Review Variability of manometric sea level from reanalyses and observation-based products over the Arctic and North Atlantic Oceans and the Mediterranean Sea

Summary

In this paper, the authors compare estimates of manometric sea level from different approaches, using numerical ocean models, gravimetry or altimetry, and in-situ observations. They present the regional timeseries and trends, amplitudes and variability, for three ocean basins, and examine how much of the regional signal can be explained by the global barystatic change. They analyse the fingerprint of several climate mode indices on the manometric sea level in the three basins.

Main comments

This is a short and to the point paper, but perhaps it is a bit too short: I am missing some details and information that I think would make it stronger and more informative/appealing, as at the end, I’m left with the question: is there one method really better than the others? The authors write that ‘The results are intended to (..) guide users in the choice of the specific product, depending on the region of interest’ (L282-283), but to me it is not clear what the choice should then be based on, as with this information it is not possible to pick a ‘best’ approach, or is there something I’ve missed? I have some major comments which can be broken down into 4 topics:

1. Uncertainties. There is very little attention to the spread in the results, and uncertainties are only sparingly mentioned or shown. For instance, Figure 1 (or any of the figures and most of the tables) shows no uncertainties, while this should be possible (?), given that for instance the GRACE dataset is an ensemble of 120 solutions. Including the uncertainties is essential to get a feeling for the consequences of using different methods in the manometric sea level in the different basins, and as it stands the three methods can only be compared very qualitatively.
2. Comparison to the global mean/total sea level change. Is it possible in figure 1 to also include (a panel showing) the global mean barystatic change for the three methods? (or at least GRACE and SLB, given the argumentation in l161?). Now showing only the global barystatic from SLB in Fig 1 feels a bit arbitrary as the reader does not know how similar (or different) these global time series are.In fact, showing the total sea level change (not only the manometric) for the global mean and the basins might be interesting too for reference, especially since for instance l.200 refers to the total change?
3. Regional differences. Is it possible to include maps: how does the manometric signal vary spatially in these basins? I understand that time series are difficult, but the authors could for instance plot the linear manometric trend (mm/yr)?
4. Figures. Please, can the figures be constructed in a colour-blind friendly way by choosing different colours (figs 1&2) and/or line styles (fig 1)? I’d suggest to change the colour bar of Fig 2 into a gradual one (choosing one colour which gets darker for higher correlation), as the colours now make it near impossible to interpret this figure. (see https://www.nature.com/articles/s41467-020-19160-7 for reasons why the rainbow scale is not a good scale to use). Alternatively: wouldn’t it make sense to provide this fig3 information in a table format, so that uncertainties can also be included? Fig 1; Would it make sense to plot the linear trends in figure 1? (it may become too busy though). Fig 2; given that these correlations are mirrored, wouldn’t it make sense to only show the half matrices, as basically one only needs the three blocks in the upper left corner of each correlation plot.  Fig 3; can uncertainties whiskers be included on the bars?

Minor comments

• Is there a specific reason for focusing on these three basins? The data covers the global ocean, doesn’t it?
• L 85. ‘assessing the multi-method mean signal’ – I don’t think this is done in the paper? I could only find this for the separate methods?
• L184 ‘significantly different’ – is this statistical significance?
• L186-188; ‘except during the first and last years’? ; is it only due to the final year that the trend is this high? How sensitive is the trend to those first and last years?
• L190 add a cross-ref to Table 3 here
• L200 ‘the global barystatic signal’?
• l203 – unclear what ‘the total trend’ is: is this the total barystatic trend, and is it in the basin or the global mean? How can the trend in a basin ‘explain’ a total trend? (the other way around sounds more logical?)
• L212 – ‘generally’: in the NA and Medi, the correlations between GRACE and other datasets are always lower than for the SLB-GREP combo, isn’t it?

Review by Don Chambers, University of South Florida

This paper looks at ocean mass (manometric sea level) variations over the Arctic Ocean, North Atlantic, and the Mediterranean Sea based on several satellite gravimetry products, as well as the sea level budget (SLB) where the steric signal is removed from satellite altimetry measurements of total sea level. This later estimate was done using steric data from analyzed T/S grids mapped from Argo floats and from an ocean re-analysis product (ocean state estimate).

I have serious concerns on the calculations over the Arctic Ocean from the SLB method (primarily from the Argo data), with slightly lesser concerns about the North Atlantic study.

How do the authors calculate steric anomalies in the Arctic when there are only small numbers of floats in this region???? As someone who is currently working on analyzing individual Argo float data for a project and not just using analyzed grids, I can assure the authors that there are not sufficient observations in the Arctic to even begin to do the calculations they are attempting. Most of the analysis grids cut-off the data at 65° because of this. If there are "values" in the grid cells, they must be from a climatology or VERY limited data and extrapolation. Unless the authors can justify that there are sufficient Argo observations in the Arctic to support their calculations, I cannot accept that any calculation of ocean mass based on altimetry - Argo data is credible in the Arctic Ocean.

