High-resolution vertical distribution and sources of HONO and  NO<sub>2</sub> in the nocturnal boundary layer in urban Beijing, China

Meng, Fanhao; Qin, Min; Tang, Ke; Duan, Jun; Fang, Wu; Liang, Shuaixi; Ye, Kaidi; Xie, Pinhua; Sun, Yele; Xie, Conghui; Ye, Chunxiang; Fu, Pingqing; Liu, Jianguo; Liu, Wenqing

doi:https://doi.org/10.5194/acp-20-5071-2020

Articles | Volume 20, issue 8

https://doi.org/10.5194/acp-20-5071-2020

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

Special issue:

In-depth study of air pollution sources and processes within...

https://doi.org/10.5194/acp-20-5071-2020

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

Articles | Volume 20, issue 8

Research article

|

29 Apr 2020

Research article |

| 29 Apr 2020

High-resolution vertical distribution and sources of HONO and NO₂ in the nocturnal boundary layer in urban Beijing, China

Fanhao Meng, Min Qin, Ke Tang, Jun Duan, Wu Fang, Shuaixi Liang, Kaidi Ye, Pinhua Xie, Yele Sun, Conghui Xie, Chunxiang Ye, Pingqing Fu, Jianguo Liu, and Wenqing Liu

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Final revised paper (published on 29 Apr 2020)
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Preprint (discussion started on 28 Aug 2019)
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Status: closed

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

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SC1: 'Comments to the manuscript by Meng et al.:', Jörg Kleffmann, 11 Sep 2019
- AC1: 'Response to interactive on the manuscript by Jörg Kleffmann', Fanhao Meng, 29 Jan 2020
RC1: 'Reviewer Comments', Anonymous Referee #1, 29 Oct 2019
- AC2: 'Response to interactive on the manuscript by Anonymous Referee #1', Fanhao Meng, 29 Jan 2020
RC2: 'Review of ACP-2019-613', Anonymous Referee #3, 01 Nov 2019
- AC3: 'Response to interactive on the manuscript by Anonymous Referee #3', Fanhao Meng, 29 Jan 2020

Peer-review completion

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

AR by Fanhao Meng on behalf of the Authors (29 Jan 2020) Author's response Manuscript

ED: Referee Nomination & Report Request started (30 Jan 2020) by Jennifer G. Murphy

RR by Anonymous Referee #3 (17 Feb 2020)

RR by Anonymous Referee #1 (23 Feb 2020)

Suggestions for revision or reasons for rejection

The Authors have done an extremely commendable revision to this manuscript. Despite the highly limited nature of their observational dataset, they have derived insight into some of the competing HONO mechanisms in the Beijing atmosphere under haze and clear pollution conditions. Pending some minor revisions and clarifications, the paper is acceptable for publication in Atmospheric Chemistry and Physics.

Minor Comments:
1) The Authors state in a number of places throughout the manuscript that aerosol production of HONO under haze conditions is dominant. This is incorrect. It is significant, but in the comparison against the ground source throughout the nocturnal boundary layer, aerosol production still only accounts for one third of the total HONO produced. This estimate is made using the upper limit for NO2 reactive uptake from the literature, so it is likely less significant that reported and more in line with a wealth of prior studies. The Authors need to do a better job of performing their calculations using upper and lower limits instead of just an upper limit estimate. A conservative calculation or one which includes the variability in the observations is more reliable. Specific comments below provide some areas where this improvement is required to produce a more balanced interpretation of the dataset. Given the very limited nature of the observations, such analysis is likely to provide more robust insight for comparison when more targeted measurements are made in the future, raising the impact of this work.

2) In Section 3.2 the Authors discuss the decreasing slopes determined using orthogonal least squares analysis. First, why the orthogonal approach was used is not clear, but presumably this was used as an extension from the revised intercomparison of the HONO measurements. The error in the measurement height must be quite a lot smaller than in the HONO measurement, which means that a least-squares regression is more likely appropriate. In either case, no examples of the regression line through the data are provided, nor are the parameters used to constrain the regression line. This limits the ability of bias in these trends to be identified. Were regressions performed through HONO data only above the surface layer? There is an exponential decrease in HONO with altitude within the surface layer that would be incorrect to apply a linear trend to, where the lowest HONO observation having the highest mixing ratio would significantly affect the slope of the line. The Authors need to clarify this approach in the manuscript so it can be compared to in future studies.

