the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 01 Sep 2026
Technical note: Assessment of OMI/MLS Satellite-Derived Tropospheric Ozone Product for predicting monthly ground-level ozone concentrations
Abstract. Ground-level ozone is a hazardous air pollutant that contributes to respiratory and cardiovascular morbidity and mortality, as well as to climate change and vegetation damage. Despite its significance, global surface ozone monitoring remains spatially sparse, particularly outside of North America, Europe, and East Asia. Satellite-based products such as the Ozone Monitoring Instrument/Microwave Limb Sounder (OMI/MLS) tropospheric column ozone (TCO) dataset offer a potential solution for improving estimates of global ozone at ground level. Here we evaluate the performance of the OMI/MLS TCO product as a predictor of global ground-level ozone by comparing it to monthly average ground-based Maximum Daily 8-hour Average (MDA8) ozone measurements from the second Tropospheric Ozone Assessment Report (TOAR-II) database (2005–2022). Linear regressions were conducted globally, as well as by year, world region, concentration range, and month. A positive correlation was found between the TCO product and ground-based measurements, although that correlation was modest (R² = 0.29 over the entire period globally). Regression parameters did not vary strongly by season, region or year. Correlations were highest in May through October and highest in Europe and lowest in North America. The regression results were used with the satellite product to generate global maps of estimated ground-level ozone for each month from 2005 to 2022. While not a substitute for in situ measurements, our ground-level ozone product based on OMI/MLS TCO shows potential as an independent observational input to global data fusion methods in areas lacking ground-based monitoring.
Competing interests: At least one of the (co-)authors is a member of the editorial board of Atmospheric Chemistry and Physics.
Publisher's note: Copernicus Publications remains neutral with regard to jurisdictional claims made in the text, published maps, institutional affiliations, or any other geographical representation in this paper. While Copernicus Publications makes every effort to include appropriate place names, the final responsibility lies with the authors. Views expressed in the text are those of the authors and do not necessarily reflect the views of the publisher.- Preprint
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Status: open (until 13 Oct 2026)
- RC1: 'Comment on egusphere-2026-4798', Anonymous Referee #1, 21 Sep 2026 reply
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RC2: 'Comment on egusphere-2026-4798', Anonymous Referee #2, 21 Sep 2026
reply
# Title: Review of "Technical note: Assessment of OMI/MLS Satellite-Derived Tropospheric Ozone Product for predicting monthly ground-level ozone concentrations"
# Manuscript Summary:
Monthly averaged maximum daily average 8h ozone (MDA8) correlates moderately with OMI/MLS tropospheric column ozone (TCO). TCO at 1-degree was paired with monthly average MDA8 and used to make a variety of regression models, which were all discarded except for the aggregate. The aggregate slope and intercept are used to generate monthly and then annual surface concentration
# Review Overview:
The manuscript has several methodology and conceptual issues that need to be addressed. The manuscripts primary conclusion is a moderate correlation between TCO and monthly mean mda8 ozone, which by itself does not merit a publication. The goal of the paper appears to be to establish TCO as a potential predictor of ozone, but does not investigate high-level issues inherent in that assertion. Many of the additional pieces of analysis are ill-posed and often not supported by the methodology. And, lastly, the manuscript needs substantial editorial improvements. The individual concerns are addressed further below. Overall, this manuscript would benefit from substantial additions.
## Methodology
The methodology often seems disconnected from the conclusions that are made.
* For example, the stratified regression results are concluded to be "not so different" from lumped application to justify use but the methods do not support direct comparison. Clearly, applying 1.077x+0.386 vs 1.289x-5.813 for 2007 would have yielded a different MAE/RMSE. The error statistics of the pooled and individual year results cannot be meaningfully be compared because (1) the population sizes are different and (2) both the dependent and independent data include trends that affect magnitude. The combined results of stratified years are not provided, and no consideration of including year as a regressor was discussed. As written, there is no comparison of stratified results to the pooled result in a way that would allow differentiation of the value of the stratified models. Further, there is no discussion about what would be sufficiently different. Without a comparison and discussion of what would be meaningfully different, the value of presenting the stratified results is not clear.
* Similar discussion applies to the regional results. Simply comparing RMSE, MAE, and R2 overlooks basic structure that affects OMI/MLS as a predictor. As a quick test, I reconstructed the AQS dataset for just the US and paired it with OMI/MLS. Becuase the US observations make up the majority of the TOAR North America dataset, this will be similar but not identical to the manuscript. For the US subset of data, the mean_mda8 and TCO statistics are r2=0.169, rmse=9.101, mae=7.196 and a mean bias of -0.256 ppb. These are not dissimilar from your own results for all of North America, which gives me confidence that you would get something similar. If I compare to the overall slope/intercept, the rmse (9.874) and mae (7.776) are quite similar to the overall -- but mean bias is substantially larger (-2.71 ppb). This could have meaningful consequences for application to mortality. A more concerning issue is the lack of seasonal amplitude in the North America only regression that is obvious when visualizing the result. This may be impacted by the US having roughly 1200 observations in the summer and just 700 in the winter. The asymmetry of seasonal observations leads to a skew in the data used for regression and may decrease the slope parameter, which raises questions about the input dataset that are not discussed. More generally, the manuscript does not currently address things like magnitude of means or amplitude of seasonality in the comparison of models. Amplitude could have important implications for OMI/MLS's value in ML model, but this is not discussed. As a result, the manuscript overlooks important physical and health application related conclusions.
