Asynchronous Antarctic and Greenland ice-volume contributions to the last interglacial sea-level highstand

The last interglacial (LIG; ~130 to ~118 thousand years ago, ka) was the last time global sea level rose well above the present level. Greenland Ice Sheet (GrIS) contributions were insufficient to explain the highstand, so that substantial Antarctic Ice Sheet (AIS) reduction is implied. However, the nature and drivers of GrIS and AIS reductions remain enigmatic, even though they may be critical for understanding future sea-level rise. Here we complement existing records with new data, and reveal that the LIG contained an AIS-derived highstand from ~129.5 to ~125 ka, a lowstand centred on 125–124 ka, and joint AIS + GrIS contributions from ~123.5 to ~118 ka. Moreover, a dual substructure within the first highstand suggests temporal variability in the AIS contributions. Implied rates of sea-level rise are high (up to several meters per century; m c−1), and lend credibility to high rates inferred by ice modelling under certain ice-shelf instability parameterisations.

In my understanding, the paper could be improved by better representing missing links in our understanding of LIG sea-level. Without modification, the paper could be read to suggest that coral and sediment records are finally reconciled and in line with GrIS and AIS modelling evidence, which is clearly not the case. This is most obvious to me for the rates of ice mass build-up, which cannot be reconciled with current understanding of ice sheet physics (see comment L192), but is also the case for the mass loss rates and large SL variability in general.
With some improvements already mentioned and as detailed further below in my specific comments, I believe the manuscript would be an interesting contribution to the discussion on LIG sea-level.
Specific comments L23 A possible contribution of GIC and thermal expansion is probably small compared to the uncertainties discussed here, but should nevertheless be mentioned somewhere in the text as a basis for the evoked residual argument. More importantly, much larger contributions may not be fully excluded from other NH ice sheets than the GrIS after 130 kyr and before 115 kyr BP (see e.g. ).
L90 I fully agree with the interpretation of a late Greenland contribution. Additional support for that may be drawn from the reconstructed temperature evolution of the NEEM ice core record (Dahl-Jensen et al., 2013). To first order, one would expect a GrIS melting (and increasing SL contribution) as long as the temperature anomaly is above zero (until ~ 118 kyr). Aside from that, I find the similarity between the presented Eirik Drift reconstruction and the Yau results rather poor. Although uncertainty bands overlap in most cases, the central estimates differ by a factor 2 (by eye ~2 m) in large parts of the LIG period, which is a big difference for a Greenland reconstruction. I suggest to change the wording from adding support "for this GrIS reconstruction" to adding support "for a late Greenland contribution". L111 I think it would help to clarify that the separation of GrIS and AIS signals is a simple difference of two records (with GrIS much smaller than the global and uncertainty on the latter of similar magnitude as the GrIS) and clarify the underlying assumptions: 1) the (corrected) Red Sea record has to be a good predictor for global SL and 2) that GL-GrIS = AIS. Note again contributions from glaciers and ice caps and other NH ice sheets.
L129 Why are the RSL uncertainty ranges of ±2.0 to 2.5 so small compared to the much larger sample based ranges? This is called "statistical uncertainty reduction" in the text. I believe it would be needed to elaborate further on this point, because most of the conclusions from this work crucially depend on it. Large SL variability, large derived mass loss rates and large derived mass gain rates are all highly disputed and problematic to reconcile with other evidence. In other words, with larger uncertainty bands, it would be possible to find a SL curve that avoids most of the controversial aspects of the record. I believe it should be also in the interest of the authors to make it as clear as possible why and how sure we can be about these narrow uncertainty bands. Conversely and as mentioned earlier, 2-2.5 m uncertainty is already quite large compared to contributions that may be expected from Greenland, which limits the usefulness of the residual calculations needed to derive the Antarctic signal.
L137 As a note on "Our results for the first time quantify significant asynchrony and amplitudedifferences between GrIS and AIS ice-volume changes during the LIG": I believe the results in  that distinguish NH and SH contributions in a probabilistic framework shows both asynchrony and amplitude-difference. The wording may need to be modified to reflect that. L141 Intra-LIG variations and the importance of different reconstructions (e.g. Red Sea vs coral) has also been discussed in . It seems appropriate to evaluate the findings in resonance with that work.
l171 If the uranium mass-accumulation-rate signal in the SO can be attributed to Antarctic meltwater releases, why do the later events during the LIG do not show at all in the record in Figure 3? I believe this requires some further discussion to justify the record as support for AIS mass fluctuations. L181 A peak (meaning a relative maximum) in atmospheric CO2 levels and Antarctic surface temperatures does not necessarily imply enough atmospheric forcing to lead to considerable mass loss by surface processes. The atmospheric CO2 forcing during the LIG compared to today is very limited and the AIS in its present state is in most places far (>5 deg) from considerable surface melt. I suggest to reformulate to put an emphasis on the ocean forcing, possibly supported by atmospheric forcing as a secondary effect.
L189 It is not clear to me why and how the GrIS comes into the discussion here, which deals exclusively with AIS processes so far. I'd suggest to remove reference to GrIS.
L192 The back-of-the-envelope calculation for ice buildup is flawed and not in line with the reality of ice sheet physics. Both ice sheets always have a mass wastage term, which compensates the received accumulation. The Greenland ice sheet constantly loses mass either by surface melting at the margins (when small) and/or due to iceberg calving (especially when the ice sheet is big). The Antarctic ice sheet must be assumed as largely marine based during the LIG with considerable calving, which continues at any time, so accumulation cannot be regarded separately to explain the regrowth. I would suggest to remove this part from the manuscript and acknowledge that there exists a real problem to reconcile the large sea-level variations in your records with current understanding of ice sheet physics.
L199 Analysis from  concludes that it is "unlikely that the rate exceeded 7 m kyr−1 and extremely unlikely that it exceeded 11 m kyr−1". There is clearly a difference if rates are evaluated on centennial or millennial time scales, but it may also be questioned if your record has the time resolution to justify centennial time scale analysis. At any rate, I think it would be needed to put your results in perspective of these findings. While the mentioned (unphysical) ice-cliff collapse parameterisations have been included in models to produce larger LIG sea-level contributions, they remain highly disputed due to their ad-hoc nature. Furthermore, the large rates of sea-level rise in DeConto and Pollard (2016) can only be found in the initial deglacial transition into the LIG (see their figure 3a), while during the LIG (where you diagnose the largest rates from your record) changes happen much more gradually. It is not surprising that large rates can be found for a full glacial-interglacial transition, while it is much more difficult to conceive such large rates from an ice sheet that is already reduced in size and also sees a forcing (oceanic and atmospheric) with less contrast. L301 If I understand the following correctly, the LIG record is still constrained by interpolation between the same amount of tie-points, even if they have been improved compared to earlier interpretations. If this is the case, this should be made clear.

