Khoo and co-authors present an impressive set of data, complemented by model simulations, to reconstruct sea-ice conditions in Powell Basin, northern Antarctic Peninsula, since the Penultimate Glacial Maximum (PGM). This study is timely as there is an immense lack of sea-ice records in the Southern Ocean, especially in the western Atlantic sector (Chadwick et al., 2022). The manuscript is generally well-written, well-illustrated, and well-supported by the data except maybe for the RI-OH temperature (see below). Below are listed some comments linked to the methods, with potential impacts on the interpretation of the data and the discussion.

Methods

Age model (section 3.1; Supp S1)

I appreciated the effort made by the author to develop a robust age model through radiocarbon dating and comparison of several proxies to the U1357 nearby site and EDML. I believe that the age model is as good as it can be for a core from this complicated region. However, I would have appreciated more information about (1) why the negative relationship between Ti and EDML d18O during the 150-27 kyrs BP shifts to a positive relationship at younger times (Fig S1); (2) why some of the most obvious tie-points were disregarded (Fig S2d for example); and (3) are the radiocarbon dates reliable? I also noted that the age model is developed by comparison to U1357 records. U1357 age model until MIS6 is based on the comparison of its MS record to EDC dust record (a different ice core than the one on which PS118 Ti record is here tuned) assuming that the MS signal is a direct proxy for dust deposition in the western South Atlantic, which is not completely true as magnetic particles and iron are transported from the Antarctic Peninsula. It is also said in the present manuscript that there are environmental and oceanographic differences between PS118 (Powell Basin) and PS67 (twin core of U1357; Scotia Sea), so I wonder if it is sensible to tune PS118 to U1357. I guess this is the best one can do, but an honest evaluation of the incertitude (x kyrs) must be provided.

The corollary is that it might prove difficult to interpret millennial changes and accurate timing of rapid changes, especially between different cores (PS118 vs PS67).

Bulk and organic geochemical analyses (section 3.2)

Most of the time the reproducibility of the measures is not mentioned (Opal, TOC, OT-TEX, OT-RIOH). Please detail them in Method section 3.2, whereby the only mention of errors is in the Results for OT.

For TEX86L (section 3.2), the authors use the calibration of Kim et al. (2010). This is surprising as they used the calibration of Kim et al (2012) in their recent publications (Lamping et al., 2020; Vorrath et al., 2023).

SOT_TEX = 50.8 * TEXL86 + 36.1

This must be explained. I wonder how this would alter the TEX86L-based OT record, which is not used in the present study because it does not follow the expected G-IG pattern. The authors claim that TEX86L might be impacted by non-thermal GDGTs, which is fine. However, it must be explained why the non-thermal GDGT sources will only affect the TEX86L (Supplement 5) and not the RI-OH.

The error in the calibration for RIOH is said to be 6°C (Lü et al., 2015). OT variability in cores PS118 and PS67 are within 2°C, which is much lower than the error. How can OT's low variability be robustly interpreted here?

Diatoms (sections 3.3 and 3.4)

I expect that counts are not CRS-free as CRS relative abundances are very variable in core PS118 (0-75%; Fig. 3). It might be good to mention it as regional (Antarctic Peninsula) studies use CRS-free counts to infer environmental conditions. What is the RMSEP for the SSST reconstruction based on IKM336?

It is not clear to me if the authors used a different transfer function to reconstruct WSIC in core PS67 (IKM172; lines 269-272) while they used MAT336 in core PS118. Sometimes different transfer functions can provide different results and I therefore wonder how robust the comparison between WSIC records in cores PS118 and PS67 is, especially when looking at small changes and timing of rapid changes.

