This manuscript attributes trends and seasonal cycles in ozone metrics (PSO and MDA8) across Europe and North America to NOx and VOC sources. Some key findings include that declining local emissions of NOx contribute to decreased O3 production in summertime but increasing import of foreign precursors leads to increasing winter and springtime O3; that natural VOC and local anthropogenic NOx are often linked in their formation of O3; and that foreign NOx is now of similar magnitude to local NOx in terms of contribution to O3 formation in several locations.

These findings are achieved using a model in which the precursor molecules are tagged by source and location. This is a considerable amount of work, which has yielded novel results. The conclusions are of interest to the community and the work fits well into the scope of the journal and special issue.

Although long, the text is clearly written and the conclusions are well supported by the data. I would recommend this manuscript for publication with only a few amendments/suggestions.

General comments

The methodology is very clear on several aspects such as the emissions inventories but no detail on the chemical model itself – how many species and reactions, how are VOC and oxidation products treated / lumped? The text refers to MOZART but it’s never explicitly introduced that you are using this scheme.

The structure of the manuscript is ok as is but perhaps could be improved. Some of the results sections begin with several large paragraphs of introduction before any results are given. Some of this text may be better placed in, or is perhaps a repeat of, the methods sections. Similarly, descriptions of figure 2 would work in the results rather than the methods.

The individual regions are described independently but never compared. Are there any key differences between regions that could be highlighted in the conclusion? If not, do all the regions need to be described in such detail?

The difference in emissions reductions between western and eastern Europe is highlighted as a reason why PSO trends may differ regionally but this hypothesis is never confirmed. There don’t seem to be large differences in PSO changes over time between the regions. Is that correct? If so, can you suggest why? A follow-up on this introductory point is needed somewhere.

The conclusion could be developed somewhat, for example by comparing the difference regions and Europe vs the US (the US emissions reductions seem more successful at reducing O3?) as stated above. There could also be greater discussion on some of the uncertainties – are emissions inventories the greatest source of uncertainty in your study? I would finally also be interested in your thoughts on how this novel tagging approach could be used in future studies – could it play a role in bias correction and identification?

Data should be made publicly available according to Copernicus guidelines

Units and trend analysis should follow the TOAR special issue guidelines. Just check if any of those are relevant to this work.

Specific comments:

L26: a concluding sentence could be useful here.

L45: In case you would like the more recent publication: Cheesman, Alexander W., et al. "Reduced productivity and carbon drawdown of tropical forests from ground-level ozone exposure." Nature Geoscience (2024): 1-5.

L56: It is worth being clear that the O3 precursors can also be transported, since this is the key part of the study.

L210-214: This is slightly hard to follow and explained much better in Table1 and the associated table caption. I would suggest you direct readers to this table earlier. I would also suggest on L213 to replace ‘many zones’ with the specific number of zones.

L230: if you plan to refer to anthropogenic VOCs as AVOCs this could be introduced earlier and then used consistently throughout (such as in the figure labels)

L226-250: This reads as results rather than methods to me. Certain aspects such as AVOCs showing an increasing trend from 2013 and global lightning NOx showing a decreasing trend are interpretations of the figure. Consider moving this to the results or giving its own subheading in the methods section.

Section 2.2 could be condensed. The definition of MDA8 is essential but the wallclock time in your specific set up could be left out.

In figure 3, is it possible to just show the source regions being considered? It is a bit unclear which 5 regions of N America and Canada are being selected at this stage.

L305: Inhomogeneous measurements combined with changing numbers of stations over time can lead to errors in mean and trend identification. An acknowledgement of the uncertainty in the observational trends would be helpful here. Christoph Frei has done a lot of work on this for temperature and precipitation fields.

L382: I agree the simulation of MDA8 against rural stations is very nice. I am not sure what the satisfactory performance across different world regions refers to.

L387: What is a 19 year month centered average MDA8 O3 broken down into 5 years?

L406: A reminder of the PSO guideline could be useful here.

L444-446: Is it possible for the PSO to be ‘single handedly’ linked with local AVOC and then linked to declining NOx emissions in the following sentence?

L525: I would pedantically argue that all ozone is equally destroyed by water, but long-range transport ozone is more likely to encounter it.

L558: perhaps refer back to the figures here

L738: Can you say why local NOx and BVOCs are so interlinked? This is an interesting finding.

Technical points:

L22: ‘productivity’ could be replaced with ‘O3 production’ or similar for clarity.

