the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 10 Apr 2026
Temporal variation of northern midlatitude baseline ozone: 48-year observational record challenges our understanding of tropospheric chemistry
Abstract. A continuous, 48-year measurement record, plus some earlier measurements, of baseline ozone at northern mid-latitudes are analyzed to quantify seasonal cycles and long-term changes of annual mean tropospheric ozone. Long-term changes are similar at all sites, and seasonal cycles are similar in the marine boundary layer (MBL) and in the free troposphere (FT), but with marked differences between those two environments. Over the last half of the 20th century, ozone concentrations increased by a factor of ~2, the seasonal cycle amplitude increased by nearly 50 %, and its maximum shifted to later in the year by 10 ± 13 days. The long-term increase ended early in the 21st century, followed by a slow decrease that reversed only a small fraction of the total earlier increase. In contrast, the seasonal cycle returned to near that of the preindustrial period. Simulations by six earth system models agree with the magnitude of the overall ozone increase and the increase ending early this century; however, observations indicate only a post-1950 increase, while models simulate a slower increase beginning in 1850. Consequently, the high bias of model simulations, while modest (~10 %) in recent years, was much larger (~87 %) in the 1950s. Qualitatively similar seasonal cycles and shifts are seen in the measurements and simulations, but simulations do not show the observed strong separation between MBL and FT behavior. We hypothesize that models simulate a background troposphere that is too NOx-rich, implying a lesser role than models simulate for methane in raising background ozone concentrations.
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RC1: 'Comment on egusphere-2026-1939', Anonymous Referee #1, 14 May 2026
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The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2026/egusphere-2026-1939/egusphere-2026-1939-RC1-supplement.pdfReplyCitation: https://doi.org/
10.5194/egusphere-2026-1939-RC1 -
AC1: 'Reply on RC1', David Parrish, 16 May 2026
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Response to Referee Comment (https://doi.org/10.5194/egusphere-2026-1939-RC1)
We thank the referee for the time and effort they put into reading our paper and formulating their comments. Since those comments are so negative in tone and recommendation, the first 4 authors of our paper choose to quickly post a response. The other 5 coauthors have not yet been able to contribute to this response.
We begin with an overall summary, and follow with point-by-point responses (in plain text) to each of the referee’s comments (reproduced in italic text).
Summary
The referee’s comments are limited to general criticisms of the conceptual and methodological foundation of our analysis, without any discussion of specific issues that might lead to quantitative, productive consideration of the soundness of our approach. Below we respond to each of those general comments, and find no indication that any issue raised by the referee could possibly change our main points or arguments, or account for the large differences between the model simulations and the results of our observational analysis as illustrated in Fig. 5 of our manuscript. It is these quantitative differences that lead to our main conclusions. The foundation of our analysis is indeed firm - we could cite many important published papers that use the same or similar foundations. In our opinion the referee’s comments cannot be considered as an objective evaluation of our paper; rather they must be judged to be a subjective effort to avoid the inconvenient truth stated in the first sentence of the final section of our paper:
- “Despite their frequent use in such manner in published studies, the current generation of CCMs and ESMs, when used alone, are not tools that can simulate the atmosphere realistically enough to provide reliably accurate answers to questions often posed for them.”
We urge readers (and the editor) to carefully evaluate our paper for themselves in the light of our more detailed discussion below.
Point-by-Point Responses
The manuscript addresses an important and timely topic: the long-term trend of baseline O3 at northern midlatitudes and the ability of current Earth system models to reproduce observed changes. The observational record analyzed here is valuable, and the authors have assembled long-term O3 datasets. However, I do not recommend publication in its current form because I have fundamental concerns about the conceptual and methodological framework supporting the main conclusions.
Thank you for this summary of your concerns. In our responses below we will particularly focus on the concerns that you raise regarding our conceptual and methodological framework.
My main concern is the estimation and interpretation of baseline O3. The manuscript defines baseline air masses as those not recently influenced by continental O3 sources or sinks, on synoptic time scales. However, this baseline is a methodological construct that depends strongly on the selection of the sites, filtering criteria, representativeness assumptions, and temporal consistency of the data treatment. The manuscript combines datasets from different environments, including marine boundary layer sites, mountain sites, ozonesondes, and aircraft measurements, each with different sampling characteristics and filtering approaches.