There may be some validity in the using the ocean state estimate, but this is also limited by the altimetry data problems over the Arctic due to inclinations of the satellites, sea ice, etc. In the manuscript between lines 185-195, the authors point out that the trend in ocean mass using the GREP method (the ocean reanalysis steric correction) is 6.2 mm/year, compared to 2.5 mm/year for the gravimetry (or only a little over the global mean rate). They comment later: "Note that the GRACE-derived trend is likely too large, as it exceeds the altimetry-based total sea level trend of 2.9 mm yr-1, although the latter is characterized by significant under-sampling at high latitudes and ice-covered regions”. 

I have to assume this later statement is referring to the GREP estimate, not GRACE. And if it is 6.2 mm/year, that means an enormous negative steric change over the Arctic (3 mm - steric = 6.2, means steric = -3.2 mm/year. This would have to be caused by either a cooling or salt gain, which doesn't really make physical sense based on observations of the Arctic warming and freshening.  This does not encourage one to trust either the GREP or the ARGO-based SLB estimate, and I suspect for the same reasons -- there simply are not enough T/S measurements there to support the calculation. IMO, the entire Arctic analysis should be stricken because the data sets being used are not adequate to measure what the authors want. If they want to include it, they need to do a much better job of describing the limitations of the various data and models in the Arctic. 

The analysis in the North Atlantic and Med. Sea is better, because the data can support this, but I am troubled by the fact the authors did not use the salinity data in the Argo-based method. They do this because of a small residual drop post 2016 that appears in global halsosteric sea level variations. While this is a legitimate concern for global studies, it is not for regional studies. There can be large, real halosteric (salinity) fluctuations that are balanced by a compensating temperature change. This is known as "density compensation" and is a common feature in T/S data where water masses are being mixed, there are large fronts, eddies, and deep convection -- all common features of the North Atlantic. I can assure you that if you look at the T/S grids (or profiles) you will see these features all over the Atlantic and Med. Sea and that they can be quite large -- tens of cm of halosteric/thermosteric sea level change, that when added cancel so the steric change is small.

Such an event happened in the late 70s called the "Great salinity Anomaly" and based on what I have been observing in the Argo profiles, something similar has been happening over the last several years. I haven't seen any papers on it yet, but my point is that the authors should NOT exclude salinity from their calculations on regional estimates. Yes, there may a small global drift, but by ignoring salinity they are eliminating signals that are tens of cm that will cancel some of the thermometric variations. These will not necessarily average to zero.

I suggest the authors recompute their Argo-based SLB estimate including salinity, and just note that the trend may be a little off at the end of the record because of the apparent salinity drift.

My final major concern is on the analysis of the relationship with various climate indices. This section is so short, that I cannot fully understand how the relationships were established or if the climate indices were smoothed in any way. For instance, the NAO has a lot of short-term (month-month) variability, while the AMO has a large 60-year oscillation which will correlate with the trend over a twenty year period. That's not really good evidence of a relationship. But not knowing exactly what was done, and how the percentages were computed, I cannot judge this. Unless the authors choose to expand this with a more thorough description of the analysis, I cannot support it being included.

There are some more minor comments, all of which should be easy to fix:

1. On the discussion of the  Boussinesq approximation: authors should add “cannot represent the steric expansion…” They can (and do) measure the non-global parts quite well.

2. It is true that reanalysis models “make barystatic and manometric terms often unrealistic” is true. But in most cases they are also non-existent! This should be added. 

3. There are some state estimates that have begun to assimilate gravimetry and do have reasonable barystatic variations: ECCO_v4r4 is one. Rui Ponte recently used it for diagnosing the freshening of the ocean in a paper in GRL.

4. “A linear trend of 0.12 ± 0.03 mm yr-1 is added to consider the contribution of the deep ocean to thermosteric sea level changes (Chang et al., 2019).” This is a value for the global average, and appropriate only for GLOBAL steric estimates. This is driven primarily by deep warming in the Southern Ocean, with lesser signals in the North Atlantic and NO evidence (or data) for such a trend in the Arctic. Please remove this "correction" for these data and merely comment on the potential of deep warming signals that are not accounted for and give some ranges -- and not just a global value! In fact, the authors should be able to analyze this somewhat with their ocean reanalysis output. What does it say? 

5. “Explained variance, as percent R2 coefficient, is used to quantify how much of the regional signal is explained by the global barystatic signal due to fast barotropic motion.” R2 (based on squaring the correlation) is NOT explained variance unless the data being compared have exactly the same variance. In this case, they likely do not. Better to compare variances: PVE = 1 – var(resid)/var(orig), where resid is the original time series minus the global barystatic signal. This is really variance explained.