Influence of aerosol copper on HO<sub>2</sub> uptake: a novel parameterized equation

Song, Huan; Chen, Xiaorui; Lu, Keding; Zou, Qi; Tan, Zhaofeng; Fuchs, Hendrik; Wiedensohler, Alfred; Moon, Daniel R.; Heard, Dwayne E.; Baeza-Romero, María-Teresa; Zheng, Mei; Wahner, Andreas; Kiendler-Scharr, Astrid; Zhang, Yuanhang

doi:https://doi.org/10.5194/acp-20-15835-2020

Articles | Volume 20, issue 24

https://doi.org/10.5194/acp-20-15835-2020

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

https://doi.org/10.5194/acp-20-15835-2020

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

Articles | Volume 20, issue 24

Research article

|

19 Dec 2020

Research article |

| 19 Dec 2020

Influence of aerosol copper on HO₂ uptake: a novel parameterized equation

Huan Song, Xiaorui Chen, Keding Lu, Qi Zou, Zhaofeng Tan, Hendrik Fuchs, Alfred Wiedensohler, Daniel R. Moon, Dwayne E. Heard, María-Teresa Baeza-Romero, Mei Zheng, Andreas Wahner, Astrid Kiendler-Scharr, and Yuanhang Zhang

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Final revised paper (published on 19 Dec 2020)
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Preprint (discussion started on 24 Mar 2020)

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

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SC1: 'Comment on Song et al. from D Heard', Dwayne Heard, 27 Mar 2020
- AC1: 'Response to D Heard', Keding Lu, 09 Apr 2020
  - AC2: 'Response to Comment of Theodore S. Dibble', Keding Lu, 17 Apr 2020
SC2: 'Comment on mechanism', Theodore S. Dibble, 28 Mar 2020
- AC3: 'Response to Comment of Theodore S. Dibble', Keding Lu, 17 Apr 2020
RC1: 'Review', Anonymous Referee #1, 04 Apr 2020
- AC4: 'Response to Referee #1', Keding Lu, 21 Jul 2020
RC2: 'Review', Anonymous Referee #2, 14 Apr 2020
- AC5: 'Response to Referee #2', Keding Lu, 21 Jul 2020

Peer-review completion

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

AR by Keding Lu on behalf of the Authors (15 Jul 2020) Author's response Manuscript

ED: Referee Nomination & Report Request started (24 Jul 2020) by Markus Ammann

RR by Anonymous Referee #1 (30 Jul 2020)

RR by Anonymous Referee #3 (20 Aug 2020)

Suggestions for revision or reasons for rejection

This paper describes a new parameterization for the reaction probability of HO2 on Cu-containing aerosol particles. The reactive uptake of HO2 to aerosol remains an uncertain but potentially important component of atmospheric HOx fate, and has gained renewed attention of late. There is thus a reasonable need for more evaluation of how HO2 reactive uptake is described in models and this paper therefore has scientific merit and is appropriate in scope for ACP.

However, I have several concerns about the scientific quality and presentation in the manuscript that I think should be addressed before the paper is published. I describe these concerns below.

1) Uncertainty - overview. There is little objective discussions of measurement uncertainty and about uncertainties regarding application of the parameterization.

1.1 There is apparently a new data set on measured gamma_HO2, but there is *very little* discussion of those measurements, how they were made, how the uncertainty was determined etc. The relative uncertainty for the new data at high Cu is nearly an order of magnitude lower than that reported for other measurements in the literature. Given that the parameterization is developed by comparing a mechanistic model to multiple data sets from different experiments - how each data point is weighted and the role of the relative uncertainty needs to be discussed. Best would be to show some portion of the raw data from the new measurements and step through how the uncertainty propagates to the reported gamma_HO2.

1.2 It seems to me that little can be concluded about the effects of RH given the spread of measurement values at the same RH. While the model has a RH dependence built in through activity coefficients and Cu concentrations, etc, there is no real comparison of the modeled predicted RH dependence with the measurements where a plot of gamma_HO2 for a given Cu mass fraction would be shown versus RH.

