Modelling the contribution of biogenic volatile organic compounds to new particle formation in the Jülich plant atmosphere chamber

Roldin, P.; Liao, L.; Mogensen, D.; Dal Maso, M.; Rusanen, A.; Kerminen, V.-M.; Mentel, T. F.; Wildt, J.; Kleist, E.; Kiendler-Scharr, A.; Tillmann, R.; Ehn, M.; Kulmala, M.; Boy, M.

doi:https://doi.org/10.5194/acp-15-10777-2015

Articles | Volume 15, issue 18

https://doi.org/10.5194/acp-15-10777-2015

© Author(s) 2015. This work is distributed under
the Creative Commons Attribution 3.0 License.

Special issue:

The Pan European Gas-Aerosols Climate Interaction Study...

https://doi.org/10.5194/acp-15-10777-2015

© Author(s) 2015. This work is distributed under
the Creative Commons Attribution 3.0 License.

Articles | Volume 15, issue 18

Research article

|

28 Sep 2015

Research article |

| 28 Sep 2015

Modelling the contribution of biogenic volatile organic compounds to new particle formation in the Jülich plant atmosphere chamber

P. Roldin, L. Liao, D. Mogensen, M. Dal Maso, A. Rusanen, V.-M. Kerminen, T. F. Mentel, J. Wildt, E. Kleist, A. Kiendler-Scharr, R. Tillmann, M. Ehn, M. Kulmala, and M. Boy

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Final revised paper (published on 28 Sep 2015)
Supplement to the final revised paper
Preprint (discussion started on 12 Nov 2014)

Interactive discussion

Status: closed

AC: Author comment | RC: Referee comment | SC: Short comment | EC: Editor comment

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- Supplement

RC C9670: 'Review of "Modelling the contribution of biogenic VOCs to new particle formation in the Jülich plant atmosphere chamber" by Liao et al.', Anonymous Referee #1, 26 Nov 2014
- AC C12922: 'Answers to Anonymous Referee 1', Pontus Roldin, 03 Apr 2015
RC C10302: 'Review of Liao et al.', Anonymous Referee #2, 18 Dec 2014
- AC C12935: 'Answers to Anonymous Referee 2', Pontus Roldin, 03 Apr 2015
RC C10346: 'Review of "Modelling the Contribution of Biogenic VOCs to New Particle Formation in the Jülich Plant Atmosphere Chamber" by Liao et al.', Anonymous Referee #3, 19 Dec 2014
- AC C12946: 'Answers to Anonymous Referee 3', Pontus Roldin, 03 Apr 2015

Peer-review completion

AR: Author's response | RR: Referee report | ED: Editor decision

AR by Pontus Roldin on behalf of the Authors (04 Jun 2015) Author's response Manuscript

ED: Referee Nomination & Report Request started (04 Jun 2015) by Ari Laaksonen

RR by Anonymous Referee #1 (08 Jun 2015)

Suggestions for revision or reasons for rejection

This paper describes results of modeling particle measurements in stirred-flow reactor chamber experiments consisting of dark and light-induced reactions of organic compounds emitted from plants (BVOCs) in the presence of ozone, SO2, and NOx. The model used a relatively detailed atmospheric mechanism to represent the gas-phase reactions with additional lumped organic reactions to represent particle formation and with a nucleation and particle growth model. Effects of different assumptions regarding the relative importance of H2SO4 and condensable organic products in the nucleation model were examined. Fair fits were obtained to the particle number and volume data, though parameters had to be adjusted to fit these data. The subject matter may be appropriate for publication in this journal, though as discussed below the irradiation experiments are not good representations of atmospheric conditions.

This is a revised version of a manuscript that I previously reviewed. This new version incorporates several improvements in the model employed, gives much better discussions of the methods and results, and has much more modest and appropriate conclusions. The main conclusion is now that the type of experiment being modeled is not ideal for evaluating mechanisms for new particle formation, though they can fit their data with several reasonable models. The results are suggestive but not conclusive, and overall the tone of the conclusion is appropriate given this. Even though the results are not conclusive the experimental and modeling results shown are of interest and do indicate effects of varying assumptions that can be made for the conditions that are studied. Because of the interest in particle formation and the complexities in modeling it, this paper makes a sufficient contribution for it to be appropriate for this journal.

Although this manuscript is an improvement over the previous version, I still have some problems with the discussion and presentation of the methods and results in some cases that I think the authors should consider. These are discussed below.