Figure 7 b/d is mislabelled in the figure caption. Same for other figures of this layout.

Figures 2 and 3 are sometimes referred to incorrectly in the text (e.g. Fig 2 written instead of Fig. 3 and vice versa)

Summary:

This paper presents a global modelling study with an innovative dual tagging analysis; the paper’s focus is on surface ozone over North America and Europe, particularly with regard to the causes of long-term changes and the seasonal cycle and its changes. In my view, the work appears to employ a state-of-the art modeling system and addresses an interesting scientific issue. However, ACP aims to publish studies with important implications for our understanding of the state and behavior of the atmosphere; I believe that the paper at present fails to advance this aim. Thus, I recommend that this submission be rejected and the paper returned to the authors with encouragement to resubmit if the authors can address 3 critical issues:

• Significant questions remain both regarding the evaluation of the modeling system and the possible corruption of observational data upon which the model evaluation and analysis are based.
• A more quantitative approach to analysis would improve the paper, both with regard to discussion of present results and discussion of comparisons and contrasts with previously published analyses.
• A clear summary is required of what new understanding of the atmosphere has emerged from this study, including the added value of the dual tagging approach, and when and for what issues that approach is required in such modeling studies.

More detailed discussions of these issues follow. In addition, several related and unrelated, major and minor issues are discussed that may be of use to the authors for their revision.

Critical issues:

• Section 3.1 is devoted to evaluation of the CAM-Chem model used in the chemical-transport simulations. In my view a much more robust evaluation is required as outlined in the following paragraphs; I believe that, in general, such evaluation is necessary before model simulations can be relied upon to provide robust results.

One aim of the authors is to explain the seasonal cycles and their changes observed in surface ozone; thus the model evaluation should move beyond an overall statistical comparison of monthly mean concentrations between model and observations; it is necessary to specifically and quantitatively evaluate how well the model reproduces the phenomena of interest, in this case the seasonal cycles and their changes. The three paragraphs on lines 339-372 discuss aspects of such an evaluation, but only qualitatively; this evaluation should be placed on a quantitative basis. Of concern are the findings in previously published intercomparisons of model simulations with observed seasonal cycles of ozone. Parrish et al. (2016) discuss such intercomparisons for marine boundary layer (MBL) sites and in the overlying free troposphere above one site. Three chemistry climate models, including a version of the CAM-Chem model used in the present study, approximately reproduced many features of the measured seasonal cycles within the  MBL, with some notable quantitative disagreements, but gave divergent results that do not agree with measurements above the MBL. Bowman et al. (2022) discuss a similar intercomparison that considers both the seasonal cycles and their systematic changes at northern midlatitude baseline locations. The available observational data were compared with simulations by 6 Coupled Model Intercomparison Project Phase 6 (CMIP6) Earth system models, again including a version of the CAM-Chem model. Substantial differences were found  between the different model simulations and between the simulations and the observations. To my knowledge, the model disagreements revealed in these intercomparisons have not been addressed in later model development. A quantitative evaluation such as presented in these two papers should be included in the present manuscript.

The authors primarily rely on an overall statistical analysis of the agreement between model simulations and observations of monthly mean ozone in specific regions. Their final conclusion (line 374) is: “Overall, we obtain very good model-observations agreement, with low biases and high correlations, ….” Three issues must be addressed regarding this conclusion. First, this evaluation is limited to comparison between model results and observations of time series of MDA8 ozone that are highly averaged, both temporally (monthly) and spatially (first over model grid cells and then over receptor regions); it should be discussed if this averaging of model result is appropriate in the context of the model results that the authors employ in the following discussion of results. Second, for the 10 receptor regions discussed in the paper (shown in Figure 4) and 5 additional receptor regions (shown in Figure S1) the average of the mean biases is indeed small (1.75 ppb), but more context is required for these mean biases. The regional mean biases range from -9.57 to 8.84 ppb, giving an overall regional mean absolute bias twice as large (3.50 ppb) as the overall mean bias. These statistics provide some evaluation of model performance in simulating average ozone concentrations, but the paper aims to quantify ozone “trends and changing seasonal cycles”. It is clear from examination of Figures 4 and S1 that there are significantly larger deviations between the observations and model results for the individual monthly means than are reflected in the regional mean biases. The authors should give a more detailed view of the time series comparison including discussion of an additional statistic (I suggest mean absolute difference), which would more relevantly quantify the differences of monthly means between model results and the observations – it is these differences that are of most importance with regard to comparison of seasonal cycles and their changes.

