General

The paper is well written, very clear, and provides a new and potentially useful analysis. The deduced trends are broadly consistent with those published previously (e.g. by Weber et al., already cited, or by McKenzie et al., 2019, DOI: https://doi.org/10.1038/s41598-019-48625-z).

Unfortunately though, I’m not yet convinced that the results for the latitude-dependent turnaround dates – which are the new finding here - are correct (presuming that the object was to find the turnaround date due to the bottoming out of manmade ODSs, rather than the turnaround due to all sources, including volcanic perturbations). If the revised analysis proves to be valid - after satisfactorily addressing my main concerns below - then the paper will be suitable for publication.

The latitude-dependence in the turnaround date is useful new knowledge (though error bars are required), and seems qualitatively consistent -at least in the southern hemisphere - with the latitude dependence in age-of-air (which should be cited). But the actual turnaround dates do seem a little early, especially in the northern hemisphere. A useful additional plot would be to compare the delay in turnaround date from some reference, say 1994, with age-of-air in the stratosphere as a function of latitude (as for example in Fig 6 of Waugh et al., 2002, DOI: 10.1029/2000RG000101). With that suggested new figure, it would be clear that the deduced turnaround date for the northern hemisphere is too early – possibly because of Pinatubo’s effect.

My main issues with the present version are:

1. It’s hard to envisage why the turnaround dates should precede the date that equivalent chlorine (EESC) reaches a maximum in the stratosphere. According to the most recent Ozone Assessment, EESC reached a peak in the stratosphere at mid-latitudes in 1998 –in reasonable agreement with the deduced turnaround dates at southern latitudes, but 4 years later than deduced here at northern latitudes, where ozone was affected by the eruption of Mt. Pinatubo.

That raises the following questions.

1. Is the merged data set of satellite data alone suitable for trend analysis such as described in the manuscript. I know at least one of the authors has claimed in the past that they should not be, which is why merged data sets normalized to Dobson values were developed (e.g., by Bodeker). Please explain what has changed that now enables you to use the satellite data directly. Please also include the resulting error in ozone trend from that source. I see a comparison with MLS gives confidence for the period since 2005, but what about the 27 year period before that?
2. Are the deduced turnaround dates influenced by aerosols from the 1991 eruption of Mount Pinatubo, which led to significant reductions in ozone in the northern hemisphere for a couple of years after the eruption? For example, if those years are omitted in Figure 4, it would appear that ozone has continued to decline more or less monotonically at 55N. An additional sensitivity analysis is required to look at the effects on the final results of omitting that period of data (e.g., all data from 1992 and 1993). Alternatively, you could try even larger values of ‘f’ to better remove short term effects. Additionally, I would suggest including aerosol impulses – possibly latitude-dependent- from volcanic eruptions as new basis functions in the analysis, as used previously by Liley et al (see Fig 2 in https://doi.org/10.1029/1999JD901157).There’s a nice depiction of these shown in Q13 of the Twenty Questions and Answers document that accompanies the most recent ozone assessment (available from https://www.csl.noaa.gov/assessments/ozone/2022/). That depiction shows that Pinatubo effects continue until after your deduced turnaround dates in the northern hemisphere, and peak EESC peaking much later, as does the minimum ozone in the lowest panel. My guess is that the steps described above will make a difference to the northern hemisphere turnaround dates, but not the southern hemisphere where Pinatubo’s effects were much smaller.

In Figure 3, please also include those blue and red curves for latitude 55 (it would be instructive to see these plots for other latitudes as well). By including the lower latitudes, the reader can better understand what the authors are getting at in line 177. Please also state the range of years over which the “slight downturn” applies. Since 2016?

Figure 5. The turnaround dates will possibly (probably?) be revised after the analysis suggested above, which will affect the subsequent trend analysis. Please also include error bars in the figure.