Numerical model (section 3.5; Supp S3)

The authors use here a single model (COSMOS) with, as far as I understood, PMIP3 paleogeography for glacial settings. I wonder whether (1) one model is sufficient; (2) how COSMOS performs compared to other PMIP models, especially in terms of sea-ice dynamics which is the weakness of most ESMs; (3) why not using PMIP4 settings; (4) which ice-sheet configuration was used (GLAC-1D (Argus et al., 2014, Peltier et al., 2015; ICE-6G_C, Ivanovic et al., 2016); (5) is it sensible to use a similar paleogeography at PGM and LGM, and at LIG and Holocene (Table S1)? As PS118 core is close to Antarctica I expect any change in ice-sheet paleogeography can strongly alter the results. More specifically, it is mentioned that WAIS may have partly collapsed during the early LIG, which never occurred during the Holocene. I wonder (1) what the impact of this partial collapse on Powell Basin – Scotia Sea oceanography, sea ice, and productivity, and (2) if it could reconcile simulated and data temperature (SST and OT, cf comment on the Discussion).

Discussion

Section 5.1

I found the overall reconstruction, interpretation, and argumentation valid. My main concern is about the fact that the sub-surface temperatures (based on OT-RIOH) are lower than sea-surface temperatures (based on diatom transfer function) in core PS118 (SST > OT), which is not supported by modern ocean conditions (please show vertical temperature profiles from both core sites) or the model (SST < OT). Given the 6°C error on the RIOH calibration, I wonder whether it is sensible to interpret absolute OT data, and if the 1°C difference between OT and SST is true and significant. For example, OT is as low at ~125 kyr BP as during the glacial periods (Fig 7, right column), which is not substantiated by the model (Fig 7, left columns) or by any of the other proxies presented (PIPSO, SST, WSIC, Productivity, SAT) in any of the cores (PS118, PS67, ice cores).

There is a long discussion associated with the difference between OT and SST, calling on the bipolar seesaw, recirculation of WDW, or melting of the ice sheet (lines 565-575; 630-641 for example) that are not substantiated by the data for the reasons expressed above. Especially, when looking at short-lived events in a chronological framework with several thousands of years of imprecision. The link to NH processes might completely change if records are moved by a couple of thousands of years. Overall, these interpretations are at odds with the model output, which I reckon may have some flaws too, but I would recommend simplifying the discussion on this specific point.

Overall, the Discussion is lengthy and tedious. I would suggest to simplify it.

Additional minor comments

The rule is to write “sea ice“ when a noun (reconstruction of sea ice) and “sea-ice” when an adjective (sea-ice concentration). Authors use alternatively “sea-ice concentration” and “sea ice concentration”. Please harmonise throughout the manuscript.

Lines 237-238 and elsewhere: Please change F. cugr with either F. curta gp or FCC as in previous publications.

Line 313 and elsewhere: I would refrain from using %TOC and %BSi as a direct measure of productivity in contouritic systems near islands. Secondary processes such as dilution, transport, and dissolution are extremely important in this setting. I wonder whether fluxes would not be a better metric.

Line 347 and elsewhere: R. leventerae (not R. leventarae). Additionally, use italics for diatom species.

Lines 480-481: I do not understand what you mean. Is it that the seasonal variations are in the same range as G-IG variations? And what? I am not sure you use this afterward in the Discussion.

Line 487: The phrasing is a bit optimistic. These values are not calculated but “attributed” based on almost barren diatom samples for WSIC and the absence of Diene and Triene for PIPSO. So it is not a real quantification. It is mentioned in the Results, but it must be mentioned again here in the Discussion.

Line 527: Replace caverns with cavities.

Lines 544-545: I do not understand what you mean. That the large decrease in sea ice in the Atlantic sector, modeled by Holloway et al. (2017), is a summer signal?

Lines 569-570: There is no mention of the Weddell Sea in Marino et al., (2015). Over-interpretation of this study.

Lines 720-723: I do not see the saw-toothed pattern in BSi and TOC across TI (Fig. 3), but I agree that the magnitude of changes appears more important at MIS6-5 than at MIS2-1.