1.3 Application of the parameterization (more about the parameterization below): There is a brief discussion of "soluble Cu" in ambient aerosol - but clearly this is the biggest source of uncertainty in using the parameterization. The author's choice of 20% of total Cu being soluble seems rather arbitrary. Really, this issue has been discussed already many years ago - there may well be enough Cu measured in ambient aerosol but whether it is in a soluble form (and also in a "free ion") form remains poorly understood. This uncertainty is compounded by the affect of organic aerosol and its morphology relative to an aqueous phase, the potential for externally mixed aerosol in an urban atmosphere (i.e. the Cu is contained in only a fraction of the total surface area), etc. The authors could show the impact of the various assumptions on the predicted gamma more clearly. Were the Cu measurements size resolved? If so, how does the Cu mass distribution compare to the total aerosol surface area distribution? What is the organic aerosol mass to inorganic mass ratio? If there was a core-shell morphology and the maximum gamma was similar to the impact of organics on HO2 uptake reported by Lakey et al, what would the current parameterization predict? Aerosol pH is likely rather uncertain, the authors should discuss a reasonable estimate of uncertainty in the ambient aerosol pH and its size dependence and how this uncertainty would impact the predicted HO2 gamma.

2) Parameterization development. The discussion of how the parameterization was developed is awkward and could at least use a different organization and in some cases more precise language. The authors should focus on the conditions and parameters which have the biggest effect first. For example, the authors do not mention the rate coefficients used to determine "keff" until the results section! In fact, the entire paragraph on the rate constants needs to be rewritten - I couldn't understand it. The authors open the paragraph saying: "The deviation of 𝛾𝐻𝑂2 between the MARK model and laboratory studies is smaller than the predicted results from the existing parameterized equation (Thornton et al., 2008;Hanson et al., 1992;Hanson et al., 1994;Jacob, 2000;Kolb et al., 1995;Ammann et al., 2013;IUPAC Task Group on Atmospheric Chemical Kinetic Data Evaluation, http://iupac.pole-ether.fr.) as shown in Figure 2. " But, it turns out to be closer to the measurements because the authors appear to have chosen a much smaller reaction rate coefficient? Please make that clear - what is the default prediction of the MARK model without any changes to achieve better agreement?? That prediction should be shown on the figure somehow. Then the discussion of what the rate constants are in the literature and what the recommended values are should be discussed clearly - please distinguish HO2(total) from HO2(aq) and O2-(aq). I assume the dissolved forms are treated separately in the model. Basically - it seems the authors are arguing the rate coefficient for various forms of HO2 in a concentrated aqueous solution are different from previous values, and they should present that clearly and why they think those rate constants are actually two orders of magnitude slower and not that the measurements of gamma-HO2 are biased low or low for some other reason (e.g solubility or diffusion limitation, etc).
The authors then state at the end: "The main reason for the differences between the original parameterization and the MARK model is the effect of including the activity coefficients of Cu ions and HO2 and the effects of reactions of different valence states of copper ions." This doesn't seem right if you changed the rate constant by two orders of magnitude - I would say that is the main difference between the original parameterization - please demonstrate that the change in this rate constant is not what affects the difference between the MARK and original parameterization (which I assume refers to the dashed line on figure 2).

The authors compare the model predictions of gamma HO2 to the data measured on ammonium sulfate aerosol doped with Cu. What was the assumed pH for the model predictions of the laboratory data? What is the basis of that prediction and could the pH vary between the different laboratory experiments if it wasn't explicitly measured? A flow tube that isn't regularly cleaned could develop and NH3 background which makes the pH possibly higher than estimated for ammonium sulfate in the absence of excess ammonia. The authors discuss that they assumed only HO2 was reacting with Cu in these experiments (at least that is what I discerned - but the language in this section is very unclear as it mentions pH of ambient aerosol being typically 3-6 and so they used the HO2 + Cu rate constant which is two orders of magnitude smaller than O2- + Cu). The authors mention that the "model selects a mass accommodation coefficient of 0.5" - but this is an input to the model, correct? Is the model prediction iterated for each measurement or how is it that the model selects? The mass accommodation coefficient alone is another source of significant uncertainty - the authors could better illustrate the true uncertainty of the model predictions based on mass accommodation and pH assumptions.

3) Presentation - as noted in the above comments, more clarity is needed in what assumptions are made, under what conditions, and what the impact of those assumptions is on the main conclusions. I find little need to show the distribution of gamma values for day and night - the two distributions look essentially the same. The only different is that HO2 reactive uptake becomes a larger fraction of the total HOx loss (because RO2 + NO goes towards zero). This seems a minor distinction to make given the bigger uncertainties in the applicaiton of the parameterization as discussed above that would be better to communicate to the broader community that might want to employ the parameterization.

