From the journal Environmental Science: Atmospheres Peer review history

20-Dec-2021

Dear Dr Jathar:

Manuscript ID: EA-ART-10-2021-000082
TITLE: Dilution and Photooxidation Driven Processes Explain the Evolution of Organic Aerosol in Wildfire Plumes

Thank you for your submission to Environmental Science: Atmospheres, published by the Royal Society of Chemistry. This manuscript has been in the review process for a relative long period of time, as we had difficulty recruiting a sufficient number of expert reviewers. For that, I thank you for your patience.
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Environmental Science: Atmospheres
Royal Society of Chemistry

************

Reviewer 1

Akherati et al. used SOM-TOMAS, a coupled OA formation-microphysics model to simulate OA evolution in several wildfire plumes in the WE-CAN campaign. To my knowledge, this is the first wildfire OA evolution modeling study with detailed oxidation and microphysics. The model is comprehensive enough for the authors to examine different factors impacting the OA evolution and extract useful information, which can be tricky for studies of OA in wildfire plume. This paper fits well within the Journal’s scope and meets the novelty requirement. Also, I see the authors try to be rigorous by e.g. exploring a number of sensitivity cases and be transparent about the caveats, and thus think that the work is of relatively high scientific quality. I recommend publication of this paper after the following issues are addressed:

Major:
1. OH concentration estimates in this paper are substantially lower than previous studies. The authors tried to discuss causes of this discrepancy. But the relevant discussions need to be improved. A lot of VOCs measured in Koss et al. (2018) can be oxidation products. If they are formed during the aging of the plume, their observed decay would be slower and may result in a lower OH in fitting. In addition, the temperatures of the plumes can be much lower than those of the BB emissions in laboratory studies. Are the slower reactions due to lower temperatures accounted for in the OH concentration estimation? While I am not suggesting that these are the main causes of the large differences in OH estimates (OH estimation in the literature studies also had issues), the discussions about the large differences should be more comprehensive, and hopefully more convincing, as OH estimates in the plumes are a key result of this paper. Also, if the authors cannot convincingly show that their OH estimates are more reliable than literature values, the latter should also be included as sensitivity cases in this study.

2. In this paper, the moment the plume reaches equilibrium height is set to t=0. No discussion for t<0 was made in the paper. I believe that the period of the plume rising is significantly long and should also be considered. Higher temperatures of the plume at lower heights may drive faster reactions. If BB emissions in field measurements and laboratory experiments are assumed be similar, substantially lower VOCs at t=0 than laboratory values may indicate Signiant VOC losses in the plume at t<0.

3. SOM-TOMAS includes OA microphysics. Regrettably, I see no results about it. For instance, size and phase state evolution of wildfire plumes can be interesting results. I believe that OA microphysics results should be included in the paper, or at minimum briefly discussed. Otherwise, why was SOM-TOMAS instead of SOM only was used?

Specific comments:
Line 140: discussions are needed on the impacts of the true Lagrangian assumption for the pseudo-Lagrangian sampling.

Line 188: why is nitrogen in BBOA neglected in this study? N is a major of BBOA. A justification is necessary.

Line 211: how are the 106 VOCs weighted in the fitting? Normally, they can have very different concentrations and measurement errors.

Line 220: this sentence is not accurate. For instance, with 60 ppbv O3 and 4e6 molec/cm3 OH, the rates of the ozonolysis of a-pinene and limonene would be ~40% of those of their reactions with OH.

Line 325: no documented evidence of HOM or oligomer in wildfire plumes is not equivalent to evidence of no HOM or oligomer. I think that they can exist in wildfire plumes. Stolzenburg et al. (PNAS, 2018, 115, 9122) showed that a-pinene autoxidation can still occur relatively rapidly at ~0 C, leading to HOM formation. Also, accretion products from highly oxidized RO2+RO2, which can be regarded as dimers, should form more easily at ~0 C than under laboratory conditions. So a more appropriate justification is needed for this simplification.

Line 418: it is unclear to me how to realize the iterations. What outputs were used as inputs of the next iteration? How robust is this iterative process? Does it lead to some extent of indeterminacy or multiple solutions depending on initial guess?

Line 430: why is there a separate bar specifically for EPISuite in each volatility bin? What is it?

Line 651: I cannot find Monte Carlo results in (c), (f) or (i).

Line 712: I disagree with this sentence. OH-High scenario also seems to be within the scatter of OA NEMR. It also looks acceptable in terms of O:C and POA fraction.

Technical corrections:
Line 349: a- or b-pinene? I cannot the first character correctly on my computer.