* The stratification of data into TCO bins is arbitrary and there is no discussion of how they were derived. Low represents 3.7% of the data while high represents 8.0%. As a result, the mid category is therefore a regression against most of the data. What would it mean to have been sufficiently different when stratified in this way? What was the benefit of stratification compared to using a transformed regressor or a second order term?
## High-level Conceptual Issues
High-level issues that are not addressed:
* The manuscript evaluates TCO as a potential proxy for ML without much discussion besides overall correlation (r2). The overall correlation applied in this way tells us very little without additional discussion. The authors note that the correlations drop precipitously when looking at individual months, but do not discuss the implications for machine learning. The monthly results may suggest that TCO is largely a proxy for season with only some spatial explanatory value available in late boreal spring or early boreal fall. This may be misleading however, because the population of input is not all in boreal domain. Some of the explanatory value may be related to latitude within a month. This generally indicates that TCO is largely a proxy for season. As a quick test, I ran two correlation tests one with cosmo=cos((month - 6) / 6 * pi) and the other with solar zenith angle (sza). For US TCO r2=0.169, but for cosmo the r2=0.340 and for sza r2=0.253. To be clear, I get better R2 from a season and solar zenith angle than from OMI/MLS. My suspicion is that TCO is providing very little in the way of spatial variation except as it relates to the solar zenith angle. Because my test dataset is only the North America, this may not be representative everywhere and I would invite the manuscript to address this concern. I would have liked to see the authors consider the source of explanatory value from TCO rather than to simply assert its usefulness based on a low r2.
* Alternative explanatory variables should have been discussed. The reliance on OMI implies the availability of several datasets. For example, OMI uses a prior model (or climatology) as an input that includes a vertical profile. By the very nature of using OMI, the study implies the existence of an alternative and potentially more explanatory variable being used as an input to the OMI retrieval. If the surface level input to OMI is a better predictor of mean mda8, what does that say about the observational constraint from TCO? The OMI/MLS dataset has to do more than correlate to be useful to a ML model. It should add information that is not available already. The value of the "observation" depends on adding value over the input as an explanatory variable.
* The manuscript introduces a tropospheric mixing ratio as a potential alternative to total column and discusses the surprise that it did not improve prediction. The surface pressure (Ps) and tropopause pressure (Pt) are being used from two independent models at two resolutions. The pressure depth (dP=Ps - Pt) of the atmosphere is being derived from TCR-2 surface pressure and tropopause pressure from NCEP WMO reanalysis. Those models have independent assumptions from the MLS stratospheric column ozone (SCO). As a result, the mixing ratio now has multiple sources of independent errors (Ps, Pt, SCO, and column ozone). The authors did not clearly establish why they anticipated improved correlation. I might suspect that this was intended to account for terrain variation (Rockies vs Coast), but nothing is clearly articulated. If terrain height is the concern, the authors should discuss the implications of the observation site terrain heigh distribution. As a minor side note, the text did not include references for either component of pressure dataset that were only discussed in the data availability section.
* Residual plots are not particularly useful when comparing a coarse predictions over short distances and without additional context. The TCO product is provided at 1-degree resolution, which is not expected to capture sub 1-degree variation. Based on the monthly performances, the spatial variation is also likely poor. As a result, you would expect high biases with high concentrations and low-biases at low concentrations. Given the low predictive value (r2<0.32) for all regions, what is the manuscript attempting to communicate?
In summary, there are conceptual and methodological high-level issues that need to be addressed. In addition, below are some line-by-line comments/suggestions.
# Line-by-Line CommentsAn incomplete line-by-line commentary:
9: In the US, pollutants are divided into "criteria" and "hazardous" -- Ozone is a "criteria" pollutant. I do not think the word "hazardous" provides particular value here, so I would recommend against it.
13: "improving estimates of global ozone at ground level" compared to what?
22: "potential as an independent observational input to global data fusion" what characteristics make this true?
27: "with ground-level concentrations elevated due to human emissions" rephrase to communicate increased near human sources of precursor emissions. ground-level ozone is generally lower than aloft. As written, this statement could be interpreted many ways.
44-54: The thesis of the paragraph appears to be that several data sources exist, but skips right over basic CTMs and says nothing about the existing skill of CTMs or reanalyses. These details seem like a critical reference for your conclusions. Is r2=0.29 globally/seasonally good compared to these other sources?
47-48: As written, you appear to argue that reanalyses are not designed to estimate ground-level ozone. While it is true that surface obs are not often in the analysis, the CTM itself is designed to predict surface-level concentrations and the reanalysis is intended to improve it... So, what point are you trying to make?
56: Since many groups use geostatistics, it seems odd to lead with a specific application from your group.