Figures
There is an overlapping shading in panel b of Figure 3 which may not be intended. Otherwise, figures are clear to me. I will comment on this comparison between the LIG reefs and the Red Sea reconstruction (RSR), both because this validation is the main focus of the claims made, and because this falls within my field of expertise. I assume that others have assessed both the statistical modelling of sedimentcore data and methods used to derive an accurate and precise SL reconstruction.
These authors claim that the RSR shows a SL maxima of +10 m between 130-126 ka, a rapid metre-scale fall between 125-124 ka, and then a second maxima between 123-118 ka. In other words a decaying double highstand. They claim this reconstruction is stratigraphically "stronger" than those derived from reefs yet fail to state uncertainties with sediment-cores records, such as theirs.
Next, they validate this decaying double highstand with reef data. They state that Seychelles reef data supports an early +10m highstand, yet offer no explanation as to why this site was chosen, other than it represents the "...best sites for combined stratigraphy and precise datings...". However, the age and stratigraphic data cited in Dutton et al study is not unambiguous and suffers from the same deficiencies as other studies. Specifically it fails to parameterise the interpretation of in-situ framework from clast deposits, fails to account for non-replication of intra-sample ages, and fails to consider stratigraphic consistency of ages and rates of framework development in both modern and Pleistocene reefs. Specifically, true age variation at individual sites ranges up to 4.5ka which is stratigraphically inconsistent and contrary to evidence from Holocene reef-accretion data showing coral ages in a 3 m vertical section varying by <1000 years (Edinger et al. 2007 EPSL 253, p37). The Vyverberg et al study is more rigorous but also fails to account for inconsistent stratigraphic ages. More importantly, it fails to consider the effect of the set-up from Southern Ocean swell which commonly produces coralgal development above mean SL (e.g. modern algal ridges can develop up to 2 m above msl on Indo-Pacific reefs).
So the main reason these authors choose a comparison with the Seychelles is because it supposedly supports their claim of an early >6 m highstand. Their uncritical acceptance of these data, however, does them no favors and suggests confirmation bias. The same is true of the Bahamas studies cited: despite good data contesting their findings, these studies were chosen because they also claim a SL drop at a similar time to the RSR.
Next they address the problem that the highstand magnitude in the RSR is 2-4 m higher than in either the Seychelles or Bahamas. To account for this they cite work from the Egyptian Red Sea coast as supporting a higher LIG SL. Unfortunately they fail to state that LIG reef units along this coast vary in elevation between +8 to +18 m and thus have been influenced by neotectonic activity associated with the rifted Red-Sea margin (as is clearly stated in . This is why these works only state a general range of LIG SL between 5-10 m, and not because there is clear unequivocal evidence that SL was higher than other records.
So rather than presenting a balanced presentation of the state of LIG SL models and how they compare and contrast with the updated RSR, we are subject to only the parts that support their model. The authors might suggest that this is covered in the supplementary information, but the fact remains that the true uncertainty has been glossed over in the main text.
My suggestion to improve the manuscript would be to concentrate more on the uncertainty related to their RSR. For example, the 124ka reversal is not the only excursion shown by their data. Once these have been covered, it would be somewhat easier to introduce the various SL models based on the reef stratigraphy and have a balanced discussion about what parts of each are more or less uncertain. Unfortunately, given the still large uncertainties associated with SL records from the LIG, my feeling is that it's a little premature to start making important claims about which icesheet was to blame. From this perspective, I don't think the manuscript presents a substantial advance over what is already known.
Reviewer #3 (Remarks to the Author): This work compares estimates of global mean sea level during the last interglacial from the Red Sea to inferred sea level contributions of the Greenland ice sheet to determine the sea level contribution of the Antarctic ice sheet over time. The Red Sea estimates build upon previous work by these authors, and new data is presented to address some of the standing controversy. The authors also present a new calculation for the Greenland ice sheet sea level contribution using published data from an ocean core near Greenland ice sheet. This new calculation agrees, within uncertainty, with estimates derived from ice cores on Greenland (Yau et al 2016). In both cases, Greenland is thought to contribute little to global mean sea level during the start of the last interglacial. However, the Red Sea estimates of global mean sea level (as well as many other less stratigraphically coherent records) suggest global mean sea level was highest during the start of the last interglacial. Therefore, there must be a significant contribution of Antarctic melt early during the early stages of the last interglacial. In fact, this specific conclusion is not new (ie. see conclusions in Yau et al 2016). However, since there are high frequency oscillations in the Red Sea record prior to significant melting of Greenland ice sheets, this work suggests that the high frequency changes in global mean sea level can be caused by a dynamics within a single ice sheet, and not just the interplay of more than one ice sheet. Ultimately, the Greenland contribution is very small compared to the size of the sea level signal recorded in the Red Sea data, so the Antarctic contribution ends up looking very similar to the Red Sea record. Therefore, a key component to this paper is the new data from core KL23, and the degree to which that core 'validates' the use of KL11 as a GMSL curve (which I will discuss in more detail below). As a whole, this work is a novel and significant contribution to our understanding of past ice sheet dynamics. The paper is very clearly written, the figures are effective, and the methods and supplementary material are detailed and extensive. While I have my own reserves about the magnitude of GMSL change suggested by the Red Sea data, the calculations presented here, and in previous work, consider many of the important uncertainties (such as glacial isostatic adjustment), and I think that the community moves closer towards understanding the last interglacial and ice sheet dynamics by critically reading this paper.
Below are some more specific comments that may be helpful to the authors: KL23 and KL11: One of the controversies over KL11 in previous work was that another core in the Red Sea did not show the same high frequency change, and that the variability of change is similar in magnitude to the uncertainty. The new data presented here from the high accumulation rate core KL23 show the same high frequency change as KL11. This conclusion can be drawn from Figure 2e. However, I think this conclusion may be easier for the reader to see without the 300 year Gaussian smoothing lines. Also, I am a little confused by the discrepancy between the (Grey) replicate tests and the red KL23 data. If I understand correctly, the Grey data represents multiple measurements from the same intervals of the KL23 core. The red data lies within the grey data uncertainty, except for the drop where the red data is much higher. Why is there such a difference here (10 meters of RSL)? I don't think this is a critical issue for the interpretations, but some clarity would be helpful. Maybe I missed something?
Lines 76-80 -Was GIA considered for the Yucatan cave deposits? If the same GIA models used for the Red Sea RSL curves are applied to the Yucatan data, does that significantly change the new age-model? I suspect it could for some of the GIA models, but it is difficult to test if those models are very useful at that location. I guess the background map in Figure 1 addresses this issue a little bit --there is little difference in the RSL calculation between GIA models at the Yucatan location. The authors may decide to include a line pointing this out. I am not sure the difference would be so small if looking at time slices within the interglacial (not just the maximum RSL).
On lines 120-121, the authors state that the KL11 core is the most detailed and the 'best' core, so it will be the focus of the paper. I could guess why central (KL11) is better than the northern core, but a more explicit statement may help the reader.
Lines 137-139 -I suggest to delete the words 'for the first time' as the results in this paper stand on their own. We thank the reviewers for their thorough and useful comments. Reviewer 1 commented that "the paper makes a great attempt to put most of the observational based evidence for LIG sea-level variability together in one publication…generously providing a wealth of details in the SI that make it possible to follow the argumentation" and that the manuscript is an "interesting contribution to the discussion on LIG sea level". This was echoed Reviewer 3; "the community moves closer towards understanding the last interglacial and ice sheet dynamics by reading this paper" and states that the Supplementary Information is "extensive and detailed". Reviewer 2 by own admission concentrated on the coral records, and may have overlooked the other evidence we present for Last Interglacial ice-sheet instability (possibly because it was in the Supplement, and we have therefore moved the palaeoceanographic support into the main paper), as well as the study's stated focus on unravelling asynchronous contributions of the Antarctic and Greenland sheets. Reviewer 2 also wanted more on uncertainty, but Reviewer 3 stated that "the calculations presented here, and in previous work, consider many of the important uncertainties." Still, we have added even stronger emphasis on where uncertainties come from (or are constrained), and how they propagate.
Our responses to specific comments are given below in blue, with actions highlighted in yellow.

REVIEWER 1
L23: contribution of glaciers, ice caps and thermostatic expansion Regarding the thermosteric component, it is important to note that detailed temperature reconstruction exists only for the surface (especially where this concerns the time-evolution of temperature through the LIG). For the vast interior of the ocean, it does not exist. Noble gas estimates of mean ocean temperature are under way, but not published yet. Overall, however, the temperature difference relative the pre-industrial present were small. McKay et al., 2011 ref.1 , using modelling and palaeo data, imply minimal contribution of thermal expansion to LIG sea level and concluded that; "it seems unlikely that thermosteric sea-level rise exceeded 0.4 ± 0.3 m during the LIG". Hoffman et al., 2017 ref.2 estimated a thermosteric contribution of 0.08 to 0.51 m to the LIG highstand using a coupled climate model. Hence, this component may have been negligible, up to perhaps half a metre or so, and this fall well within our uncertainty envelopes to our reconstructions, which are total sea-level values.
Ice caps and mountain glaciers: we are not aware of any conclusive LIG estimates of this in the literature. Yet, we expect this to be small (e.g., these processes contributed only 0.  Though the reviewer agrees with the general trend (in time) of the reconstructions we use, (s)he is concerned that the two approaches we use give central estimates that are somewhat different, even if the 95% probability envelopes overlap. We see this also, but given the cold facts of statistics, we do not feel that we are warranted to discuss differences in the central estimates exactly BECAUSE the 95% probability envelopes overlap. In our calculations of the LIG Antarctic contribution, we use BOTH of these estimates (see orange and green curves in Figure 3b). While we adhere to these principles of statistical robustness, we really like the reviewer's suggestion of a change in wording, and have accordingly implemented that. We now say "…support for the inferred late Greenland contribution" where we originally had "…support for this GrIS reconstructions." L111: Clarification of the separation of the GrIS and AIS signal We have added a sentence to the Methods section to clarify this. To specifically answer to the assumptions highlighted by the reviewer: (a) "Red Sea is a good predictor of global sea level." This is dealt with in the Supplementary  ). We have fully taken the GIA processes into account when separating the GrIS and AIS signals (i.e., the Red Sea record is GIA corrected to GMSL first).
(b) "GMSL-GrIS = AIS"; To first order (i.e., within stated uncertainties), this is a reasonable assumption, given the small (unresolvable, see above) contribution from thermosteric effects and mountain glaciers/ice caps. This argument is given in the Methods.

