The influence of future changes in springtime Arctic ozone on stratospheric and surface climate

Chiodo, Gabriel; Friedel, Marina; Seeber, Svenja; Domeisen, Daniela; Stenke, Andrea; Sukhodolov, Timofei; Zilker, Franziska

doi:https://doi.org/10.5194/acp-23-10451-2023

Articles | Volume 23, issue 18

https://doi.org/10.5194/acp-23-10451-2023

© Author(s) 2023. This work is distributed under
the Creative Commons Attribution 4.0 License.

https://doi.org/10.5194/acp-23-10451-2023

© Author(s) 2023. This work is distributed under
the Creative Commons Attribution 4.0 License.

Articles | Volume 23, issue 18

Research article

|

21 Sep 2023

Research article |

| 21 Sep 2023

The influence of future changes in springtime Arctic ozone on stratospheric and surface climate

Gabriel Chiodo, Marina Friedel, Svenja Seeber, Daniela Domeisen, Andrea Stenke, Timofei Sukhodolov, and Franziska Zilker

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Final revised paper (published on 21 Sep 2023)
Preprint (discussion started on 15 May 2023)

Interactive discussion

Status: closed

RC1:
'Comment on egusphere-2023-672', Anonymous Referee #2, 17 May 2023

Reasons for rejection
This paper has three major issues that concern me; I'm disappointed that none of my pre-review remarks were considered:
1) The reference to ozone recovery could well be misplaced. Recovery from what? Recovery should be reserved ONLY for recovery from the increases in CFCs. The paper doesn't show that this is all that is going on in their simulations, and it's very likely not. The choice of the high emission RCP8.5 scenario means other things are changing that are known to affect 21st century ozone (e.g. CH4 and N2O). These should be evaluated and the writing fully revamped to avoid sending a misleading message.
2) Experiment design, item 1: The paper uses a fixed 3-D pre-ozone hole ozone climatology. This means that the ozone distribution will be inconsistent with the wave dynamics, a known problem in such simulations. Substantially more work needs to be done to demonstrate (or not) that the results are not an artifact of this choice. A useful reference to think about is https://agupubs.onlinelibrary.wiley.com/doi/full/10.1029/2018MS001478 but there are others; the authors need to cover this literature and deal with the experiment design carefully.
3) Experiment design, item 2: The paper uses 5 member ensembles and argues that 20 years of evolution represent 100 independent points. This is unlikely to be true. I think much more needs to be done to justify such a remarkable claim. The problem may be related to item 2) above (are they still independent when ozone is allowed to vary with the dynamics?). The paper also needs to fully explain why in this case one can have so few realizations and avoid the issues identified in a strong body of other work on NAO changes showing the need for many realizations. For example, in Deser et al referenced in the paper, 40 realizations were needed; it doesn't seem plausible that adding in the ozone change (if done self-consistently per comment 1 above) would have such a big impact, unless it is an artifact as noted under item 1). https://link.springer.com/article/10.1007/s00382-016-3502-z

Citation: https://doi.org/10.5194/egusphere-2023-672-RC1
- AC1:
  'Author comment to referee report', Gabriel Chiodo, 25 May 2023
  
