Assessing the roles emission sources and atmospheric processes play in simulating δ15N of atmospheric NOx and NO3− using CMAQ (version 5.2.1) and SMOKE (version 4.6)

Fang, Huan; Michalski, Greg

doi:https://doi.org/10.5194/gmd-15-4239-2022

Articles | Volume 15, issue 10

https://doi.org/10.5194/gmd-15-4239-2022

© Author(s) 2022. This work is distributed under
the Creative Commons Attribution 4.0 License.

https://doi.org/10.5194/gmd-15-4239-2022

© Author(s) 2022. This work is distributed under
the Creative Commons Attribution 4.0 License.

Articles | Volume 15, issue 10

Development and technical paper

|

01 Jun 2022

Development and technical paper |

| 01 Jun 2022

Assessing the roles emission sources and atmospheric processes play in simulating δ¹⁵N of atmospheric NO_x and NO₃⁻ using CMAQ (version 5.2.1) and SMOKE (version 4.6)

Huan Fang and Greg Michalski

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Final revised paper (published on 01 Jun 2022)
Supplement to the final revised paper
Preprint (discussion started on 06 Jan 2021)
Supplement to the preprint

Interactive discussion

Status: closed

RC1:
'Comment on gmd-2020-415', Anonymous Referee #1, 05 Feb 2021

This purpose of this study is to use the d15N-NOx to trace the changes in d15N values along the “journey” of atmospheric NOx by incorporating 15N into an emission input dataset (which is reported on in a companion manuscript in this same journal, Fang and Michalski, 2020), to run CMAQ (the community multiscale air quality modeling system) with transport of the newly d15N species. The domain of the model study is over the Midwest US, and includes both a nested (higher resolution) grid as well as a larger grid over the entire Midwest. The simulated d15N-NOx were compared to d15N-NOx (actually d15N-NO2) measurements made in West Lafayette, Indiana, USA. These values better align than when using SMOKE from the original version, due to the consideration of mixing, dispersion, transport, and deposition of NOx emissions from different sources based on NEI estimates. The authors determine that the planetary boundary layer (PBL) height is the key driver for the mixture of anthropogenic and natural NOx emissions. The authors conclude that the performance of CMAQ simulated d15N-NOx is better than SMOKE d15N-NOx (Fang and Michalski, 2020). The next step (companion paper number 3) is to explore how tropospheric photochemistry alters d15N(NOx) by incorporating 15N into the chemical mechanism of CMAQ and comparing the simulation with corresponding measurements. This can help to evaluate and improve NOx emission inventories, which is an important first-order issue in atmospheric chemistry.

The work does address modelling question within the scope of GMD. Using d15N-NOx and d15N-NO3- in atmospheric chemistry models is a major step forward in this field, and only now possible with much better constraints on emission source values and fractionation associated with chemistry. Though we have a dearth of measurements of d15N-NOx for comparison with a model at the national or regional scale, the ability to model this parameter helps to better our understanding of its utility and target future measurement studies based on the model results. In that sense, this work is timely, important and will have an impact. The use of d15N-NOx in a modelling framework is indeed novel and overall this work, as mentioned above, is an important advance. Based on the above, I see this an important contribution to the literature. However, there are a number of major revisions that would be necessary to make this acceptable for publication. I start below with several significant general comments, then follow with detailed comments within the context of the manuscript page numbers. I cannot make this decision for the authors, but I would ask that they consider actually combining this work with Fang & Michalski 2020 -- better digesting the work in both papers to focus on the most salient model results, actually quantify the sensitivity of results to change in emissions versus change in transport within the model domain, and then reflect on how d15N-NOx and NO3- are currently being interpreted in the literature. This would represent a major step forward to being able to use this tracer quantitatively. As it stands, the premise that transport somehow would not matter for setting the distribution and seasonality in d15N-NOx is not appropriate – it is well known from a concentration point of view that this would be true, and the authors themselves point out on page 4 (lines 11-15) the “unsatisfactory” nature of the 2020 paper’s approach so why is it justified to separately publish that?

It is of critical importance to address the significant overlap between this work and the cited companion paper of Fang & Michalski (2020). The “companion paper” (hereafter referred to as FM2020) specifically concludes that the model is biased due to the lack of fractionation associated with chemistry. Here they focus on the role of transport and mixing in changing the distribution of the N isotopic composition of NOx, and conclude that the model is biased due to the lack of fractionation associated with chemistry (i.e. this is the same conclusion as FM2020). Additionally, there is significant overlap and direct plagiarism of much of the text of FM2020 in this manuscript (much of the introduction and Figure 1 is verbatim from the other manuscript), which must be modified if this manuscript is to stand alone. Why are these works separated? I think it would make much more sense to combine the two manuscripts. Much of this work under review here is repetitive with FM2020 and the real power of the results in this manuscript is limited in its current form. While I value the need to focus on the detailing the model specifics in a journal such as GMD, the manuscript here lacks any real interpretation, quantification of the sensitivity of the output to the model parameters and consideration of the implications of the predicted values compared to previous studies in the literature of interpreting the isotopic composition of NOx and nitrate. From my point of view, the only purpose of a “no transport” case study should be to 1) quantify the impact of assuming that everything is locally derived, 2) show how “wrong” that assumption is, and 3) reflect on the implication of this for previous interpretations (such as Elliott et al. (ES&T, 2007) who assume a direct 1:1 relationship of d15N-NOx to d15N-NO3- or for considering the utility of isoscapes such as that presented in Walters et al. (ES&T, 2015)).

Second, the model is compared with one set of observations of “d15N-NOx” in Indiana (within the domain of the model runs). The domain of the model is never justified in the manuscript (i.e. why focus on the MidWest?). The 2-day transport lifetime against “loss” or conversion is fair (based on Levy et al, 1997, which should be cited) but this should be brought up early on in the paper to justify the domain of the study. Additionally, the measurements that are compared with are specifically d15N-NO2 and not d15N-NOx. This is important because of the equilibrium fractionation that can occur between NO and NO2 in the atmosphere. While fractionation associated with chemistry will apparently be discussed in a future manuscript, the authors must be precise in their comparison since it is used to validate the model (here and in FM2020). Walters et al. (2018) calculate that the fractionation between NO and NO2 under the conditions where NO2 was captured is likely small, but it’s not small enough to make no difference in the comparisons being made here. If the authors feel it is a small enough difference, then this should still be stated and made clear that a direct comparison between d15N-NOx and d15N-NO2 is ok in this case. This needs to be considered and discussed in the manuscript to make the comparison between the model and observations robust.

