From the journal Environmental Science: Atmospheres Peer review history

19-Feb-2021

Dear Dr Meierdierks:

Manuscript ID: EA-ART-12-2020-000022
TITLE: Unique Calibration of passive air sampling of PAHs across seasons and locations

Thank you for your submission to Environmental Science: Atmospheres, published by the Royal Society of Chemistry. I sent your manuscript to reviewers and I have now received their reports which are copied below.

I have carefully evaluated your manuscript and the reviewers’ reports, and the reports indicate that major revisions are necessary.

Please submit a revised manuscript which addresses all of the reviewers’ comments. Further peer review of your revised manuscript may be needed. When you submit your revised manuscript please include a point by point response to the reviewers’ comments and highlight the changes you have made. Full details of the files you need to submit are listed at the end of this email.

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Environmental Science: Atmospheres strongly encourages authors of research articles to include an ‘Author contributions’ section in their manuscript, for publication in the final article. This should appear immediately above the ‘Conflict of interest’ and ‘Acknowledgement’ sections. I strongly recommend you use CRediT (the Contributor Roles Taxonomy from CASRAI, https://casrai.org/credit/) for standardised contribution descriptions. All authors should have agreed to their individual contributions ahead of submission and these should accurately reflect contributions to the work. Please refer to our general author guidelines http://www.rsc.org/journals-books-databases/journal-authors-reviewers/author-responsibilities/ for more information.

I look forward to receiving your revised manuscript.

Yours sincerely,
Dr Lin Wang
Associate Editor, Environmental Science: Atmospheres

Environmental Science: Atmospheres is accompanied by sister journals Environmental Science: Nano, Environmental Science: Processes and Impacts, and Environmental Science: Water Research; publishing high-impact work across all aspects of environmental science and engineering. Find out more at: http://rsc.li/envsci

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Reviewer 1

The manuscript presents experiments aimed at an improved understanding of the kinetics of uptake of PAHs in polyethylene sheet-based passive air samplers. It involves the following components:

- Eight 1-month-long uptake experiments at three field sites during different seasons with 8 retrieval dates each

- Derivation of the parameter controlling the exchange kinetics (i.e. the air boundary layer thickness surrounding the sampler sorbent) from the measured rate of loss of a labelled performance reference compound spiked onto the sorbent prior to deployment

- Development of a model describing the uptake of chemicals in the sampler sorbent as influenced by variable temperature.

While it is a sincere and solid effort, several major revisions would be required to make this paper acceptable for publication.

The description of the kinetics of uptake deviates from previous approaches more in terms of presentation/nomenclature than in terms of substance. Equation (1.5) is entirely equivalent to the equations used previously by others to calculate air concentrations from the amount quantified in a passive sampling sorbent, namely:

- The equations used by Lohmann et al. estimating the % equilibrium that a chemical has achieved when PE is deployed for a certain time period at a particular temperature.

- The equations used by Harner et al. estimating the effective sampling volume of the passive air sampler based on polyurethane foam.

The major difference is that others have aggregated the term A Dg / dg into a so-called inherent sampling rate RS, where here the authors aggregated the sorbent area/sorbent volume term A/V as 2/dp (line 196). Therefore, the exponent in equation (1.5) equals the exponent in those earlier equations (Note, I leave out rp as I do not know what it designates):

2 Dg t / (dp Kpg dg) = A Dg t / (V Kpg dg) = RS t /(V Kpg)

In other words, when the authors write in the abstract: “we determined uptake kinetics (or dg) in different seasons over two years at three locations. Surprisingly, air side boundary layers were almost equal in thickness at the different locations but varied seasonally by about a factor of 2” they could have just as well written: We determined inherent sampling rates RS and those sampling rates were almost equal at different locations and varied seasonally by about a factor of 2. Not writing it like this has two consequences:

1. The paper’s approach seems more innovative than it really is. On line 381, the authors have the temerity to state: “confirm the calibration of PE-passive samplers based on the air-side boundary layer as a convincing method to determine Cg, particularly in comparison to the commonly used sampling rate approach”. This is of course rubbish, as the two methods are equivalent (except for the tiny molecular size dependence of molecular diffusivity, which is ignored when applying a uniform RS for different compounds).

