Measurement report: Vertical distribution of atmospheric particulate matter within the urban boundary layer in southern China – size-segregated chemical composition and secondary formation through cloud processing and heterogeneous reactions

Zhou, Shengzhen; Wu, Luolin; Guo, Junchen; Chen, Weihua; Wang, Xuemei; Zhao, Jun; Cheng, Yafang; Huang, Zuzhao; Zhang, Jinpu; Sun, Yele; Fu, Pingqing; Jia, Shiguo; Tao, Jun; Chen, Yanning; Kuang, Junxia

doi:https://doi.org/10.5194/acp-20-6435-2020

Articles | Volume 20, issue 11

https://doi.org/10.5194/acp-20-6435-2020

© Author(s) 2020. This work is distributed under
the Creative Commons Attribution 4.0 License.

https://doi.org/10.5194/acp-20-6435-2020

© Author(s) 2020. This work is distributed under
the Creative Commons Attribution 4.0 License.

Articles | Volume 20, issue 11

Measurement report

|

04 Jun 2020

Measurement report |

| 04 Jun 2020

Measurement report: Vertical distribution of atmospheric particulate matter within the urban boundary layer in southern China – size-segregated chemical composition and secondary formation through cloud processing and heterogeneous reactions

Shengzhen Zhou, Luolin Wu, Junchen Guo, Weihua Chen, Xuemei Wang, Jun Zhao, Yafang Cheng, Zuzhao Huang, Jinpu Zhang, Yele Sun, Pingqing Fu, Shiguo Jia, Jun Tao, Yanning Chen, and Junxia Kuang

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Final revised paper (published on 04 Jun 2020)
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Preprint (discussion started on 04 Mar 2019)
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Interactive discussion

Status: closed

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

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RC1: 'Review of Zhou et al. paper', Anonymous Referee #1, 07 May 2019
- AC1: 'Reply to Anonymous Referee #1', Shengzhen Zhou, 02 Aug 2019
RC2: 'Review of Zhou et al.', Anonymous Referee #2, 21 May 2019
- AC2: 'Reply to Anonymous Referee #2', Shengzhen Zhou, 02 Aug 2019
EC1: 'Final editor comment: Categorization as Measurement Report', Barbara Ervens, 20 Apr 2020

Peer-review completion

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

AR by Shengzhen Zhou on behalf of the Authors (02 Aug 2019) Author's response Manuscript

ED: Referee Nomination & Report Request started (06 Aug 2019) by Barbara Ervens

RR by Anonymous Referee #1 (20 Aug 2019)

RR by Anonymous Referee #3 (23 Sep 2019)

Suggestions for revision or reasons for rejection

The Authors present original aerosol measurements taken on a tall city tower, including rare observations of size-segregated chemical composition. Measurement periods are short, and the Authors focused on the analysis of specific events. Their results are interesting because They were able to show that aerosol chemical components can be spatially segregated not only horizontally (because of the presence of the buildings and of the heterogeneity of the sources) but also vertically. The analysis of air mass transport and thermodynamics in the lower few hundreds meters above the ground can be blamed for such variability. In spite of such complexity, the Authors' conclusions in the abstract seem very shallow. Just a generic mention to the role of heterogenous chemistry is given. The quality of presentation is poor, and I struggled to understand what specific day of the campaign some of the figures referred to (e.g. Figure 8) and also why that day and not others? The Authors claim that the presence of low-level clouds was crucial for the production of secondary aerosols on certain days. But they do not discuss the presence/absence of clouds on other days, when concentration vertical profiles are more flat. The full elaboration lacks of a coherent analysis, and sometimes hypotheses and conclusions (e.g., about the importance of aqueous phase chemistry) are mixed up in the discussion.
Specific comments:
The Referee#2's comment on the effect of hygroscopic growth on measured impactor size-distribution, in my view, was only partially addressed by the Authors. In the study of Meng and Seinfeld (1993) quoted by the Authors, the ratio between the diameters of the droplet mode and the condensation mode was 3.5 (= 0.7 vs. 0.2), while here such ratio is only 2.3 for sulphate (= 0.75 vs 0.33; section 1 in the Supplementary). Considering that the hygroscopic growth factor for ammonium sulphate at RH 80% is about 1.4 (and obviously greater at RH values approaching the saturation), I would be more cautious in concluding that ambient RH was irrelevant in contributing to shaping the measured size-distributions.