Minor points

Line 57. Start the sentence with “The beginnings of ozone recovery were …” (Or use the word “slowdown” instead of “recovery”. I don’t think that a slowdown in the rate of depletion can correctly be described as a recovery).

Line 104. Should that be high “latitude” (rather than “altitude”)?

Line 137. Please state the period of each of these QBO terms.

Line 156, …:but ignore …’ (no ‘s’, as refers to a plural term, integrals)

Line 160. If it is valid to say so, you could add something along the lines of the following to give context. “Over the total 4-decade period since 1979, the maximum annual ozone reduction was approximately 13% at 70S, and smaller elsewhere. For example, the reduction was approximately 4% 45S, and 3% at 45N.”

Line 172. By “harder to see”, I presume you mean “less precise”. Please include error bars on your determinations of T_A., as this is the key new parameter that comes out of this work.

Line 172-173. I disagree with this statement. I agree that effects of the smaller El Chicon eruption are smoothed, but I can still clearly see what looks like a Pinatubo effect at 45N and 55N. (and at other northern latitudes in Fig 4).

Line 181. After “sharp downturn”, add the words “after around 2010”. Also, add a note that in Fig 4, the range of ozone differs markedly between rows.

Line 214. Change “led” to “leads” because that still happens (it may be best to change order of sentences too).

Line 203. There is no need to include Tables 1 and 2 because (as stated) the information there is the same as in Figures 5 and 6. The Tables could be included as supplementary data. Accordingly, remove or modify the sentence starting on line 203.

Line 222. I’d suggest a slight rewording, as follows: “However, computing the trends from either the MLR or annual average methods shows that the small decline from 15 to 65N is not significant at the 2s level (1.5 ± 2% per decade)”. I note that at no latitude shown is the change significant over this period.

Line 224. Fig 7. Please clarify whether the trend is over an 11-year period (as implied by the legend), or a 12-year period (as stated in the caption).

Line 233. Can you say anything comparable about the period prior to 2005 (see main point above).

Figure 6. Clarify punctuation in the caption. (a) ….., (b) ….

General Comments:

The authors use total column ozone data to determine the specific date at which the zonally averaged ozone stopped declining (referred to as T_A(θ)), which holds significance for atmospheric models. Subsequently, the trends of column ozone were calculated using MLR and linear regression, both before and after T_A(θ). The findings indicate that there has been only a minor recovery in the Southern Hemisphere towards the ozone levels observed in 1979, with virtually no recovery in the Northern Hemisphere, except for the Antarctic region. While these results present new insights, the robustness and interpretation of the findings require further reinforcement. Thus, significant revisions are necessary before considering the publication of this article.

Specific Comments:

Lines 83-86: The two trend research methods have distinct study areas, and it is important to explain why the MLR method might be affected by the polar night, potentially due to the solar cycle. Additionally, it might be more appropriate to include this discussion about the different study areas and the potential impact of the polar night on the MLR method within the introduction section of the methodology.

Lines 124-129: It would be better to provide more description for the Fourier-based MLR to clarify its difference from the generalized multivariate linear regression (MLR) discussed in the next paragraph.

Fig. 2: In addition to the difference in the latitude range studied by the two methods, it is worth noting that they also differ in terms of latitude intervals.

Although Fig. 3 demonstrates the fitting effects of different Lowess values (e.g., 0.05, 0.1, 0.3), it is necessary to provide a clear explanation as to why Lowess=0.3 was chosen as the optimal value in the final analysis.

The result mentioned in lines 176-177 lacks an accompanying visual display.

Fig. 4-5: Fig. 4 shows decrease in TCO after 2010 in North Hemisphere, and the authors indicated that “the apparent downturn in the Lowess(0.3) fit to MOD after 2010 is not yet statistically significant as an indicator of long-term decrease”. However, do the “Turnaround dates” (Fig. 5) calculated based on Fig. 4 in the North Hemisphere make sense statistically?

