the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 22 Oct 2026
Seasonal transitions in peroxyacetyl nitrate (PAN) drivers inform coordinated ozone mitigation in urban basin environments
Abstract. Peroxyacetyl nitrate (PAN) is a critical secondary pollutant that drives photochemical smog and threatens ecological health. Despite persistent challenges in controlling photochemical pollution in China, the mechanisms governing seasonal PAN formation and its key driving factors under complex basin topography remain poorly constrained. In this work, we integrated a comprehensive one-year observational dataset, an observation-based box model, and interpretable machine learning to elucidate the seasonal formation pathways and meteorological drivers of PAN at an urban site in the Sichuan Basin. The annual mean PAN mixing ratio reached 0.60 ppbv, with a winter peak hourly value of 6.44 ppbv. Model simulations revealed distinct seasonal formation pathways: thermal decomposition–recombination cycling dominating summer formation (75.5 %), whereas precursor oxidation served as the primary source in winter (57.1 %). Sensitivity analyses indicated a persistent volatile organic compound-limited regime for both PAN and ozone formation year-round, while nitrogen oxides varied seasonally, suppressing PAN formation in winter but promoting it in summer. Feature attribution analysis further demonstrated an obvious seasonal shift from chemistry-dominated driving mechanisms during warm seasons to stronger meteorological influences in winter, where transport-related variables accounted for 61.0 % of the cumulative feature importance. During ozone pollution episodes, peroxyacetyl radical production increased by 77.0 %, accompanied by a 91.9 % enhancement in PAN decomposition, highlighting intensified PAN cycling driven by elevated photochemical capacity. These findings uncover seasonal regime shifts in PAN formation in complex basin environments, supporting seasonally tailored precursor reduction and coordinated PAN and ozone mitigation strategies.
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Status: open (until 03 Dec 2026)
- RC1: 'Comment on egusphere-2026-5149', Anonymous Referee #1, 02 Nov 2026 reply
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RC2: 'Comment on egusphere-2026-5149', Anonymous Referee #2, 06 Nov 2026
reply
The manuscript "Seasonal transitions in peroxyacetyl nitrate (PAN) drivers inform coordinated ozone mitigation in urban basin environments" by Dong et al. presents an interesting dataset of about one year of PAN measurements at Suining in the Sichuan Basin. It attempts to analyze these measurements for additional insights using a combination of chemical box modeling and machine learning approaches. The measurement dataset in this manuscript is strong and represents interesting measurements of an important atmospheric species (PAN) and its relationship to other parameters. However, I believe the analysis and presentation of the manuscript should be improved prior to publication. I recommend that the paper be reconsidered after revisions.
I would highly recommend that the authors completely remove the machine learning parts of their manuscript and attempt to incorporate boundary layer dynamics into their box model instead. The machine learning model is circular and provides little additional value or insight once the circularity is removed. The manuscript would be much stronger if the authors focused on (1) the measurements, (2) the box model (and a deeper analysis of those results), and (3) a thorough comparison with other basins and past work on this topic. In the current version of the manuscript, the machine learning model is largely a distraction that adds little to real scientific understanding of PAN cycling. I also recommend that authors rethink how the present net versus gross PAN production and the significance they put on the PAN-PA null cycle and instead try to focus on where PAN (and PA) cycling actually impacts ozone or PM formation or other radical cycling. The authors have an excellent dataset and have developed a capable box model and could go a lot deeper into the seasonal cycling, the impact of both emissions / chemistry and meteorology on PAN / PA and radical cycling, etc. Instead, much of the analysis is very cursory and does not provide insight beyond past (more comprehensive) studies or basic textbook material.ÂGeneral Comments:
The ML model regresses a derived parameters (PANgen) against several target variables, including PAN_cycling (which it labels as a chemical factor). However, PANgen is defined as Delta PAN + PANd, whereas PAN_Cycling is defined as PANd times a branching factor (Rpa+no2). Consider Table S8 - for spring, Rpa+no2 = 0.7619 and PAN Thermal Decomposition is 0.656. In Table S10, PAN Cycling is 0.47, which is essentially the product of Rpa+no2 and PAN Thermal Decomposition (0.50). For summer, 0.7837 (R) * 2.000 (PANd) = 1.5674 ≅ 1.52 (PAN_cycling), and so on. The model is essentially predicting a value (PAN_cycling) that is identical to one of the predictors (PANd) used to generate the target PANgen derived parameter, up to a scaling factor. This will artificially inflate the significance of the ML model, as it is being asked to regress a derived parameter against a dependent target value from which that parameter is derived. This is particularly important for the SHAP attributions (Figure 4). In particular, the SHAP importance of PAN_Cycling could be driven by the thermal decomposition component used to derive PANgen.