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RR by Anonymous Referee #4 (03 Oct 2019)

Suggestions for revision or reasons for rejection

This paper discusses size segregated measurements of aerosol particle chemistry (major ions, OC and EC) conducted at three vertical levels (ground 118 m-agl and 488 m-agl) in an urban area of China. In addition to trajectories, the WRF model is used as a representation of low-level vertical profiles of temperature, RH and winds in the area of the measurements.

Overall, I find the presentation and writing of the current version to be clear.

The emphasis of the work appears to be to demonstrate that aqueous-phase production of sulphate plays a significant role in the development of the local aerosol and its vertical gradient. Additionally, it is suggested that nitrate formation is influenced by aqueous-phase processes and the presence of sea salt. In my opinion, the authors have presented fairly convincing arguments that these processes are likely involved in a potentially significant way. However, all of these processes have been known and studied for many years, and, as I understand it, the issue of how they affect local observations is really not in the purview of ACP. Therefore, as the paper now stands, I do not believe it is suitable for publication in ACP.

I have a few suggestions: 1) I think it would be valuable, and something that might have more universal appeal, to test WRF-CHEM against your observations to see how well the model does at reproducing your results. To do this, some local observations of state parameters and winds might be needed. 2) The carbonaceous components of the measurements are really under-emphasized in the paper. More emphasis on the size distributions of EC and OC in a relatively high emissions area, coupled with comparisons for other urban areas, regional and remote results might help. 3) In its current form, the paper might be more suitable for Atmospheric Environment, which has more of a focus on urban issues.

Some specific comments:
1) Page 2, lines 22-24 – When you say “highly uncertain”, do you mean sources, formation mechanisms or both? I think the formation mechanisms, at least those that you focus on in this paper, are reasonably well known. There may be issues with the carbonaceous components that better fit ‘highly uncertain’, but you don’t discuss those. Sources, because there are so many, may be highly uncertain, but you don’t address those either.
2) Page 3, lines 4 -6 - Direct emission is not a condensation process. Do you mean that the condensation mode results from condensation of gas-to-particle products condensing on direct emissions?
3) Page 3, lines 10 – 11 - There is evidence for this dating back to 1986 (e.g. Hoppel et al., JGR, 1985).
4) Page 3, line 14 – mechanical processes can also produce particles in the submicron size range.
5) Page 4, line 3 – What are “very dynamic vertical profiles”?
6) Page 4, line 13 – remove “enough”
7) Page 4, line 15 – “aerosol pollution frequently occurs”
8) Page 4, line 28 – page 5, line 3 - Instead, maybe say something like "Hence size-resolved vertical profiles of major components of PM can add to important knowledge of aerosol sources and formation mechanisms in the urban atmospheric boundary layer."
9) Page 5, lines 12-13 – I suggest something like “… were measured, and these observations are used to examine formation mechanisms and sources.”
10) Page 7, line 4 – reference date?
11) Page 7, line 24 – Please explain: e.g., do you mean things like insoluble components of dust?
12) Page 8, line 6 - Why not show PM1 in the main text? It seems that PM1 agrees much better with the sum of your ions, OC and EC, which would imply that much of the difference between your sum and PM2.5 is due to water-insoluble material.
13) Page 9, lines 9-10 – They don't appear to be very dissimilar compared with the polluted day profiles.
14) Paragraph starting “Figure 3” on pages 8-9 - This paragraph seems to have a take-away message that, in a relative sense, the carbonaceous components are more local and more of the inorganics (sulphate and nitrate) are transported from some distance. This might be a point to summarize.
15) Page 9, line 14 – “cleanER”
16) Page 9, lines 19-20 – “The reasons are unclear…”
17) Page 10, line 1 – Some mention of RH is relevant here too.
18) Page 10, lines 7-8 – If true, I suggest "… were the main components of the measured species, but the comparisons with PM1 and PM2.5 suggest these components were relatively small factors in the coarse particles."
19) Page 10, lines 25-27 – Coagulation is important for smaller particles. Please clarify. Also, how likely are either in-cloud coalescence or multiple cloud cycles to impact your results. A reference for in-cloud coalescence is appropriate (e.g. Feingold and Kreidenweis).
20) Page 11, lines 13-16 - In these conditions of fog or relatively small droplets, it is likely that H2O2 would be necessary to support significant aqueous-phase production of sulphate. Later, you mention studies about oxidants and H2O2 in particular. It would be useful to mention them at this point.
21) Page 11, line 23 – replace “on the surface including” with “with”
22) Equations 1 and 2 – I’m not sure either are necessary, but references to these reactions go way back (50+ years).
23) Page 14, line 17 – “Here we consider two…”
24) Page 15, line 5 – replace “also observed” with “simulated”
25) Page 16, line 13 – 0.06 m/s is not strong.
26) Page 16, line 18 – remove “adverse”
27) Page 17, lines 15-17 – Apply your results to such a model (WRF-CHEM).