Third, the sensitivity to the starting emissions values should be evaluated. Table 2 shows that there a very large changes in d15N-NOx when just assuming different emission rates (ie NEI 2002 versus 2016). The emission “source” value measurements, used as input for the model, report large ranges and have analytical error associated with them. It appears median values are used (though this is not specifically stated in this manuscript). Shouldn’t a range of values (or at least a high and low value) be tested for the sensitivity to changing these source values? Shouldn’t the error associated with the observations be considered in terms of what types of changes in d15N-NOx can actually be detected and therefore be considered important? The use of specific values should be better justified in the manuscript. The on-road values come from Walters et al., 2015 and are calculated based upon tailpipe measurements for a handful of specific vehicle types that yield a huge range. Yet, observations of on-road vehicles are available for the Midwest and northeastern US and if anything much better constrain this emission source value to -4.7 +/- 1.7 in Miller et al., 2017 (which is cited in the manuscript but never seems to be used; note too that Miller et al., 2017 contains measurements of roadside d15N-NOx that could be compared with the model in future studies that expand the domain to include the northeastern US). Similarly, Yu and Elliott, 2017 and Miller et al, 2018 are cited in the introduction (in a sentence that is exactly the same in FM2020), but the values from these papers are not being used in Table 2 and both Yu and Elliott and Miller et al. are important b/c they represent more robust measurements than Felix and Elliott 2014 and Yu and Elliott also focus on urban soil emissions.

Fourth, one of the key conclusions of this work is that changes in the polluted boundary layer (PBL) are critical to transport and dispersion of NOx such that the pattern of d15N-NOx is importantly changed based on the PBL height. I’m not convinced the results shown support this conclusion. Figure 6 shows the difference in d15N when using the same emissions (NEI) but different meteorology – in other words, how much difference does changes in meteorology make when holding emissions “constant”. Figure 7 shows the change in the PBL for these same runs. The pattern of important changes in the PBL do not at all match with the pattern of important changes in d15N, so how can the change in the PBL be the major driver? In fact, the changes in d15N between the two meteorological conditions is really between -1.25 and +1.25 per mil except in the westernmost edge of the domain during summer, and on the whole the best represented value of change geographically is actually zero. So what are we really learning? And how is the PBL change important if it’s greatest change is in the spring and summer in the center and eastern domain where the change in d15N is essentially negligible? Then in Figure 12, it ends up seeming that because the shape of PBL change looks like the shape of change in d15N-NOx simulated by CMAQ we can conclude that it is the driver. Why not look at PBL changes within the time frame of the only observations that are compared with. There is a lot of variability in the d15N-NO2 data shown in Figure 11, and some significant day/night differences. If the PBL changes followed those changes in d15N, then following that up with Figure 12 would be logical and more convincing of the potential for the PBL to be the driver of the d15N changes.

Fifth, “the role of deposition” section and comparison of d15N-NOx with d15N-NO3- seems out of place in this work. It is clearly shown in the literature, and much of the author Michalski’s own work, that fractionations associated with NOx cycling and the formation of NO3- are important for setting the d15N-NO3-. The only reason to include this section in the manuscript would be to show the distribution of d15N-NOx if one were to assume d15N-NOx = d15N-NO3- and reflect on the studies that have done this (seemingly incorrectly). The comparison of d15N-NOx and NO3- does reveal that some of the seasonality of the d15N-NO3- is dictated by the sources of NOx, but the values for d15N-NO3- are clearly largely offset from the d15N-NOx b/c of chemistry and partitioning between the gas and particle phases of NO3-. This would be better addressed, on the whole, as part of the next manuscript where with and without chemistry could show the change in d15N-NO3- rather than comparing with d15N-NOx. Additionally, lifetime matters more in the case of NO3-, which is often stated to have an average lifetime of 3-5 days (see for instance Xu and Penner, ACP, 2012), so transport from outside the domain would need to be considered to make a comparison with d15N-NO3- observation fruitful. Finally, it needs to be addressed why in this work there are only 8 NADP sites being compared with, while it appears that 82 measurement sites are included in FM2020?

Additional detailed comments:

There are number of language errors that should be addressed to improve the clarity of the paper – for instance “disperse” throughout the manuscript should be “dispersion”; “medium” should be “median”, “closed” should be “close”. A number of symbols (such as HNO3 and HNO4 in the introduction) do not print out correctly for some reason.

In general, for the figures (in the manuscript and in the supplement), the captions need to be improved. Most captions are extremely similar, with perhaps a words or two different, making it difficult to compare and interpret. I would suggest specifying the comparison being made (for instance, figure 6 could specify that this is a comparison of the impact of meteorology using the same NEI 2002 emissions, so the reader knows how to interpret the figure). In addition, the authors should consider adding average values over the domain to each figure – the text often specifies the average value over the domain for a specific season, but this would be much easier to compare across the seasons if the average or median value were placed in the upper right corner of each figure. For the map domain figures the y-axis is never defined and show be removed or defined. Additional specific comments on some of the figures is included below. Lastly, consider the use of significant figures throughout the manuscript – the observations are typically reported to one decimal place so why report model results to 3 decimal places?

Title: Is it necessary to have the CMAQ, SMOKE and WRF versions as part of the title? The title is a bit unwieldy; these versions could be specified in the abstract and manuscript; “plays” should be “play” and I would argue that atmospheric “processes” are not really being tested here, it’s really transport or meteorology.

Abstract:

-line 2, nitrogen dioxides should be dioxide

-line 4-5 “After NOx from different sources being emitted…” is grammatically incorrect and awkward

-line 12, estimating should be estimation; observation should be observations

Introduction:

-p4, line 3, put “of” in “isotopic composition of NOx”

-p4, line 17, what do second and third factors refer to?

