This paper attempts to construct, from ice core measurements, an index for the existence of the Maud Rise (or Weddell) polynya (MRP) over the last 200 years. The MRP was a major feature in the mid-1970s and a weaker feature at intervals since. It is clearly an important change in the ocean whose cause and effects are well worth investigating. Because there are only a few occurrences (and only one strong one) in the instrumental record, searching for evidence of past occurrences is a valuable way to approach this. The core used in the paper is well placed to “see” the MRP, and the dating is quite convincing, so the premise behind this work is a good one, and the paper should eventually be a useful publication. However there are some major issues with the way it is presented and with the construction of the so-called polynya index that need to be addressed before the paper can be published.

The main concern over the polynya index is that the paper only explains to a limited extent how it is constructed and at least one component of it seems not to be well-justified. In Figure 7a we are shown 5 ice core parameters that are said to show links to periods of polynya activity, and section 3.3.1 tries to give a mechanistic reason why each should be associated with polynya presence.

The first issue concerns the use of Na/SO4: the authors have already justified that Na should be high in polynya years. But for this index (Na/SO4) to be a useful additional piece of information they need SO4 to be low in polynya years. The authors justify this on the basis of mirabilite precipitation on se ice, which would lower the SO4/Na ratio (ie raise the Na/SO4) ratio in sea salt aerosol. However by far the majority of SO4 in this core (based on the numbers given) must be non-sea-salt sulfate, produced from marine biogenic activity, something that to first order one might expect to be high in the somewhat open waters of the polynya. The authors therefore need to reconsider whether they can really justify (mechanistically) including Na/SO4 in their index; if they do they need a better justification.

The second issue may just be presentational. How are the 5 components combined? The paper never explains this. Is each component normalised and the 5 components simply added together? This would be the simplest but assumes that all 5 components are equally good indicators of a polynya. An alternative would be to test different weights for a best fit to the satellite data. In any case this needs to be described and explained.

A final issue with the polynya index is hard to discuss because we are never shown a zoomed version of it for the satellite era (Fig 7b is for the longer period). However to my eye the index shows a good peak for 1974, but does not (despite what the text (line 380) and Fig 7a would suggest) give a peak reaching even the 0.6 threshold for the other known event in 1964. The authors need to confront this and make a better quantitative assessment of how well their composite index works over the satellite era before they discuss its extension to 1800.

I have a number of presentational and discussion points on the manuscript, but the issues above are the ones that need addressing before the other areas are considered.  Because the issue with Na/SO4 may require a recalculation of the index, and the issue about 1964 may require a reduction in confidence about previous polynyas, I class this as major revision.

Detailed comments:

Line 45 and Figure 1. Please add to the caption a description of the polynya itself, which I assume is the grey area (but this is not stated). I expected this figure to show me sea ice concentration (or some similar index): please explain better what the MODIS image is showing.

Line 75: this doesn’t quite make sense. I assume you mean “they found that snowfall increased during the 2016-17 MRP opening and assumed that this had also occurred in past MRP opening periods”

Line 96. Section X. (2.5?)

Line 101 “an ideal ice core site” typo.

Line 139-40 Mg2+, Ca2+, the “2” should be a superscript not a subscript!

Line 180. There are 2 Dey 2023 in the reference list. I think you mean the paper not the thesis. Use 2023 a and b?

Fig 2. I assume the y-axis unit should be ug m-2 yr-1?

Line 211. It would be useful to show this box (lat and long range) on Fig 1. I think you do show it on Fig 5 (but please say so in the caption).

Line 218. Please explain this metric more clearly. Do you mean it is the count of days when any pixel in the box has sea ice less than 60% or do you mean that the average across the area is less than 60%. Only the former really seems possible but it needs to be said, also how big is each pixel (ie how large an area needs to have low sea ice)?

Fig 4. If the cumulative polynya area is, as per text, a sum of daily polynya areas, then the right hand y axis should have units of km^2*days.

Line 256 and Fig 4. Can you give an estimate of what the 1974 event would show on this figure. I read 300,000 km2 persisting for a long period so I assume it would be way off scale on that red axis. I think the reader needs to have this explained.

Fig 5. You say you used 10 day trajectories and that these are endpoint frequencies. Is that right and does it make sense. Why would the position after 10 days be uniquely interesting; and is it really possible that many airmasses are still in the starting box after 10 days? Perhaps these are actually the positions throughout the 10 days but that is not what the caption says.

Line 279. Please be more precise. I think you mean that 2% of trajectories  from the MRP arrive in the 1x1 degree box surrounding the site. 

Figs 5 and 6. But I am not sure the above is very relevant. Fig 6 seems much more useful, asking what proportion of trajectories at the site come from the polynya. But you never actually state this number: what proportion of airmasses at your site came from the 48 1x1 degree boxes you identify as potential polynya sites? Please provide this number if possible.

Fig 6. Please discuss whether trajectories are also coming from other open water areas? It would be useful to draw on an average summer and winter sea ice edge to Fig 6 so we can judge whether there are also trajectories from other open areas.  This would then need a discussion in text.

Line 299 and following lines. Given 10% uncertainty on IC data, giving ranges to 2 decimal places is way too precise. Please reduce the precision through this para.

Fig 7a. I assume the red lines are smoothings, but on what timescale?

Fig 7 and section 3.3.1. We need to see the component data that go into the index across the entire record not just the instrumental period. Perhaps an extra figure in the supplement.  Most useful would be the component values with a panel also for the composite index (as per 7b) so the reader can assess which components are contributing to the overall index at peaks.

Line 323. While frost flowers undoubtedly lead to sea salt with reduced sulfate, the leading contender for sea salt from sea ice in recent years is the sublimation of blowing snow (eg Frey, M. M., et al., First direct observation of sea salt aerosol production from blowing snow above sea ice, Atmos. Chem. Phys., 20, 2549-2578, doi: 10.5194/acp-20-2549-2020, 2020 and refs therein).  However see also my major comment on the sulfate signal in this core above.

Fig 7b and section 4.1. I again emphasise that 1964 appears not to show up in the index which is surprising given what is seen in Fig 7a. Please discuss.

Line 390. The comparison with Goosse seems vague and not quantitative. Why not plot the annual peak in your and Goosse’s index as an x-y plot with statistics for how well they agree.

Line 420. I am very nervous about taking seriously an ocean reanalysis for a time and region where there is essentially no data; in particular if a polynya was present it would surely strongly change the reanalysis (earlier it’s argued that a polynya drives intense convection and changes in circulation) so this discussion seems a bit pointless. I also don’t really see what you claim in lines 431-433 – where the grey bars are seems to be nothing unusual in most of the parameters you plot. I would downplay this part of the paper (lines 424-446) which seems very speculative. 

see attached referee report