From the journal Environmental Science: Atmospheres Peer review history

17-Nov-2021

Dear Mr Hakala:

Manuscript ID: EA-ART-10-2021-000089
TITLE: Observed coupling between air mass history, secondary growth of nucleation mode particles and aerosol pollution levels in Beijing

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Reviewer 1

This study developed a simple model to predict atmospheric aerosols based on air mass exposure to anthropogenic emissions. It is interesting and will be helpful to understanding the role of atmospheric transport to air pollution. The manuscript was well organized and well written. I would like to recommend its publication after minor revisions.

1) It is expected that the emission near the observation station would have a more significant impact on the air quality compare to emission far away. I would suggest to include this in the model with weight coefficients dependent on the time or distance.
2) Including potential emission sensitivities seemed not improve the model performance. What is the resolution of the air mass trajectories?
3) As for the choice of SO2 and NO2, there was a study reported that PM2.5 was more related to NO2 than SO2 (Environmental Science & Technology Letters 7(10): 695-700，doi: 10.1021/acs.estlett.0c00403). The authors may discuss why is not the case in this study.
4) Since adding meteorology parameters did not help to improve the model while of course meteorology conditions are crucial to air pollution, I would argue that the influence of the meteorology conditions was someway considered in the model. Could the authors add some discussions on this issue?

Reviewer 2

This manuscript develops a method by calculating the air mass exposure to anthropogenic emissions (AME) to investigate how the small particles from NPF to the development of haze. And by considering the meteorological factors, this study further finds the most relevant description for predicting the aerosol volume concentration. My major concern is that the annual emission of SO2 and NOx for the year 2010 was used to estimate the aerosol volume concentration of 2018-2019 and to predict the PM2.5 during COVID period. Some discussions about the uncertainty should be given. Because after the implementation of emission reduction measures in 2013, the SO2 concentration is decreased. And during COVID period, the industrial emissions were mostly affected. Thus, I think that the effects of emission inventory on calculating AME for predicting aerosol volume during 2018-2019 should be further illustrated. I would recommend the editor to reconsider the papers after a revision by the authors.
More specific concerns/recommendations:
Page 10 Line 18: Although the aim of this study is to describe the effects of changing transport conditions, and not changing emissions. Why choose the annual emission (SO2 and NOx) for the year 2010? I am curious whether the same results can be observed in other periods, maybe choose another period to verify?
Page 11 in Section 3.1: In addition to Figure 2, the frequency distribution of the increasing AME corresponds to the growth of particle during NPF events in the 2018-2019 dataset should be given.
Page 12 Line 17: give the air mass circulates on Dec 9th in Fig. A2.
Page 12 Line 23: “changes in AME are expected to result in clear changes in the observed particle mode only if the particle size was previously limited by time and availability of precursors, reflected by the AME value, and not particle growth rate”, but the growth rate may be associated with the precursors, condensation sink and etc.? And the growth rate would decide the growth time? So, I am very confused about when the correspondence between AME and particle growth mode is related.
Page 13 Line 2: ‘steady state’ means what?
Page 15 in Section 3.2: The population density data here used is from GPW on the year of 2015. As the population density is likely related to the emission sources, time difference in population density should be considered in predicting particle volume concentration based on AME?
Page 18 Line 23: In fig. 5d, no dependency is found between the daily average RH and the changes in AME. Maybe give a case to illustrate the effects of the RH on changes in AME?
Page 21 Line 10: Here AME is the daily average AMEPRE,SO2,500m in mega grams of SO2. Is SO2 used here the annual emission for the year 2010?
Page 22 in Section 3.2.3：Here by using the same method, PM2.5 concentration is predicted as a function of AME and MLH. During the lockdown of the COVID-19, emissions from the industrial sectors was most affected, while AME was calculated based on the population density and emission inventory for the year 2010. So AME maybe more related to the anthropogenic emissions?
Page 23 Line 3：No figure 8 in the paper. Maybe the figure 9? And the figure 10 maybe represent figure 9?