3) The Authors report 1-simga limit of detection (LOD). This is a gross error and misrepresentation of instrumental capability. Detection limits are standardly reported at 3-sigma which results in measurements with approximately 50 % error, decreasing quickly to 10 % error (or less) at the 10-sigma threshold (limit of quantitation). Report the 3-sigma LOD and indicate where this threshold lies for each instrument on the Figures associated with the intercomparison and also on any plots of HONO mixing ratios where measurements are below the 3-sigma LOD. The Authors need to revise their error assigned to data between the 3-sigma and 10-sigma levels to be at least +/- 20 % of the measured value, while data below the 3-sigma LOD should be reported with +/- 100 % uncertainty. Finally, while the errors of the HONO measurements from the IBBCEAS are quantified nicely, the accuracy from the intercomparison is not actually reported. Once the LOD error re-analysis has been completed, then the slopes from the resulting intercomparisons should give a good estimate of between-instrument accuracy.

Detailed Comments:

Lines 34-37: The results of this analysis need to be updated to reflect the relative importance under haze and clean conditions according to comments below.

Lines 49-51: The references used in this sentence appear to be placed backwards. Swap them.

Line 87: Should be ‘Americas’

Line 118: Should be ‘…aerosol surfaces play a…’

Lines 161-162: Please provide an estimate of the total path length.

Lines 164-174: Revise according to Minor Comment 3. Be very clear in how the 3-sigma LOD was calculated so it can be used for comparison by others who also measure HONO by IBBCEAS. It is too bad that a standard amount of gas phase HONO was not delivered to these systems to ensure that inlet or cavity-sorption losses of HONO were not changing over time and impacting the accuracy of the measurements.

Lines 178-183: This section needs clarification. Were these measurements made at all heights? Only on the ground? Or were these instruments located in the moving basket?

Line 184: In comparison to what? Clarify.

Line 202: Please add why use of these a and b terms are reasonable to use. The paper cited is for measurements made much further south, in the Pearl River Delta. A sound justification for the use of aerosol parameters from a location so far away, with far more agricultural impact on particulate composition (also different typical T and RH).

Lines 213-219: Use all of these intercomparisons to determine some measure of relative accuracy between these four instruments (i.e. the relative standard deviation of the slopes).

Line 235: 0.05 ppb is below the 1-sigma LOD. These low mixing ratios cannot be reported with any reliability. The Authors need to reconsider their interpretation anywhere that measurements are below 3-sigma LOD.

Line 241: Delete ‘other’

Line 244: Which measurement or period these numbers correspond to is not clear. Please revise for clarity.

Line 264: +/- 0.4 ppb is very close to the 3-sigma detection limit, which suggests that these reported values may only be an evaluation of the difference in noise between the two instruments.

Lines 331-347: Apply corrections for Minor Comment 2 here and make changes throughout manuscript to match any alterations in the values of the slopes and their interpretation.

Lines 470-472: This should be calculated using the lower limit of the NO2 mixing ratio (~40 ppbv) to provide a conservative estimate of the production rate. This reads as if the upper limit was used because it conveniently matched the observations, yet all of the remaining NO2 measurements are below this value, which indicates that the aerosol surface conversion is a major contributor in isolated air parcels, but not the only contributor. This is more internally-consistent with the findings presented later in the manuscript where ground and aerosol surface contributions are compared throughout two nocturnal boundary layers after direct emissions are accounted for.

Lines 472-474: This is a comparison between the calculation and the observations, yet it is not clear which numbers belong to the calculation and the observation here. Also, the Authors should normalize to a constant time interval (e.g. pptv per hour) for both the calculation and the observation numbers, since one interval given here is 1.5 hours and the other is ‘between two vertical profile measurements’. There are other instances of comparisons between calculations and observations from here onward that make following the results difficult, if not impossible.

Lines 481-482: The end of this sentence should be modified to indicate that ground production of HONO or direct emission into the surface layer are minor contributors, according to the results of the addressing the prior comments in this section.

Line 487: The Authors should again emphasize the severe limitation of the number of transects in their dataset here. This haze event has not been characterized for how typical or atypical it may be in terms of chemical composition and so these results may not hold under a more thorough investigation of HONO formation in Beijing during other haze episodes, yet provides motivation to find out!

Lines 501-507: Upper limit used again here, should use lower limit. Calculated formation rates are in ppbv/hr while HONO increases are pptv between transects. Please use the same units for both values to make the comparison simple for your readers. Also clearly state what fraction of the total HONO production these calculated rates account for.