In Section 2 the description of the light source is still not adequate. Figure S1 shows the spectrum of the "discharge lamps used for illumination and to simulate the solar light spectrum", but not the UV lights that actually drive the photolysis reactions during the irradiation period. The spectrum on S1 has no intensity in the UV region that causes the photolysis of O3 to O1D that forms the OH radicals. To only show this spectrum implies it is the main light source, which isn't the case.

I found the discussion of the mechanisms in Section 3.1 and of the tests carried out with different assumptions about the mechanisms in Section 4.2.2 somewhat unclear. They need to clarify what they mean by "included the first order reactions of OH, O3, and NO3" with the compounds that are not in MCM. These are not actually first order reactions. Do they mean the INITIAL reactions of the compounds with OH, O3, etc? How were these represented? They mentioned using MCM pathways developed for other compounds in some cases, but not for all. It looks like they used different mechanisms and assumptions in their calculations in order to look at the effects of the differences, but the discussion doesn't clearly indicate the specific mechanisms used. Were the parameterized representations shown in Equations R2-R4 used in all model calculations or only some? What is meant in Section 4.2.2 by "condensable organic compounds represented by MCM compounds" and "simulations with only one non-volatile condensable organic compound"? Perhaps they should give examples of mechanisms for the different types of VOCs that were used in the calculations.

Figure S4 shows that treating SOA particles like a solid causes the model to predict a slower decay in particle volume when the lights are turned off. If the difference shown in the figure is significant, maybe it should be given more attention in the discussion. Or could uncertainties in how well mixing is represented in the reactor affect decay rates more than the differences between the two models shown in this figure? If this were the case, perhaps this shouldn't be mentioned at all (except to state that the data can't distinguish between these assumptions unambiguously) because the two models shown in Figure S4 may be giving the same results to within the mixing characterization uncertainty.

In Section 3.7, page 17, lines 6-11 they state that their "first attempt" to model the experiments by using the gas-phase mechanism to simulate O3 and OH it "couldn't capture" the decrease in O3 and the increase in OH during the lights-on period, so they used a model where O3 and OH were used as input data instead. Does this mean the model predicted no OH increase or O3 decrease at all or just too little, and how much too little? Or is the model predicting way too much of these, or that they are happening much faster or slower? This affects the credibility of their model and how well they are capturing the conditions of the experiments. At a minimum they should show the results of their "first attempt" on Figure 4 or something like it (not in the Supplementary materials). The difference between the model and the data would indicate how well they understand and have characterized the system. The reader needs to see this.

Poor model performance predicting O3 and OH could be explained by poor representation of the photolysis rates in the model. They said the photolysis rates were calculated from the sprectrum of the light source, but the spectrum of the discharge lamps shown in Figure S1 isn't relevant to the photolysis using the UV lamps and the UV lamp spectrum is not shown. They state the the UV lamp intensity corresponded to an "O(1D) photolysis rate of 2.9e-3 sec-1". Do they mean O3 photolysis to form O1D? This is about 15-20 times faster than this photolysis in the lower atmosphere.

The test they did to show that the model results are not sensitive to how UV photolysis is treated in the model is not convincing. If I an understanding this discussion, their model uses the measured O3 and OH as model inputs, thus forcing the model to agree with the measured radical and oxidant levels regardless of how photolysis is treated. A better test would be to see the effect on the results of the simulations where O3 and OH were produced by gas-phase chemistry. This test would almost certainly show a large effect because it is the UV photolysis that is forming the radicals.

The differences between the model and experimental results on Figure 6a and S9 are interesting because they show the importance of properly representing how the gas-phase compounds behave on the chamber walls. This is one clear result of this work. I suggest showing the data on S9 along with Figure 6a. If space is a concern then Figures 6b or 6c could be removed, because (to me) they aren't as interesting as what is shown on S9. However, the curve from S9 could be added to 6a without impacting readability if formatted properly. Alternatively, it could be added to something like Figure 8.

I am not sure that Figure 9 is necessary since it seems to have basically the same information about model performance as Figure 8. The only difference is that Figure 8 shows absolute PM formation while Figure 9 shows yields relative to how much the VOCs react. But the model simulations use OH levels derived from amounts of VOC reacting, so the model is forced to predict the correct amounts of VOC reacting in any case. Therefore, predictions in this regard are not a test of model performance.