We thank the referees for their comments which have helped us improve the manuscript. Below we give a point-by-point response to the comments made by the referees. The referee comments are shown in bold, our responses are in regular font and the text added to the manuscript is shown in red italics.
Along with this response to the referees, we provide the revised manuscript with all changes made during the review indicated with the Track Changes feature in the file titled ‘Hakala_beijing_airmass_history_review.docx’ and the final revised manuscript without showing the changes in the file titled ‘Hakala_beijing_airmass_history_revised_final.docx’. The high quality images are provided separately in a zipped folder figures.zip.
When addressing the changes made in the manuscript, we refer to the page numbers and line numbers of final revised manuscript. Note that Referee 2 refers to the page numbers of the combined submission file, which had 2 additional pages before the actual manuscript i.e. ‘Referee 2 page number’ = ‘page number of submitted manuscript’ + 2.
Referee: 1

Comments to the Author
This study developed a simple model to predict atmospheric aerosols based on air mass exposure to anthropogenic emissions. It is interesting and will be helpful to understanding the role of atmospheric transport to air pollution. The manuscript was well organized and well written. I would like to recommend its publication after minor revisions.

1) It is expected that the emission near the observation station would have a more significant impact on the air quality compare to emission far away. I would suggest to include this in the model with weight coefficients dependent on the time or distance.
It is true that with increased transport time, the effect of deposition is expected to increase and thus the response in observed volume/PM is expected to diminish. However, the effect of air mass dilution with time and distance should be included in the potential emission sensitivity fields, and with the single trajectories, assigning the air mass location to a single point can cause either over or under estimations of the exposure compared to the real situation. Since assigning correct/reasonable weights for time/distance is not unambiguous, we initially decided to use the ‘first order approximation’ of this effect in the manuscript i.e. a weight coefficient of 1 is applied to travel times <= 72 h and 0 when travel time is >72h. This is loosely based on the estimated lifetimes of accumulation mode particles, comprising most of the fine particulate mass and volume (quantities predicted with the applied method), near surface (Feichter and Leisner, 2009).
One possible way to include a ‘second order approximation’ of this effect would be to include a continuous exponential decay based on the estimated lifetime of the particles. We tested this approach by re-calculating the AMEST,Pop values using the following equation
█(〖AME〗_(ST,Pop,τ) (t)=∑_(t_b=1h)^72h▒〖A_x [lat(t,t_b ),lon(t,t_b )]×exp⁡(-t_b/τ)×1h ,〗#(1) )
where τ is now the estimated lifetime of the accumulation mode particles. The correlations between AMEST,Pop,τ (using τ = inf, 5d, 4d, 3d, 2d, 1d) and the volume concentration (using hourly and daily values) are shown in figures R1 and R2. We find that adding a term describing diminishing returns with increased travel time does not improve the performance, as the best correlation is found with τ=inf (corresponding to the formulation currently used in the manuscript) with both the daily and the hourly data. This could, on the contrary, suggest that even longer travel times past the 72 h might perform better and we will keep this in mind in the future.
Based on these results, we decided to stick with the initial formulation of calculating the AME. We added the following text (P7 L2-6) to the manuscript to clarify the meaning of the limited backward calculation time and to indicate that an alternative approach was also tested:
Limiting the backward calculation time to 72 h essentially acts as a simple weight coefficient for estimating the relevance of emissions towards the aerosol loadings with increasing travel time. In addition to this step-wise decrease in relevance, we briefly tested adding an exponential decay function to continuously describe the potentially diminishing returns from further-away emission sources but found no improvements later on in the analysis.

Figure R1: AMEST,Pop,τ (with τ = inf, 5d, 4d, 3d, 2d, 1d) vs. volume concentration using hourly data.


Figure R2: AMEST,Pop,τ (with τ = inf, 5d, 4d, 3d, 2d, 1d) vs. volume concentration using daily average data.