  General comment: we note that we had included a point-by-point response to referee#2 in the “access review” and all their comments were addressed. The paper had been corrected before going into public discussion. We believe that the referee has overlooked them, and therefore use them below in our replies. Our responses below refer to the version of the manuscript initially submitted and which went through the “access review”. The referee’s comments (RC) are quoted in italic, while the authors’ comments (AC) are shown in bold-face.
  [RC] Reasons for rejection: This paper has three major issues that concern me; I'm disappointed that none of my pre-review remarks were considered.
  [AC] As indicated in our general comment above, the referee’s comments had been fully taken into account in the access review, and we made some amendments in the manuscript. We believe that the referee has overseen these responses.
  [RC] The reference to ozone recovery could well be misplaced. Recovery from what? Recovery should be reserved ONLY for recovery from the increases in CFCs. The paper doesn't show that this is all that is going on in their simulations, and it's very likely not. The choice of the high emission RCP8.5 scenario means other things are changing that are known to affect 21st century ozone (e.g. CH4 and N2O). These should be evaluated and the writing fully revamped to avoid sending a misleading message.
  [AC] We define the ozone “recovery” in terms of future long-term changes in Arctic ozone with respect to present-day (2005-2020 baseline). As stated in the original manuscript near L123, our recovery definition differs from that of the WMO due to different baseline being used (quoting it: “We note that our definition of ozone recovery slightly differs from the WMO, in that our period of reference is present-day (2005-2020) instead of 1980”).
  Our definition of “recovery” also includes the long-term changes that are attributable to forcings other than ODS, such as GHGs. The effects of the individual GHG forcings in RCP scenarios, including the high-emission scenario considered here (RCP8.5) have been already extensively evaluated, even for the two models used in this paper (see Revell et al., 2012 for SOCOL – see Butler et al., 2016 for WACCM). In the Arctic, Methane (CH₄) and Nitrous Oxide (N₂O) nearly offset each other in terms of the stratospheric ozone changes they induce (see e.g., Fig. 2A in Butler et al., 2016), while rising CO₂ levels drive an ozone increase. As a result, the projected Arctic ozone abundances in this scenario surpass historical levels by 20-30 DU (Fig. 1 in Butler et al., 2016), which is termed by the WMO as “super-recovery” (WMO 2010; 2014; 2018; 2022). These effects are robust across models and are not the focus of our paper, which instead deals with the dynamical impacts.
  To make it clear that our definition of “recovery” also differs from that of the WMO in terms of the attributable ozone changes, we have added the following sentence near L132 of the paper that is now in discussion: “Lastly, our definition of recovery also includes the long-term trends induced by GHGs, aside from the phase-out of ODS. These induce a "super-recovery" in ozone with respect to 1980 levels (WMO, 2022)”.
  [RC] Experiment design, item 1: The paper uses a fixed 3-D pre-ozone hole ozone climatology. This means that the ozone will be inconsistent with the dynamics, a known problem in such simulations. More work needs to be done to be certain that the results are not an artifact of this choice. A useful reference to think about may be https://agupubs.onlinelibrary.wiley.com/doi/full/10.1029/2018MS001478
  [AC] As stated in the original version of the manuscript (i.e. the version which was provided in the first “access review”) near L116, prescribing an ozone forcing does not affect the climatology and variability of the two models considered in this study, as long as the climatology is derived from the same underlying chemistry-climate model and same boundary conditions (“In both models, the climatology and variability of stratospheric, tropospheric, and surface climate is nearly identical in both configurations (interactive vs prescribed, but consistent with boundary conditions, ozone - (Smith et al., 2014), even under present-day conditions (Friedel et al., 2022a)”). We further verified this, by comparing the temperature and wind climatology of the two ensembles (“Recovery” vs “No Recovery”) over the “baseline” period used to derive the ozone climatology prescribed throughout the 21^st century in “No Recovery” (2005-2019). We only found small temperature differences (< 1 K) in the upper stratosphere, likely due to an under-estimation of the heating arising from the diurnal ozone cycle, as reported in Smith et al., (2014). We found no significant changes anywhere below 10 hPa and in particular, the polar vortex strength and variability is nearly identical in both ensembles; for example, prescribing an ozone climatology does not alter the SSW frequency in both models (Friedel et al., 2022a; Oehrlein et al., 2020). Hence, we believe that our results are not an artifact of the models’ configuration in the “No recovery” ensemble.
  To make this point clearer, we had added the following sentence near L118 of the paper that is now in discussion: “We verified this by comparing the two ensembles (the "Recovery" experiments with interactive ozone vs "No Recovery" experiments with prescribed ozone) over the reference period used to obtain the ozone climatology imposed in the "No Recovery" ensemble (2005-2019). This comparison reveals only marginal differences of less than 1 K in the upper stratosphere (above 10 hPa, not shown), which are likely due to the underestimation of the heating arising from the diurnal ozone cycle (which is not captured by the monthly-mean 3-D ozone climatology, as shown in Smith et al. (2014)). However, these differences are much smaller than the dynamical impacts of long-term ozone trends in the Arctic and global stratosphere, as shown below”.
  [RC] - Experiment design, item 2: The paper uses 5 member ensembles and argues that 20 years of evolution represent 100 independent points. I think more needs to be done to justify this in light of 2) above (are they still independent when ozone is allowed to vary with the dynamics?) and to better explain why in this case one can have so few realizations and avoid the issues identified in other work on NAO changes. For example, in Deser et al 40 realizations were needed; it doesn't seem plausible that adding in the ozone change (if done self-consistently per comment 1 above) would have such a big impact, unless it is an artifact as noted under item 1). https://link.springer.com/article/10.1007/s00382-016-3502-z
  [AC] As stated in our previous reply, the ozone configuration does not significantly affect the variability, nor the background state of the two CCMs. Hence, we discard the possibility raised by the referee, according to which our results may be an artifact of the configuration.
  As the reviewer indicates, projections in the NAO are very uncertain in CMIP models, and our two models are no exception to this. Take Figure 6 (panels a and d) to appreciate how different the springtime SLP projections are in our two models and in particular, the little resemblance to a “canonical” NAO pattern in any of our two models; hence, it is not correct to frame our results in the context of NAO projections, which are, indeed, very uncertain.
  Lastly, we disagree with the reviewer on the little plausibility of any ozone effects on SLP (Fig. 6 – panels c and f) due to uncertainty in SLP caused by internal variability. In this respect, we wish to emphasize three aspects that give us confidence.
  1. There is strong coherence between stratospheric and troposphere/surface circulation changes (negative stratospheric NAM – high SLP anomaly over the Arctic). Hence, the effects of ozone reported in our paper are consistent with our understanding of stratosphere-troposphere coupling on intraseasonal time-scales. Decades of research have consistently shown that a weak stratospheric polar vortex (as a result of Arctic ozone recovery in our study) can induce surface circulation changes (see e.g., Domeisen & Butler, 2020; Baldwin et al., 2021).
  2. There is a striking similarity across the two models (compare panels c and f in Fig. 6), indicating robustness in the ozone effects, despite the two models being very different in their sensitivity (Fig. A1) and in their projected changes in SLP (Fig. 6).
  3. There is a body of evidence showing that inter-annual changes in Arctic ozone (which are on the order of 15-20%) can induce surface climate anomalies (see Calvo et al., 2015; Ivy et al., 2017; Friedel et al., 2022): note that the long-term Arctic ozone changes reported in this paper are roughly of the same magnitude (Fig. 2).
  We also note, however, that ozone-induced SLP changes are small compared to those induced by GHGs and are generally only at the fringe of significance; this pattern might become more significant with a larger number of ensemble members. The marginal significance of the tropospheric signals is noted in several places of the manuscript, such as L375 (“While the effects in the stratosphere are very detectable, those in the troposphere are only on the fringe of significance, although they are very robust across the two models used in this study”).
  In light of the above, we reaffirm the validity of our results and believe that they are portrayed and discussed in a balanced way in our manuscript.
  