L129: Red Sea statistical uncertainty reduction
In the Methods section, we explained how we analysed the probability intervals to the Red Sea sealevel record, namely following a slightly modified version of the approach by Grant et al. (2012 ref.12 ; described in their supplement). Those authors state, in their supplement: "To determine confidence limits to RSL that fully account for the combined uncertainties in both age and sea-level reconstruction (main-text Fig. 2 14] ). These probability intervals account for all of the combined uncertainties in both age and sea-level values and represent "worst case" propagation scenarios, given that no correlation was considered between any of the uncertainties. We then made N=1000 new records using independent random perturbations of all points within their probability Because of the stratigraphic coherence in the record, we find that the modal value (and median) in each 125-y pdf of MC resamplings is tightly constrained, with the mode being typically constrained with 95% bounds of only +/-2 to 2.5 m. In the Grant et al. study, for the Red Sea stack, this was +/-6 m, because the stack does not have strict stratigraphic coherence from one datapoint to the next, so that relative age uncertainties between datapoints remained much larger than in our new record. Stratigraphic coherence in KL11 revealed a coherent LIG pattern (validated by KL23), and analyses that take these stratigraphic constraints into account resulted in a much more coherent and tightly defined record. This is simply because: (1) the initial (relative) age uncertainties were much smaller than in the Grant et al. study; (2) the record is coherent throughout rather than jumping between values from different, stacked records as was the case in Grant et al. So, it makes sense that the probability maximum, median, and population percentiles all end up to be tighter-defined than in that study.
We have added some more text to the Methods to better clarify these points, but have not gone into full repetition of the Grant et al arguments, because this would be redundant. When the reviewer asks "how confident we can be", then the answer comes directly from the statistics: the 95% interval for the modal values means that if the MC exercise were run again, and again, and again, etc., 1 in 20 of the exercises might give modal values outside the envelope, while the other 19 exercises would return modal values within the range. We consider that to be rather logical, and not something that needs to be spelled out in the manuscript.
On the comment about the sea-level contributions from Greenland, which are up to ~5 m (4.1 to 6.2 m 95% credible intervals at 127 ka; Yau et al., 2016 ref.15 ), relative to which the reviewer finds our +/-2 to 2.5 m 95% probability intervals "somewhat limiting for the residual calculations," we emphasize that we have rigorously propagated ALL uncertainties into the final solutions (Figure 3), and that we then ONLY discuss signals that exceed the final 95% envelopes. Thus, we focus only on robust signals relative to all the limitations of the arguments, including those of the reviewer. We believe that this is quite clear in the manuscript, so we don't see what else may be added to make it even clearer, without adding redundant text. Also, it must be said that +/-2 to 2.5 m at 95% is very precise for palaeo-sealevel reconstructions. Of course, we would also like more precision, but it is what it is….. Either way, none of our conclusions are affected.
L137: wording "may need to be amended"… Agreed -the use of the term "for the first time" was likely to give a wrong impression. We have accordingly removed it. (we have added a statement to this effect) This structure and rates of rise compares favourably to our probabilistic assessment of KL11 (the rate of sea-level rise following the pronounced sea-level drop at ~125 ka is 0.8 m/century; Figure 2g). All K13 experiments (bar the 'only Red Sea' subset) had a ≥95 % probability of two peaks and a maximum intra-LIG rate of sea-level rise "likely exceeding 3.8 to 5.2 m kyr −1 , unlikely exceeding 6.1 to 7.6 m kyr −1 and extremely unlikely exceeding 9.5 to 10.9 m kyr −1 ". In comparison, our new probabilistic assessment suggests the fastest rate of sea-level rise occurs at ~127 ka (~3.5 m/century) and the lowest rate of rise occurs after the pronounced sea-level fall (0.8 m/century). We have added some text to reflect the similarities, but also outline the differences between statistical compilations on arbitrary timescales (which will always smooth the dataset and thus suppress rate-ofchange values) vs. comparisons between stratigraphically coherent, high-resolution records with strong independent age constraints. In addition, we emphasize in the manuscript that kilo-year averages (Kopp) are likely to hide larger centennial-scale averages (our study) L171: Southern Ocean uranium mass accumulation rate changes The spike in authigenic uranium at ~127 ka in Southern Ocean sediments is thought to have been caused by coastal freshening due to mass loss from the Antarctic ice sheet 26 . Given the position of the core (ODP 1094, South Atlantic), the authigenic uranium mass accumulation rate (aU MAR) record may be somewhat site-specific, and the likely source may then be the West Antarctic Ice Sheet (WAIS). The lack of later spikes could then suggest either that the majority of the WAIS was lost (or at least was significantly retreated inland) during the early portion of the LIG e.g., 27,28  In addition, the younger AIS melt periods in our study are much less sharp, with much lower rates of change, and could thus be sufficiently diluted in the dynamic Southern Ocean so AABW formation was not structurally inhibited. The palaeoceanographic discussion is now part of the main manuscript, and we specifically address the question about minor, younger AIS meltwater influences.
L181: role of ocean versus atmospheric forcing of AIS At present, a key process driving mass loss from the Antarctic ice sheets is oceanic warming, i.e., intrusion of warm ocean currents into sub-shelf cavities e.g., 38 . These ice sheets are also vulnerable to changes in atmospheric conditions on their upper surfaces (e.g., through increased surface melting and increased hydro-fracturing, changes in accumulation etc.) e.g., 39,40 . For example, atmospheric warming of the Antarctic Peninsula, and associated increase in surface melting caused the loss of both Larsen A and Larsen B ice shelves, and dominates the thinning of the Larsen C ice shelf e.g., 38,41 .
At line 181 to 183, we suggest that both atmospheric and oceanic processes contributed to the early LIG Antarctic mass loss. The reviewer is correct, the difference in atmospheric CO2 during the LIG is modest compared to today. However, the contrast between atmospheric CO2 levels and Antarctic temperatures (calculated from the ice isotopes) in the early LIG compared to the preceding glacial period is large, which would imply that AIS experienced sustained atmospheric warming, that likely acted in tandem with oceanic warming. The atmospheric warming is not likely caused by CO2, but by heat release from the ocean. We agree that our text was confusing, and have rephrased this line to remove this source of confusion. L192: calculation of rate of ice build-up during the LIG The reviewer states that AIS "must be assumed as largely marine based during the LIG, with considerable calving". Unfortunately, this seems to be an opinion rather than something underpinned by references. We respectfully disagree that this necessarily would have been the case throughout the LIG, for two reasons: 1) In major retreat phases, there is competition between mass loss/retreat of marine margins and/or isostatic rebound (e.g., Gomez studies cited in our manuscript). The GIA feedbacks in these studies strongly slow ice sheet mass loss/retreat through rebound and re-grounding (e.g., L199: rates of sea-level rise This is a comment of our record (coherent, centennial resolution) versus K13 (statistical compilation). It has been dealt with above, and we have brought out this kilo-year vs. centennial-scale difference in the main text. About the differences with the DeConto and Pollard (2016 ref. 20 ) study highlighted by the reviewer: in our view, the calculated high rates ARE found in the early LIG deglaciation of the AIS (except that there is an interruption in that deglaciation, likely due the GIA rebound and ice regrounding). But also, DeConto and Pollard's parameterization is the first approach to including such processes (we will not comment on the reviewers 'unphysical' argument); it's not perfect, but at least it's a step in the direction of understanding fast rates of sea-level rise, which we know have happened at other times in the past and now possibly also during the LIG. Recent analysis of iceberg keel plough marks from Pine Island Bay (Wise et al., 2017 ref. 51 ) suggest that during the last deglaciation calving-margin thicknesses were equivalent to the threshold that is predicted to trigger ice-cliff structural collapse and these authors infer rapid and sustained ice-sheet retreat driven by the marine ice-cliff instability processes (cf. Pollard et al., 2015 ref. 52 ). We think it would be too much of a tangent to discuss this in the manuscript -it is in our opinion more of a target for ice-sheet modelling than for sea-level reconstruction from observations. L301: linear interpolation of Red Sea record during the LIG period Yes, the reviewer is almost correct, other than that we did this for the age model with (non-linear) Hermite splines in a Monte Carlo style approach, adhering to stratigraphic constraints to ensure that the MC method does not introduce spurious age reversals, and then for the RSL record using linear interpolations between points. RSL interpolations are made AFTER placing the record in the time/age domain. The RSL interpolations, therefore, are linear interpolations in the age domain, but non-linear interpolations in the depth domain. We believe that the more expanded information on the Red Sea RSL method in the Methods section now presents sufficient information for this to be clear. Figure 3 shading: the shading was/is explained already, in the caption.
1. "They claim this reconstruction is stratigraphically "stronger" than those derived from reefs, yet fail to state uncertainties" This seems to be a confusion. We actually stated that: a. "stratigraphic coherence and, therefore, relative age relationships are stronger" (lines 50 to 51 in the original manuscript) (to clarify this better, we have elaborated on the stratigraphic coherence of Red Sea sediment cores in the Methods section, lines 423-436) b. the total propagated vertical uncertainty associated with the probability maximum sea-level reconstruction that we present is ± 2.0 to 2.5 m at 95 % probability (line 129 in the original manuscript; now in line 161). We have now added details on how this was determined relative to the uncertainties in individual data and in the previous Red Sea stack are given in the Methods section, lines 471-492.