-considering adding into the introduction a justification for focusing on 2002 and 2016 or at least introduce that this will be the focus and justify it in the methods section

Methodology:

-p4, line 29 remove “of” before meteorological

-p4-5, line 1, “(nitrate)” maybe should be “(e.g., nitrate”) since NOx can also be removed as other products. Also this removal as nitrate comes up without much discussion of the chemistry that converts NOx to NO3- or appropriate references within the Introduction to characterize this well so that the deposition simulations can be followed by a more novice reader.

-p5, line 1, remove “of” before chemistry

-p5, lines 5-8: throughout here “meteorology” should be “meteorological”; value should be values; “condition impacts” should be “conditions impact”

-p5, line 17, add degrees symbols to the latitudes and longitudes

-p6, lines 26-29, I think it would be more understandable to a more general audience if 0.0036 was clarified as the natural abundance of 15N. This is not technically the ratio of 15N/14N of air N2 as stated. It would also be more clear if it was stated that d15N-N2 is, by definition, 0 per mil. (the statement here become confusing especially on p11 when the “15NOx concentration equals 0.0036 of…14NOx”).

-p7, line 10, area is not stationary sources; the definition in Eq 5 include mobile sources.

-p7-8, see general comments above. It needs to be made clear how the values chosen amongst the range of measurements is specified (mean? Median? And why?); and the authors either need to justify the use of specific values or better yet update to more relevant numbers from Miller et al., 2017 and 2018 and Yu and Elliott, 2017.

-p8, line 23, “were selected based on [the] same timeframe as selected NOy d15N measurements.” The justification for the years selected should probably be presented sooner. There should be justification for the domain being focused on the Midwest – the NOx measurements compared to the model are d15N-NO2 not d15N-NOy; and I’m not sure it is relevant to compare with d15N-NO3- for this study.

-p11, line 28, Canada, in reality is not an “’emission-free zone” and transport from this region is certainly expected within the 2-day time frame. This is another example where the sensitivity to this assumption should be stated or made clear as to how it affects the results and conclusions.

Results and Discussion:

-p14, lines 9-10, here it is stated that on-road vehicles have a d15N=-2.7 +/-0.8 per mil, yet Miller et al. 2017 report consistent observations from the Midwest and northeast of -4.7 per mil on average.

-this section (3.1) of the results would be improved if there were discussed in the context of how isoscapes of NOx or NO3-, purely based on the assumption that local emissions = a local signal is not correct and that transport and mixing play a key role in setting the distribution predicted by the model

-this section (3.1) also does not discuss the potential for NO2 to be deposited quickly near roads. This is something that is hypothesized in Elliott et al. (2007) and part of why they draw the conclusions that stationary NOx sources in the Midwest explain the d15N-NO3- signals on the east coast (versus vehicles on the east coast, which are the dominant local source). Also, consider that this is suggested by the study of Redling et al. (Biogeochemistry, 2013).

-p15, line 8-9, given that this is a model it should be better accounted for why the grids located in the suburb of major cities is dominated by on-road vehicle emissions – is this because of transport from the cities? Or is this b/c urban sources decrease and vehicles become the major local source in the suburbs?

-Figure 3: the scale doesn’t appear to cover the entire range? i.e. isn’t there predicted values as low as -34.3 per mil and as high as -20 per mil? Also it should be made clear what the box in (b) represents. Same question about the scales in Figure 4.- do they cover the entire predicted range?

-p17, the interpretation here would be improved it reflected on the implications for conclusions drawn in the published literature such as Elliott et al (2007), isoscapes and similar studies that do not consider realistic transport of NOx and changes in the d15N-NOx that are clearly reflected in this model study.

-p18, lines 13-14. Please provide more context here – what measurements was made in China? How does this correspond to what is being stated here? How do these measurements indicate/agree with the evolution being seen in the model?

-p21, Figure 7, Given the argument above that the PBL changes itself do not appear directly linked to important changes in d15N-NOx, this figure does not seem useful.

-p23, lines 1-3. The statement here about emission control technologies should 1) be referenced and 2) is incorrect. Felix et al. demonstrates that emission control technologies lead to HIGHER values of d15N from smokestacks, not LOWER. This needs to be addressed.

-the most dramatic changes in d15N seem to be associated with changes in emissions. Could the authors detail what significant changes there are in emissions between 2002 and 2016 (and why) and then more directly discuss the impact on the d15N compared to quantifying the impact of meteorology alone.

-p26, line 5-7, the latter hald of the sentence starting with “The predicted d15N of atmospheric NOx over the nested domain…” is confusing – please rephrase or change to two sentences.

-p26, line 14, “closed” should be “close”

-p26, what are we actually learning from the nested-grid simulation? This section discusses what changes in the predicted values between the nested domain and the full domain, but does not really discuss how/why this matters. Figure 10 is pretty unimpressive given that the changes are less than 1 per mil, with the most change in the range of >0.5 per mil such that this would never actually be detected in observations. This figure does not seem necessary for the main text, and would again be more interesting the context of quantifying the changes in d15N that occur with changes in emissions, changes in meteorology and changes in domain.

-Figure 11 should cite the reference the observations are from and see comments above about discussion regarding the observations being d15N-NO2 not d15N-NOx

-Figure 12, see the more significant comments above. The link with PBL height is not very convincing over the whole domain based on the earlier figures comparison and Figure 12 cannot really be considered in the context of the observations in Figure 11 since the observations were only taken during summer. So why not plot the seasonality in the d15N and PBL from several locations in the domain to make the link with the PBL more concrete? There’s also no discussion of how the measurements were originally interpreted and how this review using the model changes or enhances the previous interpretation. For the figure caption add “Left axis” after the square and circle in the parentheses to be consistent with the “(x, right axis)” [Also, are there not any other observations within the domain to compare with? Elliott’s group at Univ of Pittsburgh has published at least passive sampler d15N-NO2 in Redling et al. and in Felix and Elliott 2014 in the Midwest – why are these not considered for comparison?]

-p30, line 9-16 do not seem necessary given that all of this information is in the table.