Line 512: y axis label of Fig. 4c needs to be “normalized” or “relative” OA composition. There is the same issue in other relevant figures.

Line 719: the legend is not clear. For example, what does “Post-1st transect” really refer to? Also, (c,f,i) are not properly referred to in the caption.

Reviewer 2

This manuscript investigates the evolution of primary and secondary organic aerosol (POA/SOA) in wildfire plumes by integrating results from field observations, laboratory experiments, and model simulations. Results showed that the rapid SOA formation from photochemical oxidation of volatile and semi-volatile organic compounds (VOC/SVOC) could compensate the aerosol mass loss due to evaporation of POA in the wildfire plumes during transport. The mass loading of aerosol remained similar over the course of the evolution, while its physicochemical properties altered significantly with SOA contributing to >30% of total aerosol concentration a few hours after emissions. Based on laboratory-normalized and reactivity-differentiated VOC decay, the authors reported significantly lower OH concentrations after the first hour of the plume evolution, as compared to those observed in the literature. Several insightful implications and directions were provided in the manuscript. Overall, this is a comprehensive study regarding aerosol evolution in wildfire plumes. The manuscript is well written, and the results are quite interesting and valuable to the literature. I would like to recommend its publication in Environmental Science: Atmospheres, subject to minor revisions:

1. Lines 188-189: The O-to-C and H-to-C ratios were calculated by assuming that OA was only composed of C, H, and O. However, wildfires also emit a significant amount of reactive nitrogen species that can contribute to the production of nitrogen-containing organic species. Please discuss how the presence of nitrogen-containing organic species will affect the estimation of O-to-C and H-to-C ratios in this study.

2. Line 207: The term “average VOC NEMRs” is confusing. Until reading the next few paragraphs of the manuscript, I figured out that it means the average NEMR for each VOC, not an average value for all the VOCs. Please be clear in the manuscript.

3. Lines 223-224: Using the average NEMR values for VOCs emitted from lab-generated burns can have huge uncertainties, which depends strongly on factors such as fuel type and burning condition in lab fires and field fires.

As the authors also mentioned in the later part of the manuscript, there could be systematic k_OH-dependent differences in emissions between the lab and field studies. Do the authors have any information regarding tree species (e.g., family and type) at the wildfire sites? How are these species similar to the ones used in the lab burning experiments? Instead of using the average VOC NEMR values, what if the authors use fuel-specific VOC NEMR values? How do these values change with burning conditions (e.g., flaming and smoldering)? Please discuss.

4. Lines 246-256: OH concentration was observed to be around six times higher before the first transect compared to that after the first transect, leading to much faster SOA formation before the first transect. Are there any clues about how much OVOC is primary and how much is secondary? If VOC chemistry occurred so quickly and contributed significantly to SOA formation, should OVOC be excluded in the plots in Figure 1, although I understand that this will lead to even lower OH concentrations estimated for the period after the first transect?

Compared to the literature values, the OH concentrations after the first transect estimated in this study are significantly lower. I agree with the authors that using a large number of VOC species to calculate OH concentration improves its accuracy. However, except for the approach provided in the manuscript, have the authors tried any other methods?

For example, OH concentration may also be obtained by examining the relationship between ln(VOC NEMR_field / VOC NEMR_lab) and k_OH*t for each VOC. The slope of the relationship yields an effective OH concentration. A mean OH concentration (after the first transect) can be obtained by average the values obtained for all the VOCs at a specific site. How will this OH concentration be different from the one estimated in the manuscript?

5. Line 256: “the first transect was estimated between 21 and 56 minutes of the physical age of the wildfire plume.”

Please add this information to the caption of Figure S1 regarding the calculation of sampling time to show that this time is not long so that it does not affect the conclusion about Lagrangian sampling.

6. Lines 540-543: The word slight seems inappropriate. It seems to the reviewer that OA NEMR was significantly underestimated (by ~15%). What about revising the sentence to the following:

The base simulation that assumed a semivolatile POA and oxidation chemistry for both SVOCs and VOCs (SV-POA+FullChem) underestimated the OA NEMR by around 15% compared to observations...

7. Lines 608-610: It does not seem that the contribution of VOCs to SOA was identical among different transect sets, except for the results between Sharps and Bear Trap 1. The results cannot lead to the conclusion that VOC composition was uniform across fires. I suggest rewriting or removing this sentence.

8. Figure 6: Results of Monte Carlo simulations are missing.

9. Lines 687-689: The reviewer is confused. Are the base simulation results presented in Figures 4 and 5 based on the volatility distribution observed by May et al. or based on the optimal results from the Monte Carlo simulation? Please clarify.