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ED: Reconsider after major revisions (24 Aug 2020) by Markus Ammann

AR by Keding Lu on behalf of the Authors (17 Sep 2020) Author's response Manuscript

ED: Referee Nomination & Report Request started (28 Sep 2020) by Markus Ammann

RR by Anonymous Referee #4 (16 Oct 2020)

Suggestions for revision or reasons for rejection

This review covers the 2nd revised version of the manuscript ACP-0218
“Influence of aerosol copper on HO2 uptake: A novel parameterized equation” by Huang et al

This manuscript reports an explicit model of uptake of HO2 radicals to deliquesced inorganic aerosol particles to partially reconcile previous inconsistencies among experimental measurements and parameterizations. This includes a detailed treatment of the aqueous phase chemistry of HO2 and superoxide with Cu ions, as well as considering effects of Setchenov salting and ionic strength. The model is also used to interpret data from a field campaign. The previous review rounds already covered the general aspects regarding scientific relevance and significance the topic, which are undoubted. In response to previous comments related to a dataset also included to fit a parameterization, the authors of that dataset have joined the revised version of the paper and this version now includes an updated description of experimental details and revised data analysis related to that dataset. In response to another review, the authors have expanded the model description and the discussion related to sensitivity and uncertainty. Overall, this work provides valuable new information, especially the fact that taking into account the properties of the concentrated solutions of deliquesced aerosol particles allows to calculate HO2 uptake coefficients using known and well documented aqueous peroxy radical chemistry involving Cu ions. While the model includes some complexity by involving links to nitrogen oxides and and sulfur, it lacks inclusion of the interaction with the Fe(II)/Fe(III) redox couple, which usually is associated with the presence of Cu in atmospheric particles and may have important impacts. Nevertheless, the manuscript provides progress in understanding uptake of HO2 to aerosol particles.

In spite of this being the 2nd revised version of this manuscript, still a number of deficiencies exist that should be addressed. In the comment below, I list the line numbers of the pdf file of the revised manuscript version. In principle, these concerns are rather minor in character, but still numerous. They should be addressed before the manuscript may be accepted for ACP.