2) Including potential emission sensitivities seemed not improve the model performance. What is the resolution of the air mass trajectories?
Using the potential emission sensitivity fields instead of the single trajectories improves the correlations presented in Table 1 by 0.00-0.05. These improvements are around the same magnitude as switching from using population density to the emission inventories and we do not consider this change inconsequential. It is true that with the daily averages, the improvement is quite minor as the averaging likely decreases the significance of the more accurate description of the momentary air mass source areas. With the hourly data, more clear improvements are found.
The fact that using PES does not completely change the picture is expected and the result is useful for showing that single trajectories can also be used in this type of analysis in the future. We note, however, that the single trajectories used here are calculated within the FLEXPART model from the multi-tracer retro plumes and using single trajectories from single-particle backward simulations might not perform as well compared to the PES fields. In order to clarify this, as well as to point out the less significant improvements when using daily averaging we added the following text into the manuscript (P14 L3-6):
However, the improvements are mostly visible with the hourly data, whereas with daily averaging the benefits gained from the more accurate description of momentary air mass source areas seem less significant. Here we would like to remind that in our case, the single trajectories are calculated from the multi-tracer retroplumes, and therefore single trajectories from single-tracer simulations would not necessarily perform equally well.
The resolution of the PES fields is 0.05 degrees (as stated in the Methods sections 2.2 and 2.3) and it is clearly higher than the resolution of the emission inventories (0.25 degrees) and similar to the resolution of the population density data (~0.042 degrees). Therefore we believe that the resolution of the air mass trajectories should not be an issue here.

3) As for the choice of SO2 and NO2, there was a study reported that PM2.5 was more related to NO2 than SO2 (Environmental Science & Technology Letters 7(10): 695-700，doi: 10.1021/acs.estlett.0c00403). The authors may discuss why is not the case in this study.
We assume the comment refers to the better correlation found using SO2 emissions than the NOx emissions (and not to the OMI NO2 field). Our initial thought was that this could have been related to the emission being from 2010 but since similar results are found with the updated emission inventories (see answers to Referee 2), this doesn’t seem to be the case.
Even though it was probably not implied by the referee, we would like to clarify that we do not make any claims in the manuscript about the relative importance of NOx and SO2 emissions, and choose the SO2 emission based method solely because of the slightly better performance (Table 1).
The question why the performance is found to be better with SO2 emissions here is definitely interesting but also something that would require much more analysis to answer in a meaningful manner. We deem detailed investigations of chemistry to be outside the scope of this manuscript but provide some speculation of the possible reasons:
Our method is likely more connected to predicting the total sulfate and nitrate (gas phase + particle phase) than just the gas phase concentrations that are used in the study pointed by the referee. Even though the study states that: “The coefficient for NO2 (β) was at least 3 times higher than that for SO2 (α), which cannot be mathematically explained by the relative abundances of nitrate and sulfate in PM2.5 or the nitrate/NO2 and sulfate/SO2 mass conversion ratios.”, this effect probably still has some contribution to the results.
Even though the study pointed by the referee show that the better correlation with NO2 is found at the majority of the CNEMC monitoring network sites, especially at the more urban locations, the specific location of the measurement site and e.g. proximity to vehicular emissions likely still plays a role. A similar study, comparing the responses in aerosol concentrations as a function of gas phase concentrations of SO2 and NOx, at our measurement site during winter months of 2018 shows slightly better correlation between NOx and the accumulation mode particle concentration during clean periods (r = 0.69 vs r = 0.65 for NOx and SO2, respectively) but a clearly better correlation between SO2 during haze days (r = 0.37 vs r = 0.76 for NOx and SO2, respectively) (Zhou et al., 2020).