-p30, line 18-19, “In general, the CMAQ simulations of d15N(NOx) under most of the scenarios conducted in this study, except the simulation based on NEI-2016 and 2016 meteorology, perform better than the SMOKE simulation of d15N(NOx), which only take the variability of NOx emission source into account (Table 2)”… how is “perform better than” defined? Matching the median of the West Lafayette observations or the entire range or ? This is confusing b/c the 2016 simulation compares best with the observations so the ‘except’ here seems out of place. It also seems somewhat obvious that the 2016 simulation w/ real meteorology compared to the 2016 observations would yield the best result. Maybe reporting the SMOKE results in Figure 13 would help with this too (or better yet combine with the SMOKE results for one manuscript). Also it’s important to consider again whether there are any other observations that could also be compared with within the model domain.

-p31, Figure 13, change “dots” to “open circles” in the caption; do the x’s reflect the mean? Include this in the

-p32, line 5, why the ~ signs? Try to make clear in the text here when observations are being discussed and when model output/predictions/simulated values are being discussed.

-p32, Figure 14, what is the number of measurements being represented here? Can an “n=” be included. Why the choice of only a few sites for comparison here? The seasonality based on the 8 locations is much more muted than the seasonality presented across 82 sites presented in FM2020. See above in the major comments with regards to issues with the comparison of d15N-NOx and d15N-NO3- and the lifetime/transport distance that might be associated with NO3- compared to NOx and whether the comparison here is justified. Note too that Aug, Sep, Oct are particularly different between the model and observed wet deposition – what is the cause of this?

-p32-33, “The difference between CMAQ simulated δ15N values of NOx and measured δ15N values of NO3- is caused by the following two factors: a). the mixture of isotopically lighter NOx from the surrounding area discussed in section 3.2, and b). the net N isotope effect during the conversion of NOx to NO3-, which will be addressed in future work.” These conclusions do not seem supported. The mixing in of lower d15N-NOx from the surrounding area should be reflected in the real d15N-NO3- and in the d15N-NOx – i.e. the simulations with transport from the time period when the observations were taken should be more realistic and better reflect what is observed. The second point is the same conclusion drawn in FM2020 – i.e. we need to assess the impact of chemistry b/c this is important and it makes all of the simulations here difficult to interpret as to whether they are worthwhile to interpret without the context as to whether NOx and NO3- can be realistically simulated without chemistry effects.

Conclusions:

-“The simulation indicates that the PBL height is the key driver for the mixture of anthropogenic and natural NOx emission, which deepens the gap between d15N of atmospheric NOx and NOx emission.” -> is this really proven? There is not enough evidence presented to really draw this conclusion. And it’s not really the gap between the d15N-NOx and NOx emission, its whether or not the d15N-NOx in the atmosphere is determined by local sources alone versus a more realistic treatment including transport.

-“The performance of CMAQ simulated d15N(NOx) is better than SMOKE d15N(NOx)…” -> based on what metric? And it might make more sense to make clear here that simulations that include transport (i.e. CMAQ) reveal …., while those that are based on local emission sources alone (i.e. SMOKE) reveal…

Citation: https://doi.org/10.5194/gmd-2020-415-RC1
- AC1:
  'Reply on RC1', Huan Fang, 26 Nov 2021
  All typo and gramatical errors were adjusted according to the comments. The responses to other comments are included below.
  1. “… the authors themselves point out on page 4 (lines 11-15) the “unsatisfactory” nature of the 2020 paper’s approach so why is it justified to separately publish that?”, “It is of critical importance to address the significant overlap between this work and the cited companion paper of Fang & Michalski (2020) …”
  We decided to combine the companion paper with this manuscript in order to deal with the overlapping and completeness issue.
  2. “… While I value the need to focus on the detailing the model specifics in a journal such as GMD, the manuscript here lacks any real interpretation, quantification of the sensitivity of the output to the model parameters and consideration of the implications of the predicted values compared to previous studies in the literature of interpreting the isotopic composition of NOx and nitrate …”
  The more in detail interpretation and quantification of the output have been included in the revised manuscript (In section 3.2, 3.3, 3.5, and 3.7)
  3. “Second, the model is compared with one set of observations of “d15N-NOx” in Indiana (within the domain of the model runs) …”
  The full simulation domain covers the whole Midwest while the sampling sites only locate in IN, IL, OH, and KY. As a result, the sampling site would have sufficient distance between the domain boundary to eliminate the bias near the domain boundary.
  4. “Additionally, the measurements that are compared with are specifically d15N-NO2 and not d15N-NOx …”
  Walters et al (2018) did include the d15N(NOx) values based on the measurements in Table 1 and 3.
  "The first comparison is to the only direct measurements within the domain, which occurred in West Lafayette, IN. The δ15N(NOx) values were inferred from the measured δ15N(NO2) and the calculated δ15N(NO2) shift (Walters, Fang, & Michalski, 2018)."
  
  5. “Third, the sensitivity to the starting emissions values should be evaluated …”
  The range of d15N values for any source is generally a function of equilibrium, kinetics, or reaction progress happening in that source process. For example, automobiles show a wide range of both NO_x amount and d15N values going from cold start to normal driving, but once the catalytic converter is warm the values are relatively constant because the NO_x reduction by the CC becomes constant. We are using the average to account for these effects and for simplicity. In future work hope to explicating model the sources variation in SMOKE or land surface models, but that is well beyond the scope of this work. Fig. S10 shows the uncertainties of d15N values within the research area. For most of the grids, the uncertainties are less than 5 ‰, which is well below the difference in d15N values between any two of the emission sources. For those regions dominated by biogenic source, the uncertainties in d15N values are less than 10 ‰, which is also significantly below the difference in d15N values between the emission from biogenic source and all the other sources.
  6. “Fourth, one of the key conclusions of this work is that changes in the polluted boundary layer (PBL) are critical to transport and dispersion of NOx such that the pattern of d15N- NOx is importantly changed based on the PBL height. I’m not convinced the results shown support this conclusion …”
  The more in detail interpretation and quantification of the relationship between d15N and PBL height has been included in section 3.3 of the revised manuscript
  7. “Fifth, “the role of deposition” section and comparison of d15N-NOx with d15N-NO3- seems out of place in this work …”
  CMAQ simulated the d¹⁵NO_x effect by NO_x removal using enhanced deposition. These “emission + mixing + enhanced deposition” simulations were not imposing an isotope effect related to dry/wet deposition, rather they are an attempt to show how “lifetime chemistry” alters NO_x d¹⁵N values by removing NO_x before it can be transported significant distances.
  8. “Finally, it needs to be addressed why in this work there are only 8 NADP sites being compared with, while it appears that 82 measurement sites are included in FM2020?”
  We decided to use the exact measurement from our lab at the 8 NADP site to validate the simulation, instead of using the values of literature review and compared with the simulation values at the grids contains the NADP site within the simulation domain.
  9. “Title: Is it necessary to have the CMAQ, SMOKE and WRF versions as part of the title?”
  The editor requested us to include the model’s name and the version number in the title
  10. “I would argue that atmospheric “processes” are not really being tested here, it’s really transport or meteorology …”
  Transport, mixing, dispersion, and deposition are all examples of atmospheric processes
  