I don't think the correlations between measured and modeled particle number concentrations shown on Table 3 give a good indication of which model is best, especially since they do not vary that much (from 0.887 to 0.977). Much better indications of model performance are shown in the plots shown on Figure 12. However, Table 3 is a good summary of the test calculations so is useful for that reason. Unfortunately, the correspondence between the labels on Figure 12 and the entries on Table 3 are not clear in some cases. The discussion should focus more on Table 3 and what it shows about the model. For example, no mention is made about the poor performance of the models labeled as "J=A[H2SO4]" and "J[H2SO4][ELVOCnucl]" in predicting PM before the lights are turned on, contrary to observations. Note that the model labeled "J[H2SO4][ELVOCnucl]" gives among the best correlations but I would reject it on the basis of significant overprediction of PN before the lights are turned on on the first day. Nevertheless, the last sentence of the conclusions section states that this model gives the best agreement.

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RR by Anonymous Referee #2 (17 Jun 2015)

Suggestions for revision or reasons for rejection

This manuscript is the revised submission of Liao et al. manuscript presenting results from real plant BVOC emission oxidation, leading to SOA formation. The scientific quality of manuscript has improved since the initial submission. However, the increase in the modelling details has made the manuscript difficult to follow. It is clearly missing the main message. At the end of introduction reader gets an impression that the study is to evaluate model performance, but based on the abstract it is to understand what processes are controlling SOA formation and nucleation of new particles. In the conclusion reader can find maybe the most important statement that chamber measurements are not ideal for studying aerosol nucleation. Authors should do a better job explaining what are the new findings in this study and how does those support or contradict previous findings.

Wall losses: It is stated that wall losses of compounds with low vapor pressure are their main sink. Thus it is questionable whether these compounds can be studied in smog chambers. This could be stated even more clearly than now.

SOA formation: There is some tuning of parameters with 2D-VBS setup and heterogeneous chemistry needed with MCM needed to explain observations. After this it is not a surprise that in the case of only few measurement days a good agreement can be achieved. Why is the change in the composition between day 1 and rest of the days causing such a big difference? Now it is just mentioned without too much analysis. Something wrong in the modelled chemistry? At some points it is quite difficult to follow which model is used and especially why. So again here the main findings could be emphasized more.

Nucleation parameterization: Different parameterizations were used to describe new particle formation from precursor gases. However, based on results, it seems like as good results are achieved assuming constant formation rate than with parameterizations. There are big uncertainties in the wall losses of compounds participating on new particle formation, so can this kind of chamber be used at all to study natural particle formation? How uncertain are ELVOC concentrations?

Minor comments:

Page 8, equations 1-6: Constants should be numbered to highlight those are always different with different parameterizations.

Page 8, line 26: Is the molar mass 500 g/mol or 325g/mol given on page 6?

Page 9, line 17: There is always some numerical diffusion when single particles are not followed. With fully-moving approach it is happening during new particle formation.

Page 9, line 30: Supplement does not show that at least 400 bins are required for modelling, but instead that 40 is not enough.

Page 11, lines 8-11: When particles are considered as solid, is the decrease in volume caused solely by dilution? What is the role of evaporation?

Page 15: line 22: Remove “saturation”. It is confusing to discuss about saturation vapour pressure with mixtures as saturation usually refers to pure compounds.

page 22, lines 18-19: Is it only Kelvin effect that affects mole fractions?

Table 3: Over what time are coefficients of determination calculated. The values seem quite high and differences between best parameterizations negligible. Activation type H2SO4 parameterization shows higher R2 than kinetic even it gives particles also when lights are of, which seems strange. Maybe using R2 is not a good metric here to evaluate which parameterization is the best. At least based on Figure 12 the differences should be bigger than presented in Table 3.

Figure 6: In panel c, there is only one tick on vertical axis, so impossible to see how big differences are.

Figures 8 and 9: different blue colors are too similar.

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ED: Reconsider after major revisions (19 Jun 2015) by Ari Laaksonen

AR by Pontus Roldin on behalf of the Authors (21 Aug 2015) Author's response Manuscript

ED: Referee Nomination & Report Request started (21 Aug 2015) by Ari Laaksonen

RR by Anonymous Referee #1 (03 Sep 2015)

Suggestions for revision or reasons for rejection

This paper describes results of modeling particle measurements in stirred-flow reactor chamber experiments consisting of dark and light-induced reactions of organic compounds emitted from plants (BVOCs) in the presence of ozone, SO2, and NOx. The model used a relatively detailed atmospheric mechanism to represent the gas-phase reactions with additional lumped organic reactions to represent particle formation and with a nucleation and particle growth model. Effects of different assumptions regarding the relative importance of H2SO4 and condensable organic products in the nucleation model were examined. Fair fits were obtained to the particle number and volume data, though parameters had to be adjusted to fit these data. The subject matter may be appropriate for publication in this journal, though as discussed below the irradiation experiments are not good representations of atmospheric conditions.