1) Language: the new text additions are sometimes misleading, mostly due to deficiencies in the English language. This should be fixed by a thorough work-through by the authors.
2) Abstract line 24: the IUPAC website provides a recommendation for a number of different deliquesced aerosol systems, not only cloud droplets. See also comment further below on the same aspect in the manuscript.
3) Line 26: not sure whether it is useful to have the parameterization in the abstract without explanation of symbols.
4) Line 27: The Wangdu campaign is not something the reader understands without introduction. Either explain in more detail, ‘data from a campaign in the Wangdu region’, or just ‘data from a field campaign’.
5) Lines 42-45: these sentences should be split up, and the reason for the lower reactivity in absence of transition metals should be explained, including the self reaction of HO2 that has been parameterized by Thornton et al. In addition, a language issue here: The impact of HO2 uptake is not depending on a parameterization. It is the model output, or the calculated response of some parameters to HO2 uptake that changes. This is different.
6) Line 73: symbols used in eq. (1) and (2) need to be explained
7) Same paragraph: it does not become clear enough how the uptake coefficient was retrieved from the model output. This should be briefly described here.
8) Line 106: some numbers should be given here. What is the ratio between H^cc and H_0 over the RH range considered in this study? Same sentence: why does H^cc depend strongly on the Cu concentration? The dominant solute is ammonium sulfate, which should be the main driver of salting and ionic strength, isn’t it.
9) Line 115: Two things here: the solubility of Fe is not a defined quantity, the authors may refer to the solubility of Fe-containing minerals. There are literature reports about what fraction of Fe is typically in dissolved form. In addition, there is a language issue here (many similar cases throughout the manuscript), the sentence reads like the solubility of Fe is related to its ratio to Cu, which is certainly not true.
10) Line 118: Neglecting the presence of Fe should lead to a stronger caveat for this work. The authors cite the Mao et al. (2013) work a few times, which clearly indicates a strong impact of the Cu/Fe ratio on the fate of HO2 products in the aqueous phase. Fe may reduce the contribution of recycling of peroxy radicals to lower the effective HO2 loss rate, and Fe might be relevant for the interpretation of the effect of HO2 uptake on the HOx budget in conjunction with the field data.
11) Line 135: in eq. (10) and (11), the subscript ‘equ’ is misleading, since it should refer to ‘effective’ and not ‘equilibrium’ or ‘equation’. So ‘eff’ would be better.
12) Line 148: this paragraph is not sufficiently clear. k_eff seems to be the apparent first order loss rate coefficient of HO2 in the aqueous phase (not involving solubility). Typical numbers should be provided; otherwise it would not be understandable, why a 1 M Cu(II) solution would not lead to a very short reacto-diffusive length and thus strong concentration gradients in HO2. Also the reasons for the apparently low values should be explained, as this must result from complex recycling occurring, since the first reaction of Cu(II) with HO2 is very fast.
13) Line 158: the value of the accommodation coefficient is not related to the amount of Cu. The amount of Cu may control the uptake regime, with large amounts leading to uptake becoming accommodation limited. But the value of alpha is independent of Cu, unless it is involved in the process of surface to bulk transfer of HO2. Are the authors confusing accommodation coefficient with uptake coefficient? Also Table 1 is misleading, as the data in column seem to be uptake coefficient, as indicated in the Table caption, but inconsistent with the column header.
14) Line 162: probably related to the previous, the high accommodation coefficient for HO2 does not automatically mean it has a high loss rate. It only means that gamma may get large, if a strong sink is available in the condensed phase.
15) Line 164: language: The MARK model probably does not make the selection of alpha, but the authors selected it.
16) Line 167: as mentioned before, please clarify the column header of the table and the caption (alpha or gamma)
17) Line 172: first sentence: language!
18) Line 178: SMPS = Scanning Mobility Particle Sizer or Scanning Mobility Particle Spectrometer
19) Line 179: aerosol particles were produced using a …
20) Line 198 and following: while the model is indeed used to explore the RH dependence of HO2 uptake and associated aqueous phase chemistry, the comparison to experimental data is not really covering a substantial RH range. So that is essentially limited to the effect of the Cu(II) concentration.
21) Line 230: HO2 uptake at low Cu content: the figure should be plotted in log y-scale to demonstrate that the remaining uptake at low Cu content is driven by self reaction of HO2 (should be second order in HO2).
22) Line 231: What does the sentence ‘The threshold is also consist in …’ mean? What are droplets?
23) Line 233: I understand that increasing Cu content drives uptake to the accommodation limit; but why should that be determined by the solubility?
24) Line 254: the Thornton et al. (2008) parameterization was developed for deliquesced aerosol particles, not cloud droplets. This repetitively comes up below again.
25) Line 262 and following: as mentioned above, the Thornton et al. and IUPAC recommendation has not been suggested for dilute aqueous droplets but actually for deliquesced aerosol particles. As discussed in Thornton et al. but also in the comments accompanying the IUPAC recommendations, the fact that k_TMI is lower than the actual known rate coefficient of HO2 or O2- with Cu(II), is assumed to likely result from the combined effects of solute strength effects. It is indeed the added value of this work to make this aspect more quantitative. The authors could emphasize this somewhat more to detail the individual contributions of Setchenov salting, of ionic strength and of the recycling efficiency among the cupper and peroxy species to the reduction of the effective rate coefficient. The advantage of eq 15 is that it correctly represents the transition between the reacto-diffusive regime (when k_eff is higher) to the homogeneous bulk reaction regime covered by the parameterization suggested in this work (eqs 18-21)
26) Line 310 and following: the authors should clearly state that this parameterization is only reasonable as long k_eff remains sufficiently small, such that no HO2 gradients within particles develop. While they seem to show that this is valid with the mechanism involving Cu only, it is not granted that this is still true when for instance including Fe ions in the mechanism which could leading to an increasing sink for HO2 if the recycling efficiency is shut off; similar effects may occur in presence of organics.

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RR by Anonymous Referee #3 (19 Oct 2020)

ED: Publish subject to minor revisions (review by editor) (19 Oct 2020) by Markus Ammann

AR by Keding Lu on behalf of the Authors (25 Oct 2020) Author's response Manuscript

ED: Publish as is (26 Oct 2020) by Markus Ammann

AR by Keding Lu on behalf of the Authors (26 Oct 2020) Author's response Manuscript

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Short summary

Accurate calculation of the HO₂ uptake coefficient is one of the key parameters to quantify the co-reduction of both aerosol and ozone pollution. We modelled various lab measurements of γHO₂ based on a gas-liquid phase kinetic model and developed a state-of-the-art parameterized equation. Based on a dataset from a comprehensive field campaign in the North China Plain, we proposed that the determination of the heterogeneous uptake process for HO₂ should be included in future field campaigns.

Influence of aerosol copper on HO2 uptake: a novel parameterized equation

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Influence of aerosol copper on HO₂ uptake: a novel parameterized equation