2.
Balance (or reviewer perceived lack thereof) in representing/synthesising available LIG sea-level data; "confirmation bias" and the "uncritical acceptance" of the Seychelles and Bahamas coral sea-level records We are a bit surprised by this comment, given that we clearly described and acknowledged the ongoing debate regarding the nature (rate, amplitude etc.) and number/existence of sea-level oscillations during the LIG (lines 25-26, 43-45, 75-76, 154 and 313 in the original manuscript), the divergent and often contradictory field evidence e.g.,57 (lines 74 to 75, 313 to 322 and in section 1 of the original Supplementary  Information), and that we presented extensive stratigraphic evidence for LIG sea-level oscillations from different archives (e.g., corals, sedimentary sequences) for >20 sites (which filled 12 pages of the original Supplementary Information section 1). Hence, we think that we did extensively demonstrate that there is substantial debate, and that we're not hiding that at all. Note that reviewer 1, in contrast, was actually highly complimentary about the "wealth of details in the Supplementary Information that make it possible to follow the argumentation." Regardless, we have now drawn attention to the debate more directly in lines 80-90. Moreover, we added another (very recent) site study to Supplementary Information section 1, about West Caicos.
In addition, we summarised the key benefits and limitations of both coral-based reconstructions and the sediment-core-based Red Sea record in the second paragraph (lines 47-59 in the original manuscript; now lines 52-64 in the revised manuscript). For even more thorough review of the uncertainties, limitations, benefits, and also the opportunities associated with all different methods of reconstruction past sea levels (e.g., coral, salt-marsh, sediment cores), we refer to several excellent books and review papers that are readily available already (e.g., van  The reviewer then contends that "uncritical acceptance of these [Seychelles and Bahamas] data, … does them no favours and suggests confirmation bias", and that we "claim Seychelles and Bahamas coral records "represent the 'best sites' for comparison". We find this in conflict with the extensive assessment that we actually provided in the Supplementary Information. It is true that we did bring the specific Seychelles and Bahamas records out our synthesis of Supplementary Information section 1, but only after they were assessed along with all the others (see also Figure 1, and Supplementary Figure S3). It is quite clear from those representations that there is no one single, perfect LIG sea-level site, as we now specifically highlight in lines 87-90), but that there is an emerging pattern. We have brought the selection criteria for the Seychelles and Bahamas much stronger to the fore in Supplementary Information section 1c A few other potential sites fulfil our criteria of the combined detailed stratigraphy and large number of U-series ages; e.g., the Yucatan, Western Australia and Barbados. We did not use the well-dated and stratigraphically well-characterised Yucatan record (Blanchon et al., 2009 ref.62 ) because this is a backstepping reef sequence (i.e., no superposition of LIG reef units, and therefore no strict stratigraphic control), and because the authors did not provide any information on the palaeo-water depth of the corals dated. The elevated reef sequences of Western Australia provide compelling evidence for higher than present sea levels (~+2 to +4 m above present) 63 In view of the above, and in the absence of peer-reviewed literature (that we could find) concerning the objections that the reviewer raises about some of these sites, we maintain that the Seychelles and the Bahamas are among the best to compare with. More importantly, our argument does not hang on the similarity of the Seychelles and Bahamas coral records to the Red Sea sea-level reconstruction, especially given also the palaeoceanographic support, which the reviewer seems to have overlooked (main text Figure 3; Supplementary Information section 6). To ensure that the palaeoceanographic evidence is considered with equal weight, we have brought that entire suite of material out of the Supplement and into the main paper (separate section in Discussion, including Figure 4).
Further, in response to specific comments the reviewer made about the Seychelles and Bahamas: Although these might better be addressed to the authors of that study, e.g., through a Comment, we here address our views on these concerns.

(a) in situ vs clasts:
We have used all the available information as published, as long as no published objections are available. The samples used in our comparison, (Figure 2f and S3) were clearly described as in situ samples, and they pass our age reliability screening (we use them as an inverse weighted mean for replicate analyses). "While some of the outcrops are entirely composed of cemented reef rubble, the others that we focused on consist predominately of in situ coralgal framework and cemented coralgal rubble", "We targeted in situ coral and associated biota from each lithostratigraphic unit for sampling." In sum, the reviewer's concerns about working with loose coral clasts seem unjustified in the context of the material we focussed on. Hence, we have decided not to add any text to this effect to the manuscript, because it would only lead to confusion and because it really is tangential to the actual scope of our study. (c) fails to consider stratigraphic consistency of ages and rates of framework development: There are no straightforward stratigraphic relationships between individual coral colonies. Unlike sediment layers, coral reefs grow in 3-dimensions, so that a prograding reef may contain a wide range of ages along the same elevation (or terrace), and these may be interlocked in a complex 3-dimensional manner. The implication is that data cannot be rejected where multiple ages are observed for a single elevation (as opposed to for a single coral sample). Likewise, age inversions that are identified on the basis of age and elevation data alone cannot be rejected out of hand because such relationships may be consistent with 3-dimensional development of the reef.
With respect to the comment that coral ages should vary by less than 1,000 years per unit, we emphasize that this value was obtained for a specific reef in one specific location (Huon Peninsula, Papua New Guinea), where the total age range per horizon was found to be 800-1060 year (Edinger et al., 2007 ref.73 ). It remains undetermined if that may be projected to other regions, given that each reef is its own complex system that comprises primary and secondary growth frameworks, marine cementation, mechanical and biological erosion, and post-depositional diagenesis. It is widely acknowledged that, for both modern death assemblages and fossil assemblages, understanding of the time-averaging taphonomic processes "of corals and other non-molluscan reef groups […] is still nascent" (Kidwell, 2013 ref.74 ).
In the 3 new sites presented by , samples were taken from different units of the described stratigraphic sequence (sites 4, 7 and 19A). For each of these sites, the U-series ages of the samples are in stratigraphic order (the samples SY36 and SY37 are prima facie out of sequence but these two dates overlap within uncertainty and are very close in elevation, and can thus not be statistically or stratigraphically distinguished).
The reviewer then contends that the rates of framework development in the Seychelles record of  are inconsistent with those described for general reef framework development, which (s)he relates to Holocene data from the Huon Peninsula study. First, we again question whether insights from specific locations may be applied to other locations. Reef frameworks tend to accrete much more slowly (0.1 to 1 cm/yr) than individual coral colonies (~1 to 10 cm/yr; Hopley et al., 2007 ref.75 , and also Supplementary Information section 5). More importantly, no generalisations can be made because substrate availability, water depth, energy and trophic conditions are key factors that determine accretion rates ( However, for the three sections mentioned above (sites 4, 7 and 11), rates of accretion varied from 0.13 to 0.3 m/ka (0.013 to 0.003 cm/yr). Such rates are in line with Holocene reconstructions (above) and with average accretion rates for exposed and semi-exposed/sheltered reef settings in the Indo-Pacific (0.15 to 1.2 cm/yr and 0.1 to 2.5 cm/yr, respectively) (Montaggioni, 2005 ref.60 ).
Overall, these comments would be better addressed to the original authors (and their reviewers) and we have decided not to add any further text on these tangents to our arguments to the Supplementary Information, especially given that we were given no specific references to substantiate some of the concerns that were voiced.
(d) Southern Ocean swell and "coralagal development above mean SL" No additional references were given for this comment, but in view of the position of the Seychelles close to the equator, Southern Ocean swells seem unlikely from an oceanographic point of view. Without references or concrete information, we could not address a point framed like this.
In any case, the modern reef assemblages of Mahé (Seychelles; Taylor, 1968), prior to an extensive El Niño bleaching event which reduced species diversity (Goreau, 1998), indicates that for most shores (other than very exposed) corals and coralline algae occur below mean low water neap (MLWN) and the majority below mean low water springs (MLWS), so NOT up to 2 m above mean sea level as stated by the reviewer (which, incidentally, likely is a value gleaned from Tahiti; Cabioch et al., 1999-and its application to the Seychelles is questionable). Algal ridges on Mahé are restricted to windward and partially exposed reefs and can extend 0.5 m above the reef flat, which is still within the eulittoral zone (Taylor, 1968). Most importantly, "the shallow waters around the granitic [Seychelles] islands provide an effective barrier to long-period swell waves" (Braithwaite et al., 2000 ref.78 ). We have not added any text about this because we feel that it is a confusing tangent with limited relevance to the sites discussed.