The authors also conflate "chemical" and "meteorological" parameters. They assume that Chem_precursor and PAN_Cycling are "Chemical factors", but these are based on box model results that are largely driven by meteorological parameters (temperature, relative humidity, UV / solar radiation, etc.). Essentially the only meteorological parameter of significance not incorporated into the box model is the BLH. If the authors incorporated BLH into their box model (as some other studies have done), they could remove the ML part of the manuscript altogether and make the result much cleaner. Alternatively, authors should look at different meteorological parameters (T, RH, solar radiation, etc.) separately rather than grouping them into two modeled parameters. In the current manuscript, "chemical" and "meteorological" are conflated to such a degree it is essentially impossible to disentangle the two factors in a relevant manner.
On a more conceptual level, authors focus a lot on PAN-PA cycling rather than net changes in PAN. Consider a case where the PAN-PA system was at a steady state so there was no net production or destruction of PAN, then ΔPAN = 0 but Chem_precursor and PAN_Cycling could be significant. It might make more conceptual sense to look at PA branching ratios, offset from steady state, or something that would actually have a direct impact on ozone and radical formation rather than focusing on what is essentially a null cycle. See, for example, LaFranchi et al. 2009 (https://doi.org/10.5194/acp-9-7623-2009).
Comparison to other basins
There is a significant number of measurement campaigns in other similar basins internationally that are largely ignored (or only addressed in a cursory manner) in this manuscript. It would be much stronger if the authors considered the relationship between their results and those of previous studies. Some examples of sites where these issues have been studied and addressed already include Uintah Basin (as well as Salt Lake City) in Utah, USA; Mexico City Basin, Denver-Colorado Front Range, USA; Po Valley, Italy, among many others. Many of these results found similar conclusions to this manuscript (e.g. relationships between emissions, chemistry, inversion layers and boundary layer structure, relationships to ozone, etc.) but presented in a much stronger way than in this manuscript. Many of the "novel" findings of the current manuscript are essentially restatements of patterns or results already discovered in other basins in China, Europe, and the United States. The authors of this manuscript should directly address the existing literature on this subject, show how their results agree with or contradict past studies, and what additional value their analyses provide beyond the existing literature.
Specific Comments:
L1-2 (Title): This title is very strongly overstated. The paper promises results that "inform coordinated ozone mitigation in urban basin environments" but focuses on empirical correlations between a small set of parameters at a single ground site, while offering little novel advice or suggestions to inform ozone mitigation in the Sichuan Basin. Furthermore, it does not do a thorough job of comparing the results from the Sichuan Basin to measurements in other basins (except on a very cursory level), and thus promising results that apply across "urban basin environments" is not supported by the text of the manuscript. I recommend that the title be revised to focus more on what the paper actually shows, argues, or demonstrates rather than grossly overstating the results and conclusions. Alternatively, the authors should increase their discussion of mitigation strategies and provide a more thorough comparison to observation in other basins (in China and internationally). As it stands the title is not an appropriate reflection of the content of the manuscript.Line 33: Authors make the argument here that PAN causes significant risks to ecosystems and human health. If this is the case, they should provide quantitative thresholds (acute or chronic) at which human and ecosystem health effects become significant and show that their measurements exceed those thresholds.
Lines 38-40: The framing here is weak and very vague - the authors claim that PAN processes remain "difficult to disentangle" and that there is "substantial uncertainty ... limiting our understanding...". I think the introduction would be much stronger if the authors were more specific about what aspects are difficult to disentangle (and why), what past studies have done to attempt to disentangle them and where the gaps remain, and how they can address those gaps. What is the source of the uncertainty and how will resolving the uncertainties improve our understanding of these issues? Right now it is very vague.
Lines 59 - 61: This is very vague framing - The authors argue that studies "remain inadequate" (inadequate how?) and that it "hinders management" (hinders management how?). This section would be significantly improved if authors were more specific about what aspect of past studies was inadequate and how those inadequacies directly affect management practices. Vague, shallow statements like this are essentially fluff unless they can be supported by examples or specifics (possibly with additional citations) showing exactly where the inadequacies are and why they are important.
Lines 45, 62-63, etc.: Throughout this manuscript authors discuss "non-linear" relationships and controls, yet most of their discussions and figures are of linear relationships. What is the non-linearity (and how is linear even defined), where does it come into the analysis, and what specific benefits does inclusion of the non-linear factors provide to the models? These issues are not really addressed in the manuscript.
Line 67: Authors claim that the study "provides new insights into PAN evolution". However, their discussion and conclusions do not really provide much in the way of novel insights beyond observations of known patterns (consistent with textbook-level materials) in a different study area. Authors should make it more clear in the manuscript what the "new insights" they provide are and demonstrate that they are actually "new insights" (perhaps discussing why they were missed previously).