2. The paper may be less accessible to many in the community than it could be, which may diminish its impact.

There, I suggest it is necessary to highlight explicitly, (i) that the approach presented here is equivalent to earlier approaches and (ii) how the parameters introduced here relate to those that the community of PAS users commonly have employed.

Paragraph line 381-389 needs to be completely rewritten, as it is exceptionally misleading to the casual reader. In particular, a clear distinction has to be made between intrinsic sampling rate and empirically observed sampling rates. Also, while it is correct that “the determination of precise sampling rates is complex, and errors are easily made for calibrating the passive samplers”, the current study does nothing to ameliorate or avoid that complexity. Just as an inherent sampling rate is influenced by wind speed and wind angle, so is the dg. Just as an effective air sampling volume or the % equilibrium are influenced by temperature, so is the approach advocated by the authors.

The model approach as presented is not a novel as it is made out to be. In the cover letter the authors write: “For the data evaluation, we implemented a numerical model to predict uptake curves onto the sampler and to fit the atmospheric concentration. This model accounts for temperature fluctuation and gives precise insight into sampling kinetics and equilibration times, which the commonly used exponential equation cannot provide”. While such an approach may not have been applied previously to PE-based PAS, equivalent approaches have been presented for the XAD-PAS by Armitage et al. (Environ. Sci. Technol. 2013, 47, 13546-13554, Environ. Sci.: Processes Impacts 2015, 17, 1228-1237) and the PUF-PAS by Petrich et al./Herkert et al. (Environ. Sci. Technol. 2013, 47, 8591-8598, Environ. Sci.: Processes Impacts 2018, 20, 210-219, Environ. Sci. Technol. 2016, 50, 6690-6697)

In some regards those earlier approaches are superior to what is presented here. For example, Armitage et al. (i) do not have to assume that the uptake kinetics is controlled by the air side resistance only, (ii) have implemented an explicit wind speed dependence of the inherent sampling rate (or of the air boundary layer thickness dg, if you prefer) and (iii) allow for time-variant concentrations during sampling.
I note, that the latter two aspect are completely ignored here, even though the uptake curves in Figure 3 surely are strongly influenced by the temporal variability of the wind speed and of the air concentrations of the target compounds during the deployment. Obviously, Cg appears in equations (1.7) and (1.8) and could be adjusted for each time step, if it were known. Similarly, dg must clearly be a function of wind speed and appears in those equations. The reason that only Kpg and Dg are adjusted for temporally variable temperature (and not also dg for wind speed and Cg) is that temperature variability during deployment is easily measured, and not because it is necessarily more important than wind speed variability or Cg variability.

The paper is not sufficiently forthright in stating the assumptions underlying the presented approaches and models. See details below.

I would like to see a more honest accounting of the uncertainty propagating through the presented calculations. For example, the Kpg values easily have a standard error of half a log unit. How does this affect the results?


Detailed comments:

Line 93: I find the selection of anthracene as the performance reference compound very unfortunate on multiple counts. Anthracene is the most labile PAH and known to be readily susceptible to reaction with atmospheric photooxidants - it reacts more than six times faster than phenanthrene with the OH radical (Brubaker and Hites, J. Phys. Chem. A 1998, 102, 6, 915–921). Loss of PAHs from passive sampling sorbents as a result of reaction with photooxidants has previously been reported (Jariyasopit et al., Atmos. Environ. 2015, 120, 200-204, Melymuk et al., Atmos. Environ. 2017, 167, 553-565), though admittedly not for polyethylene-based samplers. Can the authors really be sure that degradation is not at least in part responsible for the observed disappearance of D10-anthracene from the polyethylene sheets?

Another shortcoming of anthracene is that it is so volatile to be lost very quickly (Figure A3 in section 4 in supplement). While it could be used here in experiments with very short initial deployment periods, the authors admit that only the first few days of the month-long experiment were suited for the derivation of the rate of loss of anthracene. Accordingly, anthracene would completely fail as PRC during “normal” use (i.e. involving deployments of a week and longer), as the loss after 4 days of deployment would already be too high to allow for the reliable derivation of a rate of loss.

Smaller comments:

Line 41: “distinctively” is not the appropriate term in this context. Better use something like “strongly”, “remarkably”, or “rapidly”. In general, while the English of the manuscript is reasonably OK, it could benefit from some serious proof-reading by a native speaker. Another example: “exemplary” in the context of contaminants of concern (line 69) does not make sense, as it means “representing the best of its kind”.