  Citation: https://doi.org/10.5194/gmd-2020-415-AC1
- AC2:
  'Reply on RC1', Huan Fang, 26 Nov 2021
  All typo and gramatical errors were adjusted according to the comments, the suggested citation were added. The responses to other comments are included below.
  
  1. “… the authors themselves point out on page 4 (lines 11-15) the “unsatisfactory” nature of the 2020 paper’s approach so why is it justified to separately publish that?”, “It is of critical importance to address the significant overlap between this work and the cited companion paper of Fang & Michalski (2020) …”
  
  We decided to combine the companion paper with this manuscript in order to deal with the overlapping and completeness issue.
  
  2. “… While I value the need to focus on the detailing the model specifics in a journal such as GMD, the manuscript here lacks any real interpretation, quantification of the sensitivity of the output to the model parameters and consideration of the implications of the predicted values compared to previous studies in the literature of interpreting the isotopic composition of NOx and nitrate …”
  
  The more in detail interpretation and quantification of the output have been included in the revised manuscript (In section 3.2, 3.3, 3.5, and 3.7)
  
  3. “Second, the model is compared with one set of observations of “d15N-NOx” in Indiana (within the domain of the model runs) …”
  
  The full simulation domain covers the whole Midwest while the sampling sites only locate in IN, IL, OH, and KY. As a result, the sampling site would have sufficient distance between the domain boundary to eliminate the bias near the domain boundary.
  
  4. “Additionally, the measurements that are compared with are specifically d15N-NO2 and not d15N-NOx …”
  
  Walters et al (2018) did include the d15N(NOx) values based on the measurements in Table 1 and 3.
  
  "The first comparison is to the only direct measurements within the domain, which occurred in West Lafayette, IN. The δ15N(NOx) values were inferred from the measured δ15N(NO2) and the calculated δ15N(NO2) shift (Walters, Fang, & Michalski, 2018)."
  
  5. “Third, the sensitivity to the starting emissions values should be evaluated …”
  
  The range of d15N values for any source is generally a function of equilibrium, kinetics, or reaction progress happening in that source process. For example, automobiles show a wide range of both NO_x amount and d15N values going from cold start to normal driving, but once the catalytic converter is warm the values are relatively constant because the NO_x reduction by the CC becomes constant. We are using the average to account for these effects and for simplicity. In future work hope to explicating model the sources variation in SMOKE or land surface models, but that is well beyond the scope of this work. Fig. S17 shows the uncertainties of d15N values within the research area. For most of the grids, the uncertainties are less than 5 ‰, which is well below the difference in d15N values between any two of the emission sources. For those regions dominated by biogenic source, the uncertainties in d15N values are less than 10 ‰, which is also significantly below the difference in d15N values between the emission from biogenic source and all the other sources.
  
  6. “Fourth, one of the key conclusions of this work is that changes in the polluted boundary layer (PBL) are critical to transport and dispersion of NOx such that the pattern of d15N- NOx is importantly changed based on the PBL height. I’m not convinced the results shown support this conclusion …”
  
  The more in detail interpretation and quantification of the relationship between d15N and PBL height has been included in section 3.3 of the revised manuscript
  
  7. “Fifth, “the role of deposition” section and comparison of d15N-NOx with d15N-NO3- seems out of place in this work …”
  
  CMAQ simulated the d¹⁵NO_x effect by NO_x removal using enhanced deposition. These “emission + mixing + enhanced deposition” simulations were not imposing an isotope effect related to dry/wet deposition, rather they are an attempt to show how “lifetime chemistry” alters NO_x d¹⁵N values by removing NO_x before it can be transported significant distances.
  
  8. “Finally, it needs to be addressed why in this work there are only 8 NADP sites being compared with, while it appears that 82 measurement sites are included in FM2020?”
  
  We decided to use the exact measurement from our lab at the 8 NADP site to validate the simulation, instead of using the values of literature review and compared with the simulation values at the grids contains the NADP site within the simulation domain.
  
  9. “Title: Is it necessary to have the CMAQ, SMOKE and WRF versions as part of the title?”
  
  The editor requested us to include the model’s name and the version number in the title
  
  10. “I would argue that atmospheric “processes” are not really being tested here, it’s really transport or meteorology …”
  
  Transport, mixing, dispersion, and deposition are all examples of atmospheric processes
  
  Citation: https://doi.org/10.5194/gmd-2020-415-AC2
RC2:
'Comment on gmd-2020-415', Anonymous Referee #2, 04 Mar 2021

Please see pdf for comments

Citation: https://doi.org/10.5194/gmd-2020-415-RC2
- AC3: 'Reply on RC2', Huan Fang, 26 Nov 2021
  
  1. “I agree with the first reviewer about the scope of this paper being too narrow, and I think that reviewer’s suggestion of combining this work with Fang and Michalski (2020) would be appropriate ...", "I have serious concerns about the overlap in content with Fang and Michalski (2020). "
  
  We decided to combine the companion paper with this manuscript in order to deal with the overlapping and completeness issue.
  2. "I am not sure what we are learning from the many figures showing the seasonal variation in δ15N concentrations for transport only, transport with different emissions, transport with different meteorology, and transport with deposition on, etc ..."
  
