the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
Formation and chemical evolution of SOA in two different environments: A dual chamber study
Abstract. A dual chamber system was deployed in two different environments to study the potential of ambient air, that was directly injected into the chambers, to form secondary organic and inorganic aerosol. A total of 16 experiments took place during March 2022 in a polluted environment in the Po Valley, Italy which is dominated by anthropogenic emissions. Another 15 experiments were conducted in the Pertouli forest, Greece which is dominated by biogenic emissions. In both campaigns, ambient air containing highly oxidized (average O:C 0.7–0.8) aerosol was the starting point of the experiments and its chemical evolution under the presence of OH radicals was followed. In the Po Valley SOA formation was observed in all experiments but one and the formed SOA ranged from 0.1 to 10 μg m-3. Experiments conducted under more polluted conditions (usually at night and early morning) had significantly higher SOA formation, with the concentration of the organic aerosol at the end being about four times higher than the initial. Also, production of 4–230 μg m-3 of ammonium nitrate was observed in all experiments due to the high levels of ammonia in this area. The produced SOA increased as the ambient relative humidity increased, but there was not a clear relationship between the SOA and temperature. Higher SOA production was observed when the PM1 levels in Po Valley were high. Contrary to the Po Valley, only one experiment in the Pertouli forest resulted in the formation of detectable SOA (about 1 μg m-3). This experiment was characterized by higher ambient concentrations of both monoterpenes and isoprene. In two experiments, some SOA was formed, but its concentration dropped below detection levels after 30 min. This behavior is consistent with local formation in a chamber that was not well mixed. Although both environments have OA with O:C in the range of 0.7–0.8, the atmosphere of the two sites had very different potentials of forming SOA. In the Po Valley, the system reacts rapidly forming large amounts of SOA, while in Pertouli the corresponding SOA formation chemistry appears to have been practically terminated before the beginning of most experiments, so there is little additional SOA formation potential left.
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RC1: 'Comment on egusphere-2024-1317', Anonymous Referee #1, 02 Jul 2024
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The study of Aktypis et al., presents SOA particle formation potential measurements of ambient air at two distinctively different sampling sites, a remote forested area, and a polluted environment. By utilizing a unique, portable dual chamber system, the authors can perturb (or age) the emissions in one chamber, while the second chamber “holds” the ambient emissions as a control. Interestingly, the initial aerosol particles introduced to the chambers were quite oxygenated, as indicated by their high O:C values, and were oxidized further to yield even more oxygenated particles with O:C as high as 1.1. Overall, the authors describe well their findings, however, I do believe that they fail to discuss the potential pitfalls of their approach and methods. As I describe in more detail in my comments below, the addition of HONO as an OH source can significantly alter the chemical regime of the experiments, potentially resulting in unrealistic SOA formation potentials. Additionally, the authors under-utilize available gas phase measurements that can aid in the interpretation of their findings that currently, is rather weak. I hope that my comments below will help the authors to strengthen their arguments and lead to a publishable version of their manuscript.
Major comments:
1. As the authors mention in their methods, HONO was added to the perturbed chamber as an OH source, resulting in NO mixing ratios of 0.5-1ppm (guessing that ppms of HONO were added), with consequent potential implications of its uptake to the particle phase. This further yields several considerations such as:
i) significant alternation of the chemical regime comparing to the ambient – noting that the highest NOx values, even in the polluted environment, are just of the order of a couple of tens of ppb (Squizzato et al., 2013; also cited by the authors). An altered chemical regime could therefore alter the SOA formation potential to an unknown extent, biasing the presented results.
ii) significant formation of inorganic nitrates, as the authors also observe in their study. The substantial presence of nitrates in the particles promote the uptake of water, increase the polarity and further increasing the already unrealistically high absorptive mass. Particularly at the polluted site, concentrations of hundreds of ug m^3 of nitrates could drive the partitioning of a lot of the available IVOC/SVOC to the particle phase, skewing the interpretation of the SOA formation potential.