Fig. 5: The reason for the near symmetry in the early turnaround dates of the Brewer-Dobson ozone upwelling region (±25°) warrants further investigation. It is important to consider that there is considerably more longitudinal asymmetry in topography, land, and ocean distribution in the Northern Hemisphere (NH) compared to the Southern Hemisphere (SH). Consequently, the planetary wave drag may differ between the two hemispheres, which could contribute to the observed differences in ozone recovery patterns.

In lines 194-195, it is mentioned that the Spring Antarctic Ozone Hole and polar vortex winds led to a delay in high latitudes in the Southern Hemisphere (SH) until 1997. However, it is important to note that these phenomena should occur every year. Therefore, additional evidence, such as models or observations, is required to support the author's claim and provide a more robust explanation for the observed delay in high SH latitudes until 1997.

This paper's conclusions are not entirely consistent with those of Weber et al. (2022), despite utilizing similar data and methods. To explain the differences between the two studies, further analysis and investigation are needed. Possible factors contributing to the disparities could include variations in the data preprocessing techniques, differences in model configurations, or the incorporation of additional variables in one study compared to the other. A thorough comparison and evaluation of these factors may shed light on the discrepancies observed between the two studies.

Technical Comments

The abbreviation "TCO" should be defined and explained in line 53 rather than line 64.

The legend of Figure 4 (e.g., 35°N) should be revised.

In lines 216-218, the text presentation and punctuation should be adjusted for clarity and accuracy.

Review of Herman et al. Total Column Trends from the NASA Merged Ozone Time Series 1979 to 2021 Showing Limited Recovery to 1979 Amounts after Declining into the Mid 1990s.

GENERAL COMMENTS

The submitted manuscript presents an analysis of the 'Merged Ozone Dataset', calculating ozone trends using two different methods for 10 degree wide latitude bands, before and after a latitude-dependent "turnaround" time which the authors identify using Lowess smoothing.

This subject (stratospheric ozone depletion and recovery) is of iconic importance to the atmospheric sciences.

Further, the Merged Ozone Dataset itself has proven to be of enormous value within this field and the dataset has been well utilized for trend studies.  

However I believe the current work needs major revision before being suitable for publication.

The study of Weber et al. 2022, (hereafter W2022), referred to on multiple occasions by the present authors - but not sufficiently engaged with in my opinion - may be considered the conventional approach at the current time by the community, and forms one of the foundations for the 2022 WMO/UNEP Ozone Assessment. W2022 includes the MOD as one of the datasets analysed, along with four additional satellite and ground-based records.

The main differences between the analysis of MOD contained in W2022 and the present work are the use by the authors here of the latitudinally dependent turnaround time, and a somewhat different regression model.

In general, researchers experimenting with variations to the most popular approach is a good thing for science, but with it, there does need to be sufficient motivation, explanation and comparison provided along with it, otherwise it offers no value in addition to what has already been done.

In this case I believe the authors need to explain their reasoning much better.

I like the use of heavy smoothing to enable the low frequency changes in the ozone timeseries to appear more clearly. However, the significance of the "turnaround" times identified by the smoothing is not clear to me. The word "turnaround" can only have meaning in the context of a long-term decline followed by recovery (or vice versa). The authors seem to really mean by "turnaround" the first local minimum since 1979. As can be seen in Figure 4, for some latitude bands the first minimum does not show much evidence of being a "turnaround" at all, as the identified time point was later followed by relatively large decreases and even oscillations in subsequent years. This is quite different to picking a turnaround year based on EESC, where calculating before-and-after trends is in effect a test of the hypothesis that ozone levels are following ODS concentrations, once other identifiable influences have been accounted for. It is of course always possible to calculate a trend between any two arbitrary years, but what does it tell you?

My second major concern is related to this point, which is that the choice of regressors in the regression model here seems quite odd to me, and more appropriate for tropospheric ozone rather than stratospheric. There is no dynamic term of any sort and no term for stratospheric aerosol.    