Bahamas coral sea-level record
When the reviewer states "the same is true for the Bahamas, despite good data to contest their findings", then it is not clear what "the same" stands for? Surely not Southern Ocean swell. The comment is simply too vague for us to be able to address it. Also, the "good data contesting their findings" part of the comment is unsubstantiated. It gives us nothing to work with because no references are given, and it insufficiently clear which of our findings these data would contest. We stress that the Bahamas one of the more complete records around. It has well-documented stratigraphy (two superimposed LIG reef units), which stands even without any datings. But in addition, there are lots of high-quality ages. New work from the region again confirms a massive intra-LIG unconformity, exposed over a 5km distance (nearby West Caicos; Kerans et al., 2019 ref. 79 ). The latter has been added to Supplementary Information section 1. 3. The 2-4 m 'discrepancy' between the Red Sea record and the coral records from the Bahamas and Seychelles; and our failure to discuss the Red Sea coral record in view of neotectonics. First, we refer clearly to the source papers for the range of 5 to 10 m from Red Sea reefs. The source study actually deals with the neotectonics (as correctly mentioned by the reviewer), and the final range for sea level that we obtain from the study is based on the conclusion of Plaziat et al. themselves (the source study), which they came to after taking the various deformations into account. It would therefore be misplaced for us to make such corrections again because that would distort the careful work represented in the source studies. Second, the higher than "normal" (which the reviewer does not specify) position of LIG corals in the Red Sea may be exactly because (neo-)tectonics might be needed to allow registration of the highest phases of the LIG, as we have outlined in Supplementary

4.
Balance (or reviewer perceived lack thereof) in representing/synthesising available LIG sea-level data and possible refocusing of the manuscript. Thanks-We can see where this perception came from (we relied too much on the Supplement), and we have accordingly added text to the main manuscript (and the caption of Figure 2) to make this clearer.
On the comment that the paper may focus too much on the reversal around 124 ka, we disagree. It is an important (but not exclusive) part of the comparison with coral records, but our paper is much broader than just the coral records (that make up <20% of the study). The actual focus is on unravelling the timing relationship between the Antarctic and Greenland ice-mass histories in a statistically relevant manner with full propagation of all uncertainties, and then on comparing this with key palaeoceanographic data. The clearly crucial separation for the AIS vs. GrIS story resides close to 125-124 ka, which likely is where the impression comes from that we are only interested in that. But the reviewer ignores that we do actually discuss THREE meltwater events (R1, R2 and R3). We are not yet in a position to discuss the nature of the potential "R4" at ~120ka because there is less agreement about its sea-level position (see Figure 2f, g). For Antarctica, our reconstruction suggests that it is an event that is already within the general accretion phase, when variations will be differently controlled than during "deglaciation" phases. Our paper is more focussed on the LIG highstand and how it came about.

Presentation of the KL23& KL11
Thanks -We have adjusted the graph to make the smoothings much less prominent.

Replicate data (KL23)
This is the nature of replication. It is perhaps not nice to see, but it is what comes out of repeated analyses. Note that the uncertainty on the grey box is small because it is the Standard Error of the mean: SD/SQRT(N). The standard deviation (SD) on each of the replicate RSL values is portrayed by the blue cross. Hence, it is obvious that individual measurements may drift quite a bit whereas a mean of several replicates is much more constrained. Still, we do not wish to show this interval using ONLY the means because the red values were all measured in one go one mass spectrometer, whereas the grey values represent analyses on another mass spec more than a year later. The a-priori comparability between red and red is therefore more certain than comparability between red and grey. Given that the SD cross is shown and that the grey values were described in the caption as means with SE bars, we think this was sufficiently clarified already, and left the text as it was.

GIA and Yucatan speleothem record
The reviewer is correct. This was a clear oversight; thanks for spotting it. We have addressed this by adding this, with considerable elaboration and including Figure 1   4. L120-121 KL11 "best core" Note that we actually state that KL11 is from the "best (central) location for Red Sea quantification". The sea-level calculations (Siddall et al., 2002 ) are focused on the central Red Sea (18 to 20 °N). The northern sector of the basin has more complex oceanography (i.e., overturning and the formation of Red Sea Deep Water), and also some influence of Mediterranean weather systems. Siddall also gave tentative calculations for the northern Red Sea (worked out to approx. a linear variation of δ 18 Ocalcite with distance from the Hanish Sill), which does give a reasonable sea level solution for δ 18 Ocalcite records at the latitude of KL23, but they are less well constrained than for the central sector. The central Red Sea cores are also more suitable than northern/southern cores because they are not subject to variability linked to Mediterranean weather influences, or (as is the case in the southern Red Sea) greater variability associated with seasonal incursion of Gulf of Aden Intermediate Water. We have added some text to clarify this -lines 148-153.

L348 authors meant Figure 2e
Good spot -thank you. Yes, we did mean Figure 2e and have corrected this in the manuscript. We have carefully cross-referenced all figure calls in the revised manuscript and supplement.   Their analysis uncritically accepts the claims of these studies yet critically dismiss other models of LIG sea level that don't fit with their RSR data. "..We did not use the well-dated and stratigraphically well-characterised Yucatan record (Blanchon et al., 2009ref.62) because this is a backstepping reef sequence (i.e., no superposition of LIG reef units, and therefore no strict stratigraphic control), and because the authors did not provide any information on the palaeo-water depth of the corals dated." Yet they fail to cite the most detailed study of the Yucatan site (Blanchon 2010 Coral Reefs 29:481-498, DOI 10.1007/s00338-010-0599-0) where continuity between reef units is clearly demonstrated proving a strict stratigraphic control, and where the depth limitations of the corals is provided along with elevations of the reef crest, (which provide accurate SL positions of stillstand during the LIG). So, at the risk of repeating my original comment, these authors have cherry picked the studies they want to represent LIG SL history (Bahamas, Seychelles) and use them to confirm their RSR findings. This is conformation bias: an uncritical acceptance of the claims made in papers supporting their argument and a dismissal of arguments and models that do not fit their data.
Furthermore, in their response, the authors now state that their minds are made up and that: "... It is quite clear from those representations that there is no one single, perfect LIG sea-level site, as we now specifically highlight in lines 87-90), but that there is an emerging pattern." Obviously this 'emerging pattern' is based on their uncritical acceptance of the papers that fit, and dismissal of papers that don't. The fact of the matter is that there are at least 2 well-documented models of LIG SL based on reef data. So instead of picking sides why not just acknowledge this in the body of the paper and provide a balanced assessment of the published literature on this topic (and not just paraphrase the original articles as has been done in the SI).
Second, the Authors then address my comment on their uncritical acceptance of studies that failed to consider stratigraphic consistency of ages and rates of framework development. They respond that: "...There are no straightforward stratigraphic relationships between individual coral colonies.... coral reefs grow in 3-dimensions, so that a prograding reef may contain a wide range of ages along the same elevation (or terrace), and these may be interlocked in a complex 3-dimensional manner. The implication is that data cannot be rejected where multiple ages are observed for a single elevation (as opposed to for a single coral sample). Likewise, age inversions that are identified on the basis of age and elevation data alone cannot be rejected out of hand because such relationships may be consistent with 3-dimensional development of the reef." No references are provided for their 'chaotic model' of prograding reef development. They continue that: "...With respect to the comment that coral ages should vary by less than 1,000 years per unit, we emphasize that this value was obtained for a specific reef in one specific location (Huon Peninsula, Papua New Guinea), where the total age range per horizon was found to be 800-1060 year (Edinger et al., 2007ref.73)." So in other words, they dismiss published work as 'just one study, on one reef' and prefer their apparently imaginary 'chaotic model' where corals of any age can live side by side in the same horizon. One is left with the impression that these authors will go to any lengths to dismiss valid scientific work that provides inconvenient data.
The rest of their response is a lengthy but unconvincing argument as to why non of the review comments I made apply to their use of reef data to support their claims. And to be honest, I have neither the time nor inclination to address them, other than to say they follow the same modus operandi as alluded to above.
If the editor wants to accept this paper based on the other reviews, my suggestion would be to require that the authors state in the body of the text that the Yucatan LIG reef sequence is a valid and well-supported competing model of LIG sea level but is at odds with their preferred scenario (ie, a double highstand punctuated by a ephemeral SL fall). In other words, provide a balance view of the LIG reef literature, not the biased view they provide.
Reviewer #3 (Remarks to the Author): The revised document is an improvement on the original. The new manuscript, combined with the response to the reviews, addresses the issues raised.

