Alteration of the size distributions and mixing states of black carbon through transport in the boundary layer in east Asia

Miyakawa, Takuma; Oshima, Naga; Taketani, Fumikazu; Komazaki, Yuichi; Yoshino, Ayako; Takami, Akinori; Kondo, Yutaka; Kanaya, Yugo

doi:https://doi.org/10.5194/acp-17-5851-2017

Articles | Volume 17, issue 9

https://doi.org/10.5194/acp-17-5851-2017

© Author(s) 2017. This work is distributed under
the Creative Commons Attribution 3.0 License.

https://doi.org/10.5194/acp-17-5851-2017

© Author(s) 2017. This work is distributed under
the Creative Commons Attribution 3.0 License.

Articles | Volume 17, issue 9

Research article

|

12 May 2017

Research article |

| 12 May 2017

Alteration of the size distributions and mixing states of black carbon through transport in the boundary layer in east Asia

Takuma Miyakawa, Naga Oshima, Fumikazu Taketani, Yuichi Komazaki, Ayako Yoshino, Akinori Takami, Yutaka Kondo, and Yugo Kanaya

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Final revised paper (published on 12 May 2017)
Supplement to the final revised paper
Preprint (discussion started on 08 Jul 2016)

Interactive discussion

Status: closed

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

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- Supplement

RC1: 'Review of "Alteration of the microphysical properties of black carbon through transport in the boundary layer in East Asia," by T. Miyakawa et al., submitted to Atmospheric Chemistry and Physics.', Anonymous Referee #1, 20 Jul 2016
- AC1: 'Responses to the reviewers’ comment', Takuma Miyakawa, 18 Oct 2016
RC2: 'Review of Miyakawa et al', Gavin McMeeking, 10 Sep 2016
- AC2: 'Responses to the reviewers’ comment', Takuma Miyakawa, 18 Oct 2016

Peer-review completion

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

AR by Takuma Miyakawa on behalf of the Authors (19 Oct 2016) Author's response

ED: Reconsider after major revisions (08 Nov 2016) by Ryan Sullivan

Dear Authors,

Thank you for submitting your revised manuscript. Unfortunately, you have not adequately addressed the many comments and concerns raised by the Referees in your Response to the Referees, nor have you significantly revised your manuscript to consider the Referee comments. In many cases your response to the Referee does not actually directly address the question being raised. Instead you focus on another aspect loosely related to the question raised by the Referee, instead of directly answering the question. In some other cases, your response to the Referee involved just deleting the section/sentence in your manuscript in question. This does not properly address the question or concern under discussion, and further weakens the quality of the science and strength of your arguments presented in your paper. Some more specific comments follow below.

(Note that I looked at the Track Changes version of the manuscript submitted with the Author’s Response when making my decision, and therefore the incorrect version of the manuscript originally submitted and then updated on Nov. 8th did not affect my decision.)

In order to proceed with peer review, you will need to further revise your manuscript to properly address the many important and valuable points and concerns raised by the Referees. Please note that the 2nd Referee echoed the comments raised by Referee #1, highlighting the importance of these comments. As part of your revisions, you must also produce a new more comprehensive Response to the Referees that properly responds to the specific comments being raised. In your point-by-point response please paste the section of the manuscript text that has been changed to address that point, so it is immediately clear how the manuscript has been revised to address that question. Your revised manuscript submitted actually contains only a few substantial revisions. The manuscript must be revised to properly addressed the major comments raised during peer-review. Be sure to address the specific question that was raised by the Referee, instead of side-stepping the issue by discussing a different but related issue.
In your revisions please refrain from making small numerous changes to the manuscript text, correcting typos and grammar, etc. These distract from focusing on what revisions were made to the actual science, results, and arguments of the paper. It is not appropriate to make so many extensive changes to the manuscript’s language and wording while it is undergoing peer review.

In your Response summary a major revision you listed in your bulleted list was revision of the manuscript’s Discussion section, yet this was in fact barely changed. Only the final paragraph was significantly modified, and this did not change the central points raised in the Discussion.

I agree that the focus only on the sulfate concentrations measured by the ACSM is odd and seems inappropriate. At other points in the paper the importance of organic components mixed with BC are discussed. The ACSM measurements should be presented, so the contributions of all the major species measured at these sites is known (e.g. sulfate, nitrate, organics, others).