I believe that the authors should think the potential biases of their experimental setup (see additional suggestions on my comments throughout) to the measured SOA formation potential and provide a clear discussion of the implications for each measurement site, as well as when comparing the two campaigns. Currently, I do not believe that the general conclusions that are being drawn are adequately supported by the presented analysis and discussion.
2. I believe that the authors under-utilize the available measurements of the gas phase components from the PTRs to interpret their results. I understand that the quantification in one of the sites was challenging, however, I strongly believe that even qualitatively, very useful information can be obtained to interpret their findings. PTR-MS is a powerful technique (Yuan et al., 2017), able to identify hundreds of organic precursor compounds entering the chambers. For example, more information can be given regarding the initial composition of the VOC, and their consumption during aging, potentially explaining the differences in the measured SOA particle formation potentials. I feel that nearly completely neglecting these measurements presents a relatively weak and one-sided story that could be significantly stronger if these measurements were utilized for the interpretation of the findings.
General comments:
- I believe that the introduction (particularly the paragraphs 3-5) could be re-written to be a bit more focused to the hypothesis of the paper. This also applies to the whole structure of the paper, which currently, doesn’t feel very coherent.
- Section 2.5: I think that a lot more information is needed here regarding the calibration procedures of the HR-AMS, as well as the PTR. For example, how was the AMS calibrated (including for particle sizing); how overfitting was prevented during the HR data analysis? Similarly, what was the procedure to ensure accurate assignment of ions on the PTR (including calculations for transmission, and ionisation efficiency); were there standards? What were the detection limits (where available)?
- Following to my comment above, I believe that the measured concentrations are quite high to capture size distributions of the components using the AMS (>20 ug m^3 per bin; FigS2, S4). What procedures, and QA/AC of the data, have been followed to ensure that the instrument was operating correctly?
- I believe that the discussion in the comparison of the AMS spectra in section 3.4 is a bit weak. Given that the AMS heavily fragments the aerosol, and the PMF factors are based on a relatively small pool of available fragments to derive the different organic classifications (e.g., LV-OOA), I don’t think it is surprising to find similarities between such factors across different sites. Perhaps additional discussion is required here.
Other/minor comments:
L33: please rewrite, syntax is not great.
L40-43: Please rewrite this sentence, particularly, I don’t understand the “.. atmospheric aging, etc.,” in the context of this sentence.
L44: A reference would be nice here.
L47: Not sure what you mean with the “and the particle phase” in the context of this sentence, please re-write.
L50-60: I think it might worth mentioning here that a lot of recent literature (including articles that the authors have published) have showed that the interactions of the oxidized precursors in the atmospheric environment could be another potential reason for model-measurement discrepancy (McFiggans et al., 2019; Schervish and Donahue, 2020; Voliotis et al., 2021; Takeuchi et al., 2022).
L74: An additional 12-17% mass compared to what? This is not very clear to me, please re-write.
L76: To my understanding, this paragraph is reviewing the aging of bVOC under various conditions and not solely the later generation products. For example, looking at the previous sentence, the authors are referring to high vs low humidity experiments. Therefore, I am not very sure how this last sentence was derived based on the content of this paragraph. I’d suggest changing this statement or re-structure this paragraph to be more focused (see also general comment 1).
L80-81: Not sure this sentence has any meaning in the context of this paragraph. I understand that the health effects of SOA are important, but I believe this statement is unnecessary here.
L113: Perhaps you want to connect these two sentences, “, due to …”, or rephrase the second sentence as it is grammatically incorrect.
L170: It is not very clear to me whether the seed was injected during the photo-oxidation experiment or when the chamber was flushed, and the experiment had finished. In the latter case, since make-up air is not added (based on Kaltsonoudis et al., 2019), I’d expect that the surface/volume ratio of the chamber would be significantly different at the end than at the beginning of the experiment, and therefore the wall-losses would be time-dependent. This could lead to an over-estimation of the particle/gas wall-loss and thereby underestimation of the SOA formed. If I got this wrong, please re-write this section to be clearer.