Line 43: replace (2020) with (17).

Line 54: While it is indeed widely purported that “the air-side boundary layer is controlling the uptake process of semi- and low volatile atmospheric compounds onto various polymer passive samplers”, it is not necessarily correct. There is considerable evidence to the contrary (for polyurethane, see e.g. Zhang et al. Environ. Sci. Technol. 2011, 45, 10509-10515 and Okeme et al. Chemosphere 2017, 168, 199-204). Similarly, on line 186, claiming this assumption to be “verified” doesn’t make it so. In particular, I note that diffusion in PE is not as fast as in other polymers (Rusina et al. Chemosphere, 2007, 68, 1344-1351, Narvaez Valderrama et al. Environ. Sci.: Processes Impacts 2016, 18, 87-94), making it more likely for diffusion into the polymer matrix to contribute to the uptake resistance.

Line 57: The statement “For the translation of measured concentrations on passive air samplers into reliable atmospheric concentrations, not only partitioning coefficients need to be known, but also the exchange kinetics between air and sampler under different temperature conditions and emission scenarios” is misleading as the partition coefficient of the target chemical between atmospheric gas phase and the passive sampling sorbent does NOT need to be known when using a true kinetic sampler. That is only true for what the authors call “non-infinite sink PAS” (line 211). Also, it is not readily apparent how the “emission scenario” of a compound should influence kinetics of air-sampler exchange.

Line 73: “highly variable” instead of “ranging”

Line 74: Here the authors refer to “specific PAH distribution patterns and fingerprints” that could be related to emission sources. Later in the same paragraph they suggest to use the remarkable constancy of atmospheric PAH compositions in their sampling and quantification strategy (“Characteristic patterns of PAHs in air may remain relatively constant over certain time periods and geographic areas”). These two statements directly contradict each other. Obviously, if you use a technique that relies on the assumption of constant compositional patterns, you cannot use that technique to record specific compositional patterns indicative of certain emission sources.

Line 77: “grass hopping” presupposes environmental persistence that is sufficiently long for a SVOC to undergo repeated cycles of settling and re-emission. PAHs generally are not sufficiently persistent in either atmosphere or surface media for this to be a viable fate process.

Line 82: It is not clear what is meant by “equilibrium concentration” here. Equilibrium of what type (thermodynamic, kinetic)? Equilibrium between what phases?

Line 97: The argument that the PE thin sheets were chosen as the sampling sorbent, because of “simplicity of function” is hardly convincing, when the presented study makes it abundantly obvious how complex the interpretation of data gained from “non-infinite sink PASs” really is. Simplicity of function in a PAS requires a high capacity sorbent that acts as close to an infinite sink to the target compounds as possible. It would be nice to see some honest acknowledgement of the user of a PE-based PAS that the complexity the study is trying to address is an inevitable outcome of choosing a low capacity sorbent! And more importantly, it is not without alternative, as PAS based on high capacity sorbents do exist.

Table 1: The molecular mass for phenanthrene is not 128.23 g/mol. Also, if molar volume and MW are the same (as for ANT and PHE), the diffusion coefficient should be numerically the same as well, no?

Table 1: The partition coefficients between PE and the gas phase reported by Lohmann are estimates with very considerable uncertainty. I suggest that Table 1 needs to report that uncertainty quantitatively (e.g. using a confidence interval or standard error).

Table 1: The table reports enthalpies of vaporization, presumably because the authors follow the example of Lohmann to use it to approximate the internal energy of polyethylene-gas phase transfer. The equality between DHvap and DUPE/G is an assumption of largely unknown validity and accuracy.

Line 138: Provide a rationale for the mixing with ultrapure water during the processing of the extracts.

Line 171: The meaning of the statement “we compared blank-corrected concentrations on the sampler versus eliminating the concentrations below this limit” is not clear to me.
Equation (1.2): The parameter rp in the denominator is not defined anywhere in the manuscript. It is also not possible to infer what it may mean, as the units in the equation are balanced without it (if it is assumed that Kpg is unitless).

Equation (1.2) contains variables labelled Dg and Kpg, but on line 194 and in equation (1.3) Dg-PRC and Kpg-PRC are used. Make sure to use consistent parameter naming.
Line 199 promises an equation for calculating individual uptake rate constants, but no such equation is presented.