This is the third version of a manuscript that I previously reviewed. This second version incorporates several improvements in the model employed, gave much better discussions of the methods and results, and had much more modest and appropriate conclusions. The main conclusion is now that the type of experiment being modeled is not ideal for evaluating mechanisms for new particle formation, though they can fit their data with several reasonable models. The results are suggestive but not conclusive, and overall the tone of the conclusion is appropriate given this. Even though the results are not conclusive the experimental and modeling results shown are of interest and do indicate effects of varying assumptions that can be made for the conditions that are studied. Because of the interest in particle formation and the complexities in modeling it, this paper makes a sufficient contribution for it to be appropriate for this journal.

Although the 2nd version was a significant improvement over the previous version, I still had some problems with the discussion and presentation of the methods and results in some cases that I thought the authors should consider. I believe the current (3rd) version and the authors' response to my previous comments addressed my major concerns, and I believe it is acceptable for publication after addressing only a few minor issues, discussed below.

In Section 3.1, Page 6, lines 15-20, they say that they represented only the initial reactions of OH, O3, and NO3 with some compounds whose subsequent reactions were not represented in MCM "considered as a sink of OH, O3, and NO3 without any other influence on ... gas-phase chemistry. However, at least the OH reaction are not really sinks for OH, they regenerate most of the OH back after some NO to NO2 conversions. The NO to NO2 conversions (which affect ozone formation and, indirectly, radical levels) are also ignored in the O3 and NO3 reactions that are neglected. This isn't important in this application because the error in ignoring the regenerated OH doesn't matter, since they are using OH calculated from consumption rates in the model, and their main interest is calculation of rates of formation of particle precursors, not O3. However, it would have been less of an approximation to use reactions of the most similar MCM species, as they did with the other compounds considered more important. They don't need to re-do the calculation, but just point out that this approach affects accuracy in the model in predicting radicals and ozone. Note that the discrepancies shown on Figure 3 cannot be explained by this omission in the model.

It might be useful to include in Table S1 a footnote indicating how the subsequent reactions were represented, which could be (1) based on MCM for this compound, (2) based on MCM for another compound (state which), or (3) only the initial reaction is represented, not the reactions of radicals or species formed. This is stated in the text, but having the footnotes here is a good reference and may allow shortening the text if desired by the editor.

The curves with the yellow dashed lines on Figure 4, which seem to be exactly on top of the solid black line, should included in the legend on the figure as well as the figure caption.

I didn't notice this in my previous review, but it looks like Table 2 has three columns. It might be helpful to have column headers in this case.

In Section 4.2.1, page 22, lines 4-6 they state that their model simulations shown on Figure 6a with FEP parameters was about 2-3 times higher than observed. They should say this is for Day 1. For Days 2-4 the overprediction wasn't near as much (about 50% higher).

It would have been helpful to me if Table 3 showed which simulations used "R1" and "R2" so the reader doesn't have to refer back to elsewhere in the text to see what this means. Either that use terms that correspond to the captions on Table 3 when discussing Table 3 and Figure 11 in the text. My understanding is that R1 corresponds to "SQT ox by O3" and R2 corresponds to "SQT ox by OH". If I am not understanding this correctly, then the discussion has to be clarified.

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ED: Reconsider after minor revisions (Editor review) (08 Sep 2015) by Ari Laaksonen

AR by Pontus Roldin on behalf of the Authors (09 Sep 2015) Author's response Manuscript

ED: Publish as is (11 Sep 2015) by Ari Laaksonen

AR by Pontus Roldin on behalf of the Authors (14 Sep 2015)

Short summary

We used the ADCHAM model to study new particle formation events in the JPAC chamber. The model results show that the new particles may be formed by a kinetic type of nucleation involving both sulphuric acid and organic compounds formed from OH oxidation of volatile organic compounds (VOCs). The observed particle growth may either be controlled by the condensation of semi- and low-volatililty organic compounds or by the formation of low-volatility compounds (oligomers) at the particle surface.