4) Since adding meteorology parameters did not help to improve the model while of course meteorology conditions are crucial to air pollution, I would argue that the influence of the meteorology conditions was someway considered in the model. Could the authors add some discussions on this issue?
Arguably the most crucial effects of meteorology on air pollution come from the changing air mass transport conditions and changes in the mixing layer height. These meteorological factors were also found to have very significant impacts here and are explicitly included in the model. Whether meteorological variables in addition to these two (e.g. T, RH, WS) have (or are even expected to have) crucial effects on air pollution is much more debatable.
In section 3.2.2 we discuss some of the possible effects that the additional meteorological variables might have as well as speculate the reasons why no significant correlations are found. For WS, no significant correlation is expected as the wind conditions are accounted for in the back trajectories. For discussing the lack of correlation with RH and precipitation, we have already included separate (and even quite lengthy) paragraphs in section 3.2.2., where especially the significant co-correlation between AME and RH is pointed out as an important factor.
In terms of T we briefly mentioned that “[The negative correlation] with temperature could be related to increased volatility at higher temperatures, but it can also reflect the seasonal changes in emissions and aerosol formation mechanisms in general”. We now further looked at the residual dependency on the deseasonalized temperature, and the residual dependency on temperature when the AME values are calculated using monthly SO2 emissions instead of the annual average emissions (Fig. R3) to further confirm that the latter speculated reason is the more likely one. We added the following text to the manuscript (P16 L18-21):
A weak positive correlation with the residuals and deseasonalized temperature (r = 0.18; not shown) suggest that the latter explanation might be more probable. This is further supported by a very weak positive correlation with the residuals and temperature if the AME is calculated using monthly emissions instead of the annual average.
We also modified the previous sentence (P16 L17-18) to clarify that by ‘seasonal changes in emissions’, we refer to the anthropogenic emissions being generally lower during summer. We also removed the very end of the sentence to reduce ambiguity. The modified sentence now reads:
The [negative] correlation with temperature could be related to increased volatility at higher temperatures, but it can also reflect the seasonal changes in anthropogenic emissions, as the emissions are generally lower during summer.
A brief mention about the weak positive residual correlation with RH when using the monthly emissions in the calculation of AME was also added (P17 L9)
Similar positive correlation is also found when using deseasonalized RH data or AME values calculated using monthly emissions (r ~ 0.2; not shown).
Related to the presented discussion, we wish to state that even though investigating the dependencies on the additional meteorological variables is likely more sensible when using the monthly emissions in the calculation of AME, our goal of highlighting the impact of changing transport conditions is more apparent when using the average emissions (since in this case the AME only changes if the transport conditions change). Also in the calculation of AME, the anthropogenic activity field Ax is intended to work as a proxy for describing all the relevant anthropogenic emissions towards aerosol formation, and it is not trivial if all of these emissions would be expected to share similar seasonal variability as e.g. the SO2 emissions. Finally, we want to point out that even if the monthly emissions are used, the residual dependencies on the additional meteorological variables are not strong enough to merit their inclusion in to the simple predictive models, and that the final results as well as the conclusions drawn in the manuscript would remain essentially unchanged.

Figure R3. Same as figure 5 in the initially submitted manuscript, but with using monthly emissions of SO2 in the calculation of AME instead of the annual average.


 
Referee: 2

Comments to the Author
This manuscript develops a method by calculating the air mass exposure to anthropogenic emissions (AME) to investigate how the small particles from NPF to the development of haze. And by considering the meteorological factors, this study further finds the most relevant description for predicting the aerosol volume concentration. My major concern is that the annual emission of SO2 and NOx for the year 2010 was used to estimate the aerosol volume concentration of 2018-2019 and to predict the PM2.5 during COVID period. Some discussions about the uncertainty should be given. Because after the implementation of emission reduction measures in 2013, the SO2 concentration is decreased. And during COVID period, the industrial emissions were mostly affected. Thus, I think that the effects of emission inventory on calculating AME for predicting aerosol volume during 2018-2019 should be further illustrated. I would recommend the editor to reconsider the papers after a revision by the authors.
During the analysis phase of this manuscript, the MIX 2010 emissions (and MEIC 2012) emissions were the most recent publicly available emission inventories (from the meicmodel.org website) and we decided to use the MIX emissions for the wider coverage over Asia and not only Mainland China. We also want to point out that the model performance is not dependent on the magnitude/absolute amount of the emissions, but rather their relative spatial variability, which is why we considered the 2010 emissions usable. Only if the model was re-applied with a different emission inventory without tuning the fit-coefficients, would the magnitude of the emissions play a role.
However, since the emission reductions likely have spatial variability (i.e. emissions are not reduced by a constant factor everywhere), the use of 2010 emissions might be problematic and could potentially cause over/underestimations of the importance of emissions from specific areas. Therefore we re-calculated the AME values using the (now available) MEICv1.3 emission for SO2 and NOx on the year 2017. We also believe that emissions outside of Mainland China do not significantly influence the calculation of AME as the air masses rarely travel over areas with significant emissions outside Mainland China (see Fig. R4 and A1), and that therefore the partly lacking coverage of the MEIC emission inventory is not an issue. Since we fully agree with the reviewer on that most recent emissions should be used in the analysis, we have re-calculated all of the presented results in the manuscript with the updated inventories and replaced the previous results. This caused some changes in Figs. 4-8, A1, A3, A4 and Tables 1 and 2. Several parts of the text were also modified to state the use of the new emission inventories as well as to more accurately describe the updated results. We will not list all of the specific page and line numbers here, but all the changes are visible through the use of the Track Changes feature in the revised manuscript. Overall, the results stay very similar and no changes in any main conclusions are needed. This also highlights the relatively small changes in the spatial distribution of emissions between 2010 and 2017 and displays the robustness of the applied method.
Regarding the comment about ‘predicting’ the PM2.5 during COVID period, we want to emphasize that when we apply the model with constant emissions to the COVID period, we are not trying to predict the actual PM2.5 concentrations during COVID. The aim of this approach is to evaluate the effect of the emission changes during COVID on PM2.5; If the prediction with the constant emissions still resembles the observations, we can conclude that the emission changes (regardless of the most affected sectors) during COVID did not significantly impact PM2.5 formation. If, however, the constant emission prediction would have been clearly larger than the observed concentrations, we could have concluded that the emission changes reduced PM2.5 formation significantly. Using constant emissions to evaluate the impact of (unknown) emission changes is a widely used approach in modelling. We feel that this is sufficiently described in the manuscript. For example, on P21 L6-7 we state that “Since no emission changes are considered in the predicted PM2.5, the expected result from the reduced emissions in 2020 would be that the observed PM2.5 concentrations fall below the predicted ones.”