10. Line 704: The figure legend in Figure 7 is confusing. For example, it took me a while to figure out that “pre-1st transect” represents “OH-High”. Why not use OH-High, OH-Low, OH-Power fit, OH-Ambient, just like Figure S11?

11. Lines 709-711: It seems to the reviewer that “OH-High” provides the best fit, at least for the Taylor Creek Fire, the most representative Lagrangian dataset. Does it suggest that the OH concentration after the first transect was underestimated in this study?


Technical Points:

12. The caption of Figure 1: “Solid red lines represent the linear fit to the data and the red bands capture the uncertainty in the fit (1).”

There are three solid red lines. The bands are missing. I guess that the first and the last (from up to down) lines give the uncertainty of the fit and the error “1” represents one sigma deviation?

13. Line 449: Error for “-pinene”.

14. Missing label c in Figure 4, label i to l in Figure 5, label a to i in Figure 7.

This text has been copied from the PDF response to reviewers and does not include any figures, images or special characters.

We thank both reviewers for their comments. Below, we have provided responses (red regular) to all
reviewer comments (black italic) and included revisions made to the manuscript (blue regular). Parts of
the original manuscript for reference are shown in magenta regular.
Reviewer #1
1. Akherati et al. used SOM-TOMAS, a coupled OA formation-microphysics model to simulate OA
evolution in several wildfire plumes in the WE-CAN campaign. To my knowledge, this is the first wildfire
OA evolution modeling study with detailed oxidation and microphysics. The model is comprehensive
enough for the authors to examine dif erent factors impacting the OA evolution and extract useful
information, which can be tricky for studies of OA in wildfire plume. This paper fits well within the
Journal’s scope and meets the novelty requirement. Also, I see the authors try to be rigorous by e.g.
exploring a number of sensitivity cases and be transparent about the caveats, and thus think that the work
is of relatively high scientific quality. I recommend publication of this paper after the following issues are
addressed:
We thank the reviewer for making the time to read through our paper as well as the positive comments.
2. OH concentration estimates in this paper are substantially lower than previous studies. The
authors tried to discuss causes of this discrepancy. But the relevant discussions need to be improved.
We agree with the reviewer that the manuscript demands a comprehensive discussion of wildfire plume
OH. Accordingly, we have dedicated a fair amount of the text in Section 2.2 to clearly outline the
differences in the OH estimates between this and earlier work, the potential reasons for those differences,
and the uncertainty in the OH estimates reported in this work. Section 2.2, which is entirely dedicated to
the estimation of OH concentrations and exposures, has a word count of nearly 1800 and includes two
figures and 1 table. Furthermore, we have undertaken a rigorous sensitivity analysis in Section 3.2 using
five different estimates for OH, the results for which have been highlighted in Figure 7 for the Taylor
Creek Fire and in Figure S11 for all other Fires. Finally, in Section 5, we have restated the role that OH
plays in the photochemical evolution of OA in wildfire plumes and provided recommendations for how
uncertainty in OH estimates could be reduced in future work. We have consistently discussed the
importance of OH throughout the manuscript and do not feel that the discussion needs to be expanded any
further.
3. A lot of VOCs measured in Koss et al. (2018) can be oxidation products. If they are formed
during the aging of the plume, their observed decay would be slower and may result in a lower OH in
fitting.
The reviewer is correct. We did consider the fact that VOC oxidation in the wildfire plume could
contribute to the production of oxygenated VOCs that could bias calculations of OH concentrations. This
is discussed in Section 2.2: “Since the OH estimates were developed based on the observed decay of all
species including reactive oxygenated VOCs, any chemical production of oxygenated species should bias
our OH estimate lower. Hence, based on the inclusion of the reactive oxygenated VOCs alone, our OH
estimates potentially present a lower bound estimate. When OH was calculated from hydrocarbon VOCs
measured by the PTR-ToF-MS to eliminate the influence from including oxygenated VOCs, the inverse
relationship was weakened and produced OH concentrations that were at least a factor of 2 lower than
those listed in Table 1, both before and after the first transect.”.
Perhaps, the bigger question that the reviewer is asking is: what are the proportions of primary and
secondary OVOCs and, further, how do these proportions evolve with time and vary by species? There is
limited evidence in the literature on this point. For instance, Coggon et al. (2019) have found that in
laboratory experiments performed on biomass burning smoke, there was little to no production of phenol
or furan for photochemical exposures under a day, with abundant primary emissions for both species.