This lack limits the interpretation of the trends calculated, particularly in the light of Figure 4, and the conclusions offered currently in the manuscript are similarly extremely limited.  

The details of the regression are also not properly explained, and the overall ability of the regression model to fit the timeseries in each band is not given, either in total or for the different regressor variables.

Further, I note, with a small number of exceptions, there is a general lack of engagement with the literature from the last ten years or more which is disappointing.

Specific Comments

Lines 37-67 Most of the introduction talks about the Antarctic ozone hole, which is not the focus of the rest of the work. The introduction barely mentions ozone depletion in the mid-latitudes or tropics, which is the main focus of the rest of the work.

Line 43 In fact, most of the activation takes place on liquid droplets, eg Tritscher et al.

Line 71 Dameris and Baldwin 2012 is nicely written but there has been a lot of work on this subject since then.

Line 95-96 This is quite a hand-waving comment, and doesn't explain why the spring build-up is smaller in the SH than the NH for example.

Line 99 Is that true? What about the TOMS/OMI series? (Perhaps it can't be called continuous).

Line 124 I would not say MLR is necessarily 'Fourier based', just that your implementation is.

Line 131 What is the meaning of 'generalized' here?

Lines 139-141 You should give the source of the data you are using for the proxies.

Line 142 I assume the five coefficients rather than seven is as a result of p in equation (2) only running from 1 to 2 rather than 1 to 3?

Line 148 When you say "the linear deseasonalized trend" do you mean the constant term, b0?

Lines 148-149 As mentioned earlier, you should give some indication of how successful the regression model is in being able to account for both short-term and long-term variations in ozone, preferably breaking down the influence of each of the proxy terms.

Lines 155-157 I don't feel you have explained the second method adequately. I take it to mean you are simply fitting a linear trend to the annual ozone averages – is that right? What is the motivation of the second method?

Lines 163-165 The text implies to me you are considering this range of turnaround times to represent the ozone response to EESC changes – if not, how can you talk about "the" "turnaround"? I would like to see your thinking much better explained here.

Lines 173 I don't think it's true that even your heaviest smoothing removes the effect of Mt Pinatubo, it still seems evident at both 45 N and 55N in Fig 3.

Lines 174-176 Do you have any basis for making this statement?

Line 177 You don't show 5 S and 5 N in Fig 3 though.

Line 192 Why does the turnaround year vary across this range of latitudes then? (ie it's markedly earlier at the equator).

Lines 194-195 Do you have any basis for making this statement?

Lines 198-200 This would only be true if the model is driven by observed dynamics though, and includes all relevant factors such as stratospheric aerosol, wouldn't? How do you know it isn't unforced variability?

Line 205 – In Weber et al. 2022, their Figure 3 shows that the pre- and post-  trends (after regressors have been accounted for) are approximately in a ratio of 3:1 as expected from EESC – this doesn't seem to be so for your calculated trends.

Lines 214-215 Do you mean, mixing of ozone-poor air from the vortex into the midlatitudes?

Lines 235-251 I would like to see some discussion of the meaning of your results in the conclusion, and comparison with other work.

Lines 253-274 You should discuss the fact that you're comparing total ozone with stratospheric ozone and why you presumably don't think changes in tropospheric ozone over this period need to be considered.

Line 272 The discrepancy in the tropics looks like it might well be real – what do you have to say about that?  

References

Tritscher, I., Pitts, M. C., Poole, L. R., Alexander, S. P., Cairo, F., Chipperfield, M. P., et al. (2021). Polar stratospheric clouds: Satellite observations, processes, and role in ozone depletion. Reviews of Geophysics, 59, e2020RG000702. https://doi.org/10.1029/2020RG000702

World Meteorological Organization (WMO), Scientific Assessment of Ozone Depletion: 2022, GAW Report No. 278, 509 pp., WMO, Geneva, 2022.