  References
  Baldwin, M. P., Ayarzagüena, B., Birner, T., Butchart, N., Butler, A. H., Charlton-Perez, A. J., et al.: Sudden stratospheric warmings. Reviews of Geophysics, 59, e2020RG000708. https://doi.org/10.1029/2020RG000708, 2021
  Butler, A. et al.: Diverse policy implications for future ozone and surface UV in a changing climate, Environ. Res. Lett. 11 064017, DOI 10.1088/1748-9326/11/6/064017, 2016.
  Calvo, N, L M Polvani, and S Solomon: On the Surface Impact of Arctic Stratospheric Ozone Extremes. Env. Res. Lett. 10, no. 9 Environ. Res. Lett. 10, doi:10.1088/1748-9326/10/9/094003, 2015.
  Domeisen & Butler: Stratospheric drivers of extreme events at the Earth’s surface, Commun Earth Environ 1, 59, https://doi.org/10.1038/s43247-020-00060-z, 2020.
  Friedel, M., G. Chiodo, A. Stenke, D. Domeisen, S. Fueglistaler, J. Anet, and T. Peter: Springtime Arctic ozone depletion forces Northern Hemisphere climate anomalies, Nature Geoscience, DOI:10.1038/s41561-022-00974-7, 2022.
  Ivy et al: Observed connections of Arctic stratospheric ozone extremes to Northern Hemisphere surface climate, Environ. Res. Lett., doi: 10.1088/1748-9326/aa57a4, 2017.
  Oehrlein, J., G. Chiodo, and L.M. Polvani: The effect of interactive ozone chemistry on weak and strong stratospheric polar vortex events, Atmospheric Chemistry and Physics, DOI:10.5194/acp-20-10531-2020, 2020.
  Revell, L. E., Bodeker, G. E., Huck, P. E., Williamson, B. E., and Rozanov, E.: The sensitivity of stratospheric ozone changes through the 21st century to N2O and CH4, Atmos. Chem. Phys., 12, 11309–11317, https://doi.org/10.5194/acp-12-11309-2012, 2012.
  