Second, the high correlations the authors cite (generally r > 0.9) are a) expected and b) not universal (3 of 15 r values are 0.62 or smaller); large r values are expected simply because the variability in both model results and observations is dominated by large seasonal cycles that are approximately in phase; if annual averages were compared, the correlations would be much lower. Examination of the figures strongly suggests that the smaller r values very likely indicate spurious observational data; the origin and influence of these spurious data must be assessed as discussed further below.

Third, from a skeptical viewpoint, we must be mindful of a subtle issue associated with model-observation comparisons such as the authors present in Section 3.1 (and that are also utilized in many such comparisons in the published literature). Chemical transport models do not treat all relevant processes from first principles of physics and chemistry; rather there are a great many parameterizations embedded within the computer code of the models. Over past decades those parameterizations were developed and tuned so that the models reproduce mean observed ozone concentrations as closely as possible. Consequently, attempting to evaluate the performance of models simply from comparison of means of observations with model results involves a degree of circular reasoning – the models were developed to agree with observations, so such agreement cannot be taken as independent confirmation that models perform properly for the correct reasons.

Finally, the treatment of ship emissions and possibly the MBL structure constitute one apparent shortcoming in the modeling methodology that must be addressed; I believe this is a wide-spread shortcoming of chemical transport models, and has significant impact on this study’s results. The model treatment of ship emissions is not discussed in detail in Section 2, but the authors do quantify ozone produced from this emission source. Unless the model includes some sort of plume-in-grid treatment for ship plumes, it must be expected that the influence of ships is signficantly exaggerated (e.g., Kasibhatla et al., 2000). I am aware of only a single observational study that provides a detailed characterization of ship plume evolution (Chen et al., 2005). This study shows that the photochemical perturbation of the marine boundary layer (MBL) due to a ship plume is largely limited to the first few hours of plume evolution, while the plume is still narrowly confined (FWHM ~ 3 km). Thus, an effective model resolution < 1 km is required to accurately treat ship emissions. However, I suspect that the model utilized in this study (as well as many other studies) immediately distributes the ship emissions throughout the 1.9⁰×2.5⁰ model cell; this is expected to lead to a large overestimate of ozone production from ship emissions.

One zeroth-order check that the authors should perform is a comparison of their total marine ozone production from ship plumes with their total ship emissions NOx during the photochemical active season of the year; approximate agreement with a 4.25:1 mole/mole ratio is expected (i.e., production of 10 O₃ molecules per NOx emitted during the day, based on the Chen et al., 2005 study), and loss of 1.5 O₃ molecules per NOx emitted during the night, assuming that NOx is lost as N₂O₅ at night). Duncan et al. (2008) further discuss this issue. This comparison should be limited to ozone production from ship emissions within the MBL at northern mid-latitudes.

A second zeroth-order check that the authors should perform is a comparison of their simulated vertical profile of ozone within and directly above the MBL with observations. Ozone sonde data from Trinidad Head (e.g., Fig. 15, Oltmans et al., 2008, Fig. 12, Parrish et al. 2016 or Fig. 1, Parrish et al., 2022) are available; these represent the marine environment, so they should be compared with model simulations from a grid cell offshore of northern California. Note that Fig. 12 of Parrish et al (2016) compares the measured vertical gradient of ozone with simulations from 3 global models, one of which is a version of CAM-Chem model that was used in the present paper. Importantly, the observed strong near-surface vertical gradient of ozone over the ocean clearly indicates that the MBL is a region of strong domination by ozone loss; a spuriously large ozone source within the MBL, such as overestimate of the ship emission source, would be expected to disrupt the relatively strong vertical gradient through that level.  Notably, none of the 3 models reproduced the observed ozone gradient within the MBL.