L215: Could this differential transmission of particles vs gases have affected the partitioning of the organics, and thereby the results from this work? Perhaps a bit of discussion would be beneficial. Also, in relation to my major comment 2, a similar analysis for the transmission efficiency of the gases using the PTR mass spectra could be beneficial.
Fig. S2b: According to the methods section, the SMPS has a range up to 700 nm, and the AMS 1000nm, while the displayed lines for both instruments are reaching >1um; is this a result of fitting? More information is needed here to interpret the results/corrections.
L246: Would be nice to know the variance, and/or the range here rather than just the average.
L272: I personally dislike expressions like “enormous” (here and later in the manuscript) in scientific papers. I would recommend this is removed as it is not affecting the subsequent quantitative statements. Also given the amount of HONO, isn’t this expected (see major comment 1)?
L282: I presume here you are showing results from the AMS and not the PTR. Can you please make this clear?
L310 and L426: This looks quite a big variation in the OH levels that could considerably affect the comparability of the results. What was the reasoning behind this variation? Can you also add the estimated OH on the related tables per experiment and discuss the results in this context?
L324-325: Can you please elaborate why/how the no-SOA case was a test of the system?
L369-370: Can you add a reference here to support this statement?
L390-394: I think you can conduct an ion balance to calculate the amount of organic/inorganic nitrate to be more quantitative.
L483-485: Although I am generally supportive of this argument, looking at the table 2, it looks like in certain experiments, the O:C was lower than the high SOA case (experiment 1), implying less oxygenated aerosol. How do you interpret that in the context of this statement?
L486-488: Could the different T and RH affected the partitioning and thereby your results?
L492-493: Given that you are flooding the system with HONO (and thereby nitrates) and the high fragmentation of the AMS, isn’t it expected that you will see similarities in the spectra?
L531-532: Given my major comments for the unrealistically high NOx leading to a different chemical regime, while forcing the oxidation to progress, I am not sure if you can reach to a such general statement here. I am not disputing the fact that later generation products can contribute to the SOA particle formation, however, I am not sure how important this is for the real atmospheric environment and whether you can derive such general statements.
L547-549: Given the extremely low precursor concentrations (at least given the limited analysis of the PTR data), isn’t it expected that not enough SOA us being formed? Additionally, could it be expected that in low VOC and extremely high NOx atmosphere (due to HONO) the SOA formation could be completed inhibited? Unless you expect to see heterogeneous reactions? In which case the experimental setup is probably not ideal to decouple this. This further links to my general comment 2 related to the utilization of the PTR data to interpret the findings.
L555-557: Given that the night-time experiments produced the highest amounts of SOA in the FAIRARI campaign while no night-time experiments conducted in the SPRUCE-22 campaign, how you can reach to that conclusion? Could perhaps the difference be attributed to the diurnal profile of the VOC emission in each site? By quickly looking at the literature, it seems that the peak of the bVOC emissions in coniferous forested areas could be early morning or late afternoon evening (e.g., Borsdorf et al., 2023), where no experiments were conducted in this study (table 2). Could the design of the study be biasing the obtained results, and the comparison of the SOA formation between the two sites?
References
Borsdorf et al., 2023; https://doi.org/10.3390/atmos14091347
McFiggans et al., 2019; https://doi.org/10.1038/s41586-018-0871-y
Takeuchi et al., 2022; https://doi.org/10.1038/s41467-022-35546-1
Schervish and Donahue, 2020; https://doi.org/10.5194/acp-20-1183-2020
Squizzato et al., 2013; https://doi.org/10.5194/acp-13-1927-2013
Voliotis et al., 2021; https://doi.org/10.5194/acp-21-14251-2021
Yuan et al., 2017; https://doi.org/10.1021/acs.chemrev.7b00325
Citation: https://doi.org/10.5194/egusphere-2024-1317-RC1
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