Lines 734-737: This statement is true from the PIPSO, BSi, and TOC point of view in core PS118. There are however no significant differences in WSIC between the LIG and the Holocene in this core (Fig. 4). Can we infer that sea-ice seasonality was greater at the LIG? Can it be linked to different seasonal distributions of the regional insolation (Bova et al., 2021)? A greater sea-ice seasonality is however not corroborated by the simulated sea-ice maps (Fig. 5).

I also note that BSi changes appear larger across TI than across TII in core PS67, maybe also changes in SSST (Fig. 4). How does it fit with the interpretation based on PS118 data?

Figures

Figures 3-4: Please label the plots in each figure (Fig. 3A, etc…) and refer to full labels in the main text to ease reading.

Figures 5-7: Please reverse plots with PS118 data below PS67 data to fit the latitudinal distribution of the core. It will probably be easier to follow.

Figures S4-5: Please label each record.

Review on Khoo et al., ‘Ice-proximal sea-ice reconstruction in Powell Basin, Antarctica since the Last Interglacial.

Wee Wei Khoo and Co-Authors present a new multi-proxy reconstruction from Powell Basin, Antarctica, over the past 145 ka. This multi-proxy study addresses glacial-interglacial changes in sea ice (using IPSO₂₅ in combination with HBI-trienes, diatom assemblages and transfer functions), paleo-productivity (using total organic carbon and biogenic silica) as well as ocean temperature (using GDGTs, diatom transfer functions). Further, the authors compare numerical model output for sea ice as well as sea surface and subsurface temperature to their proxy reconstructions for specific time slices. With their study they reconstruct nearly perennial sea ice cover during glacial time periods and variable sea ice conditions during interglacial periods for the study area. By comparing the recent interglacial (Holocene) with the last Interglacial (MIS5e) they find indications for a relationship between the deglacial amplitude and interglacial warming. With this study, Khoo et al. contribute greatly to the general understanding of glacial-interglacial transitions, a process especially important in regard of future climate warming, in a climatically highly important area.

I need to point out, that, due to my lack of expertise in this discipline, I cannot evaluate the quality and application of the numerical model. I strongly advise for a reviewer with an expertise in that field.

General comments

Please apologize if I misunderstood something.

The overall presentation of the manuscript is, with few exceptions, excellent. Several high-quality figures support the text.

The application of the multi-proxy approach is excellent in terms of sea-ice reconstruction, as it is built on two independent well-established sea ice proxies (IPSO₂₅ and diatoms), with that approach sea ice is reconstructed seasonally, which gives important new insights. This study contributes greatly to the knowledge of sea ice within warming/cooling climate phases and the comparison to model output contributes to the general reliability of future model predictions.

In general, this is an excellent manuscript and I congratulate Khoo and Co-Authors to this nice study. Hence, I have only minor comments.

One of my biggest concerns is, that Khoo et al. focus in their Introduction on the active role of sea ice in the climate system. Further, they mention to identify potential tipping points in the ice-ocean-atmosphere system by reconstructing past sea-ice changes. In the Discussion, the authors exclusively discuss the reaction of sea ice to meltwater or solar forcing. Instead of discussing the active role of sea ice in the climate system and potential tipping points, they discuss the forcing mechanisms on sea ice. Which is, nevertheless, extremely important to understand.

In the Abstract, sea ice-glacier interactions are put into focus, which is only shortly mentioned in the Introduction. In the Discussion this process is only mentioned in Chapter 5.2.

I have the feeling the Authors could be more precise here and try to set the focus of this study more clearly.

I noticed, that a lot of abbreviations are used, which often are not necessary because terms are not used regularly throughout the manuscript. This makes the manuscript hard to read: e.g. HSSW only used 3 times, SOM only used once, HASO also only used once. I would recommend to only use abbreviation if a term is used more than 3 times.

Specific comments

Abstract

• A lot of detail is given on the used proxies, the model study, however, is not mentioned.
• The general outcome of the study is very short. I would appreciate a bit more detail.