Lines 510-516: The clarity of writing here makes this challenging to follow. Given the limitations given in the discussion here, it would seem that this vertical transect was not a very good case study for analysis. It may be better to remove this from the discussion.

Lines 521-522: The Authors state ‘presumably dominated’, yet they performed a quantitative assessment. Give the calculated fraction of the observed total HONO production. Clearly state that it only applies for a limited number of transects over a short period of a given night.

Lines 546-547: The Zhang et al (2018) observation in Beijing during haze has a value much higher than given here. Is this a typo? If not, then this much higher observation should be moved to the next sentence. A period should precede ‘However’ as well, instead of a comma.

Line 559: The Authors are creating confusion here. The aerosol surface conversion of HONO in the residual layer dominated its production in that layer, but this does not tell us anything about how important aerosol conversion is throughout the nighttime troposphere until it is compared in the following discussion of surface production. Revise this here to ‘is an active HONO production mechanism during haze episodes’ to improve accuracy and clarity.

Line 568: Revise to use the lower limits calculated and/or give the mean with +/- corresponding to reach the upper and lower limits. This will give a much better picture of the chemistry in this very nice comparison section of the discussion.

Line 598: Again, only an upper limit is used here, yet a reactive uptake coefficient of 10^-6 is common to find in the literature. The lower limit or the entire range should be explored. The upper limit use here, again, suggests the Authors are more interested in the upper limit of aerosol conversion importance rather than providing a balanced perspective. Given their extremely limited dataset, caution in the interpretation of this data will make the results of this work more valuable for future comparisons. Please revise here and for the calculations moving forward through the remaining discussion.

Lines 609-610: And when the reactive uptake of NO2 is 10^-6, then how does it compare? The Authors should provide the fraction of aerosol HONO production to the total calculated here to indicate its importance. It is only one third of the total, at the upper limit, which means it is important, but not dominant.

Line 619: Revise this section according to manuscript changes throughout.

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ED: Publish subject to minor revisions (review by editor) (24 Feb 2020) by Jennifer G. Murphy

AR by Fanhao Meng on behalf of the Authors (03 Mar 2020) Author's response Manuscript

ED: Publish subject to technical corrections (25 Mar 2020) by Jennifer G. Murphy

I commend the authors on their substantial improvements to the manuscript. I have some minor suggestions for technical corrections (below) but I do not need to review the paper again before publication in ACP.

Comments:

The period on line 114 should be a comma because the second sentence is actually just the last part of the previous sentence.

Lines 166 – 170 – Why are two different ranges being used to describe the detection limits? Is it because the first set are for 30 sec averages and the second set are for 15 sec averages? I suggest that the authors move the information about the 3-sigma detection limit for 30 sec averages (line 166-167) to after the sentence ending on line 172 about the ground-based system to avoid confusion.

Line 193 Aerodyne should be capitalized

Figure 3 – please clarify what height the NO, NO2 and HONO measurements are from in this figure

Figure 7 – I find a pie chart a very unusual choice to display this data. The authors can keep it if they prefer, but I think the data would make a lot more sense displayed as a histogram with bars indicating the frequency of the ratio of HONO_emit/HONO in increments of 0.1 (i.e. 10%).

Equation 5 – The authors don’t mention it, but this version of the equation relies on the assumption that the uptake of NO2 to form HONO doesn’t cause a significant change to the NO2 concentration over the time period of interest. This assumption appears very valid here, but I think it’s worth mentioning this explicitly so that if future researchers want to apply this method, they understand the limitation or caveat.

Author contributions – I find the last sentence in the author statement to be confusing. You have clearly outlined the separate contributions of FM and MQ, so why say that they are ‘the same’?

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AR by Fanhao Meng on behalf of the Authors (01 Apr 2020) Author's response Manuscript

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Short summary

Nitrous acid (HONO), a major precursor of the OH radical, plays a key role in atmospheric chemistry, but its sources are still debated. The first high-resolution vertical measurements of HONO and NO₂ were conducted in Beijing to investigate the nocturnal sources of HONO at different stages of pollution. The ground surface dominated HONO production by heterogeneous conversion of NO₂ during clean episodes, but the aerosol production was an important nighttime HONO source during haze episodes.

High-resolution vertical distribution and sources of HONO and NO2 in the nocturnal boundary layer in urban Beijing, China

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Interactive discussion

Peer-review completion

High-resolution vertical distribution and sources of HONO and NO₂ in the nocturnal boundary layer in urban Beijing, China