Figure R4. Map showing the number of times that the daily average potential emission sensitivity fields have any contribution from a specific grid during 2018-2019. Note that here the daily average potential emission sensitivities are presented only with ones and zeros, and that the contribution of near-by areas to the actual potential emission sensitivity value is therefore significantly larger.

More specific concerns/recommendations:
1) Page 10 Line 18: Although the aim of this study is to describe the effects of changing transport conditions, and not changing emissions. Why choose the annual emission (SO2 and NOx) for the year 2010? I am curious whether the same results can be observed in other periods, maybe choose another period to verify?
See answer to the opening comment. In short, very similar results are obtained also with the updated emission inventories describing emissions on the year 2017.

2) Page 11 in Section 3.1: In addition to Figure 2, the frequency distribution of the increasing AME corresponds to the growth of particle during NPF events in the 2018-2019 dataset should be given.
We gather that this comment and the comments no. 4 and 5 all concern the same issue and provide our combined answer to all of these here.
First of all, we want to clarify that we do not think or attempt to claim that increasing AME is a requirement for NPF event growth, but rather we try to show that the AME value essentially acts as a limiting factor/ceiling for the maximum diameter that the particles produced in the NPF event can reach at the observation site. To touch on the comment no. 5, by ‘steady state’ we refer to the situation where this maximum diameter is reached. We’ll explain this a bit further using an analogy between a NPF experiment in a flow tube and the AME. If we consider a flow tube with constant SO2 (or other) emissions along the tube length, our AME value (in this analogy) at some point along the tube would be directly proportional to the distance between the start of the tube and the point of our observation. Let’s assume that the point of our observation is located 10 m from the start of the tube, and that this now corresponds to a constant AME value of 10. If we now initiate NPF in the tube by illuminating it with UV (uniformly throughout the tube), we could begin to observe NPF and particle growth at the point of our observation, even though the AME is constantly 10 (i.e. increasing AME is not required for observing particle growth during NPF). However, after the observation has continued long enough for us to observe air that was located at the beginning of the flow tube at the onset time of UV radiation (t=10m/flow velocity), we would reach a steady state in our observations and continuously observe an unchanging particle size distribution. Of course, in the real world situation several factors can change while our calculated AME stays constant, preventing a similar steady state from occurring, but the analogy should hold true to some degree. For example, during 7th Dec the AME stays relatively constant around 2-3e3 (Fig. 2 in the manuscript) and this seems to ‘allow’ growth until few tens of nm. Since we do not think that increasing AME is required for particle growth during NPF, we also feel that providing the “frequency distribution of the increasing AME corresponds to the growth of particle during NPF” as requested in the comment no. 2 is not necessary (or relevant/meaningful) and hope that the referee agrees. We did, however, modify a sentence in the text (P10 L18) that previously read “In the cases of continuous growth, also the AME increases simultaneously with increasing particle size”, which now reads
In the cases where growth to large particle sizes is observed, also the AME clearly reaches higher values
as we think this sentence might have been a source of confusion contributing to the referee comment no. 2.
Returning back to the flow tube analogy and now to the sentence quoted by the referee in comment no. 4, our idea was that if the AME value changes before the steady state is reached, we would not observe significant changes in development of the particle size distribution as the growth would still continue regardless of this change. However, it is true that even during the growth phase before the steady state, changing the AME (observation point closer or further in the flow tube) would cause changes in the amount of accumulated emissions (and in the real world also condensation sink etc. as pointed by the referee) and therefore also in the observed growth rate and the development of the particle size distribution. We therefore agree with the referee that this sentence is more confusing (and incorrect) than clarifying and decided to remove it completely. The following two sentences continuing on the subject and mentioning the ‘steady state’ (which is issue of referee comment no. 5) are also removed.