Summary
Overall, I think the authors have responded well to the reviewers comments. For a number of points, I do have some concerns, for which I give additional comments to the first review and provide some additional comments. I think it is a well written manuscript, but I do think that several points need to be clarified or more critically discussed in the manuscript before it can be published. Specifically, the points raised by reviewer 1 under L171, L192, and my two main points below.
Regarding the rebuttal, answers to reviewer 1.
L23: The authors have not responded to the reviewer's comment on NH ice sheets contributions after 130 kyr and before 115 kyr BP. This is slightly mentioned in the caption of Figure 3, but I feel also that they can contribute to variability above -10 m (L393). This should be included in the text when discussing the residual curve of Figure 3b. L171: In general, I think your response focusses on discussing evidence for WAIS retreat during the LIG than on answering the question of reviewer 1. In the discussion of the palaeoceanographic data, I think you should include a bit more how this possible link between meltwater release and the MAR of site 1094 can be established and/or masked, not only the later lack of variability in MAR (as pointed out by Reviewer 1), but also the high peak during the deglaciation, prior to HS11 as shown in Figure 4g. Also, most data you refer to in Figure 4  L192: I agree with Reviewer 1 and would request serious alteration to the text, both in the main text and supplement. In terms of the answers given by the author, I don't feel you fully answer the reviewers comments. Specifically, your point 1 the GIA feedback actually causes your retreat phase to be slower, so further away from the large rates shown by the RSL record. Even if the WAIS was completely removed, large parts of the AIS will still considerable produce icebergs.
As reviewer 1 also argued, current research of the AIS, including strong physics for ice sheet retreat, do not show this large variability on such relatively short time scales. If it would be fully the AIS, the curves in Figure 3b go from a really warm Pliocene AIS (> 10 m sle) to an almost LGM configuration (closing in on -10 m sle) within 7000 years! Also, the discussion under #6 in the supplement, you argue that "mass loss would need to become almost zero". I think this statement should be completely removed! As Reviewer 1 states, this is an unrealistic case. If the GrIS or AIS are to be smaller than present, this is due to warming and thus an increase in mass loss. On the contrary, mass loss through iceberg calving will actually increase when the ice sheets are advancing.
For your ball-park assessment, if you consider the state of today's ice sheets, I think most importantly you need to consider the total mass budget of the ice sheets and cannot consider mass gain (through snow accumulation) alone. Hence in the current climate, the maximum contribution to sea level from the AIS was 0.73 ± 0.31 mm/year, and GrIS was ~1. Similar to the reviewers statement, I would like to see a statement (or similar to) as reviewer 1 suggests: ".. and acknowledge that there exists a real problem to reconcile the large sea-level variations in your records with current understanding of ice sheet physics." The sentence in Lines 269-272 should be revised to something like: "Given that the sea-level signal is a net result of ice build-up and ice loss, considerable rates of sea-level lowering are hard to reconcile due to expected increase in iceberg calving when the ice sheet is advancing".

Review
Below are a number of short comments to be addressed by the authors.
Line 45-47: You also use numerical modelling results (for the GrIS) so this statement should be adjusted. I do think that it is required to include numerical models to fully disentangle the contributions from the AIS and GrIS, either climate, ice sheet or GIA models, or a coupled model including these components.
Lines 178: To me the amplitude, especially the peaks between 130 and 127 ka do not 'seem' larger but definitely are larger. This should be reworded in the text.
Line 287-288: I wouldn't say the agreement with the high, relative short-term, variability is supported by the palaeoceanographic data.

Main comments
Besides the comments raised by reviewer 1, I also have two main concerns with the discussion of the RSL variability. I hope the author can address these remarks in the manuscript and provide a more critical discussion on their interpretation of the results.

1) On the absolute numbers and large variability
After reading the paper, I do feel your conclusions are largely based on two things: 1) the variability of the RSL itself, which is not supported (yet) by other sites, as you discuss. And 2) the GrIS contribution used to derive the AIS variability shown in Figure 3.
In terms of the variability, the absolute numbers are not discussed. I do think it is a very nice RSL record, and your statistical methods seem robust. But I do question of these high temporal and amplitude variability is a real signal of sea level caused by the AIS alone. Do you think they are a real sea level signal, only caused from ice sheets? I would plea that they are a result of regional variability that cannot be ascribed to the AIS alone. As Reviewer 1 pointed out a couple of times, the large variability is hard to reconcile with current understanding of ice sheet dynamics.
Currently the discussion (and in the Conclusions, paragraph starting at Line 301), largely focusses on possible causes in the polar regions, whereas I think that there lies a more regional cause in the high amplitude, and millennial scale variability. Therefore, I think in the discussion you should mention the robustness of the absolute numbers: Is it an amplified signal, resulting from perhaps ocean dynamics or local runoff or something influencing the original d18O data? Specifically, I think you cannot name the curve in Figure 3b 'AIS' because to me it is clear that the variability that is shown by the green/orange curves is not AIS alone.
2) The choice of the GrIS contribution For the GrIS contribution, I would like to see some more discussion. There are quite a number of studies that derive a (time varying) GrIS contribution during the LIG. These should be mentioned (referred to) in the introduction, around lines 43-45. As reviewer 1 also pointed out, I don't think the GrIS will differ very much, and most modelling studies more or less agree on the GrIS contribution during the LIG. But contributions are not constant initially I think, especially the studies that include longer simulations (Tabone, Goelzer). We thank the reviewers for their thorough and useful comments. Our responses to specific comments are given below in blue, with actions highlighted in yellow.