Introduction

In the Abstract you put the focus on sea ice-glacier interactions, which is also discussed later in the Discussion. However, in the Introduction, this is only mentioned in one sentence, and the focus is laid on the feedback mechanisms of sea ice on solar radiation and ocean circulation. More information on the glacier-sea ice interaction specifically for Antarctica would be nice.

L48-54              Jumping between proxy archives here, which is very confusing. Please separate sedimentary and glacial proxies

L56-64              I agree with your statement, that the number of LIG sea ice reconstructions are limited,

However, in your text you mention 184 studies in sea ice in Antarctica summarized in Crosta et al., (2022). This is in strong contrast to the general phasing you use, as reconstructions being “limited” and scarse”. Hence, I would recommend to change the wording in L56 and L64, to point out that biomarker studies (with their advantages over other proxies) are few in Antarctica.

L117-125          I would recommend to formulate the research question you aim to answer more clearly. Here you mention to close a knowledge gap, which I feel is not sufficient enough and not doing right by the relevance of your study.

Results

L320                 input instead of inputs

Discussion

L525-528          Could you elaborate more on the lack of SSST and OT reduction at your core site in Powell basin. How do you explain this while associating it with increased meltwater inflow from the Antarctic Ice Sheet?

L539-545          How do you explain the strong seasonality in sea ice concentrations in Powell Basin?

L657-702          I appreciate the acknowledgement of the large age uncertainties for the Holocene, however, the low data availability in your record should also be acknowledged. The interpretation of warm/cold or more/less sea ice phases of the Holocene is based on one data point only. I am not sure if it is wise to interpret these small-scale Holocene changes in your record. I would rather focus on the general glacial-interglacial trends, which is the focus of your study and the strength of your records. At least be more careful in the Holocene section of your Discussion.

Figures

Fig 1

• The insert map should at least include an overview circulation and regional names, e.g. Scotia Sea, otherwise it is hard to follow Chapter 2. Maybe a map showing the Atlantic Sector with regional names, currents, etc. would be more sufficient.
• The dashed light blue line (summer sea ice extent) is barely visible

Fig 4

• This figure is the key figure of the manuscript, but hard to decipher as it holds a lot of records and data. Please add numbers, letters, etc. to refer to the single plots in the figure captions. I see that the authors try to establish a color-coding distinguishing between different core locations (PS62/219-1 always in orange-brown colors). Maybe this could be done better. Further I am not sure if plotting the diatom species cugr. And F. obli on the same axis. Variations of F. obli are hardly visible.
• OT_RI-OH’ plot: Please indicate in captions what the light blue and dark blue (running average?) lines represent.

Fig 5

• The brown star (PS62/219-1) is hard to see with dark blue background. The red line (15% sea ice coverage) is hardly visible at all.

Fig 6

• I understand SSST_diatom for PS118_63-1 is not available for the PGM and LGM, it is irritating to have an ‘empty’ graph. I would suggest to add an ‘n.a.’ onto the graph where data is not available
• The SST scale could be adjusted, as the largest change occurs within the SST range of -2 – 14 °C, if you adjust the SST scale the critical changes would stick out more.

Fig 7

• Here the OT scale should also be adjusted, shown OT stop around 15-16°C but the scale goes up to 21°C
• What does the dark blue line indicate? Running average of OT?

Supplementary Material

Fig S1

• Could you please give more detail on the comparability of XRF Ti counts and EDML - d¹⁸
• I do not understand how you choose peaks for calibration in both records, and why you excluded two of them.
• Why do you use Ti counts alone? A more sophisticated approach would be to use element ratios? (Hennekam & deLange, 2012)

Hennekam, R., deLange, G. (2012). X-ray fluorescence core scanning of wet marine sediments: methods to improve quality and reproducibility of high-resolution paleoenvironmental records. Limnology and Oceanography: Methods 10

Fig S2b

• I find it hard to see a correlation pattern here. There should be more information on how the peaks where chosen (or not) for calibration).

Table S1

• What reservoir correction did you use?