  Citation: https://doi.org/10.5194/egusphere-2023-672-AC1
  - RC2: 'Reply on AC1', Anonymous Referee #2, 26 May 2023
    
    I will comment quickly only on my point 1. It is simply inappropriate to define "recovery" any way you like, without regard to well established conventions in the field by now, as employed in the international WMO assessment process and many previous papers. This should be changed throughout if this paper is to be publishable, and the paper should also conduct runs that make clear what drives the conclusions: CFCs? I doubt it in 2100. CH4? N2O? CO2? These each have vastly different implications.
    
    Citation: https://doi.org/10.5194/egusphere-2023-672-RC2
RC3:
'Comment on egusphere-2023-672', Anonymous Referee #3, 05 Jun 2023
The paper by Chiodo et al documents climate changes that can be attributed to future increases in Arctic stratospheric ozone due to removal of ozone depleted substances and increase in greenhouse gas (GHG) concentrations. They show that projected Arctic ozone increase in spring, if happens in isolation from GHG increases, would lead to a warmer Arctic stratosphere, weaker polar vortex and more negative Arctic oscillations. While GHG induced changes will dominate, the ozone induced changes are nevertheless sizable and cancel out some of GHG induced changes. The authors used two independent atmosphere-ocean models to demonstrate that the results are robust across models.

The paper is well-written and well-illustrated. I find the results interesting and potentially publishable. My major concerns are with the methodology and interpretation of the results as explained below:

The authors mix simulations with interactive and prescribed ozone but attribute the results to the differences in ozone, claiming that the different methodology does not have an impact on the results. I understand that the prescribed present day 3D ozone results in similar present day climate as the interactive ozone (as per discussion in lines 118-124). This is expected because applied present-day 3D climatological ozone is roughly coincident with present-day dynamical fields. However, as the dynamics will change due to GHG increases there will be mismatch between future dynamics and present ozone field, which will likely affect the results. I do not know how large the effect will be, however this surely needs to be considered as a caveat and its implications discussed.

One way to avoid the above caveat is to consider an interactive “no-recovery” run with ODS fixed at present levels. The comparison of such run with the “recovery” run will demonstrate a true effect of Arctic ozone recovery on the climate. Such a “no-recovery” run will nevertheless include Arctic ozone increase due to intensify BD circulation, making the difference in ozone, and also in ozone induced effects, smaller than what is shown in the present paper. In fact, I am surprised the authors did not consider fixed-ODS simulations which should be available from CCMI data sets for both SOCOL and WACCM. I strongly recommend including such CCMI runs to the paper. If it turns out that the difference between recovery runs and fixed-ODS runs won’t be large in the Arctic I would be cautious in using term “influence of ozone recovery” in the title of the paper because ozone recovery implies a recovery from the effect of ozone depleting substances and not necessarily the influence of GHG increases.

I strongly suggest providing quantitative information in the abstract when reporting on the effect of ozone recovery. For example, when you say that ozone induced changes cancel out some of the GHG changes it would be good to know the size of the cancelation.

I believe that after the authors address the above comments, I could recommend the paper for publications.

Minor comments:
L19 How about QBO effects on ozone?
L25-26: I miss mentioning of low temperatures which are the key meteorological factor favoring stratospheric ozone depletion
L59: Fusco and Salbi (1999) would be a more relevant reference in this context:
Ref.: Fusco, A. C., and M. L. Salby, 1999: Interannual variations of total ozone and their relationship to variations of planetary wave activity. J. Climate, 12, 1619–1629

L159: Was 5m/s threshold used by Butler and Domeisen (2021)?
L238: hODS -> ODS
L274: I think WACCM has insignificant response in the polar vortex (Fig. 1d)
L297: What does “fully offsetting any GHG effect”
Citation: https://doi.org/10.5194/egusphere-2023-672-RC3
RC4:
'Comment on egusphere-2023-672', Anonymous Referee #1, 06 Jun 2023
Overall
This is an interesting study that indicates a role of future ozone changes on the circulation response which generally acts in the opposite sense to circulation changes induced by greenhouse gases. I think there is some issue with the wording of “ozone recovery” as used throughout (see Major comment) but I think the results overall are compelling and may be suitable for publication after major revisions.
Major
I agree with other reviewers that this paper may be improved by changing the wording throughout from the response to “Arctic ozone recovery” to something else, even though the authors have tried to more clearly define what they mean by “ozone recovery” on line 133. Since the end of the century is considered, the ozone changes that have occurred by then are beyond the time where changes can be related solely to recovery and instead will be largely due to GHG changes, which will also be strongly scenario dependent. This would be a relatively easy fix, as it’s essentially just changing the wording throughout- for example the “Recovery” experiment could instead be called something like “RCP8.5 ozone changes” or something to that effect. The title could simply be "The influence of springtime Arctic ozone changes on stratospheric and surface climate". I think this will vastly improve the understanding and meaning of the work because readers will get less caught up in how "recovery" is defined and what is meant, and the wording will better reflect what is being done.