3) Page 12 Line 17: give the air mass circulates on Dec 9th in Fig. A2.
We added panels showing the air mass history on Dec 4th 00:00 and 12:00 LT as well as Dec 9th 12:00 into Fig. A2 so that the figure now covers the full time range of Fig. 2 + one extra panel in the beginning and in the end. We also changed the panel titles in Fig. A2 so that midnight is expressed as the 0th hour of the next day rather than the 24th hour of the previous day. This is better in line with the x-labels in Fig 2., which were also modified to display the time of midday in addition to the changing date at midnight.

4) Page 12 Line 23: “changes in AME are expected to result in clear changes in the observed particle mode only if the particle size was previously limited by time and availability of precursors, reflected by the AME value, and not particle growth rate”, but the growth rate may be associated with the precursors, condensation sink and etc.? And the growth rate would decide the growth time? So, I am very confused about when the correspondence between AME and particle growth mode is related.
See answer to the second comment. In short, after re-visiting the referenced statement, we also found it confusing and even incorrect and decided to remove the statement completely.

5) Page 13 Line 2: ‘steady state’ means what?
See answer to the second comment. ‘Steady state’ is no longer mentioned in the revised manuscript.

Page 15 in Section 3.2: The population density data here used is from GPW on the year of 2015. As the population density is likely related to the emission sources, time difference in population density should be considered in predicting particle volume concentration based on AME?
During the analysis stage of this manuscript the GPW v4.10 was the most recent one, which was the reason why we were using population density data for the year 2015. The next version (v4.11) including the population density for the year 2020 has, however, recently become available and we now updated our calculation of AMEPop to utilize this data instead. This caused minor changes in Figs. 1-3, Fig A1,Table 1 and the table of contents entry, as well as and in the text where the used population density data in specified. Qualitatively, the results stay the same. Quantitatively, the correlations in Table 1 are actually seen to decrease slightly (by 0.00-0.02).

Page 18 Line 23: In fig. 5d, no dependency is found between the daily average RH and the changes in AME. Maybe give a case to illustrate the effects of the RH on changes in AME?
Figure 5d (4d in the revised manuscript) shows the dependency, or the lack thereof, between RH and the fit residual (log(V)-log(Fit)), not RH and AME. This indicates that RH does not give significant further information for predicting the volume concentration when changes in AME are accounted for.
However, a dependency between AME and RH is found, as shown by the positive correlation coefficient between these variables in Fig. A4 (r = 0.59), and this positive correlation is likely to contribute to the lack of correlation mentioned in the comment and explained in the manuscript (P16 L25-30). We added a small clarification to the end of the sentence starting from P16 L28 to indicate that both of the described situation are reflected by the increasing AME values:
[Since no RH dependency is found after accounting for the changes in AME (Fig. 4d), some of the effects attributed to elevated RH might actually be related to shifts in air mass transport pathways over generally more polluting areas, as well as to more aged emissions], both reflected by the increasing AME values.
Also, we want to clarify that we believe the correlation between AME and RH is not because of RH affecting the air mass transport routes or emissions (AME) but rather the other way round, where the air mass transport route affects the local RH as explained in the text (P16 L30 – P17 L3).