  The more organized interpretation and quantification of the output have been included in the revised manuscript in section 3
  3. "The conclusion that the PBL is the “key driver for the mixture of anthropogenic and natural NOx emission” seems odd ..."
  
  The more in detail interpretation and quantification of the output have been included in the revised manuscript in section 3.3
  4. "Please add quantitative metrics to the abstract to more precisely communicate the impact that adding CMAQ’s process-level understanding has on the evaluations in Indiana."
  
  Confirmed
  5. "Page 2, Line 31: Better add the reference to the FIVE mobile emission model (McDonald et al., 2018: https://doi.org/10.1021/acs.est.8b00778) to these references."
  
  Confirmed
  6. Page 3, Line 18: Consider changing “NOx/NOy” to “NOx” or “NOx and NOy”
  
  Confirmed
  7. "Section 2.1: Why run with an extracted domain? Was this just to make the model go faster?"
  
  To eliminate the bias near the domain boundary
  8. "Much of section 2.3 can be moved to SI. The main manuscript can just state what models and version numbers were used for each part."
  
  Confirmed
  9. "Page 10, Lines 3-18: It is hard to understand exactly what was accomplished in the deposition velocity tuning approach and what its limitations are. This would all be solved if the authors were able to include chemistry in the study and turn chemistry off for a transport+deposition only case."
  
  Including chemistry in the study and turn chemistry off is what exactly we did. The more in detail explanation of deposition have been included in the revised manuscript in section 3.7.
  10. "Section 2.6: We need some idea of how the emission datasets performed against coincident observations from routine networks for conventional pollutants like NO2, EC, O3 and particulate Sulfate to check that they were processed with reasonable assumptions."
  
  We decide to give up this section, and explore the sensitivity of emission dataset in future work
  11. "Please consider removing Tables S1 and S2 from the supplemental information. Just refer readers to the MCIP user guide."
  
  Table S1 and S2 were summarized from user's guide, it is easier to understand for the reader and more relevant to the corresponding section in the manuscript.
  12. "Section 2.7: I’m not sure what is meant by the ‘research area’ and ‘emission-free zone’. Is it just U.S. versus Canada? The term ‘nested’ usually refers to an area of higher resolution. Although this doesn’t strictly have to be the case, I urge the authors to consider renaming their ‘nested’ grid..."
  
  We do not have emission dataset in Canada, thus when the air mass transports out of the Midwest, the atmospheric NOx is diluted. In addition, we set atmospheric NOx δ15N = 0‰ for initial condition and boundary condition, the air mass from Canada, or boundary of the domain could flattened the atmospheric δ15N(NOx). Details in section 2.2.2-2.2.4. The term 'nested' was changed to 'extracted'
  
  13. "Page 14: Rather than using Fig. 3 to show the expected dispersion of NOx in the model domain, why not include a figure as a barplot that quantifies the differences in weighted average δ15N values for the different categories discussed like agricultural areas, big cities, highways and EGUs?"
  
  Fig. S6 in the revised manuscript
  14. "Page 14, line 28: Consider adding a figure with distance from power plant on the x and δ15N on the y to show the decay along a couple of trajectories from an important facility."
  
  Fig. 6 in the revised manuscript
  15. "Page 18: Is there any data to evaluate the PBL heights?...", "Page 18, line 12: Why not have a figure showing the positive correlation between PBL height and δ15N ..."
  
  Fig. 9 and Fig. 10 in the revised manuscript
  16. Fig 7 can go to the SI.
  
  Confirmed
  17. "Fig. 10 is not terribly informative other than to show that the southern boundary should probably also be restricted for the nested area."
  
  The purpose of this analysis is showing how the simulation over the extracted domain improve the performance (by 1‰ near the southern boundary)
  18. I recommend moving Section 3.7 to the first section of the Results.
  
  We decide to start with the interpretation and quantification of the simulation first, then comparing with the measurements.
  19. "Strongly recommend putting Figs. 11 and 12 together so that measurements and models are on the same figure. Why not pair the model and obs in time for the figure ..."
  
  Fig. 11 and Fig. 12 shows the characteristic of measurements and simulations, the comparison between them are in the next figure and the associated paragraphs in the manuscript
  20. "Fig. 14: Consider normalizing both panels to remove influence of chemistry bias. It seems like there is a signal here that the CMAQ modeling is able to capture, but it is hard to tell."
  
  We do agree the normalization could make the figure looks more beautiful. However, the similar monthly variation and seasonal trend with the gap between the simulated d15N(NOx) and measured d15N(NO3-) is exactly what we are expecting, since there are isotope effects associated with the photochemical transformation of NOx into NOy. After including the 15N into the chemical mechanism in our future work, this gap will be resolved.
  
  Citation: https://doi.org/10.5194/gmd-2020-415-AC3

Peer review completion

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

AR by Huan Fang on behalf of the Authors (05 Jan 2022) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (14 Jan 2022) by Slimane Bekki

RR by Anonymous Referee #2 (28 Jan 2022)

Suggestions for revision or reasons for rejection

Thank you to the authors for combining the two companion manuscripts and drafting this more cohesive and complete story. While there is limited amount that can be learned from the approach without the chemistry turned on, there are a lot of key parameters introduced here and sensitivities explored that are worth documenting in GMD.

In addition to the minor comments below, I have one main reservation remaining. The language is often awkwardly phrased or unnecessarily verbose throughout the text and needs some more polishing. It doesn’t interfere with communicating the meaning of the science but streamlining the details and focusing on the main points would crystallize the main messages better. I estimate 25-30% of the text could be cut down or moved to the SI. That said, I understand the authors want to move along to the full-science study with chemistry.

1. P2L5: “What is meant by “gasoline and diesel in vehicle emissions?” I think some words are missing from this sentence.