The response regarding the proposed small contribution from washout is not clear. This should be discussed more clearly and quantitatively in the main text, with citations to key references, instead of just putting all the details in the SI. Please provide a much more detailed response regarding this calculation and the inherent assumptions and uncertainties in your response to Referee #1. The calculated washout lifetimes seem to be unrealistically long.

Referee #1 Comment on Line 284: Your response and revisions do not adequately address the questions raised regarding the appropriateness of using the correlation between CO and SO4 to conclude that the SO4 was secondary and coated the BC particles. While SO4 and its precursors are co-emitted with CO, there are many other possible combustion sources that emit CO but emit much less SO2/SO4. Assuming that most or all of the SO4 and CO measured were co-emitted is not a justifiable assumption.

Referee #1 Comment on Line 317-319: Your response does not actually address the point raised regarding how the slopes in Fig. 6b do not appear to be different enough to justify your conclusion that the controlling removal process is rainout.

Referee #1 Comment on Line 372 regarding the BC peak diameter from the SP2: You state that a difference in ~1 fg BC can be resolved within the SP2’s uncertainties, but do not state these uncertainties. Your response is too vague and requires more specific quantitative details to adequately respond to the Referee.

Referee #1 Comment on Line 373: You have not addressed the main concern raised regarding the supposed evidence for the selective removal of large BC particles, and how this evidence is not clear in the presented size distributions.

Referee #2 comment on SP2 BC mass/number distributions: The Referee’s question regarding the need for more details on when BC core vs. shell diameters are being discussed has not been addressed.

Referee #2 comment on ACSM data: The focus only on the sulfate measurements is not appropriate. You need to expand the results presented to discuss the full set of measurements from the ACSM. Your response regarding this question did not satisfactorily answer the Referee’s question. Discussing how SO2 and CO share the same emission sources (which as discussed above is not a great assumption) does not actually explain why you don’t present ACSM measurements of other aerosol components such as organics, ammonium, or nitrate. If you are going to assume that sulfate is the only major secondary aerosol component mixed with the BC (line 195), you must justify this assumption based on the measurements available. I would be surprised if there were not significant contributions from other secondary species such as organic carbon. On Page 343 you discuss another study that did observe organic coatings on BC particles in East Asian outflow.

Ryan Sullivan
ACP Co-Editor

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AR by Takuma Miyakawa on behalf of the Authors (16 Jan 2017) Author's response Manuscript

ED: Reconsider after major revisions (28 Jan 2017) by Ryan Sullivan

AR by Takuma Miyakawa on behalf of the Authors (30 Jan 2017) Author's response Manuscript

ED: Referee Nomination & Report Request started (03 Feb 2017) by Ryan Sullivan

RR by Anonymous Referee #1 (11 Feb 2017)

Suggestions for revision or reasons for rejection

Review of acp-2016-570, Alteration of the size distributions and mixing states of black carbon through transport in the boundary layer in East Asia, by T. Miyakawa et al.

The revised manuscript takes into account most of the reviewers' comments on the first version and I recommend that it be published when the items below (most of which are minor) are addressed. There are several instances where the wording is awkward; for these I have made recommendations on alternative wording.

Comments.
Line 86: The word "control" seems a bit strong, as it could easily be argued that global- and regional-scale distributions are controlled by sources; perhaps "strongly affect" or "have a large influence upon"

Line 113: define quantitatively what diameter range "fine mode" refers to

Line 140: how is Dcore different from MED? If they are the same, then this should be explicitly stated, or better yet, only use one term for this quantity.

Line 146: The statement that the particles were not so thickly coated seems at odds with the statement that the ratio was as high as 4 (line 145) or even 2.5 (line 146) – these seem like rather large coatings. Figure 8 indeed shows that Ds/Dcore is typically ~1.4 or so, but the statement as given on line 146 is unconvincing.

Lines 163-164: It is not the uncertainty that is minor, but rather the contribution to the mass that was outside the measured range – a very different quantity.

Line 178: This sentence is redundant to one on line 167 that stated that the average discrepancy was "comparable to the uncertainty of the COSMOS", which is not the same as "within the uncertainty." Perhaps remove one of the statements.

Line 370: It is not clear what is meant by "lower envelopes of correlations", especially as something that can be compared to a slope.

Line 377: It appears the authors meant to state ~10 mm rather than ~1 mm.