Page 21 Line 10: Here AME is the daily average AMEPRE,SO2,500m in mega grams of SO2. Is SO2 used here the annual emission for the year 2010?
In the calculation of the AMEPES,SO2,500m we consider the air mass residence time and the emission intensity i.e. if an air mass spends 1 day in a grid where annual SO2 emissions are 1 Gg, the AME value will increase by 1 day*1 Gg/365 d = 2.7 Mg. We modified a sentence in the methods section to more clearly indicate that we are indeed using the annual average emission intensities (and not annual emissions in the literal sense). The modified sentence now reads (P8 L21):
In the cases of SO2 and NOx, we use the annual average emission intensities for the year 2017…
The use of the updated emission inventories is also now mentioned.

Page 22 in Section 3.2.3：Here by using the same method, PM2.5 concentration is predicted as a function of AME and MLH. During the lockdown of the COVID-19, emissions from the industrial sectors was most affected, while AME was calculated based on the population density and emission inventory for the year 2010. So AME maybe more related to the anthropogenic emissions?
Unfortunately, we are not sure we fully understand the question here. AME (air mass exposure to anthropogenic emissions) is most definitely closely related to anthropogenic emissions. We also want to clarify that by anthropogenic emissions, we refer to all emissions related to human activities including emissions from power, industry, residential, transportation and agriculture sectors. While the population density might mostly reflect residential emissions, all of the sectors are included in the SO2 emission inventory, and the SO2 emissions are the only activity field used in Section 3.2.3. In the first answer (to reviewer 2) we clarified the use of constant emission and the meaning of the model prediction during the COVID period, which might also be relevant here.
If the reviewer means to suggest that the close resemblance of the predicted and observed PM2.5 concentrations during the COVID lockdown might indicate that the PM2.5 in Beijing is mostly controlled by residential emissions (which did not change as significantly as the industrial emission), we agree that this could be a possible explanation. However, most other studies seem to have concluded that the main reason was the increased secondary aerosol formation, which is consequently the explanation we chose to present in our manuscript. In case any further unclarities remain, we kindly ask the reviewer to reformulate the question.

Page 23 Line 3：No figure 8 in the paper. Maybe the figure 9? And the figure 10 maybe represent figure 9?
After combining some of the individual figures into different panels of a same figure during the late stages of the manuscript preparation, we had apparently forgotten to update the figure numbering. We found that in addition to a figure with the number 8, also a figure with the number 4 was missing. The figure numbering (and referencing) is now corrected everywhere in the manuscript. (No additional figures were added, only the numbering was incorrect). Thanks for pointing this out!

In addition to the changes listed in this document, we also made some minor linguistic/spelling changes, all visible with the Track Changes feature.

References:
Feichter, J., and Leisner, T.: Climate engineering: A critical review of approaches to modify the global energy balance, The European Physical Journal Special Topics, 176, 81-92, 10.1140/epjst/e2009-01149-8, 2009.

Zhou, Y., Dada, L., Liu, Y., Fu, Y., Kangasluoma, J., Chan, T., Yan, C., Chu, B., Daellenbach, K. R., Bianchi, F., Kokkonen, T. V., Liu, Y., Kujansuu, J., Kerminen, V. M., Petäjä, T., Wang, L., Jiang, J., and Kulmala, M.: Variation of size-segregated particle number concentrations in wintertime Beijing, Atmos. Chem. Phys., 20, 1201-1216, 10.5194/acp-20-1201-2020, 2020.

29-Dec-2021

Dear Mr Hakala:

Manuscript ID: EA-ART-10-2021-000089.R1
TITLE: Observed coupling between air mass history, secondary growth of nucleation mode particles and aerosol pollution levels in Beijing

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. I have copied any final comments from the reviewer(s) below.

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Environmental Science: Atmospheres
Royal Society of Chemistry

Reviewer 1

My comments were fully addressed. I can recommend its publication in Environmental Science: Atmosphere.

Reviewer 2

None.