Minor
Line 8- 12: These sentences could be better written/clarified, because the beginning of the sentence is “Under the high-emission scenario examined in this work, Arctic ozone returns to….” which describes what happens to ozone due to both changes in ODS and GHG together. But then the sentence goes “Thereby, it warms the lower stratosphere, …” and here it is not clear whether you are still talking about the response in the RCP8.5 climate, or the part of the response due to ozone alone. Perhaps it should also be stated more clearly that these changes due to ozone alone are generally opposite in sign to the changes due to GHGs.
Line 50-54: The sentence structure is quite confusing here… is the “including e.g. a delay in the breakdown of the stratospheric polar vortex” referring to ozone depletion or ozone recovery? I would assume it is referring to ozone depletion, but then in the next sentence “These dynamical changes extend to the troposphere, resulting in a negative phase of the SAM…” is no longer referring to ozone depletion (presumably) but ozone recovery. I would rethink how these sentences are structured because as is it is confusing which impacts are related to ozone depletion vs ozone recovery.
Line 76-77, line 140: This is related to my major comment #1, but these sentences are an example of why “recovery” is not quite accurate here- because the RCP8.5 ozone changes that occur include both ozone recovery + GHG effects (at least by the end of the century). For example, this sentence could instead be phrased “to better understand the role of springtime Arctic ozone changes in a future climate over the 21^st century … , isolating them from the effects of GHGs alone.”
Line 126, line 134, line 240: would be helpful to keep emphasizing, here and elsewhere, that this will show the impact of long-term ozone changes *for one scenario*; as the ozone response (and its influences on dynamics) may be quite sensitive to which scenario is selected.
Table 1: How much does interactive ozone matter? I imagine a third simulation could be done with prescribed, evolving ozone, and the prescribed and interactive ozone simulations are then compared, which may identify how much ozone-circulation coupling matters vs how much of the response here attributed to ozone recovery is just due to dynamic changes that are also helping to drive ozone changes. Along these same lines, the way that the response to ozone alone is currently derived is assuming (GHG+ozone) – (GHG alone) = ozone alone, but what if there are non-linearities in the response to the first term that may arise from ozone-circulation coupling under climate change?
Line 150: you may need to subtract the global-mean Z10 at each time step has EOF1 may not reflect the NAM in the future but instead start to capture the changing heights due to climate change- see Gerber et al. 2010: https://agupubs.onlinelibrary.wiley.com/doi/full/10.1029/2009JD013770
Figure 1 and Line 252: To be clear- is the RCP8.5 response the same as the “Recovery” response, or is there a difference?
Line 290: Here Fig 1a-b is referenced but doesn’t Fig 1 show the “Recovery” run (influence of both GHGs and ozone)? May be worth having an equivalent Fig 1 in the Appendix for the “No recovery” simulation that could be reference instead, since that is what is being discussed here.
Line 302: According to Butler and Domeisen (2020) and Butler et al (2019), both early and late FSWs induce a shift towards negative NAO (but the timing determines when the negative NAO occurs).
Line 321: It’s not clear to me what is being shown in Fig 5 a/d… it says something about the “ozone-induced temperature changes”, does that mean this is Recovery-NoRecovery and if so why is it labeled RCP8.5? And if so why does it not seem to match Fig 3? The caption could be more clear and the text here could better explain what is being shown.
Line 391: What is meant by “a correct representation of the ozone recovery”? (how can we know which future projection is “correct”?). Along these lines… since many if not most CMIP5 models used prescribed ozone (not interactive)- what implications are there given the results of this study? i.e., those models should all have the exact same influence induced by Arctic Ozone, suggesting that for those models’ ozone response would not be an additional source of uncertainty (e.g., differences in the ozone response could not explain the difference in polar vortex response across those models). This may be worth pointing out/discussing.