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ED: Reconsider after major revisions (08 Oct 2019) by Barbara Ervens

AR by Shengzhen Zhou on behalf of the Authors (21 Dec 2019) Author's response Manuscript

ED: Referee Nomination & Report Request started (16 Jan 2020) by Barbara Ervens

RR by Anonymous Referee #4 (04 Feb 2020)

Suggestions for revision or reasons for rejection

The revised paper has improved, and it offers a useful look at the potentially more important processes in the evolution of the components of aerosol particles in this region. The authors enhanced the discussion of OC and EC, and they now include some comparisons with the results of WRF-Chem simulations. However, I find the comparisons and their discussion to be a little disappointing for the following reasons:

• The comparisons are not shown in the main text.
• There are no comparisons with OC, EC or NaCl.
• Other than to say that “it might not be well simulated”, there is no attempt to assess the model’s simulation of cloud with cloud observations (e.g. Figure S11), which is fundamental to their argument for cloud processing.
• Overall, the discussion seems hurried. It does not carefully consider all the major issues that may be associated with the comparison to their measurements and the use of the model to develop the conceptual picture they present in Figure 9.

The authors state that model evaluation “is beyond the scope of this study”, yet they use the model results (e.g. Figure 7) to build their concept of the processes affecting haze formation in this region (Figure 9). This is not evaluation for the model. It should be evaluation to support your results, in other words, “does the model support their portrayal of the processes?”. I suggest addressing that broader question by addressing the following more specific questions:

• Is it reasonable to expect that these data represent the grid box(es) that are being compared?
• How do the WRF-Chem simulations of OC, EC and NaCl compare to the observations? This will help to further identify model limitations.
• If WRF-Chem does not simulate sulphate in a reasonable way, then might it be because the temperature structure and winds of the lower levels are incorrect (as suggested by their statement that SO2 was underestimated “possibly due to the insufficient upward transport of SO2”), because SO2 emissions are underestimated or because of a deficiency in the aqueous phase conversion of SO2 to sulphate (e.g. representation of cloud; underestimation of oxidant concentrations; etc.)?
• Based on RH, it would seem that the model gets the clouds about right in the winter. Is that correct? What about autumn?
• If upward transport is the problem, then is it valid to use the profiles in Figure 7 to develop the concept shown in Figure 9?

Other comments:

1) Page 1, line 21 – I find the statement starting with “Great progress has recently been made” needs to be referenced. I don’t understand how great progress can be made at ground level, without making it aloft. Ground level and the air above are connected. If you match things well at the ground, but not above, then it is not progress. I suggest the authors think more about their opening statement.
2) Page 2, line 4 - "droplet mode" is a less commonly used term. It has basis, but you need to discuss it first before using it. Also, it presumes the process that you are trying to establish. Use it in your discussion, but I suggest removing 'droplet' here and on line 7 as in my next comment.
3) Page 2, lines 7-10 – I suggest "Our results suggest that much of the sulfate and nitrate are formed from aqueous-phase reactions, and we attribute coarse mode nitrate formation at the measurement site to the heterogeneous reactions of gaseous nitric acid on existing sea-derived coarse particles in autumn.
4) Page 2, lines 10-11 - This sentence is repetitious. Reduce to "Case studies show that in combination with stagnant weather conditions, sulfate and nitrate from aqueous-phase and heterogeneous reactions contribute to haze formation during autumn and winter in the PRD region." Also, define 'PRD'.
5) Page 3, lines 8-12 – I believe that ‘droplet mode’ resulted from "fog" studies. Often, there are significant differences between fog and cloud, and those differences are reflected in residual size distributions. It seems that you are knowledgeable about this, but you need to make it clear in this paragraph.
6) Page 4, line 15 – Change “the vertical size-resolved chemical composition” to “size-resolved chemical composition in the vertical”
7) Page 4-5, lines 28-2 - “Additionally, more consistent evidences of aerosol formation through heterogeneous reactions are needed from field measurements, laboratory experiments and model simulations.” Is awkward. Perhaps “Additionally, more studies of aerosol formation resulting from heterogeneous reactions are needed from field measurements, laboratory experiments and model simulations.”
8) Page 5, lines 17-20 – There is no mention of modelling here. Evaluation of the model is not one of your objectives, but the use of modelling in evaluating your observations is part of your work, and I think it should be mentioned.
9) Page 8, line 25 – page 9, line 4 – I don't see the need for this classification. It adds unnecessary words, and you never use it beyond here. You only have 3 measurement altitudes, and you do not use “Type…” in any of the figures. Just start with ay something like, “We classify the ... components into those peaking at the ground, those peaking at 118 m and those peaking at 488 m”, and modify the remainder of the paragraph accordingly. Also, I think these statistics should be in the main text, if you are going to discuss them here.
10) Page 9, line 15 – “likely”; line 18 – “cleanER”
11) Page 12, lines 15-18 – The proposition you refer to here was put forward decades ago. Re-write as "The coarse-mode nitrate was likely formed ... coarse particles (e.g. Anlauf ...)."
12) Page 12, line 20 - 6 - This equation isn't necessary. I suggest removing it and adding the references to the list beginning with Anlauf et al.
13) Page 12, lines 21-22 – This sentence repeats what is said four lines above. Remove it, and add the references to the “(Anlauf et al….)” list.
14) Page 12-13, lines 28-1 - At best, "activation" is misleading in this context. Substantial water uptake by coarse NaCl particles can, and more likely occurs without true 'activation'. Replace with something like "Sea salt particles can grow by water uptake in fogs and clouds." I think this entire discussion could be better integrated and shortened, since the preference of HNO3 for NaCl over Calcium compounds that you mention is likely related to water solubility. I would make this point on line 25, and then refer to deliquesced particles, fog droplets and cloud droplets. As it stands now, it is as if the aqueous-phase processes are in addition to whatever drives your finding, stated on lines 22-24, and as further demonstrated by the repetitious statement on line 5 of page 13.
15) Page 14, line 2 – “were slightly higher”
16) Page 14, line 11 – “demonstrating more aged aerosol” - Are you saying this simply because the aerosol was sampled at a higher elevation?
17) Page 14, lines 12-15 – Might some of the winter salt particles be attributed to dry salt lakes in the interior of China?
18) Page 14, line 18 – “smallER”
19) Page 14, lines 21-22 – But the profiles of SO4=and OC differ. Secondary contributions to SO4= appear to be more elevated than OC, at least in autumn.
20) Page 14, line 24 - The ratio is determined by 2 quantities. A change in the ratio doesn't necessarily result from a change in just one of those quantities. Maybe the ratio at the source differs, or maybe precipitation near the source remove some of the particles, including EC, after which the sulphate, nitrate and OC are replenished by secondary reactions. The statement, “indicating the presence of secondary organic aerosols”, needs more justification.
21) Page 15, lines 24-25 – What about radiative cooling?
22) Page 16, line 1 – Should be Fig. 7a?
24) Page 16, lines 14-15 – "Our results suggest that aqueous-phase and heterogeneous reactions contributed significantly to the sulfate and nitrate in the PRD region during this episode.
25) Page 16, line 2 – As in my first review, this is NOT "strong convection". I suggest "Low-level cloud was observed during this period, associated with weak convection simulated by WRF.”
26) Page 17, line 3 – What is meant by “aggravated”?
27) Page 17, discussion at end of Section 3.3 – There is no discussion of precipitation in the paper. Was there precipitation? If so, might it have played a role?
28) Page 17, line 23 – Figures S13 and S14 should be in the main text.
29) Page 18, line 21 – “Vertical characteristics and potential formation processes of…”

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ED: Reconsider after major revisions (05 Feb 2020) by Barbara Ervens

AR by Shengzhen Zhou on behalf of the Authors (18 Mar 2020) Author's response Manuscript

ED: Referee Nomination & Report Request started (25 Mar 2020) by Barbara Ervens

RR by Anonymous Referee #4 (12 Apr 2020)

ED: Publish subject to minor revisions (review by editor) (14 Apr 2020) by Barbara Ervens