There are also indications of possible corruption of observational data relied upon in this paper. As noted earlier, Figures 4 and S1 include data that disagree strongly with model simulations and are simply physically unreasonable (e.g., too large in Fig. S1d and too small in Fig. 4i). Further, the authors discuss an anomalous drop in 2012 in the number of rural TOAR stations. Figure S8 shows that this drop was only in the US, not Europe, although southern Europe shows a peak in 2012 and western Europe shows a drop in 2017, both of which are unexplained. Northeastern US also shows a rather large increase in site number after 2015. The US ozone data are available from the US EPA data archive; that archive does not include the TOAR site classification, but the total number of US sites reporting ozone observations increased from 1241 in 2000 through 2010 and remained relatively constant at about 1450 for the three 2011-2013 years, followed by an accelerating decrease to 1231 by 2024. There is no indication of a drop in the number of stations in the US in 2012. Since the US monitoring network remains relatively constant from year-to-year with only small numbers of stations coming on line or closing, and with no systematic movement of sites to or from rural areas, it is clear that the data that the authors extracted from the secondary TOAR archive does not accurately reflect the parent EPA archive from which the TOAR data were obtained. These two features of the observational data make it imperative that the source of these problems be tracked down, and the observational analysis included in this paper be thoroughly evaluated and revised as necessary before included in a submitted manuscript.

• Sections 3.2 and 3.3, which comprise nearly half of the paper, present and discuss the results of the study. However, the discussion is largely a qualitative catalog of features apparent in the observations or model results. That discussion should be extensively revised to replace that qualitative catalog with more systematic and quantitative analysis approaches of the model results, comparisons between model results and observations, and between results in different receptor regions. The separation of long-term changes from the seasonal cycle (i.e., detrending the data before analyzing the seasonal cycle) is often very important, but the trends in ozone over the 2000-2018 period are so weak that this is not essential in this study. A Fourier series or spectral analysis, such as used by Parrish et al. (2016), Bowdalo et al. (2016) and Bowman et al. (2022) is recommended.

Sections 3.2.1, 3.2.2 and 3.3.1 are primarily successive, isolated discussions of the ozone contributions in successive receptor regions, and much of this discussion is repetitive between regions. The authors provide little context for this discussion, so the reader is faced with unconnected qualitative descriptions and numbers; an improved organizing context is needed. I suggest that the authors successively discuss each of the ozone contributions over all receptor regions in these sections, much as done in Section 3.3.2. For example, it would be informative to compare and contrast the anthropogenic NOx contributions to ozone in the receptor regions. As expected, Figure 5 shows that contribution decreases along western North America from the Southwestern US (with many large urban areas) to the Northwestern US (with few large urban areas); in this regard, it would be useful to include the western Canada receptor region, which is not similarly discussed in the paper. It would also be of interest to quantitatively examine the correlation between that ozone contribution and the total local anthropogenic NOx emissions over all receptor regions.

Insightful comparisons and contrasts with previously published analyses are essential. The quantitative results derived by the authors should be compared and contrasted with published results obtained by similar or differing analytical approaches to those quantifications; this further discussion must be based upon an in-depth literature review of published analyses of ozone trends and seasonal cycles and their changes over North America and Europe. Two specific examples of potential literature comparisons are summarized below; these examples should be considered as illustrative, but not as a comprehensive list of needed discussion topics.

Of great interest would be to fit the temporal evolution of the local anthropogenic contribution in each receptor region to an exponential function, rather than the linear analysis the authors employ. Parrish et al. (2025) and papers cited therein have shown that local anthropogenic enhancements of surface ozone in North American regions have decreased exponentially with a time constant of 21.8 ± 0.8 years. From similar analyses, Derwent and Parrish (2022) report exponential time constants for the local anthropogenic contribution of 18 ± 4 years over the United Kingdom and 37 ± 11 years over continental Europe. Comparison of the present model results to those observationally derived results would be quite useful.

Multiple other modeling studies have reported contributions to ozone that differ quantitatively from the present results. For example, Mathur et al. (2022b) find that “stratospheric O₃ (ranging between 6 and 20 ppb) constitutes 29%–78% of the estimated Spring-time background O₃ across the continental United States” while the present paper quantifies significantly smaller impacts: “the stratosphere contributes up to 6-8 ppb in the Southwestern US” (the US region of maximum stratospheric influence) and 4-7 ppb in the Northeastern US. Comparisons and contrasts of quantitative estimates from multiple studies are required in this paper.

• A clear and concise summary of what new understanding of the atmosphere has emerged from this study is lacking. The final section of the paper discusses Conclusions, Limitations and Future Outlook; it lists many findings, but it is not clear to me either what is new in this analysis, or which of the findings required the dual tagging system to uncover. That material should be revised to clearly and specifically answer several questions: What new knowledge of atmospheric chemistry emerged from this work? The paper does utilize a relatively novel tagging approach; can the authors provide the reader with a concise summary of when or for what issues the joint NOx and VOC source tagging is required? Or can they at least clearly summarize what additional information was provided by that technique in this study? (After all, the technique does greatly complicate the analysis, and in the end the added benefits are not clear to me.)