Technical
Line 32: mitigating ->mitigate
Line 33: remove “as”
Line 36: can remove second “stratosphere” after “Antarctic” as stratosphere is already specified
Line 47: “still subject” -> still a subject
Line 48: may be clearer to say “the downward influence of ozone recovery on the region with the largest…”
Line 54: More recent references could be included here, e.g. Banerjee et al. 2020
Line 56: specify “warmer climatological stratospheric air temperatures”
Line 58: Charlton and Polvani (2007) reference- is this the most appropriate paper for this sentence?
Line 95: “model” -> should this be “model ozone” or just “ozone”?
Line 98-99: change semi-colon to colon, add period after references
Line 108: do you mean, you run two “experiments” as listed in Table 1? (as is it could be interpreted as you run two ensembles of 5 members each for each experiment in Table 1).
Line 115: “as ensemble mean” -> “as the ensemble mean”
Line 148: “large-scale changes” -> “large-scale dynamical changes”
Line 223: “inducing” -> “which induces”
Line 238: was “hODS” mentioned before, and what is the meaning?
Line 276: “We note that signal” ->“we note that the signal”
Line 289, 313: replace semi-colon with period
Line 295: “on an ensemble mean” -> “in the ensemble mean”
Figure 5 caption: the panels referred to in the first sentence of the caption don’t match with the text/what is being shown
Line 323: “panels” is misspelled
Line 330, 370: I don’t think “anticipating” is the correct word here
Line 334: two “first”s in this sentence, could remove one
Citation: https://doi.org/10.5194/egusphere-2023-672-RC4

Peer review completion

AR: Author's response | RR: Referee report | ED: Editor decision | EF: Editorial file upload

AR by Gabriel Chiodo on behalf of the Authors (29 Jul 2023) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (01 Aug 2023) by Martin Dameris

RR by Anonymous Referee #3 (10 Aug 2023)

RR by Anonymous Referee #1 (16 Aug 2023)

Suggestions for revision or reasons for rejection

The authors addressed the majority of my comments. I have a few very minor/technical comments remaining.

Ar1.7 response: I had suggested being careful with the calculation of EOF1 in a future climate (currently the EOF loading pattern is calculated over the entire period 2005-2099). The authors argue that the IPCC report uses a simpler definition that involves the zonal mean surface pressure differences between 35N and 65N without removing any trends ahead of time. However, I think my point was missed (partly my fault; I suggested removing global-mean height value for each day but I think the easier solution is to base the EOF loading pattern on the 2005-2020 period rather than the full period as is currently done). Per Gerber et al. 2010, the EOF method applied to geopotential heights will at some point stop picking up the NAM as the dominant mode of variability, and instead pick up the climate change-related height increases everywhere as the dominant mode. Thus, EOF1 stops being the NAM if some care is not taken in its calculation in future climate scenarios. Note that the EOF1 calculated per Gerber et al. 2010 will still reflect long term changes in the NAM (because the data projected onto the loading pattern will still contain the trend).
The IPCC report method likely worked because in that case they are using a difference between the regions where the NAM centers of action maximize, so the relative differences still reflect the NAM pattern.
I would suggest using the EOF loading pattern calculated for the 2005-2020 period rather than the full period and then this may ensure there are no issues. As mentioned in the Gerber paper “When long data sets are used, however, one must be careful to define the annular mode patterns and indices in such a way that they always reflect internal variability. McLandress and Shepherd [2009] and Morgenstern et al. [2010a] address this concern in long integrations (similar CCMVal-2 REF-B2 simulations as considered here) by computing the NAM relative to shorter 40 year periods at the beginning and/or end of the integration. “

Line 15-16: here, it says “In the stratosphere,” but then goes on to refer to the springtime Northern Annular Mode. Are you referring to the stratospheric NAM here, or the surface NAM?

Line 55: could change “ozone depletion trends over the recent past” to just “ozone depletion” to avoid duplicate phrase in the next sentence.

Line 59: suggest “a shift towards the negative phase of the Southern Annular Mode (SAM)” – it could also be made more apparent that this sentence is referring to future ozone recovery.

Line 324: there are two erroneous “are”s here and two “a”s

Hide

ED: Publish subject to technical corrections (17 Aug 2023) by Martin Dameris

AR by Gabriel Chiodo on behalf of the Authors (18 Aug 2023) Author's response Manuscript

Short summary

Stratospheric ozone protects the biosphere from harmful UV radiation. Anthropogenic activity has led to a reduction in the ozone layer in the recent past, but thanks to the implementation of the Montreal Protocol, the ozone layer is projected to recover. In this study, we show that projected future changes in Arctic ozone abundances during springtime will influence stratospheric climate and thereby actively modulate large-scale circulation changes in the Northern Hemisphere.