The validity of equations (1.4) and (1.5) is predicated on a number of important assumptions, which are never mentioned. The most important is that the Cg is constant during the time period of passive sampler deployment. This assumption is rarely valid. On lines 401-402 it is revealed that the concentration of some PAH dropped by an order of magnitude during the deployment period!

Line 212: “partitioning coefficient … in the gas phase” makes no sense. A partition coefficient applies to two phases.

Line 263 and Table 2: There is something seriously off with the reported wind speeds, as they are implausibly high. They are about one order of magnitude higher than what could be reasonably expected for an inland region in central Europe. 31 m/s corresponds to 110 km/h!

Line 269/270: This is a very unfortunate formulation, as it confuses thermodynamic terms with kinetic ones. The Kpg has no impact on the kinetics of air-sorbent exchange (which is expressed as the inherent sampling rate Rs or the boundary layer thickness dg), unless the air side is NOT rate-limiting! The same is true for line 326, where “seasonal difference of uptake kinetics can be linked directly to the variation of the partition coefficient with temperature”. Same for line 339: “change of kinetics”. Please rephrase these formulations, as they are extremely confusing to a reader not intimately familiar with the mechanistic basis of passive sampling.

Line 273: the reported numerical values for dg lack units.

Line 276: A range from 33 % range in wind speed is not particularly broad.

Line 281: The authors write: “comparable exchange kinetics can be obtained for different locations”. The three sites in this study were very similar in character as well in close proximity. I would expect much larger differences in dg if more diverse study sites were selected (e.g. highly wind-exposed coastal sites, wind-sheltered forested sites).

Line 285: The statement “numerical model accounts for the hourly change of concentrations on PE during the sampling period” is misleading. This model only accounts for the hourly change in temperature. It ignores the hourly change in wind speed, which also influences the hourly change of concentrations on PE during the sampling period.

Line 286: Quantify that uncertainty! What would the loss rates l for D10-ANT and the dg be, if the average temperature during deployment were used instead.

Figure 2: I don’t think this figure is very effective. I presume it is meant to illustrate (i) the huge range in the equilibration time scale for different PAHs, (ii) the large variability in the equilibration time scale for one PAH caused by temperature changes, and (iii) the minor variability in the equilibration times scale caused by the small wind speed differences investigated in the current study. I think there should more effective means of getting these points across.

Line 341: Here it says “the numerical model provides reliable information on the main influences on uptake curves, exchange kinetics and atmospheric concentrations simultaneously.” This exaggerates what the model can do. Ultimately, the model depends on the availability of temporally variable parameters (Cg, windspeed, temperature) to make quantitative inferences as to the “main influences”. In the provided example, only one of these parameters is actually known as a function of time and therefore only its influence can be accounted for when calculating the uptake curve.

Line 352: “which was in close agreement”

Figure 4: I am not really clear what Figure 4 is meant to convey, other than the fact that the dg determined in this study varied little between the three sites and between the various sampling period. This was already shown in Table 2. Deviations from the 1:1 line are entirely explained by the dg values in Table 2. Also, it is not surprising at all, as the three sites are similar and in close proximity and wind speed does not have a large seasonal variability in central Germany. The agreement would look a lot less impressive, if the deployments had included locations and time periods with high or low average wind speeds.

Line 429: I think the authors here mean the extent of sorption to particles and not the strength of sorption. The phrase “more strongly bound” is therefore incorrect.

Line 580: Author names are incorrect

Line 726: What processes are captured by this half-life? What is meant by photodegradation? Reaction of the PAHs in the gas phase with the hydroxyl radical? Why would that be a reasonable estimate of the reaction rate constant for PAHs sorbed to PE? Why is anthracene not part of that estimation considering it has the highest reaction rate constants for atmospheric degradation processes?