Major issues:

• The format of Figures 5 and 9 should be improved to better illustrate the authors’ discussion. Most of the source contributions are so small that their magnitudes and variation are difficult to discern in the present format. Improvements should include a) using a more nearly square format to more clearly show any systematic changes over the two decades, and b) perhaps using a log-scale for the ordinate to more clearly illustrate the magnitude of all source contributions. The nearly square format would be more easily obtained by a) moving the region labels into blank spaces within the graphs and b) by not repeating the years on the abscissa of each graph. (Similar comments apply to Figures 7 and 10.) The log-scale would also be more appropriate for showing the long-term ozone changes due to changes in anthropogenic emissions, since those emissions are expected to decrease in an approximately logarithmic fashion (i.e., linear on the log scale). Figures 6, 8, 11 and 12 are more readable, but could be improved by changing the ordinate scale to 0 to 30 in the 2^nd and 3^rd column graphs; this would cut off the top of the anthropogenic NOx contribution for the NE US, but it would be useful to duplicate this contribution in all of the 1^stcolumn graphs.
• In Section 3 the authors discuss the long-term changes in ozone and its components in terms of linear trends derived from a Theil-Sen approach; these trends are collected in Table S1. Several issues should be discussed in this regard. First, the emissions illustrated in Figure 2 appear to be non-linear; thus, at least some of the long-term changes can be expected to be non-linear. The authors should discuss why they employ a technique that can only quantify the linear aspects of the long-term changes. Logan et al. (2012) quantify changes in linear slopes (i.e., trends) over a 3 decade long data record; perhaps such an analysis should be employed in the present discussion? Second, the authors report values they derive for the significance of their derived trends; this significance only informs us regarding whether the trends are significantly different from zero (it is not clear to me what is implied by a trend of zero with a significance of 1 – that seems nonsensical). The authors should report 95% confidence limits for their derived trends if they indeed judge a linear analysis is adequate to quantify statistically significant long-term changes; these confidence limits are of much greater interest than the significance statistic, as they provide a basis for judging quantitative comparisons such as the authors give on lines 451-453; as presently written, it is not clear that the -0.24 ppb/yr (1.0) trend derived from the observations differs significantly from the -0.35 ppb/yr (0.99) trend derived from the model results. Finally, and most importantly, the significance values (and potentially any calculated confidence limits) are apparently greatly over-optimistic. If I understand correctly, each region has only a single PSO value each year. Given the limited (i.e., 19) number of PSO values combined with the relatively large interannual variability and autocorrelation that characterize observed time series of ozone concentrations, only modest significance values (and relatively wide calculated confidence limits) are expected. Importantly, for time series of annual PSO values, autocorrelation over multiple year must be considered in deriving reliable confidence limits. Fiore et al. (2022) discuss this issue more fully.
• More generally, the authors provide few confidence limits for the quantitative numbers given. It is generally acknowledged that any scientific paper presenting results of quantitative analysis must include confidence limits for the quantitative findings. This last comment applies to all of the quantitative results presented in the paper. I realize that it is difficult to quantify confidence limits for model results; nevertheless such quantification is essential. Developing such confidence limits could come both from the additional statistical analysis indicated as needed in the first Critical Issue discussed above, better quantitative treatment of the seasonal cycle and its shifts as suggested in the second Critical Issue, also discussed above, and further bolstered from quantitative comparisons of the results from the modeling study presented in this paper with other observational and modeling results, again indicated as needed in the second Critical Issue.
• The sentences on lines 496-499 are contradictory and obscure an important point: “The model reproduces the 19-year average seasonal cycle over different parts of North America very well. For western regions, we see a consistent systematic positive bias of 2-4 ppb. For  eastern regions we see a very good reproduction of the seasonal cycle during winter and spring but a notable overestimation during summertime (italics added).” The italicized words are where the contradiction arises. The authors further discuss the summertime overestimate, in multiple places. I suggest a single, consistent discussion of this feature over all of the North American regions.
• Lines 532-533 state that “Figures 6e and f show the average seasonal cycle of MDA8 O3 in Southwestern US which is similar to that for the Northwestern US ….” I agree that the shapes are somewhat similar between the two regions, but the minimum-maximum difference is significantly smaller in the Southwestern US (~12 ppb) than in the Northwestern US (~22 ppb). This mis-judgement, evidently based on a qualitative assessment of Figure 6, emphasizes the need for the utilization of a quantitative analysis of the ozone seasonal cycles, as detailed above in the discussion of second Critical Issue. There is a similar but smaller mis-judgement in the following comparison of the Southeastern US and Northeastern US seasonal cycles.

