The manuscript presents an important piece of work to evaluate tropospheric ozone trends for 30 years or longer from ozonesonde and surface measurement and from two chemical models. The authors have conducted a careful analysis on the trend calculation, compared the consistency and inconsistency with previous studies, uncovered the model disability to reproduce the ozone trends, and discussed the possible reasons. In general this work is well-motivated, the analyses are comprehensive and easy to follow. Using two global models for long-term ozone trend analyses is particularly appreciable. Interestingly at almost the same time another paper comes up in ACPD using the same model (GEOS-Chem) to evaluate and attribute global tropospheric ozone trends (Wang et al., 2022, ACPD, in review), and I am glad to see that the two papers review the same important topic, and consistently point to the positive ozone trends from observations and the challenge for model to reproduce these trends.

I recommend this work to be published in ACP after moderate revisions. Below are some questions and comments that may help the authors to further strengthen their analyses and improve the presentation.

1. Terminology. The authors may use term “background ozone” or “baseline ozone” in literature review and analyses (e.g. Line 97, Line 474, Line 202, …). Please try to clarify the terms when they first appear in the text. The authors may have known that policy-relevant background ozone has a more rigorous definition in US as ozone concentration without national anthropogenic sources. This should not be the same as “rural” defined in TOAR. Is there a clear definition on “baseline ozone”?

2. Trends from ozonesonde and their representativeness of free tropospheric ozone. The robustness of trends derived from ozonesonde is an important topic being argued a lot. The authors have tried to make sure that they select ozonesonde sites with frequent sampling and the trends are consistent with surface sites nearby. I appreciate all the efforts. There are also studies suggesting that more profiles per month are required for robust trend quantification at a single ozondesonde site, and aircraft observations from the IAGOS project may provide better quantification of tropospheric ozone trends (Gaudel et al., 2020; Chang et al. 2020, 2021). I wonder whether the authors can try to reconcile their analyses with these existing literatures. It would be great if the authors can also utilize the aircraft (IAGOS) observations for evaluating the ozonesonde trends but if not some discussions are also acceptable.

3. GEOS-Chem sensitivity simulation. I appreciate that the authors applied the UCX scheme in their GEOS-Chem simulation for a better presentation of stratospheric chemistry. I wonder when the authors fixed anthropogenic emissions in their sensitivity simulation, did ozone-depletion-species also be fixed in the model? Or in other words, whether stratospheric influences from GEOS-Chem should be analyzed from the “Meteorology” simulation or in the “Emission” simulation? This should be clarified both in Section 2.2.1 and in Section 5.2.

4. GMI vs GEOS-Chem simulations. The authors use two chemical models and find that the GMI model produces larger ozone trends than GC. I am curious that whether the difference in anthropogenic emission inventory (and trends) may contribute. Could the authors show the emission trends used in the two model?

5. Section 3.3. In Figure 5 we see a site in eastern China with negative surface ozone trend that is not consistent with other site in the East Asia. Is this negative trend spread across all seasons? Is there any previous report that explains the negative trend?

6. Section 3.4, Line 489-492: I didn’t get clear information from the analyses at WLG site. The authors argue that “expect similar trends in the Japan FT since increasing ozone over Japan is influenced by transport from China”. But WLG is located at the west of the eastern China (not influenced by polluted outflow there), while the Japanese sites may by affected by the outflow but should mostly be constrained in springtime, why we should expect similar ozone trends at both sites?

7. Line 497: where does “up to 1.7 ppbv per decade” come from?

8. Line 517: What does “primary influences” mean?

9. Section 3.5. I few that the title of “Drivers of observed ozone change” is misleading. I am not sure whether the change of 5^th ozone alone can be used to indicate ozone drivers of emission or transport. Why not integrate this part with the model sensitivity studies? In particular, I am not convinced by the statement in Line 549 that “multiple previous analyses suggest that regional ozone increases are best explained by transport”. Transport from where? Why transport is a more likely reason than NOx reduction to explain 5^th ozone increase in US and Europe?

10. Line 566-567: Again, it would be important to compare the emission trends used in GMI and GC.

11. Section 5.1. Line 690-691. Wang et al. (2022, in review) shows that aircraft emissions may be an important source of trend underestimation in chemical models.

12. Section 5.2. I am curious about the stratospheric influence on tropospheric ozone. First, are both models show consistent pattern of ozone trends in the upper troposphere and lower stratosphere? A latitude-altitude plot of modelled ozone trends from the two models would be plausible. Second, I wonder what processes may contribute to increasing STE in the GMI model, is it more likely due to recover of ozone hole or changes in STE dynamics?

Reference:

Chang, K.-L., Schultz, M. G., Lan, X., McClure-Begley, A., Petropavlovskikh, I., Xu, X., and Ziemke, J. R.: Trend detection of atmospheric time series: Incorporating appropriate uncertainty estimates and handling extreme events, Elem. Sci. Anth., 9, 10.1525/elementa.2021.00035, 2021.

Chang, K.-L., Cooper, O. R., Gaudel, A., Allaart, M., Ancellet, G., Clark, H., Godin-Beekmann, S., Leblanc, T., Van Malderen, R., Nédélec, P., Petropavlovskikh, I., Steinbrecht, W., Stübi, R., Tarasick, D. W., and Torres, C.: Impact of the COVID-19 Economic Downturn on Tropospheric Ozone Trends: An Uncertainty Weighted Data Synthesis for Quantifying Regional Anomalies Above Western North America and Europe, AGU Adv., 3, e2021AV000542, 10.1029/2021AV000542, 2022.

Chang, K. L., Cooper, O. R., Gaudel, A., Petropavlovskikh, I., and Thouret, V.: Statistical regularization for trend detection: an integrated approach for detecting long-term trends from sparse tropospheric ozone profiles, Atmos. Chem. Phys., 20, 9915-9938, 10.5194/acp-20-9915-2020, 2020.