REVIEWER 2
We thank Reviewer 2 for his/her comments.
Our paper primarily is about the asynchronous contribution of the polar ice sheets to LIG sea level, not about how well the discrete coral data compare with each other and with the Red Sea record. If we were we to remove comparison with the coral data entirely, then our conclusions would still stand. However, ignoring the wealth of hard-won coral data would constitute a serious disservice to the wider palaeo community. Moreover, any reader would immediately (and reasonably) ask why we did not evaluate the coral-based information. This is why we present an integration of: (i) our Red Sea records; (ii) the (often divergent) coral and other evidence of LIG sea-level instability (main text and Supplementary Information); (iii) palaeoceanographic evidence from both hemispheres that indicates polar ice-sheet instability; (iv) brief discussion of ice-sheet mass balance and mechanisms of change/feedbacks that may go some way to explain such sea-level oscillations. Inclusion of all these aspects in the manuscript is essential, given that they are all interconnected, and that any inferred LIG sea-level variability eventually needs to satisfy all of these aspects (or usefully explain why some are not satisfied). Thus, we consider it unfortunate that Reviewer 2 only focusses on the coral aspects of the study, ignoring our effort to integrate the various strands of evidence.
We were disappointed to see the accusations of "confirmation bias", "uncritical acceptance of papers", "cherry-picking" and that we would "go to any lengths to dismiss valid scientific work that provides inconvenient data". In fact, we explicitly acknowledge (in several places, lines 80-83, 97-99 and Supplementary Information, Part 1) that the occurrence, magnitude and timing of and LIG sea-level oscillations is far from settled in the coral data, because of divergent and often contradictory field evidence. We have endeavoured to provide an overview in the supplement (covering 80+ papers in this section alone), which is more extensive than we have found anywhere else. In review round 1, both Reviewers 1 and 3 found the Supplementary Information extensive and detailed, which is diametrically opposite to the statements of Reviewer 2. Given that the coral sea-level field is moving toward accepted data-quality criteria, we clearly stated those underpinning our selection coral records. We were even more stringent than many recent studies in that we required not only U-series data quality and density, and elevation-criteria, but also a criterion of clearly described stratigraphic context. Reviewer 2 argues that the Yucatan data series (Blanchon 2010  Regardless, we thank the reviewer for bringing the Blanchon (2010) ref.1 paper back to our attention, and for completeness we have added this to the Supplementary Information. Given Reviewer 2's comments that we "take sides", we understand that we had still insufficiently emphasised the divergence in coral data for the LIG after the first revision. The relevant specialists will need to reconcile those divergences, and as suggested by the reviewer, all we can do is further emphasize the debate within the coral community. We have therefore removed the coral compilation graph from main text Figure 2. Alternate models are now listed in the Supplementary Information section 1  We were remiss to not provide sufficient references for our what Reviewer 2 terms our "chaotic" model of reef development. We thank the reviewer for pointing this out, and rectify this omission in the revised Supplementary Information. This section sought to highlight for the non-specialist community (given the multiple facets of the manuscript) the difference in depositional regimes for coral reefs and sediment cores, where the former does not necessarily accumulate monotonically, and most interpretation is predicated on the assumptions that fossil reefs are autochthonous, and that fossil assemblages faithfully record living assemblages (e.g., Pandolfi et al., 1995 ref.17 , Greenstein andPandolfi, 2003 ref.18 ). We hope that this addition to the Supplementary Information clears up this misunderstanding.
As for the our "dismissal" of the Erdinger et al. (2007) ref. 19 study of reef accretion, as "just one study, on one reef". Indeed, we do highlight that this is one study from a particular location. We felt compelled to make that point in light of the complex, and often interacting factors that govern coral/reef growth (e.g., Dullo, 2005 ref.20 and discussion above).
However, looking at rates of reef accretion was a good suggestion and so, rather than dismissing the comment (as is implied in the second review), we went on to demonstrate that LIG accretion rates for the Seychelles are consistent with Holocene accretion rates for that same location, and also in line with Holocene accretion rates for (relatively) nearby sites in Mauritius and the Seychelles (0.031 cm/yr; Camoin and Webster, 2015 ref. 21 ). Of course, our (and any other) calculation of reef accretion rates is subject to the following important caveats: (i) that reworking and/or displacement has not significantly disturbed the reef (e.g., Davies, 1983 ref.22 ), and (ii) that there are minimal coring artefacts (e.g., Blanchon and Blakeway, 2003 ref.23 ).
In summary, we appreciate Reviewer 2's expert insights, though we object to their suggestions that we are being dishonest. The majority of criticism/concerns that were raised in the first review ought to be settled with the authors of the original studies. Regardless, we attempted to address those concerns in our first response, only to be dismissed with "the rest of their response is a lengthy but unconvincing argument… [unsubstantiated opinion with no references] …and to be honest, I have neither the time nor the inclination to address them, other than to say that they follow the same modus operandi [dismissal of inconvenient data?] alluded to above". We feel that this is (1) a bit strong and misrepresenting our effort, (2) at odds with the other reviewers, (3) based on an assessment of only a fraction of our study.
Still, the actual comments were helpful, and we have now accordingly: (a) brought the omitted study into our synthesis, (b) transparently presented the other LIG sea-level hypotheses from coral data, and (c) provided a richness of references about why we state that reefs have more complicated stratigraphic make-up than deep-sea sediment cores from hardly bioturbated basins. We hope that this alleviates the reviewer's concerns.

Reviewer 3
Thank you. The revised manuscript ("an improvement on the original") benefited from your useful and insightful comments.