Linees 379-380: last sentence can be removed with no loss of information

Line 398: The fraction of BC seems to be the same with or without rain (2.4 vs 2.5%); this seems to require some discussion.

Line 402: The statement that cloud processes affected the relative abundance of ammonium sulfate is true, but misleading, as it seemed that the only effect was a reduction in the ammonium nitrate, why would result in an increase in the relative abundance of ammonium sulfate. To focus on clouds affecting ammonium sulfate seems to misrepresent what actually occurred. Thus this statement requires a bit more discussion.

Line 403: Rather than state that the concentrations of OM increased from average in case 2, it would be better to state that OM seemed to be removed during precipitation, which attributes a physical explanation to the observation. That is, unless the authors are arguing that OM is formed during transport under dry conditions (which seems to be the statement made on lines 403-404 without supporting evidence).

Line 421: I don't see where the APT values for the "outflow without BC loss" and "outflow with BC loss" are given. These criteria were selected based on delta_BC/delta-CO ratios rather than APT values.

Line 427: The size distributions of BC in Figure 7 differed among all three graphs; what the authors mean is the shape of the size distributions different primarily at BC diameters less than 0.1 micrometer.

Lines 428-430: This statement is presented without evidence; it may be true, but merely stating it as true because it is one explanation is not sufficient.

Line 479: A simple calculation would give a good estimate for the amount of coagulation experienced over 1 day, which I would think would be quite low.

line 711: It should be stated that the +/- 20% is from the 1-1 line.

There were a few places where the meaning was not clear, or where sentences were awkward to read, probably because of language difficulties. Suggestions are presented for how these could be reworded.

Line 49: "exhibits on hygroscopicity" – perhaps "exhibits increased hygroscopicity"

Lines 77: "… of BC during the cloud droplets formation, in air masses…: - perhaps "… of BC in air masses …"

Lines 84: "the cloud processes" – perhaps "through cloud processing"

Line 92: "synthetically" – meaning not clear; perhaps omit this word

Lines 93-94: sentence reads awkwardly; perhaps "This study determined that the transport efficiency of BC aerosol particles through the PBL was substantially reduced by wet removal."

Line 162: "distributions, to the outsides of the measurable…" – perhaps "distributions outside the measurable"

Line 272: "migrating anticyclone and cyclone" – not clear what is meant; do the authors mean that both occur together, or that one of each was observed, or that either can be typically observed?

Line 274: sentence reads awkwardly; perhaps omit.

Line 320-321: perhaps "Possible uncertainties in this estimate result from inaccuracies in the parameterization of the washout rate."

Lines 311-329: entire paragraph seemed repetitive and could have been stated in 3-4 sentences

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RR by Gavin McMeeking (27 Feb 2017)

Suggestions for revision or reasons for rejection

Rather than review the revised manuscript in full, I have focused on an evaluation of the strength of the responses to the comments raised by myself and the other reviewer, and as to whether they adequately address the comments. While many of the changes have improved the manuscript, there still remains areas where the reviewer comments have not been addressed, as detailed below.

Responses to Reviewer #1

Response to Line 56 comment: The changes/additions to Section 3.2 are good, but I am confused by the second-to-last statement in the response: “The rainout process is a major process to reduce the loss of aerosols in wet removal”. Is this just a typo, since the calculations show only a minor estimated contribution? I think the terms washout and rain out should be avoided, and instead use “in-cloud” and “below-cloud” scavenging to describe the different physical processes.

Response to LIne 152-154: Also a useful addition, however change “the discrepancy can be partly attributed to …” to “the discrepancy may be partly attributed to”, since it has not been established whether there is a difference in the SP2 response to BC in remote air and FS.

Response to reviewer comment on line 317-319:

The final line of text in Section 3.4 states “the changes in SO4/CO correlation were largely controlled by the rainout process and weakly influenced by aqueous-phase formation during transport.” The argument in the response to the reviewer is that the aim is to determine the impact of the cloud process on aqueous-phase formation of SO4. The difference in slopes in this case is also small, and neither the response nor the revised manuscript addresses the main point of the reviewer comment that questions the significance of the different relationships in the data. A stronger response, and argument in the revised text, would provide uncertainties in the regression coefficients and discussion of the significance of the differences in the relationships. The underlying reasons given by the authors (wet removal and in-cloud formation) are certainly plausible, but not proven based on the data shown here.