Reviewer 2

The paper presents an interesting approach to calibration of partitioning passive samplers for monitoring semivolatile organic compounds in atmosphere. Although the approach itself is original and useful, I think that the applied compound uptake model suffers from some oversimplifications that are worth considering. I think major revisions are needed before the paper can be accepted for publication.
General comments:
1. It should be stressed that it is assumed that passive samplers only sample PAHs from the gaseous phase. However, this cannot be entirely guaranteed if dust particles deposit on the sampler surface during exposure. Partitioning between deposited dust and LDPE may influence the concentration calculated from passive sampling data, depending on phase ratio, initial concentration in both phases, PAH accessibility, and temperature dependent distribution coeffcient. Deposition of particles perhaps can be minimised by using suitable deployment device - something worth discussing.
2. Authors suggest D10-anthracene as performance reference compound. One must consider that this compound easily undergoes photodegradation. Again, in order to efficiently use it, one must take measures to prevent photodegradation. Please discuss.
3. Authors automatically assume air-side control of the mass transfer of PAHs to the sampler. This can be verified based on the comparison of the mass transfer coefficient in LDPE is compared to the mass transfer coefficient measured in the experiment. This is possible since diffusion coefficients of PAHs in LDPE are available in literature ( https://doi.org/10.1002/app.31704). Seeing a very limited effect of wind velocity on the calculated air boundary layer thickness δ_g brings some doubt about the validity of the assumption. Please provide a proof.
4.I think it is an oversimplification to automatically assume a substance-independent air-side boundary layer thickness. From the mass transfer theory, the mass transfer coefficient in air is proportional to the flow velocity and compound`s diffusion coefficient in air k_a∼D_a^2/3. This in turn indicates that the effective boundary layer thickness increases with increasing diffusion coefficient according to δ_g∼Da^1/3. When sampling compounds with different molar volume, this will become apparent. Moreover, diffusion coefficient is temperature-dependent, as authors actually partially implemented in the model. Thus, I think the effect of molecule size on the mass transfer coefficient should be considered in the model or it should be justified why it was neglected.
5. The calculation of gaseous concentrations of non-monitored substances based on concentration of a single compound and assuming a conservative compound pattern is highly uncertain. It is based on emission pattern constant in time and space, which may be valid in a certain region, but cannot be applied in general. I am very sceptic about using such approach.
Specific comments: In Line 214 it is stated that Kpg depends on wind speed. I think that is not correct since partition coefficients should not depend on flow velocity.

Dear Dr. Wang,

thanks for taking care of the reviewing process of our manuscript - and reminding us on the revision process.

We now happily submitted the revised manuscript and are looking forward for your feedback.

Sincerely,
Jana Meierdierks

04-May-2021

Dear Dr Meierdierks:

Manuscript ID: EA-ART-12-2020-000022.R1
TITLE: Unique calibration of passive air sampling for field monitoring of PAHs with polyethylene thin films across seasons and locations

Thank you for your submission to Environmental Science: Atmospheres, published by the Royal Society of Chemistry. I sent your manuscript to reviewers and I have now received their reports which are copied below.

After careful evaluation of your manuscript and the reviewers’ reports, I will be pleased to accept your manuscript for publication after revisions.

Please revise your manuscript to fully address the reviewers’ comments. When you submit your revised manuscript please include a point by point response to the reviewers’ comments and highlight the changes you have made. Full details of the files you need to submit are listed at the end of this email.

Please submit your revised manuscript as soon as possible using this link :

*** PLEASE NOTE: This is a two-step process. After clicking on the link, you will be directed to a webpage to confirm. ***

https://mc.manuscriptcentral.com/esatmos?link_removed

(This link goes straight to your account, without the need to log in to the system. For your account security you should not share this link with others.)

Alternatively, you can login to your account (https://mc.manuscriptcentral.com/esatmos) where you will need your case-sensitive USER ID and password.

You should submit your revised manuscript as soon as possible; please note you will receive a series of automatic reminders. If your revisions will take a significant length of time, please contact me. If I do not hear from you, I may withdraw your manuscript from consideration and you will have to resubmit. Any resubmission will receive a new submission date.

The Royal Society of Chemistry requires all submitting authors to provide their ORCID iD when they submit a revised manuscript. This is quick and easy to do as part of the revised manuscript submission process. We will publish this information with the article, and you may choose to have your ORCID record updated automatically with details of the publication.

Please also encourage your co-authors to sign up for their own ORCID account and associate it with their account on our manuscript submission system. For further information see: https://www.rsc.org/journals-books-databases/journal-authors-reviewers/processes-policies/#attribution-id

Environmental Science: Atmospheres strongly encourages authors of research articles to include an ‘Author contributions’ section in their manuscript, for publication in the final article. This should appear immediately above the ‘Conflict of interest’ and ‘Acknowledgement’ sections. I strongly recommend you use CRediT (the Contributor Roles Taxonomy from CASRAI, https://casrai.org/credit/) for standardised contribution descriptions. All authors should have agreed to their individual contributions ahead of submission and these should accurately reflect contributions to the work. Please refer to our general author guidelines http://www.rsc.org/journals-books-databases/journal-authors-reviewers/author-responsibilities/ for more information.