Line 78 / Section S1: For a paper based mostly on an empirical measurement dataset, the PAN measurements are not sufficiently explained. Authors do not provide any accuracies, precisions, or uncertainties on their measurements, nor do they address the accuracy of their calibrations, degree of drift over time, etc. They mention weekly zero / span checks and monthly calibrations but do not provide any quantitative discussion of what the actual uncertainties in their measurements are. It is impossible to assess their data (or how well their models fit their data) without knowing how uncertain the data is.
Lines 87-88: NO2 measured by the Model 42i analyzer (as the difference between NOx and NO) will contain contributions from other NOz species (HONO, PAN, etc.) that might be reactive on the heated molybdenum catalyst. Possibly not relevant, but the authors should at least be aware that their NO2 measurements is not "true" NO2 (e.g. CAPS, photolytic conversion, etc.) and might contain contributions from other nitrogen species.
Line 114: Explain the "magic number" factor of 3600. Shouldn't the units of this also be ppbv per hour and not just ppbv? The units are confusing and inconsistent across the manuscript and should be checked (ppbv vs ppbv per hour, etc.). Are Chem_precursor and PAN_cycling concentration values (ppbv, as stated) or rates (ppbv / hour, etc.) or something else?
Section 2.3:
You are using machine learning to fit a derived parameter (PANgen) that is dependent upon multiple measured parameters (PANt+1, PANt) and another derived parameter (PANd), which also factors in meteorological parameters (e.g. temperature). This is very confusing why the authors chose to use PANgen instead of running the model against their measured parameters (e.g. PAN or deltaPAN). There are lots of assumptions that go into their choice of derived parameter. They also regress PANgen against Chem_precursor and PAN_Cycling, which are not independent (they also depend upon temperature, for example).
Based on these assumptions, they run three models (results in Fig S3) that essentially give identical results (RMSE = 0.5638 vs RMSE = 0.5645). They choose the model with the lowest RMSE (by less than 0.001 out of 0.56) and base their results on this model. Is it possible that a slightly different set of training versus testing data could have given a different model? I think they should either provide uncertainties on their estimates or provide additional justification for choosing XGBoost versus Random Forest (or LightGBM).Lines 181+: Authors should define somewhere what their +/- means (mean +/- 1 standard deviation, or something else) throughout the paper.
Line 191: What defines an "exceedance day"?
Lines 194 - 196: Showing a correlation between PANgen and O3 does not necessarily imply a linkage between "net PAN formation" and "photochemical activity". It is possible that additional factors (temperature, BLH, UV / sunlight, etc.) could be driving the correlations? In several places in this manuscript, authors look at correlations between parameters and assume a causuality relationship when their might or might not be one.Â
Lines 198 - 200: The authors focus a lot on the PAN / O3 relationship but do not address the potential link between PAN, photochemistry, meteorology, and PM. An example of one possible framework in a similar system is Womack et al. (2019, https://doi.org/10.1029/2019GL082028), which shows how nitrogen chemistry and ozone chemistry link summertime ozone and wintertime PM issues. I think downplaying the PAN / O3 / PM connections could be a missed opportunity for the authors of this paper to gain more from their data.
Line 207 - 209: "precursor formation ... with basin meteorology, plays an important role in shaping PAN formation" - this is relatively obvious / textbook-level material rather than new or novel insight. I recommend the authors try to be more specific or show how the specific new insights they provide from their analysis go beyond the basic textbook material and provide novel understanding of the system.
Lines 214 - 215: If the OBM-MCM model shows "satisfactory representation" of the processes controlling PAN formation, why do the authors then need the additional ML model? They claim that they can explain their data largely with the box model, which weakens their argument that the ML models are necessary or provide new insights.
Section 3.2.1: This section is called "PAN Budget Analysis" but a considerable portion of the text (and Figure 2) are focused on PA budgets and PA radical cycling. Please be more clear about when you are discussing PAN versus PA (and the relationship between them) - they are related but they are not the same.
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Citation: https://doi.org/10.5194/egusphere-2026-5149-RC2
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- 1
In this study, the seasonal formation and loss pathways of atmospheric PAN at an urban site in the Sichuan Basin were comprehensively investigated through integrating a one-year observation dataset, an observation-based box model, and interpretable machine learning. Their results revealed that the recombination of PA radicals and NO2 formed through PAN thermal decomposition was the dominant source for atmospheric PAN in Summer, Spring and Autumn, whereas PA radicals formed through photooxidation of typical carbonyls became the dominant PAN source in Winter. In general, the manuscript is well-organized, and results sound reasonable. Therefore, this reviewer recommends the manuscript for publication in ACP.