Dear Authors,

thank you for your revised manuscript. I agree with the referee that the manuscript has improved and the modeling represents now an essential part of the study, but I also share the following concerns with the referee:

The understanding of the main underlying processes, namely SNA formation, has not greatly advanced as they have been explored in many previous studies. Admittedly, your data set is new and rather unique as vertically resolved data are not commonly available.
Your efforts to add a model component to your study is an aspect that exceeds many previous studies that only focus on presenting measurement data. Given the uniqueness of your data set, it might have been a chance to identify weaknesses in the representation of SNA formation in the widely used WRF Chem model that could improve this model and thus provide an improved tool for the community. However, you state that such recommendations for model improvement are beyond the scope of the study.
Such conclusions on model performance and recommendations on how to advance it would be needed to make your study stand out from other studies that only focus on data showing SNA formation. I do not agree that your study ‘reports substantial new results and conclusions from scientific investigations of atmospheric properties, and processes within the scope of the journal.’ Further it does not include sufficient ‘substantial advances and general implications for the scientific understanding of atmospheric chemistry and physics.’ - which are the standards of research articles published in ACP.
https://www.atmospheric-chemistry-and-physics.net/about/manuscript_types.html

I would like to draw your attention to a new manuscript category, recently introduced to ACP for manuscripts that 'report substantial new measurement results, but where the implications for atmospheric chemistry and physics are less developed. These manuscripts could be published as Measurement Reports that present substantial new results from measurements of atmospheric properties and processes from field and laboratory experiments. Analysis of the measurements may include model results and conclusions of more limited scope than in research articles.'

In order to finalize the review process for your manuscript, I suggest you three options:

1) Your manuscript can be published as a Measurement Report. In addition to the minor/technical changes listed below, you would need to change the title to “Measurement Report: Vertical distribution of atmospheric particulate matters within urban boundary layer in southern China: size-segregated chemical composition and secondary formation through cloud processing and heterogeneous reactions”. Please also contact the editorial office (editorial@copernicus.org) and request re-categorization of your manuscript, referring to my suggestion.

2) You expand on the description of the model performance such that it is clear which processes are poorly represented in WRF Chem and what the most sensitive parameters and processes are. In addition, you need to restructure your manuscript such that the observation/model comparison represents a major part of the paper. In addition, there should be an additional section where you discuss which conclusions you draw based on this comparison and what the greatest needs are for model improvement in terms of physical/chemical/meteorological aspects in order to improve SNA description in models. Please take the referee comments also into account. I might send out the revised manuscript to referees.

3) You consider a different journal for your manuscript that is more focused on local air pollution.

Best regards
Barbara Ervens

-----------------------

Minor/technical comments:
p. 1, l. 25: replace ‘were’ by ‘was’
p. 3, l. 20: replace ‘reaction mechanisms’ by ‘reactions’
p. 5, l. 1: This sentence seems to partially repeat the text from the previous one: “quantification of the aerosol formation through heterogeneous reactions under real atmospheric conditions” and “more studies of aerosol formation resulting from heterogeneous reactions are needed from field measurements”. Please reword or shorten.
p. 9, l. 22: replace ‘likably’ by ‘likely’
p. 12, l. 17: add ‘by’ (formed by the heterogeneous reactions…)
p. 14, l. 18: replace ’much’ by ‘very’
p. 14, l. 20: ‘Jaffrezo’ misspelled
p. 16, l. 21: Did you use WRF or WRF-Chem for these simulations?
p. 16, l. 22: add ‘on’ (than on event days)
p. 17, l. 20: ‘Figure 10 …’
p. 17, l. 22 : add ‘it’ (while it was in ….)

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AR by Shengzhen Zhou on behalf of the Authors (16 Apr 2020) Author's response Manuscript

ED: Publish as is (20 Apr 2020) by Barbara Ervens

AR by Shengzhen Zhou on behalf of the Authors (25 Apr 2020) Manuscript

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Short summary

In this work, measurements of size-segregated aerosols were conducted at three altitudes (ground level, 118 m, and 488 m) on the 610 m high Canton Tower in southern China. Vertical variations of PM and size-segregated chemical compositions were investigated. The results indicated that meteorological parameters and atmospheric aqueous and heterogeneous reactions together led to aerosol formation and haze episodes in the Pearl River Delta region during the measurement periods.