I look forward to receiving your revised manuscript.

Yours sincerely,
Dr Lin Wang
Associate Editor, Environmental Science: Atmospheres

Environmental Science: Atmospheres is accompanied by sister journals Environmental Science: Nano, Environmental Science: Processes and Impacts, and Environmental Science: Water Research; publishing high-impact work across all aspects of environmental science and engineering. Find out more at: http://rsc.li/envsci

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Reviewer 1

Line 42: Address is misspelled

Line 200: rotameter

Line 269: kg instead of Kg

Line 271: Rs instead of RS

Line 410: "in winter we would expect slower losses of the PRC and thus thicker air-side boundary layer" I agree that one would expect slower loss of PRCs in winter, because of a lower temperature. However, this is because the partitioning coefficient Kpg would be higher and NOT because of a different thickness of the air boundary layer.

Lie 455: “Thus, in this case the exchange between PE and air over seasonal time-scales is more influenced by the physical-chemical properties of the target compounds than by temporal variation of δg”. Careful, this is only the case, because the wind speed at the study sites showed very limited spatial and seasonal dependence. In a global study such as GAPS (line 431), you would encounter a much wider range of wind speeds and thus in δg.

Reference 7 and 65 are identical

Dear Dr. Wang,

Thank you for your careful evaluation of our manuscript!
We have now revised the manuscript based on the last review. Below you find our point by point answer to the remarks.

Line 42: Address is misspelled
> Corrected

Line 200: rotameter
> Corrected

Line 269: kg instead of Kg
> Corrected

Line 271: Rs instead of RS
> Corrected

Line 410: "in winter we would expect slower losses of the PRC and thus thicker air-side boundary layer" I agree that one would expect slower loss of PRCs in winter, because of a lower temperature. However, this is because the partitioning coefficient Kpg would be higher and NOT because of a different thickness of the air boundary layer.

> Thanks for that comment, we agree that the loss of PRCs in general is mainly influenced by the temperature and the resulting Kpg. This statement was yet referring to the potential influence of photodegradation, we tried to clarify that now:
“If photodegradation was causing significant loss of PAHs from PE, we would expect a correlation to solar radiation leading to faster losses of the PRC and thus (artificially) thinner air-side boundary layer in summer, which was not the case.”

Lie 455: “Thus, in this case the exchange between PE and air over seasonal time-scales is more influenced by the physical-chemical properties of the target compounds than by temporal variation of δg”. Careful, this is only the case, because the wind speed at the study sites showed very limited spatial and seasonal dependence. In a global study such as GAPS (line 431), you would encounter a much wider range of wind speeds and thus in δg.

> Thanks for that comment, we emphasize this point more clearly now:
“Thus, in this case (with rather stable sampling conditions) the exchange between PE and air…”

Reference 7 and 65 are identical
> Corrected

05-May-2021

Dear Dr Meierdierks:

Manuscript ID: EA-ART-12-2020-000022.R2
TITLE: Unique calibration of passive air sampling for field monitoring of PAHs with polyethylene thin films across seasons and locations

Thank you for submitting your revised manuscript to Environmental Science: Atmospheres. After considering the changes you have made, I am pleased to accept your manuscript for publication in its current form.

You will shortly receive a separate email from us requesting you to submit a licence to publish for your article, so that we can proceed with publication of your manuscript.

You can highlight your article and the work of your group on the back cover of Environmental Science: Atmospheres, if you are interested in this opportunity please contact me for more information.

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Thank you for publishing with Environmental Science: Atmospheres, a journal published by the Royal Society of Chemistry – the world’s leading chemistry community, advancing excellence in the chemical sciences.

With best wishes,

Dr Lin Wang
Associate Editor, Environmental Science: Atmospheres

Environmental Science: Atmospheres is accompanied by sister journals Environmental Science: Nano, Environmental Science: Processes and Impacts, and Environmental Science: Water Research; publishing high-impact work across all aspects of environmental science and engineering. Find out more at: http://rsc.li/envsci

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