This summary of our approach is basically correct, except for the over-emphasis on the strong dependence of defining baseline conditions and of different filtering approaches. Our definition of baseline conditions in this manuscript has no significant dependence upon any of the issues the referee mentions, and the referee identifies no particular dependence that we could discuss further. The little filtering that we do are simply reasonable efforts to minimize recent influences of continental O3 sources or sinks on the analyzed data; further those filters have been consistently used in many published studies over past decades. Importantly, there has been no adjustment of filtering criteria (or selection of measurement sites) to “tune” the results to fit any preconception. The marine boundary layer data are the only extensively filtered data sets, since they are collected at land-based, coastal surface sites; such filtering there is essential to avoid continental influences. These filtering approaches have been extensively discussed in the literature for Mace Head (see Derwent et al. (2024) and references therein), and for the Pacific MBL (see Parrish et al. (2009), and updates in Parrish et al. (2020) and our present paper). We performed no filtering of the mountain site data – all archived data are included in the analysis. We also performed no filtering of the ozone sonde and aircraft data, except for exclusion of data below an altitude where continental influences are expected, i.e., 3 or 4 km; such selection of particular altitude intervals for ozone sonde and aircraft data are commonly utilized (e.g., Steinbrecht, et al., 2021). Note that our earlier paper (Parrish et al., 2020), analyzing the earlier portions of these same data sets then available, give more details of the data treatment, which are not repeated in the present paper.
It is also important to realize that the analysis of data sets from such different environments (marine boundary layer sites, mountain sites, ozone sondes, and aircraft) is a significant strength of our paper, since we find consistent results across all data sets. This consistency further demonstrates that our filtering approaches are both reasonable and effective.
This issue is particularly important because the manuscript uses the derived baseline to make broad hemispheric-scale interpretations. The argument that these sites can represent northern midlatitude baseline O3 relies on a conceptual model of a relatively well-mixed free-tropospheric reservoir. While this may be a useful first-order approximation, I do not think the manuscript sufficiently demonstrates that this assumption is robust enough to support the strength of the conclusions. Processes such as STE, long-range transport, changes in precursor emissions, wildfires, dry deposition, and regional differences in chemical regimes can all affect the interpretation of background O3. A more rigorous sensitivity analysis of the baseline definition and filtering procedures would be required before the central conclusions can be considered reliable.
Our analysis is designed to rely on absolutely no conceptual model. Rather, at the inception (i.e., before any analysis was initiated) of our earlier paper (Parrish et al., 2020), we selected the 8 “best” available data sets (an MBL site, a mountain site and 2 airborne data sets on or over the western part of each of two continents, Europe and North America) that we expected could provide the most precise (i.e., longest and least variable) and accurate (i.e., well-characterized measurements by well-respected researchers) analysis of the long-term changes and seasonal cycles of northern midlatitude baseline O3. The analysis of those data sets demonstrated zonal similarity (within statistical confidence limits) of those changes and cycles in the results all 8 data sets. Thus, the conceptual model of a relatively well-mixed free-tropospheric reservoir arose from the results of the analysis, but the analysis in no way relied upon that, or any other, conceptual model.
In this regard the first sentence of Section 4 has been changed by adding 3 words so that it now reads: “An underlying qualitative conceptual model of tropospheric ozone guides the interpretation of the analysis in this paper.”
The influence of the limited ambiguity of the baseline definition and associated filtering approaches at MBL sites has been thoroughly discussed previously (Derwent et al., 2024, and references therein and Parrish et al.. 2009); none of the present discussion is affected by any ambiguity in these issues.
My second major concern is the use of polynomial fits as the main framework for interpreting long-term O3 trends. The manuscript relies heavily on cubic polynomial fits to infer the timing of the O3 maximum, the post-2000 decrease, and the apparent slowing of that decrease. However, these polynomials are descriptive mathematical functions with no direct physical or chemical interpretation. As the authors well know, tropospheric O3 is controlled by nonlinear chemistry involving NOx, VOCs, methane, CO, photolysis, deposition, transport, and stratospheric transport. Given the existence of more explicit CTMs and Earth system model simulations, I find it difficult to justify why the core observational interpretation is built primarily on polynomial functions.
We believe this comment reflects a difference in understanding between us and the referee on the usefulness of observational analysis and its place in advancing our understanding of atmospheric chemistry. Our analysis, based on polynomial fits to measured long-term O3 time series, aims to quantify the statistically significant information regarding the long-term O3 changes contained in those time series. In our analysis of the 8 selected, observed O3 time series, we find that generally 4 parameter values capture all of the statistically significant information contained in each of those time series regarding long-term changes of mean annual ozone, and we derive those 4 parameter values from cubic polynomial fits to those data. The justification for building the core observational interpretation on polynomial functions is two-fold. First, those functions make no a priori assumptions regarding the functional form of the long-term changes that we wish to quantify, and second, the polynomial coefficient values derived in fits of those functions to O3 time series provide a tidy quantification of all of the statistically significant information in the fitted data sets regarding the long-term changes of interest. Please note that a polynomial fit to a time series is closely akin to a use of a Taylor's series expansion, a perfectly general treatment of any analytic function. Also, please note that this quantification allows the quantitative description of the timing of the O3 maximum, the post-2000 decrease, and the apparent slowing of that decrease to which the referee refers; a descriptive mathematical function with no direct physical or chemical interpretation is exactly the technique required for such quantification - it is precise and accurate to the extent provided by propagation of error techniques utilizing the derived parameter value confidence limits. Direct physical or chemical interpretation can only come from atmospheric models, which we do not attempt to provide. Of practical utility is that those parameters provide benchmarks for evaluating results of such models; i.e., if CTMs and Earth system model simulations calculate long-term O3 time series comparable to those measured, then a successful evaluation would find that the polynomial fit to the model simulated time series reproduces (within the specified confidence limits) those derived in our analyses. Failure of that reproduction would indicate a model shortcoming.
