Source attribution of near-surface ozone trends in the United States during 1995–2019
Abstract. Emissions of ozone (O3) precursors in the United States have decreased in recent decades, and near-surface O3 concentrations showed a significant decrease in summer but an increase in winter. In this study, an O3 source tagging technique is utilized in a chemistry-climate model to investigate the source contributions to O3 concentrations in the U.S. from various emitting sectors and regions of nitrogen oxides (NOx) and reactive carbon species during 1995–2019. We show that domestic emission reductions from energy and surface transportation are primarily responsible for the decrease in summertime O3 during 1995–2019. However, in winter the emission control also weakens the NOx titration process, resulting in considerable increases in O3 levels from natural sources. Additionally, increases in aviation and shipping activities and transpacific transport of O3 from Asia largely contribute to the winter O3 increase. Changes in large-scale circulation also explain 15 % of the O3 increasing trend.
Pengwei Li et al.
Status: final response (author comments only)
RC1: 'Comment on acp-2022-678', Anonymous Referee #1, 13 Jan 2023
- AC1: 'Reply on RC1', Pengwei Li, 08 Mar 2023
RC2: 'Comment on acp-2022-678', Anonymous Referee #2, 17 Jan 2023
- AC2: 'Reply on RC2', Pengwei Li, 08 Mar 2023
Pengwei Li et al.
Pengwei Li et al.
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Title: Review of acp-2022-678
This manuscript details a multi-year ozone tagged contribution analysis. The specific value is the attempt to explain observed trends with trends of model contributions. I think this manuscript has high value, but needs some additional analysis to be published. Below are sections that summarize comments related to model performance, methods, and editorial notes. Last, is a line-by-line section that has more specific feedback.
# Model Performance Evaluation
Generally, this manuscript is missing basic model evaluation in the body and supplement. The current manuscript jumps into trends of contributions and only mentions evaluation in the conclusions. In particular, only evaluation in China is ever discussed. The manuscript focuses on trends associated with titration without ever demonstrating the model reasonably captures the phenomenon. The representation of titration in the Eastern US by the model is important given that it drives the trends. Given that coarse models (2x2.5 degree) are often extremely biased at nighttime, the authors should provide some evidence that nighttime titration is reasonably simulated and/or describe how model artifacts may play a role in the trend. Overall, it seems odd that performance over China is used to suggest underestimation of long-range transport while the performance and possible errors of local contributions are omitted.
# Methods Feedback
In the methods sections, more detail is needed on several fronts. The emissions are currently under-described even though they are well referenced. Recommendations are made in the line-by-line section. Similarly, the model-observation pairing is mostly left to the reader to infer. Again, recommendations are made in the line-by-line.
# Editorial Feedback
Especially in the conclusions, there are several statements where increase/decrease seem to be used incorrectly. These incorrect directional statements should be corrected. See line-by-line section for specific recommendations.
The section describing the overall trends would benefit from a table. The descriptions and parenthetical references make it somewhat difficult to easily compare. See line-by-line section for specific recommendations.
Lastly, recent application of a very similar system was made by Butler et al. 2020. That publication is referenced, but more should be done to compare these methods and results to those. From a methods standpoint, it would be nice to provide a short summary that explains how these experiments are different. From a results standpoint, you should compare the overlapping 2010 year for comparable. Are the results comparable for overlapping (2010) or proximate years? If not, do methodological differences explain discrepancies?
* 117, please describe the depth of the first layer and the number of layers in near the surface (e.g., under 2km). This helps contextualize the model representation of titration later.
* 121, please describe how the stratospheric values are set. Are they based on climatological values? Are they scaled based on something?
* 146, are XTR tags really neither NOx nor VOC? Are they included in both?
* 159, It says CO and CH4 are not tagged by individual sources? Does that mean just by regions? Or, all CO is lumped? The wording is currently unclear. Particularly interested for CO.
* 164, as you note, this limitation of CO seems odd.
* 168, It would be useful to note here (in addition to later) that TgN and TgC are shown in the appendix.
* 173, This seems like an important methodological shift. Can the authors highlight whether conclusions are robust to analysis from 1995-2015 or 1995-2019?
* 175, Can you clarify what "present-day" means here? Is this a climatology based on a range of "present-day" years or a specific year?
* 177, Please elaborate on Price parameterization. I think you are saying online parameterization based on simulated cloud top heights. There are also climatologies based on Price, so it is good to be clear.
* 180-185, Please clarify whether the simulation is being sampled only at observation site-days or averaged seasonally and then sampled at sites.
* 200, The results should start with some estimate of model performance over the target analysis areas. At least, 1) a map of the model with obs scattered on it for an early year and a late year and 2) a description of how basic performance stats change over time. Because this paper focuses on the JJA and DJF, I would expect the model performance to have a similar separation. This will help the readers contextualize results.
* 205, Please add lightning NOx in the supplemental figures.
* 214, related to 180-185, are these trends based on the model only at observation sites or based on averages of the regional "box"
* 214: Looking at Figure 4b, there is a lot of heterogeneity in the western summer trends. The Western cities are fairly isolated leading to misrepresentation by coarse global models. Can you discuss what would happen if you only looked at CASTNet or rural monitors? Or just the IPCC sites?
