources, nssNa fraction can be over-estimated. As a consequence, the critical parameter ssNa can be significantly under-estimated and the error can propagate to the nss-SO4 calculation.
I’m aware that using the correct procedure to calculate a reliable ss-Na fraction could imply many changes in the manuscript figures and text, if ss-Na values obtained with the equation system are significantly different from those obtained by using totCa as crustal marker. Therefore, I’d suggest that the Authors test the differences in ss-Na calculation with the two different procedures, at least for a sub-dataset of samples in which the contribution of ss-Ca appears to be relevant (i.e., for samples enriched in sea salt, for which totCa cannot be used a-priori as crustal marker). If this test is positive (i.e., if the ss-Na values calculated with the two methods are quite close each other), Authors could leave unchanged figures and text. On the contrary, ss- and nss-fraction of all the components (Na, Ca, sulfate etc.) should be revised.

Dear Authors

before definitively accepted, I would like to see the data deposited in an official database, e.g https://cera-www.dkrz.de/WDCC/ui/cerasearch/
(contacting the leading author is not a long term solution).

"... using a robust regression method that is known to be less sensitive to a possible heteroscedasticity and non-Gaussianity of the model residuals" Please can you specify what method was used? and give some details?

Thank you
Joel