2. P2L20-24: It’s not clear from the abstract how SMOKE only can yield a prediction of concentration of isotope. Consider deleting and focusing instead on…

3. P4L2: Consider revising “N2 = 0.0036” to “(15N2/14N2)air = 0.0036”. Is that correct?

4. P5L3: Recommend rewriting: “simulations by the CMAQ (Community Multiscale Air Quality) modeling system.”

5. P5L5: Fang et al., 2021 is not in the citations list.

6. P5L11: Please rewrite to “The EPA trace pollutant emissions mode…”

7. Fig. 2 caption: there is no light purple in t Fig. 2.

8. Equation 4: Is ‘t’ the vehicle travel time? Please specify in the text. Does the onroad diesel use the same equation for its isotope contribution or are there different parameters? Does t vary throughout the simulation or is -2.7 assumed constant throughout? I didn’t quite understand from the text.

9. P9L29-30: replace ‘blur’ with ‘disperse’ and ‘blurring’ with ‘dispersion’.

10. P9L36-P10L6: This paragraph is a bit awkward. I recommend starting out mentioning that chemistry will be explored later. Then define what you mean by “enhanced deposition”. Then mention that you assume no difference in the deposition of the isotope and the stable NOx. The explanation of the impact of deposition on hypothetical powerplant emissions is fine to remove, in my opinion.

11. Sections 2.2.1-2.2.4: These sections are organized and titled in alignment with CMAQ in puts and processes but often sensitivity runs are mentioned within these sections without being explicitly introduced. I recommend creating a section 2.2.5 that explicitly lists and describes every simulation. Also, the names of these simulations vary. Sometimes the first one is called ”emission only” and sometimes it’s called “no transport”.

12. P10L32: A clean atmosphere is not necessarily ideal. Was the model provided time for ‘spin-up’ or initialization so that evaluation against observations would be more appropriate?

13. Section 2.2.3: Please include a sentence to explain why chemistry needed to be emulated with enhance deposition. The paragraph transitions from deposition to chemistry abruptly and needs some more detail there.

14. P11L6: “2.2.4”?

15. P11L8: This is not a complete sentence.

16. Fig. 3: Is this tons/day or tons N/day? The text on page 12 uses both units. I suggest sticking with one if possible.

17. Fig. 8: I don’t think the inset for Indiana is discussed. Why is it so dramatically different from the results in the same location for the larger domain?

18. Fig. 16: I’m glad this comparison is here. Please make sure the x and y axes are equivalent for at least the last figure, but preferably for all of these panels. It will be interesting to see what happens with realistic deposition and chemistry.

19. Fig. S19: Consider promoting to the manuscript. I can’t tell what symbols are the NADP values I should be looking at.

20. PBL height analysis: I’m glad this was added to the study. The discussion is rather vague though – the authors just ascribe large isotope effects to the stronger effect of atmospheric processes. Can you please expand on this? Are these point source emissions that are being mixed back down to the surface? Or some other explanation?

21. P31L18-19: How are the authors concluding that uncertainties in the simulation are less than 5 part per mil? Do they mean variability instead of uncertainty? Please explain how uncertainty is estimated in the text.

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RR by Anonymous Referee #1 (08 Feb 2022)

Suggestions for revision or reasons for rejection

This is a second round review. This manuscript is substantially improved from the previous version and the combination of the two manuscripts was definitely warranted. There are number of errors and a need for some better organization for the manuscript to be publishable, as these do change the scientific meaning of the results in several places. Of key importance is that authors do a better job of distinguishing NOx versus NO versus NO2. This needs to be made very clear upfront in the manuscript and if the authors are going to choose to use NOx as a shorthand when referring to NO or NO2 then that needs to be spelled out specifically. NO is the primary emission from all sources in this work, except potentially diesel emissions. This is never mentioned nor discussed and has an important context here since there are no direct observations of d15NO alone and what the model is actually simulating is the release of NO, not the release of NOx. This should be rectified if the authors want the atmospheric chemistry community to be interested in this work.

It is easiest to document suggested changes in order of the manuscript. Some are very minor typos, others are more significant and should be revisited.

Abstract -
It should be made clear in the abstract the difference between SMOKE and CMAQ (i.e. that the latter includes mixing and transport). This will help setup the reader for why these two models are used and what differences can be expected.

Spell out NADP since this is the first use and also make clear that these are rainwater nitrate measurements.

Introduction-
Page 3, Line 3: The very first word of the introduction should not be a symbol – define nitrogen oxides first, then use NOx subsequently.

Line 16: It seems strange to give a single percent (15%) and then give a range of values for soil NOx emissions. It would be better to introduce the range in total NOx emissions from global models and then point out the uncertainty range associated with individual sources such biogenic soil emissions. Also, it should be explained what soil emissions represent (ie. Nitrification and denitrification.

Line 17-18: Satellite observations should be mentioned as reference cited in this sentence include these.

Line 24: change “while acting” to “versus acting” or similar, otherwise the sentence is incomplete

Line 40-41: Natural versus anthropogenic sources is not correct here as anthropogenic sources themselves has distinct isotopic range. I suggest you remove “natural and anthropogenic” from the sentence

Page 4, line 11: change “implement” to “implementation”

Line 20: add “species” after d15NOy

Figure 1 caption: CFPP needs to be defined in the figure caption.

Page 5, line 4-7: might make sense to have this sentence be past tense since that paper is already published.

Throughout section 2 and its subsections there needs to be consistent use of n values, consistent use of ranges versus average values, consistent discussion of methodologies and there needs to appear a discussion of NOx versus NO2 versus NO. Many of the measurements are not able to be compared to one another as some measure NOx and some measure NO2.

Page 7, line 1-4: Miller et al and Yu & Elliott both use active sampling techniques for collecting soil emissions. Not clear what “using a similar methodology at the end of Line 1 means, sinc the previous study mentioned used a passive sampling technique. Further, the passive measurements should report an n value and not a range since I believe these two numbers represent two discrete measurements that represent month long averages.

Section 2.1.2 – it needs to be justified why Miller et al (2017) is not included. This was brought up in the previous review both reviewers. This study is an actual on-road study that captures the mix of tailpipe emissions. The Walter’s study is more representative of tailpipe type measurements, not the signal that is found on-road when vehicles are moving under real traffic conditions with a mix of vehicle types. The Miller study seems more representative in this case. If it is not, it should be reasoned why other values are being used.