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Major points:
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Specifics:
Lines 17-18, “distinct seasonal formation pathways” is better changed as “distinct difference of PAN formation pathways among seasons”; “whereas precursor oxidation” is suggested as “whereas photooxidation of typical carbonyls”.
Lines 19-21, the description seemed inconsistent with the results, e.g., both PAN and O3 formation belonged to transition regime in Summer, rather than VOCs limited.
Lines 21-24, this statement should be careful because BLH could not simply classified as a transport-related factor.
Lines 24-25, the intensified PAN cycling was not attributed to elevated photochemical capacity.
Lines 215-217, “production of the radicals via the Chem_precursor and PAN_Cycling pathways was extracted to quantify their contributions to PAN formation” is better replaced by “production rates of PA radicals via the Chem_precursor and PAN_Cycling pathways as well as the major PA loss rates were extracted to evaluate their relative contributions to PAN formation (Table S8, Fig.2)”.
Lines 217-218, this sentence can be deleted.
Lines 218-220, It is better noted the meaning of radical_cycling. What’s the different between radical_cycling and PAN_Cycling? Besides PA formation through the carbonyls’ photolysis and their reactions with OH, the reactions of OH with other VOCs may also produce PA, e.g., MTBE.
Lines 222-227, the comparison seemed a little bit of confusion, please rephrase the sentences, e.g., listed as the same order of contribution pathways as yours. Â Â Â Â
Fig. 2, the title of this figure should be “Diurnal variations of the PA budget and the relative contributions (%) of different precursors to PA in daytime (08:00-20:00, embedded pie charts).
Lines 232-233, the description was inconsistent with Fig. 2. This sentence is suggested as “PA formation pathways exhibited pronounced seasonal shifts in daytime, with contributions of PAN_Cycling (Chem_precursor) being 73.3% (26.7%) in Summer, 63.1% (36.9%) in Spring, 52.9% (47.1%) in Autumn and 33.5% (66.5%) in Winter. How did you obtain the data of 75.5% and 57.1% in this sentence?
Lines 233-242, it is better to discuss the three major PA loss pathways in the four seasons to reveal that the reaction of PA with NO2 was the dominant PA loss pathway for PAN formation in Summer, Spring and Autumn, while the reactions of PA with NO2 and NO were comparable in Winter. Both the formation and loss pathways of PA in daytime were better respectively illustrated as pie charts in the upper and lower panels in Fig. 2. The description and discussion should be consistent with the Figure.
Lines 246-247, the rear half sentence is better deleted because it seemed inconsistent with the results illustrated in Fig. 3.
Lines 260-261, it is better to specify the contributions, e.g., PAN and O3; “and between PAN and O3 formation pathways” can be deleted.
Lines 261-262, this sentence was meaningless, can be deleted.
Line 262-265, “a more dominant role” is better replaced by “a greater role”; “although” should be “whereas”.
Lines 265-268, it is better to illustrate the RIR values of CO in Fig. 3 to support the statement.
Lines 287-290, this sentence seemed unclear. It is better to integrate the results of box model (Fig. 2) with the SHAP analysis for revealing the higher contribution of Chem_precursor to PAN, namely, the PAN_Cycling was slower in Spring than in autumn and summer. Considering the much stronger PAN_Cycling in Summer than Autumn, the approximately same contribution (15%) of Chem_precursor to PAN in Autumn and Summer may be attributed to the stronger photochemical activity in Summer than Autumn.
Lines 290-293, why did you assign BLH as the influential transport-related factor? Air temperature at ground levels strongly affect BLH, resulting in the distinct diurnal variation of BLH. In my opinion, the influential factor of BLH may be attributed to sunlight intensity. Why didn’t you select sunlight intensity (e.g., the TUV measured) as a key factor for ML training?
Lines 300-301, it is better to specify the strongest responses.
Lines 301-302, the strongest influence of PAN_Cycling on PAN concentration should be in Summer, rather than in Spring and Autumn.
Section 3.3.2, this section can be omitted because it presents very few new information for understanding the sources and sinks of atmospheric PAN in comparison with those of OBM and SHAP results.
Lines 347-348, it is not proper to say substantial shifts in PA radicals source pathways because all PA radicals source pathways existed in both clean and O3 episodes.
Lines 349-351, why was the contribution (69.6%) of PAN thermal decomposition to PA lower than the overall result (73.3%) illustrated in Fig. 2? All the percentages listed in this section are better double checked to make sure the consistency with the values illustrated in figures.
Lines 358-364, these sentences are better rephrased for clear description.
Lines 373-375, the description is about the results in Spring, whereas Fig. 6 shows the results in both Summer and Spring.