Reviewer 4
We thank the reviewer for their insightful comments and the opinion that, in our first response, we "responded well to the reviewers comments".
In response to the concerns regarding our initial response (to Reviewer 1), our comments are as follows: Page 3 of 8 L23: NH ice sheets contributions after 130 kyr and before 115 kyr BP: We understand this to mean Northern Hemisphere glaciation toward the end of the LIG. Where we talk about sea level below -10 m, there are indeed issues to contend with regarding re-glaciation in the North, as was explained in the caption of Figure 3. We fully agree that this should have been discussed in the text, and have accordingly brought that into lines 175-181.  25 ) (for reasons such as logistical difficulties of recovering cores from these regions, poor preservation and/or low sedimentation rates, and the difficulty of dating these sediments; NB. we are in a major logistics proposal at the moment to remedy this omission in the existing core availability). Future development of more records is essential for revealing provenance of the meltwater pulses, and of their Antarctic-wide nature. This is not something anybody can answer yet.
Basis for interpreting the IODP Site 1094 aU MAR signal as meltwater release and how this might be "masked": For background, though this is covered in Hayes et al. and we do not repeat it in our manuscript. The interpretation of the uranium MAR as a meltwater signal was made as authigenic uranium (aU), which is produced at or below the sediment-water interface, is a sensitive proxy for the oxygen content of sediment pore waters (e.g., Klinkhammer and Palmer, 1991 ref.26 ). Therefore changes in the aU MAR can be used as a 'tracer' of changes in the ventilation of the oceans, especially where sediment flux (potential dilution of aU) and the supply of organic matter (which enhances aU deposition) can be controlled for (as was done by the original authors, Hayes et al., 2014 by calculating a 'focusing factor' from 230 Th xs and the time integrated production of 230 Th, and 230 Th normalised opal flux, respectively). This indicates that, during the interglacial, the spike in aU MAR seen in IODP 1094 cannot be explained by dilution, nor by enhanced aU production with increased organic matter (vertical and lateral supplies of organic matter decreased during this interval, Hayes et al., 2014 ref.27 ). Therefore, this spike is attributed to decreased bottom water oxygen content as a consequence of reduced Antarctic Bottom Water (AABW) ventilation in response to freshening of Antarctic coastal waters (Hayes et  (iii) reduced organic flux supressing the formation of aU (the 230 Th normalised opal flux continues throughout the LIG, although at lower values than for the peak in aU MAR at 125 ka). Given the supporting δ 13 C and sortable silt data, a reduced amount of meltwater input (and hence resumption/increased of AADW formation and therefore increased bottom water oxygenation) seems the more likely.
We have clarified this discussion in the manuscript (lines 226 to 249 and lines 256 to 268) to make the link between the aU MAR and other palaeoceanographic data presented more explicit.
High aU MAR peak during the penultimate deglaciation: This is also covered in Hayes et al. (hence, not for us to repeat). To explain in more detail: During the interval prior to HS11, the aU MAR increases due to the poor bottom water oxygenation of the AADW (as there is no enhanced supply of organic material, i.e., low opal flux 27 , and aU production is not enhanced). The low oxygen content (i.e., poor ventilation of the bottom waters) could arise from other processes (other than meltwater) that cause enhanced stratification of the ocean such as thick and year-round sea-ice cover, or wind driven changes in upwelling over the Antarctic Zone of the Southern Ocean, as have been demonstrated for that last glacial and deglacial intervals e.g.,28,33-36 . The increased aU MAR during the deglacial coincided with with an increase in the supply of organic material (increased opal flux) which also enhanced aU production at the site . The subsequent decline in this first peak in aU MAR was driven by the increased oxygenation of the bottoms waters as overturning increased (i.e., increased ventilation) as the deglaciation progressed 27 . This can no longer be explained away in terms of uncertainties in just the data, given that high variability is seen in many different sources and approaches. Therefore, the disagreement highlights that: (a) changes in the Last Interglacial were unprecedented relative to the modern/observational era (but may possibly be approached in the future); (b) the record of modern direct observations of ice sheet mass loss are simply of insufficient length to disentangle the various ice sheet forcing mechanisms and feedbacks (e.g., Steig  The latter (c) may be especially important when identifying the high-end and/or rapid mass loss in past warm intervals (e.g., the collapse of the reverse bed slope marine sectors of the AIS e.g., refs.47,48 ). These factors have contributed to the continuing uncertainty surrounding the contribution of ice sheets to past (and future) sea level rise (e.g., IPCC AR5 ref. 49 , Bamber and Aspinall, 2013 ref. 50 ). We also note with interest the drastic increase in the range (total magnitude) of potential ice-sheet contributions estimated for future sea-level rise, given recent attempts to refine process understanding and representation within ice sheet models (Bamber et al., 2019 42 ). This illustrates how observations cannot be dismissed, but need to be used to identify discrepancies with modelling results, so that we can try to work out how reconciliation might be achieved. The palaeo record puts strong bounds on this ongoing debate because it (and it alone) incorporates all known and unknown processes and feedbacks, including those that act over a variety of timescales (i.e., equilibrium response of the ice sheets to climate forcing).
Hence, we stress the importance of getting strong data constraints out into the public domain, so they can be used to challenge and interrogate models. This process is going to be very important for working out potential future sea-level change. Regardless, we have changed the main text (lines 274 to 292) and Supplementary Information section 6 to be more in line with the reviewer's suggestions and referenceswith thanks.
In response to specific queries: (i) GIA feedback: GIA feedback slowing mass loss: Reviewer 4 seems to be confused. We do not argue that this mechanism helped cause the high rates of rise. Instead, we argue that it provided a negative feedback that had stabilising effect on grounding line retreat (e.g., Gomez et al., 2010 ref.51 ). The negative feedback is inferred to explain the dual rise structure (hence, it causes the "interruption" of the rise). This mechanism modulated AIS retreat during the Holocene (Kingslake et al., 2018) ref. 52 , and is important when considering future evolution of the AIS, especially the marine based WAIS. However, most studies that predict unstable ice mass loss do not include GIA feedbacks (i.e., that help to prevent runaway loss from unstable configurations) because this is computationally non-trivial and complicated by coupling difficulties (e.g., de Boer et al., 2017) 53 . We emphasize this mechanism because it acts on timescales that are important for estimating sea-level contributions to the LIG, and to provide impetus for including this mechanism in LIG (and future) modelling. We have retained mention to this, but clarified the context to make this clearer (lines 274 to 277).
(ii) Even if the WAIS was completely removed, large parts of the AIS will still considerable produce icebergs: Agreed, mass loss from AIS sectors other than the WAIS would be possible. However, there is currently a paucity of observational data (particularly proximal sediment cores) with which to test this. In general, I think the authors have replied well to comments from all reviews. There's quite some discussion on several points in the manuscript, but overall these are now noted in the text and/or supplement.
Concerning the reviews (I have not read all in full detail), I think there's quite some work to be done to get a coherent picture of all LIG data, and the separate contributions of the GrIS and AIS, and possible other factors that impact regional sea level changes. This paper will certainly add to that discussion, which is by far not done yet.
Reviewer #5 (Remarks to the Author): This paper presents an intriguing interpretation of Last Interglacial sea level and ice sheet contributions. This paper comes to me after having already been reviewed my several people and with a rebuttal from the authors addressing the comments of 4 reviewers.
I think the argument presented by the authors is very interesting and may be largely correct -in that the Antarctic and Greenland ice sheets may have had their peak contributions to LIG sea level asynchronously-which is largely evident already from the existing literature. There are several issues that prevent me from supporting publication of the manuscript in its current form, as follows: (1) The authors emphatically state in the abstract that this paper presents "new data" in the abstract but do not specify what kind of data, nor can I find any indication of new data anywhere in the text, methods, or supplement, nor any reference to a new data table. The only thing here I see that is new is a new age model for the Red Sea RSL reconstruction across the LIG, which appears to be a function of moving a single tie-point to stretch the curve. To that end, this is more of a new interpretation of existing data, but it seems disingenuous at best to make a claim for new data when it is not transparent at all that this is true.
(2) Many of the key claims and numerical calculations rest on understanding the uncertainty of the proxy data that they are using. The authors appear to be rigorous in their discussion of the uncertainties and in propagating them through, but then report the rates of sea-level changewhich feature prominently in the discussion section -with no uncertainties attached to them! What are the uncertainties here, are they larger than the rates themselves? This is critically important in the interpretation and assessing the significance of the values they present.
(3) Also with respect to uncertainty, they demonstrate in the supplement a variety of GIA models and then apply a GIA correction, but again, it does not appear that they have attached any uncertainty to the GIA correction from my reading of the supplement. This correction is pivotal. It can change the total sense of direction of the evolution of GMSL over the LIG based on what the GIA prediction is for the Hanish Sill. If they have chosen the wrong curve, then this can totally change the timing and magnitude of AIS contribution as they calculate. Can they address this and perhaps present two different scenarios on how it changes the calculation? Though their predicted RSL curves are quite flat for the ICE-3 and -4 scenarios that they prefer, this disagrees with the prediction of Lambeck et al., 2011, QSR, who also used a larger Eurasian ice sheet in his ice model and showed 4-5 m drop in RSL (with no excess meltwater) during the LIG at sites near the sill. The larger point being that there is significant disagreement between models about what this GIA correction is. It seems to me that this correction really drives the conclusions about when and how much the AIS contributed to GMSL. Given that, it is not clear that they can claim to know when and how much the AIS contributed, given the existing uncertainties.
(4) Fundamentally, this is yet another age-model revision of the Red Sea RSL record, of which there have been many. The movement of the tie point (from 123 ka to 118.5 ka) shifts many ages outside of their previously reported uncertainty (from earlier papers), and although the authors cite a 1.2 ky uncertainty, based on past revisions to this age model, why should one believe this statement to be true given previous adjustments to the age model? The authors choose a 118.5 ka tie point, but based on the available data, it seems that tie point could just as easily be 116 or 117 (+/-1.2) or 119 ka… The justification for why this particular number was chosen was lacking. Because the discussion centers so much on the rates, the uncertainties here are important. I'm not really sure how the authors can address this except not to emphasize the rates -or timing.
Other considerations: ---The discussion of the coral data is extensive in the supplement, but lacking a summary there of what is seen. It seems like some basic summary statements could help here, e.g., it seems clear that the majority (all?) of the sites record multiple phases/generations of reef growth, that existing dates show a progression of younger reefs on above, on top of older reefs, are the reefs in direct superposition at all the sites (except the tectonic uplifting ones), etc.. You have emphasized that there are differences, but stating the commonalities and extracting what you learn from this comparison would be more useful and would justify the very long and detailed description in the supplement. As is, there is a detailed supplement, and then some statements are made in the main text that were not emphasized in the supplement, so it is not clear how one supports the other.
---In the conclusion section, the authors provide some discussion of possible reasons for such high rates, but none of these point to the Red Sea as part of the explanation. For example, is it possible that these oscillations are amplified by climate feedbacks that affect the evaporation/precipitation balance in this region? ---Why is a different Red Sea curve (polynomial curve) used in Supplemental figure S3 rather than the core that is mostly discussed in the text? ---Also in Supp Fig S3, 10 ), and so on. The same is true in extenso for orbitally tuned chronologies and radiocarbon calibration studies. We fail to see how chronological improvements can be seen in any other way than as a symptom of progression of the science. The 1.2 ka age uncertainty (at 95%) derives from Grant et al. ( , 2014, and is not adjusted here for the sections where the age model is kept constant relative to that age model. When performing the probabilistic assessment for uncertainty propagation, we use the newly diagnosed uncertainties from Supplementary Figure 2. These are larger (therefore, more conservative) than the Grant et al. uncertainties in the interval 120-110 ka (Suppl. Fig. 2). This was perhaps not too clearly stated; we have added substantial text to the Methods to clarify this.
Choice of 118.  13 . We therefore imposed the Yucatan speleothem temporal and elevation constraint on the Red Sea record, such that there is only a marginal, 2.5 % chance that the Red Sea record exceeds the Yucatan record at 118.5 ka (i.e., the upper bound of the 95% confidence interval sits at this elevation at 118.5 ka). This may not have been sufficiently clear; we have added a sentence to the Methods section in the main manuscript to clarify this. Also, we emphasize that -in validation - Figure 2f shows the KL11 probabilistic curve alone, and it is evident that also its 95% probability zone for individual datapoints (light grey) drops below 0 m at the same 118.5 ka. We do not use this as an argument, but only in validation, to avoid circularity.

Coral data -lack of summary in the Supplementary Information:
The format of the section 1 of the Supplementary Information is a direct consequence of previous reviews. We did initially synthesise the emerging consensus from (mainly) coral records, especially sites that had been intensively sampled, with good stratigraphic control, and well-dated, in both the Supplementary Information and as a plot in figure 2. However, original reviewer 2 was adamant that this synthesis should be removed, and we did so accordingly. But a moderated synthesis still exists in the Suppl. Info section 1.
The current reviewer may have missed the previous (fierce) debate with reviewer 2, and thus may be expecting something that we also liked to include, but we were told previously to leave this out in no uncertain terms.
6. Red Sea -potential for the amplification of the sea-level signal through climate feedbacks: This is a misconception. The Red Sea method is based upon the sea level control of the residence time of sea water within a highly evaporative semi-enclosed basin. The various influences on δ 18 O calcite are well constrained  and fully included in the sea-level model's uncertainty through sensitivity testing  ref.14 . That study demonstrates that the effect of changes in sea level far exceeds changes in other factors such as evaporation and temperature. Specifically, temperature increase INcreases sea-water δ 18 O but DEcreases calcite δ 18 O through water-to-calcite fractionation; both processes are fully accounted for in the model and its sensitivity tests. Finally, the model uncertainty bounds span conditions in which the basin is "locked" year-round in winter conditions, and year-round in summer conditions; effectively, this gives ±50% allowances in temperature and evaporation uncertainty. This exceeds even reconstructions of glacial-interglacial contrasts in the area, let alone centennial variations. The fact that the rates are found in signals that exceed the method's uncertainty bounds (after