Summary: The authors assess the suitability of and differences between reanalysis products regarding winds over the Southern Ocean and the Southern Annular Mode index. They find considerable differences among four contemporary products. They then proceed to characterize the UKESM1 model w.r.t. how it simulates those winds and the SAM index, and what drives multidecadal trends in them. They find that ozone depletion dominates in summer and during the period of increasing ozone-depleting substances (i.e. the late 20^th century) but in the 21^st century and in other seasons, ongoing greenhouse gas increases drive weaker trends that in the 21^st century are counteracting the impact of ozone recovery.

I don’t have any major issues with the paper but also struggle to see the new, fundamental insights presented by the authors regarding what drives trends in the SAM. The review of the literature does not acknowledge several papers, including foundational ones, that have generally made these points. The comparison of the re-analyses is of course useful, but again the properties found here have at least partly been found in the literature before. The point is made that UKESM1 well represents trends in the SAM index. That may be the case. However, UKESM1 has also been found to simulate quite a large ozone depletion (as acknowledged by the authors), meaning it simulates stronger ozone forcing than any of the few other CMIP6 models with interactive ozone that have been studied, and almost certainly stronger than observed (although observations prior to 1979 are scarce). I thus hypothesize that this fairly large ozone forcing is compensated by difficulties with correctly propagating the dynamical impacts of ozone depletion into the troposphere, i.e. only a muted response ensues in tropospheric pressure and winds. Perhaps the authors can elaborate on this point further.

Below are several papers that should be touched upon in the discussion:

Son S-W, Tandon N F, Polvani L M and Waugh D W 2009 Ozone hole and Southern Hemisphere climate change Geophys. Res. Lett. 36 L15705

Son S-W et al. 2010 The impact of stratospheric ozone on Southern Hemisphere circulation changes: a multimodel assessment J. Geophys. Res. 115 D00M07

Simpkin & Karpechko, 2012, doi:101007/s00382-011-1121-2

Eyring V et al. 2013a Long-term ozone changes and associated climate impacts in CMIP5 simulations J. Geophys. Res. Atmos. 118 5029–60

Gerber E P and Son S-W 2014 Quantifying the summertime response of the austral jet stream and Hadley cell to stratospheric ozone and greenhouse gases J. Clim. 27 5538–59

Seok-Woo Son et al 2018 Environ. Res. Lett. 13 054024, DOI 10.1088/1748-9326/aabf21

Morgenstern, O. (2021), JGRA, 126, https://doi.org/10.1029/2020JD034161

Maybe not all of these need to be discussed separately, but a more in-depth review of the literature would be in order. Morgenstern (2021) also reviewed some observational products for the SAM index and also found that R1 is an outlier, particularly during southern winter.

Up to normalization, the SAM index presented here is the “Gong & Wang” index (Gong, D., & Wang, S. (1999). Definition of Antarctic oscillation index. Geophysical Research Letters, 26(4), 459–462. https://doi.org/10.1029/1999GL900003). It forms the basis for the Marshall index which as noted is derived from 6 stations, i.e. it is not a zonal mean. This should be acknowledged.  

As for the behavior of the UKESM1 model, Morgenstern et al. (2020, https://agupubs.onlinelibrary.wiley.com/doi/full/10.1029/2020GL088295, and 2022, https://agupubs.onlinelibrary.wiley.com/doi/full/10.1029/2022JD037123 ) and Keeble et al. (2021) show that Antarctic ozone loss in this model is stronger than in observations and other CMIP6 models. That should be emphasized more strongly, I think. I’m not sure that the trends at 60-90 degreesS are more realistic than elsewhere (not according to Morgenstern et al. 2020). The amplitude of the trend is just larger than elsewhere.

Minor points:

P2L41: I don’t understand how the polar vortex can be “accelerated”. How about “deepens”? There is evidence that the polar vortex is more long-lived with ozone depletion than without, with everythin else in a model remaining unchanged.

P2L70: There could be effects other than the wind-driven ocean circulation that can limit the usability of a model such as UKESM1 for simulating the uptake and transport into the abyss of CO2 by the Southern Ocean, such as the quality of simulation of Antarctic bottom water formation. I’m not sure about UKESM1, but in other models this has certainly been found deficient, with impacts on the carbon cycle. So a more careful formulation here might be in order, such as that atmospheric drivers of ocean uptake in this model are fine.

P5L133: I suggest rather than comparing the Marshall index to the Gong & Wang index, to simply calculate the index in the same way as Marshall, i.e. using the 6 locations. Then you compare “oranges to oranges”. Alternatively, you can show that the two derivations yield nearly the same results.

P5L161: Rather than discussing biases here (which is fine), the interesting question is how trends in TCO compare to observations, because trends in TCO are linked to climate change. Here I’m not convinced (following Morgenstern et al. 2020) that UKESM1 is more suitable because the bias over the Antarctic is smaller than elsewhere.

P6L169: Surely you are not actually “modifying emissions” but rather surface mixing ratios of ODSs (which are globally uniform and follow a prescribed scenario). I would not use the word “emissions” in this context.

P6L175: In 1950 there were about 0.6 ppbv of Cl in the atmosphere due to CH3Cl, plus traces of CFCs that had been invented in the 1930s. So it’s not quite correct to say that “no ODSs” reached the stratosphere. Just the large increases since 1950 do not reach the stratosphere in this experiment.

P6L180: The assumption of linearity (needed to attribute any differences between ozone-hist and ozone-1950 to GHGs) is a little dangerous because of nonlinear couplings between GHGs and ODSs, such as reflected in the roles of NOx and HOx (both affected by GHGs) in interfering with halogen-catalyzed ozone depletion. It would be better to have a simulation GHG-1950 in which the leading GHGs (CO2, CH4, N2O) are held constant and ODSs follow their usual trajectory. Not sure why this does not exist in AerChemMIP, but if you can produce these simulations, that would certainly help allay this concern.  