Minor issues:

• Line 31: The phrase “… especially towards the end of the 20th century” would be more accurate if changed to “… especially during the last half of the 20th century”. Substantial ozone increases in the troposphere have been documented over that entire period.
• Line 56: The authors state that “This is due to the long-enough atmospheric lifetime of ozone (about 3-4 weeks) which allows it to traverse intercontinental distances and affect the air quality of regions far from the location of its chemical production or the location of the emission of its precursors.” This statement is true as written, but should be discussed a bit further. The loss processes leading to that lifetime are dominated by loss in warmer, more humid tropical regions. Further, this lifetime refers to the total photochemical loss processes integrated over the entire globe; considering net ozone tendency, the effective lifetime of ozone in an air parcel transported in the free troposphere at northern midlatitudes (the zone of focus of this paper) is on the order of several months. This is long enough that the free troposphere can be considered a reasonably well-mixed reservoir, further emphasizing the importance of transport over intercontinental distances within this latitude zone.
• Lines 63-64: The authors correctly note that studies have identified “increasing trends in wintertime and background ozone concentrations at many sites in North America, particularly at the US west coast”. For completeness, it would be useful to further point out that such increases have also been identified throughout the background troposphere at northern midlatitudes including in the free troposphere, but that ozone in this latitude zone reached a maximum in the first decade of the 2000s (e.g., Parrish et al., 2020; Derwent et al., 2024).
• Lines 79-81: The authors could expand this sentence for completeness. As Derwent et al. (2024) discuss, a hierarchy of models is required to fully understand tropospheric ozone. We require not only statistical interpretations of observational data and well-evaluated atmospheric chemical transport models, but also conceptual models that simplify and capture the essence of the most salient physical and chemical processes that control observed ozone abundances.
• Lines 88-102: It seems to me that this paragraph overemphasizes the shortcomings of the perturbation Is it not possible to simply limit the approach to such small perturbations that the atmosphere processes are not significantly changed, and the results approach perfect accuracy?
• Table 1 lists 9 regional oceanic tagged regions. However, these regions are not mapped in either the paper or the Supplement. Please include such a map; for example, it is of interest to understand how the North Atlantic Ocean is divided into 3 separately tagged regions.
• Lines 264-274 describe the derivation of MDA8 values from the model output, and lines 287-292 describe the derivation of MDA8 values from the TOAR rural observations. Please discuss if these methods are completely compatible, or if differences in the procedures may possibly be important.
• Lines 278-279 state: “We use these receptor regions to perform area-weighted spatial averaging of MDA8 O3 values before analysing the trends and contributions. Please explain the process of “area-weighted spatial averaging”, and why it is used rather than simple averaging.
• Lines 405-406 note “that for all regions in North America, the observed PSO exceeds the WHO guidelines throughout the 2000 -2018 period.” It should be emphasized that the WHO guideline is based on the highest tail of the MDA8 distribution, while mean values are discussed in this paper. Thus, the exceedance of the WHO guideline over North America is indeed profound, as reflected in the difference in the WHO (~50 ppb) and US EPA (70 ppb) guidelines.
• Line 450 contains a typo – the WHO guideline is 51 ppb.
• Each panel of Figures 5 and 9 illustrates a time series of a “Residual O3” contribution. I have not found that quantity defined or discussed in the manuscript. Can this be eliminated? If not please define and discuss.
• Lines 727-728 state that “the increasing contribution of natural NOX emissions we find in our study, especially during the summertime, is most likely due to the increasing ozone productivity of these emissions.” This appears to be speculative; if this statement is to be included in the Conclusion section, it should be shown to be true through quantitative analysis.
• Lines 729-730 state that there is “… a smaller effect in the springtime, when long-range transport of ozone produced from foreign anthropogenic NOX emissions is more important.” I believe that in the literature there is ongoing discussion regarding whether ozone produced from foreign anthropogenic NOX emissions or ozone of stratospheric origin is of most importance for springtime surface ozone over North America (if not also Europe); I suggest that the authors mention both of these sources in this context.

References not included in the manuscript under review

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