57: "multiple-model ensemble" that sounds great... What were the ensemble member? Statistical CTM? Reanalysis?
60-61: "6-month ozone seasonal maximum of monthly average daily maximum 8 h ozone (OSDMA8)" I read this as the max({mean(C_m): m \in 4-9}). I suspect however that this is the 6-month seasonal *mean*.
67-70: A threshold based analysis seems like a very specific detail when your own analysis provides only r2 and you do not provide the range of r2 for these applications.
72-79: This paragraph is weird. It opens with satellites are good for overcoming missing data, highlights how bad the sfc/col distinction is, highlights how it has been considered a bad predictor.... What is the thesis of the paragraph?
84: OMI/MLS isn't an instrument, so it doesn't have sensitivity to any particular part of the atmosphere. This is poorly written.
90: ... and [derive] linear ...
101: Does OMI measure "height" of the ozone column? I don't think that's true.
102-103: A key point that is omitted here is that MLS is a limb view while OMI is a nadir view. This is central the the ability to distinguish SCO.
105: "generally agree well with" Perhaps you mean "to coincide/overlap with"?
107: There is nothing raw about a derived product from two instruments that have been regridded and averaged.
113-116: Did this help or hurt with correlation? [I asked this question without reading results because processing observations often introduces independent error.]
118: Consider replacing 1270 with Mw/R/T0/g or something to provide clarity about the method.
131: What types of filtering and QA are done to create monthly means? 75% completeness at the daily level? Monthly level?
162-163: I would not expect this at all. You are taking mean DU from a subset of days and combining it with monthly mean Ps Pt.... At best, you re adding a smoothing function. At worst, you're pairing disparate definitions of the troposphere and acting as if they align.
191: What made you choose these ranges? (low: 43k; mid: 1031k (88%); high 94k) What is the geographic distribution of the categories?
199: Figure 2 uses a scatter plot which is completely saturated throughout much of the range.
200: The peak R2 within any month was 0.163 or R=0.4. Most were lower than that... that would seem to suggest that the R2 of 0.29 overall is largely the ability to predict the month of the year.
207-208: "not so different" You should justify this. Also, why not include a reference where all you know is the sin of doy or T?
269-270: What makes this a informative in areas without monitors?
272: How would these results be insightful given that they have very little explanatory value and most is seasonality?
Citation: https://doi.org/10.5194/egusphere-2026-4798-RC2
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- 1
This is a useful technical note that provides the first systematic evaluation of the OMI/MLS tropospheric ozone product as a predictor of surface ozone and demonstrates its potential value as an independent observational input for global data fusion applications. The analysis is clear and the conclusions are appropriately cautious.
The manuscript could be strengthened by providing a physical interpretation for the observed relationships and a more comprehensive assessment of uncertainty and systematic regional biases. A clearer demonstration of the added value of the derived product relative to existing global ozone datasets would be welcome, but that is very likely a separate piece of work.
General comments
At the moment, the note reads largely as a validation study followed by application of a global linear regression. What do the results tell us about the physical relationship between column ozone and surface ozone? Why does OMI/MLS perform better in some regions than others? What does the observed stability of the regression over time imply about ozone vertical structure?
I would recommend some discussion about the role of ozone vertical profiles, boundary layer depth, STE, regional differences in ozone production regions as a way to explain why North America performs substantially worse than Europe and East Asia.
The authors argue that the OMI/MLS data product could be useful as an independent observational input for data fusion. How does their data product compare with existing machine learning products? How does it compare with chemical reanalyses? Even a limited comparison over a few regions would help the reader understand the usefulness of the OMI/MLS data.
The manuscript reports a range of mean statistics but uncertainty propagation is not discussed in depth. Even uncertainties on regression coefficients would be useful as a starting point, but the technical note would benefit further from, for example, spatially distributions of uncertainty estimates, confidence intervals on predicted ozone, and regional uncertainty assessments. This would help the reader (and ultimately a user of their data product) to understand where the data should and should not be trusted.
The residual maps shown in Figures 4-6 are very interesting but there is relatively limited accompanying discussion. Persistent biases over California, the Mediterranean, and parts of China suggest that important processes are not captured by the global regression. Do the authors have any insights into the role of topography, regional photochemistry, boundary layer dynamics, or transport effects?
This reviewer encourages the authors to explore the regional and seasonal dependence of the regression models in greater depth, particularly through out-of-sample experiments. For example, how does a global regression calibrated without North American observations perform when evaluated over North America? Conversely, does excluding North American data improve or degrade predictive skill over Europe or East Asia? Such cross-validation experiments would provide a more rigorous assessment of the transferability of the global model and could yield valuable insights into the extent to which the observed relationships are region-specific versus globally robust. The results may also help identify whether certain regions contribute disproportionately to the global regression and inform the potential use of regionally tailored models.
Specific comments
In the intro (line 30), introduce the impacts on humans, plants, and stratosphere so it is consistent with the structure of the following text.
Generally, please report mean stats with a more appropriate number of significant figures in Tables 1-2.