P12L373: Reproducing the trend in winds is not sufficient to conclude that the model successfully reproduces ozone depletion. Based on other literature, I think it somewhat exaggerates ozone depletion, but then struggles to fully transport this dynamical driver into the troposphere. I suggest to rephrase this, allowing for this cancellation of errors.

P13L423: I would replace “poleward jet trend” with “poleward progression of the jet latitude” or similar.

P14L429-430: Winds don’t “accelerate” or “slow down”, they “increase” or “decrease”.

P13L445: A more robust approach would use multiple models (there are more full-chemistry models in the CMIP6 archive) and use an emergent-constraint analysis (making use of historical biases in these models) to produce a multi-model projection of future winds over the Southern Ocean.

P14L448-457: This is a surprising, ocean-centric conclusion to this paper, given that the Southern Ocean plays almost no role in the rest of the paper. Perhaps you can refocus this to reflect more on the actual findings of this paper?

Figure 1: Which period and which level do the plots refer to? This information should be in the caption. Ditto figures 2, 3, and table 2 (the level needs to be indicated).

Tables 2 and 3: Here it would be fairly straightforward to complement this with data for selected CMIP6 models that are comparable to UKESM1, such as CESM2-WACCM, EC-Earth-AerChem, CNRM-ESM, or more. Given the large ozone depletion in UKESM1, contrasting it with models with weaker ozone depletion (the weakest would be found in MRI-ESM2), perhaps something useful can be learnt about the role of ozone forcing.

Figure 4: Again here the definition of the mean jet position should be included, especially at which level the winds are evaluated.

This study examines recent observed trends in near-surface winds over the Southern Ocean using multiple reanalysis products and an observational SAM index.  Historical and future forcing runs with UKESM1 are used to attribute the recent trends using scenarios with/without ozone depletion and with two levels of greenhouse gas emissions.  Consistent with prior studies, ozone depletion and recovery strongly affect the wind trends prior to 2050, with subsequent trends being dominated by increasing greenhouse gases.

This is a sound scientific study, but at the same time, isn’t terribly novel.  Apart from examination of observed trends in the newest reanalysis data sets, the relative importance of ozone and greenhouse gas forcings in circulation trends over the 1950-2100 trend has already been well established by previous studies.  As the other reviewer notes in detail, this study lacks good contextualization of its results within the previous literature on the subject.  Another weakness of the study is that only one model is examined (UKESM1).  Given that there are known biases in how this model captures observed ozone depletion (as the authors discuss), I think the study would benefit from the inclusion of results from CMIP6 DAMIP experiments to put the UKESM1 results in better context.  For this reason, I’m suggesting major revisions. 

Major comment:

Given that the interactive ozone chemistry in UKESM1 may lead to too strong ozone depletion and exaggerated circulation trends, I think these results should be placed in the context of other simulations.  As the authors acknowledge, the CMIP6 DAMIP hist-stratO3 simulations are also problematic in how they prescribe ozone, but I think it would be useful to contrast the trends simulated in UKESM1 with those from prescribed ozone simulations.  While neither set-up may be correct, it would give readers a sense of the spread of possible circulation trends due to ozone.  Unfortunately, many authors unfamiliar with the ozone problem just assume that the DAMIP simulations accurately capture ozone-induced circulation trends.  My personal opinion is that the circulation trends in the hist-stratO3 simulations are way too weak, so the authors’ simulations from UKESM1 may be a nice way to illustrate this.

Minor comments

Line 16: R1 is not a common abbreviation for the NCEP-NCAR reanalysis.  In the abstract, please use NCEP-NCAR, or define the acronym R1.

Lines 48-52:  Another paper to consider in the literature review is Barnes et al. (2014):

Barnes, E. A., N. W. Barnes, and L. M. Polvani, 2014: Delayed Southern Hemisphere Climate Change Induced by Stratospheric Ozone Recovery, as Projected by the CMIP5 Models. J. Climate, 27, 852–867, https://doi.org/10.1175/JCLI-D-13-00246.1.

Lines 88-94:  I don’t think it’s good practice to continue using the NCEP-NCAR reanalysis.  This is a very old reanalysis that is known to perform poorly in many applications (as indeed you show here).  I would recommend focusing on the three more modern reanalyses that were formulated in the past decade (as opposed to in the 1990s).

Line 177: For easy reference for readers, it might be nice to have a table describing what these four experiments are with associated ozone and greenhouse gas forcings listed for each one.

Line 241:  You need to define how the jet position is located.  Presumably this is just a wind maximum in latitude, but there are often assumptions about how to locate the maximum between grid points (interpolation, etc.).

Line 382: Figure 7 should not be cited here, as it only shows trends for the historical period not the 2000-2049 period.

Line 385: Why is the effect of ozone recovery stronger when greenhouse gas levels are larger?  Is this expected from prior studies?  If so, they should be cited here.

Line 388: Why is the GHG-driven wind acceleration larger in winter and spring?  Is this expected from prior studies?  If so, they should be cited here.

Table 1, NCEP-NCAR:  I think the proper citation here would be Kalnay et al. (1996):

Kalnay, E., and Coauthors, 1996: The NCEP/NCAR 40-Year Reanalysis Project. Bull. Amer. Meteor. Soc., 77, 437–472, https://doi.org/10.1175/1520-0477(1996)077<0437:TNYRP>2.0.CO;2.

Figure 1 caption: Please list the time period used to construct climatology in the caption (1980-2019).