Gaudel, A., Cooper, O. R., Chang, K.-L., Bourgeois, I., Ziemke, J. R., Strode, S. A., Oman, L. D., Sellitto, P., Nédélec, P., Blot, R., Thouret, V., and Granier, C.: Aircraft observations since the 1990s reveal increases of tropospheric ozone at multiple locations across the Northern Hemisphere, Sci. Adv., 6, eaba8272, 10.1126/sciadv.aba8272, 2020.

Wang, H., Lu, X., Jacob, D. J., Cooper, O. R., Chang, K.-L., Li, K., Gao, M., Liu, Y., Sheng, B., Wu, K., Wu, T., Zhang, J., Sauvage, B., Nédélec, P., Blot, R., and Fan, S.: Global tropospheric ozone trends, attributions, and radiative impacts in 1995–2017: an integrated analysis using aircraft (IAGOS) observations, ozonesonde, and multi-decadal chemical model simulations, Atmos. Chem. Phys. Discuss. [preprint], https://doi.org/10.5194/acp-2022-381, in review, 2022.

Review of Multidecadal increases in global tropospheric ozone derived from ozonesonde and surface site observations: Can models reproduce ozone trends?                                                                                    

By Amy Christiansen, Loretta J. Mickley, Junhua Liu, Luke D. Oman and Lu Hu

This is an excellent paper, and certainly appropriate for publication in ACP. I have just a few points that the authors should address before publication.

My main concern is that the authors are a bit too casual about possible bias changes in the ozonesonde data and the way that may increase uncertainty in their derived trends. For example, the Japanese stations changed from the KI sonde to the ECC sonde in the 2000s. The authors cite Tanimoto et al. (2015) to claim “…but this switch did not impact long-term trends”. That is unlikely; even a difference of a few percent in average response can induce a large error in calculated trends. Figure 5 of Tanimoto et al. does in fact indicate a difference of this magnitude. Minor instrument changes or changes to preparation procedures can also make significant differences, as the effect of data revisions shows (see, e.g. Figure 15 of Tarasick et al., 2016). These additional uncertainties are more difficult to estimate than the statistical uncertainty output by standard packages, but they should be considered and discussed.

Minor points:

Line 16: “…suggesting the importance of emissions in observed changes.” Or of surface (land use) changes?

Line 20: “…reflect the global increase of background ozone.”  Really? I would have thought this reflects the reduction of NOx due to emission controls. But this should then be more evident at sonde sites with more urban influence, so the authors could perhaps say something about this.

Lines 69-74: These are large differences. Can the authors offer any explanation for the wide range of estimates? Also, please quote trends either in per year or per decade: the mixture of units is confusing to the reader.

Lines 79-81: “The impact of STE on tropospheric ozone trends is potentially substantial: the observed interannual variability of the Brewer-Dobson circulation in the stratosphere leads to changes of ozone levels in the northern mid-latitudes of ~2% (Neu et al., 2014).” This sentence seems at first to contradict itself, especially since the point of the Neu et al. paper was that the impact of STE on tropospheric ozone variability was NOT substantial. The authors should make it clear that they are referring to short-term trends.

Lines 121-122: The authors should also note the endpoints for the Tarasick et al., 2016 trends (1966/1980-2013). This may be one reason for “mixed” results.

Lines 135-138: “Parrish et al. (2014) and Staehelin et al. (2017) showed that four state-of-the-science chemistry-climate models overestimate the absolute ozone mixing ratio by 5-17 ppb at mid-latitude background sites and capture only about half of the observed ozone increase over the last five decades…”.  Actually, no. A much more comprehensive analysis by Tarasick, Galbally, et al. (2019), which examined biases in historical measurements in great depth, has found smaller increases in surface ozone, of the order of 50%, which are in general agreement with model predictions. In addition, the analysis of ice-core data by Yeung et al. (2019), which the authors cite, and the independent analysis of aircraft and balloon data by Tarasick, Galbally et al. (2019), also both support a smaller increase of surface ozone, of the order of 50%.

Line 186: How interpolated? Are these integrals between midpoints, or a point estimate?

Line 190: Figure 1 is nice, but a table identifying the ozonesonde sites, and the dates of their records (as well as breaks, for sonde type, or other reasons) would be very helpful.

Figure 3 caption: It would be helpful to restate here that the points correspond to the 47-layer GEOS-Chem reduced pressure levels.

Figure 4: How are the 800-400 hPa values calculated?

Lines 453-454: “Our results are consistent with other global analyses of surface ozone data …”  Some citations are in order here.

Line 473: “baseline ozone”. What is “baseline” ozone? The authors also refer to “background” ozone. Are they the same?

Line 515: Note that Syowa also changed from CI to ECC sondes.

Lines 544-545: I’m not sure that the increases in 5th percentile ozone due to decreased titration from NOx would necessarily translate to global changes in ozone. This could be a localized effect, more evident at sonde sites with more urban influence.

Lines 681-684: As noted previously, the large Parrish et al. (2014) estimate of the ozone change has not been supported by subsequent analysis (Tarasick, Galbally et al., 2019; Yeung et al., 2019), so a finding that this is “consistent with our current analysis” may not be the best advertisement for the authors’ work, especially to lead this section. However, Tarasick, Galbally et al. also found that “…the uncertainty in the estimated increases … depends more on the modern region chosen for comparison than on the historical data. Data representativeness [of modern data] thus seems to be the more important source of uncertainty.” The authors may want to mention data representativeness; it’s an important topic, and especially pertinent when one is using only a small number of observation sites for evaluation of models.

Line 688: Characterizes? Something is wrong with this sentence.