Additional minor point, but the range shown in the figure 6a is different from that stated in the revised text. The range shown in the plot includes the upper/lower limits associated with each of the Kanaya ranges...it may be better to give the same range in both (mean values?), whichever is most appropriate for the comparison.

Response to reviewer comment on line 343:

The inclusion of “absolute” size distributions does not directly address the main point of the reviewer comment, that there is little evidence of preferential loss of larger BC particles relative to the loss of smaller particles. The new Figure 7c is more helpful, showing a trend, though quite noisy, in the mode BC core diameter. A stronger response would also note that the more important parameter to examine here would be total particle diameter, not just that of the BC core. Just because the BC core is small does not mean that the total particle diameter, including a coating, is also small, and therefore may be as easily scavenged as a bare or weakly coated larger BC core.

Response to reviewer comment on line 345:
The response to the reviewer is weak. It does not address the main point of the comment, that concentrations are too low for coagulation to be an important process in removal of small BC particles. Given the manuscript focuses on changes in BC size distributions it seems such a fundamental topic should be discussed, even briefly, in the manuscript.

Response to reviewer comment to line 372:

I’m not clear which uncertainty in section 2.1 is being referred to in the response to this comment, but while I would agree that the SP2 can resolve quite small differences in rBC mass (assuming constant material properties), I think the uncertainty the reviewer is talking about here is the statistical uncertainty associated with the spread in the data, and whether there is a significant difference in fg/particle for the two conditions. Note that the comparisons of log-normal fit MMDs in Table 2 is less reliable because it includes an assumed density, which might not be constant for the two cases.

Response to reviewer comment to line 373:

The response to this comment somewhat undercuts the response to previous comments and the usefulness of Figure 7c. If size distributions change again during subsequent aging following the wet removal process, then is the apparent decrease in BC core size shown in Figure 7c meaningful or simply a random example where post-wet removal aging processes happen to give a somewhat smaller average BC core size? Could a slightly different aging process following wet removal lead to a larger average size? On this basis I think any conclusions drawn regarding size dependent loss of BC should be removed or at minimum highly qualified noting the confounding factors the authors have pointed out in several of their responses.

Responses to my comments:

First general comment (BC removal processes):

The additional discussion of BC removal processes is good, but suggest changing “Their” to “previous” in line 56 of the revised manuscript, and giving a very brief summary of the Kanaya et al. (2016) dry deposition results in section 3.2. For example, “The dry deposition in this region has already been evaluated by Kanaya et al. (2016), who found minimal decrease in BC/CO ratios for air masses unaffected by wet removal but with different transport times.” The addition of a quantitative examination of below cloud scavenging is good.

Second general comment (BC core versus shell; SP2 operating parameters):

The inclusion of SP2 operating conditions during the study is a good addition, however I do not think the response really addresses my point about the physical meaning and impacts of the BC core size versus the diameter of the mixed particle (core + shell). The BC core diameter is not the relevant diameter for CCN activation or other in-cloud scavenging processes, unless all particles are uncoated. I feel the manuscript should more clearly address this point, as well as the implications for some of the observations. For example, if most of the particles detectable by the SP2 are coated to the point where they roughly interact and/or activate in/as cloud droplets in a similar fashion then we would not expect a strong size dependence of removal. A more thorough and quantitative treatment of the interactions of BC particles mixed to varying degrees with other material with clouds would greatly strengthen the manuscript. While a full-blown microphysical modeling study would probably be beyond the scope of the investigation, some theoretical work treating particles as a simple core-shell morphology mixed with sulfate and organic aerosol and applying this to Kohler theory could be a great addition and strengthen the science presented.

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ED: Reconsider after minor revisions (Editor review) (27 Feb 2017) by Ryan Sullivan

AR by Takuma Miyakawa on behalf of the Authors (29 Mar 2017) Author's response Manuscript

ED: Publish as is (14 Apr 2017) by Ryan Sullivan

AR by Takuma Miyakawa on behalf of the Authors (18 Apr 2017)

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Short summary

We have deployed a single particle soot photometer (SP2) to characterize black carbon (BC) aerosols near industrial sources in Japan in the early summer of 2014 and at a remote island in the spring of 2015. The observed changes in the SP2-derived size distributions and mixing state of BC-containing particles with air mass transport are connected to meteorological variability (transport pathways and air mass histories) in spring in east Asia.