* 216-223, I found it difficult to keep the text organized in my mind. I recommend adding a table here.
Table X: Trends by season (DJF, JJA) for observations and the model sampled at observation sites (right?).
It would also be good to add some clarify on what "well produce" means Based on a 95% certainty, the CI are not overlapping for Eastern winter or Western summer. The CIs for Western winter are barely overlapping and only after rounding. The model seems to clearly reproduce the trend only for Eastern summer.
For me, the titration performance in the East raises questions about the West. The model seems to dramatically overestimate the reduced titration in the East. Given the population density of the East, the titration is likely more widely spread. Due to the population sparsity of the West, the overestimated titration is likely diluted. How does this impact the conclusion about well representing winter in the West?
* 236, I am surprised to see STR (stratosphere) in both NOx and VOC. Is that via XTR?
* 241, can you add error bars to the figure?
* 243-247, I think this is a very interesting finding! If the atmosphere is increasingly NOx sensitive, that should have important implications for VOC tagging in later years. Can you discuss that a bit more?
* 247-251, What role does the location of monitors play in the conclusion here? Is there a strong spatial gradient to the SHP contribution? This is important because the populations tend to be skewed toward near the ocean. In an ideal world, it would be interesting to see a few maps (1995 and 2019) of contributions trends that have a strong spatial gradient.
* 259, I find this to be a particularly interesting finding that has implications for the estimation of climate/air quality co-benefit assessments. I wish it was expanded a bit in the conclusions.
* 272, I find this confusing. Most of this sentence makes perfect sense to me. It is introduced, however, in the context of reduced VOCs. At aircraft heights, you say that only NOx increase. Does that mean that there are no aircraft VOCs? If so, are you suggesting that VOCs at 6-10km were meaningfully reduced and that contributed to the large aircraft trends?
* 280-282, Similar comment to earlier. The spatial nature of this enhancement is important. It'd be great to see a map of the contribution and trends.
* 283, I don't think this is strictly speaking true. Your lightning emissions are parameterized based on simulated clouds. Can you clarify that this is only true for VOC?
* 289, Butler et al compared January and July in Figure 5. It isn't clear to me that the contribution maximized in DJF vs MAM.
* 295, Specify anthropogenic and/or that you are excluding soil NOx. Soil NOx in summer has a large anthropogenic component and the contribution from soil is likely "domestic" (e.g. Lapina et al. 2014).
* 316, This is definitely interesting... I'm struck however by the dramatic overestimate in the trend, which might be related to the models representation of vertical mixing in winter.
* 326-327, The idea that South Asia, and Southeast Asia East Asia "equally contribute" is a somewhat surprising finding. Many previous refereed articles show a decreased transport efficiency from India (S. Asia) to the US compared to East Asia. Similarly, Butler et al 2020 showed significantly larger East Asia contribution than South Asia. Can you highlight why your results would be so different?
* 335-350, This discussion really highlights the oversimplicity of linear trends. The authors do a good job noting this is likely associated with transport. It would be good if they connected it to known meteorological cycles. A quick look shows that ENSO cycles are likely accounted for by the time averaging, but the Pacific Decadal Oscillation (PDO) is not. This highlights why the trend is likely not significant. It is likely made up of ups and downs seen in the PDO. A 5-year average of the NCEI PDO index shows that the winters of these two periods are of opposite signs (despite inter annual variability). This is in part because in mid 1998, the PDO index shifted. This leads to a smaller difference between summers than winters. You could also reference the Lin et al. paper about the position of the jet stream.
* 342, I think it is a mistake to call the comparison of two five year periods "anomalous".
* 355-357, I think you got the signs of change wrong here. You showed decreasing in the summer (controls) and increasing in the winter (lessening titration).
* 355-357, You showed that it could only replicate the decreasing trend in the eastern summer and the increasing trend in the western winter. You showed that the trends for Eastern winter and western summer were *not* well captured. The trends were significantly different. So, it is wrong to say that it did well in the conclusion.
* 359-361, You need to be clear when you are talking about the model regions and when you are talking about the observed sites as sampled by the model. Are these trends at select sites? Are these trends representative of the larger region? Or the population weighted concentrations?
* 364, This is a little less clear to me. The VOCs were also reduced. How do you distinguish between reduced VOC trends and reduced NOx OPE impacts on VOC trends.
* 391, This was a 3.7 ppb/decade decrease (not increase.
* 392-393, The authors are offering only one of several equally permissible explanations. As you note, one is that the Asian trends are underestimated. Another is that the coarse model overestimates the decrease associated with domestic reductions. Another is that stratospheric variability is underestimated. Another is that the trend in ships contributions are underestimated. What makes the authors confident that this is the only hypothesis to highlight?
* 393-396, 1) The authors should show this model performance if their conclusions rely upon it. 2) The local peaks in China will depend on near surface vertical structure while the continental scale outflow may not. So, you could only says that it "consistent with the low contribution from Asian sources" since you cannot say that it definitively explains anything.
* 396-397, It is unreasonable to think that model evaluation of China is worth discussing, while model evaluation over the US is not.