Line 22: remove “s” in this sentence

Page 8, section 2.1.3: this section does not make mention of the methods used, nor does it distinguish what was measured in terms of NOx vs NO2.

Line 19-20: how can a range of 9 to 26 lead to an average of 4.51? Please double check.

Page 9, line 36: change the terminology of “d15NOx effect” as this is not an accurate statement. It’s really the effect on d15NOx

Line 37: unbold “not”

Page 10, line 6: change “the” to “a”

Page 11, line 3: change “to” to “in”

Page 14, line 2-3: please also define the anthropogenic fraction since that is used several times in the text below

Line 21: change “the clear” to “a clear”

Line 20-24: justify to the reader why your are selecting April to June to show here (I assume b/c this is the season when soil NOx emissions should be maximum?)

Page 15, Figure 5 caption: explain that the white box is defined in the Figure 6 caption.

Page 18, line 8: change here since April to October is not a “month”

Page 20, line 20: change to “a seasonal”

Line 22: change to “NOx was emitted”

Line 31: this line does not make sense, please rephrase.

Page 20, Figure 8: draw a line to make clear that the insert is Indiana (ie draw a line to the state to connect it) or label the smaller box just above as Indiana to make clear to the reader.

Page 21, line 18: This should start a new section as the emphasis here is no longer on seasonality and rather on the impact of different meteorological fields.

I would argue that Figure 9 and 10 could be combined with a different coloring or dashed lines to represent the different years of met fields.

Page 22, line 4: add “the” before simulation

Figure 11 is unnecessary as the text described this very well and the changes are smaller than even the analytical reproducibility of measurements so there is no way to even test where this distribution is realistic (and the boundary lines are clearly not realistic/an artifact of the model domain).

Page 24, Section 3.5: the phrasing here would be better as NOx loss rather than NOx deposition. The increase in NOx deposition is purely artificial – i.e. this is not, for instance, testing a range in the literature to look at sensitivity. It is a change in the amount of NOx loss to simulate what happens to the isotopic composition given NOx loss from the atmosphere.

Page 25, line 7: remove “of atmospheric”

Line 9: there is no Figure 12a. Figure 12 is not really utilized in this section and it is never explained why a particular time point in the model is chosen for this comparison. Either robustly explain the purpose of the figure and the conclusion being drawn from it or remove it.

Line 10: change “as a similar fashion” to “in a similar fashion”
Line 17: change to “lead to lower”

Line 19-20: change to “atmospheric NOx on a seasonal basis”

Line 20: the range here says a maximum of 5.34 per mil but the figure range only goes to 4 per mil?

Line 25-27: the sentence beginning with “The enhanced deposition simulation somehow presents the isotope effects….” This sentence is not accurate. This cannot represent the fractionations associated with chemistry. What it does show should be the focus here. And it should be explained here that this is used as a proxy for NOx loss from the atmosphere as would be the case in conversion to NOy species. But this is not at all representative of how and why chemical processes would lead to fractionation of NOy species.

Page 26, line 4: change “comparing” to “compared”

Page 27-28, Section 3.6: the two paragraphs of this section are repetitive. This section should be re-organized. I would suggest making the section on comparison to observations its own as Section 4, etc. And the beginning of the section should explain what observations will be used for comparison purposes with the model. It should also be explained what the observations represent and how NOx was computed from d15NO2 measurements. It should also be explained by isotopic measurements of nitrate in rainwater from NADP sites is used as a comparison here as well. Then move onto the actual comparisons.

Page 28, line 20: change to “based on 2002”

Page 29, line 1: “collect” should be “collected”

Line 3: change to “show similar monthly variations”

Line 10: chage to “NO3- are about”

Page 30: The paragraph below Figure 16 belongs before the previous paragraph and these two paragraph are repetitive and should be edited further.

Figure 16: It’s not clear what is being gained from the Figure 16 comparison. The text focuses on discussion of how the seasonal variability is captured. Clearly the ranges are not always captured and while in some cases the variability is decently captured (i.e. R2>0.4) we are not really learning anything by comparing the data in this way. And it is not discussed as to why some comparisons are good and others are not at all. How can we expect the model to ever get d15NO3- values exactly right when chemistry is not even included in the model? It would make a lot more sense to compare seasonal averages or time series from the model versus time series of the observations and focus on the relative changes from season to season rather than leading the reader to expect that there should be a 1:1 relationship for the model-observation comparison. Further the last line of this section (page 31, line 10) is not appropriate speculation. There’s nothing to justify this statement and again the model is not simulating nitrate fields.

Page 31, Conclusion:

The discussion of “uncertainty” needs to be clarified. This is not addressed earlier in the text, so it is not clear how an uncertainty of less than 5 per mil (line 18) was determined. The word uncertainty does not make sense in the context here. And discussion of uncertainty is also unwarranted since the model does not consider/test the full ranges of the observed NOx source signatures for different emission sources. In fact the word uncertainty is used again to describe the uncertainty in NOx emission, which is documented in the literature. Really what is being discussed is the narrow range predicted by the model – or so it appears to me.

Line 28: this sentence makes no sense and it is never discussed in the text that there is such a large uncertainty in NOx power plant emissions.

Line 35 and 37: change the phrase “are possible to be”

Line 37: change “estimated” to “predicted” and add “to be” following NOx

Line 44: what constitutes a “better” simulation? Ie. Based on what is it deemed better?

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ED: Publish subject to minor revisions (review by editor) (17 Feb 2022) by Slimane Bekki

AR by Huan Fang on behalf of the Authors (19 Apr 2022) Author's response Author's tracked changes Manuscript

ED: Publish as is (02 May 2022) by Slimane Bekki

AR by Huan Fang on behalf of the Authors (09 May 2022) Author's response Manuscript

Short summary

A new emission input dataset that incorporates nitrogen isotopes has been used in the CMAQ (Community Multiscale Air Quality) modeling system simulation to qualitatively analyze the changes in δ¹⁵N values, due to the dispersion, mixing, and transport of the atmospheric NO_x emitted from different sources. The dispersion, mixing, and transport of the atmospheric NO_x were based on the meteorology files generated from the WRF (Weather Research and Forecasting) model.