We find it difficult to understand why the reviewer is so concerned with our use of polynomial fits. The literature is filled with studies that rely on various linear trend analyses to interpret long-term O3 changes, but all such linear trend analyses are simply fitting a time series to the simplest polynomial - a 1st order polynomial, i.e., a straight line. The goals of linear trend analyses is similar to our analysis goals – to provide a tidy quantification of statistically significant information in the fitted data sets regarding the long-term changes of interest, and the derived slopes are similarly used as benchmarks for evaluating model simulations. However, linear trend analysis has two drawbacks. First, it implicitly assumes that the long-term change is linear; thus, it is severely limited in effectively describing O3changes of differing functional forms. Second, as the referee notes, tropospheric O3 is controlled by nonlinear chemistry involving NOx, VOCs, methane, CO, photolysis, deposition, transport, and stratospheric transport, so there is good reason to expect significant nonlinearity in long-term O3 changes, important atmospheric information to which linear trend analysis is blind.
A related concern is that the manuscript moves from descriptive fits to causal interpretation without sufficiently linking the observed changes to explicit drivers. The discussion raises changes in anthropogenic emissions, methane, NOx-rich versus NOx-poor chemical regimes, and model biases, but the analysis does not explicitly test these mechanisms. Instead, the drivers are inferred largely from temporal patterns and comparisons with model simulations. In my view, this is insufficient to support some of the stronger claims, particularly the hypothesis that models simulate a background troposphere that is too NOx-rich and consequently overestimate the role of some processes while underrepresenting others. This may be an interesting hypothesis, but it is not demonstrated convincingly by the analysis presented.
We do recognize that “the manuscript moves from descriptive fits to causal interpretation without sufficiently linking the observed changes to explicit drivers.” Such linkage could only come from an atmospheric model that simulated all relevant chemical and physical processes, and successfully reproduced the quantitative benchmarks that we provide regarding long-term changes and seasonal cycles of baseline O3. It is our conclusion that existing models have not yet achieved that success, so it is not yet possible to directly address this concern of the referee. Given our conclusion, we did not aim to provide such modeling in this manuscript.
We do agree with the referee that: “The discussion raises changes in anthropogenic emissions, methane, NOx-rich versus NOx-poor chemical regimes, and model biases, but ….” We do believe that it is important to discuss possible reasons that models so poorly reproduce observations, rather than simply describe the obvious discrepancies. Consequently, we aim to couch all such mechanistic discussions in terms of “suggestions” and “hypotheses”, rather than “findings” or “conclusions”. (If we have fallen short of that aim in Section 4 of the paper, we will correct such shortcomings.) With regard to the referee’s concern about “particularly the hypothesis that models simulate a background troposphere that is too NOx-rich”, we must point out that “A hypothesis is an assumption, an idea that is proposed for the sake of argument so that it can be tested to see if it might be true” (https://www.merriam-webster.comlast accessed 14 May 2026). We present this hypothesis in the spirit of this definition, and firmly believe that it is valuable to formulate possibly correct ideas on important scientific topics, even in the absence of analysis convincingly demonstrating its validity.
For these reasons, addressing individual technical aspects or adding clarifications would not be sufficient. My concerns are not mainly about presentation or isolated details, but about the methodological foundation of the manuscript. The conclusions depend critically on how baseline O3 is defined and extracted, as well as on the use of polynomial fits to infer chemically meaningful long-term behavior. Without a more rigorous and physically grounded treatment of baseline representativeness, trend estimation, and chemical drivers, I do not consider the manuscript suitable for publication.
We disagree; please see the summary of our reasoning at the beginning of this response.
(Note that references cited herein are given in our original manuscript).
David D. Parrish
Charles A. Mims
Richard G. Derwent
Ian C. Faloona
Citation: https://doi.org/10.5194/egusphere-2026-1939-AC1
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AC1: 'Reply on RC1', David Parrish, 16 May 2026
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