Assuming this is the case for the majority of oxygenated VOCs measured by the PTR-ToF-MS (i.e.,
primary emissions of oxygenated VOCs are significantly larger than those produced through secondary
reactions), the assumptions made in our work towards estimating OH seem reasonable. We have added
the following sentence to share this finding: “Although there is limited evidence, Coggon et al. (2019)
have found in laboratory experiments performed on biomass burning smoke that there was little to no
production of reactive oxygenated VOCs, such as phenol and furan, relative to these species’ primary
emissions.”.
One way to account for the production of oxygenated VOCs is to run an explicit gas-phase chemical
mechanism (e.g., Master Chemical Mechanism (MCM) (Saunders et al., 2003; Jenkin et al., 2003),
Generator of Explicit Chemistry and Kinetics of Organics in the Atmosphere (GECKO) (Aumont et al.,
2005) to simulate the oxidation chemistry in the wildfire plume and determine OH concentration profiles
that matched the time-dependent evolution of both VOCs and their oxidation products. Clearly, such a
task would require significant development of the gas-phase chemical mechanism, especially to represent
oxidation chemistry of oxygenated aromatics and heterocyclic compounds, VOC classes that remain
poorly characterized. To that second point, we have added the following text in Section 5: “Specifically,
ongoing and future work needs to focus on developing and applying analytical and modeling techniques
to estimate OH concentrations in wildfire plumes. For instance, recently, Peng et al. (2020) calculated
HOX (OH + HO2) production rates in wildfire plumes sampled during WE-CAN from the photolysis of
nitrous acid (HONO), O3
, and other smaller aldehydes (e.g., formaldehyde) and ozonolysis of alkenes.
Similarly, OH concentrations could be constrained by developing and applying explicit gas-phase
chemical mechanisms to reproduce the time-dependent evolution of VOCs and their oxidation products.
Such techniques need to be leveraged to study OH concentrations both across and within plume transects
and potentially be used to evaluate earlier, more simpler, estimates for OH.”.
4. In addition, the temperatures of the plumes can be much lower than those of the BB emissions in
laboratory studies. Are the slower reactions due to lower temperatures accounted for in the OH
concentration estimation? While I am not suggesting that these are the main causes of the large
dif erences in OH estimates (OH estimation in the literature studies also had issues), the discussions
about the large dif erences should be more comprehensive, and hopefully more convincing, as OH
estimates in the plumes are a key result of this paper.
The average temperatures in the wildfire plume varied between 272 and 282 K, and these data are
presented in Figure S2. For a given wildfire plume the temperatures varied slightly across the transect sets
for the Taylor Creek and Silver Creek Fires (<5 K) and did not vary much across the transect sets for the
Bear Trap 1 and 2 and Sharps Fires. As the reviewer points out, these temperatures are lower than the 300
K assumed in calculating the kOH for the different VOC species and reported in Table S2. The temperature
dependence on kOH has only been reported in the literature for a handful of species and for very few of the
VOCs considered in this work. Regardless, when we examined the temperature dependence on kOH for
select VOC classes reported in Atkinson and Arey (2003) (alkanes, isoprene, monoterpenes, single-ring
and multi-ring aromatics), we found that the kOH varied from -10% (for alkanes) to +20% (for
monoterpenes) for the lowest average temperatures measured in the wildfire plume (i.e., 272 K) compared
to the kOH value at 300 K. As the reviewer points out, this relatively small sensitivity to temperature is insufficient to explain the OH differences estimated in this work compared to that in the literature. We
have added the following sentence to Section 2.2: “Here, we used kOH values reported at 300 K to perform
this analysis. As kOH values for well-studied VOCs such as alkanes, alkenes, and aromatics are only ±20%
off at the cooler temperatures in the wildfire plume compared to those at 300 K, accounting for the
temperature-dependent kOH is unlikely to change the OH estimates presented here.”.
5. Also, if the authors cannot convincingly show that their OH estimates are more reliable than
literature values, the latter should also be included as sensitivity cases in this study.
We agree with the reviewer. Accordingly, we have undertaken a rigorous sensitivity analysis in Section
3.2 using five different estimates for OH, the results for which have been highlighted in Figure 7 for the
Taylor Creek Fire and in Figure S11 for all other Fires. The results from that sensitivity analysis in the
revised manuscript are reproduced below:
“Results from simulations performed to assess the sensitivity to the OH estimates are presented in
Figure 7(a,d,g). The use of a power function fitted to the OH exposure data to determine OH
concentrations (OH-Power Fit) produced results that were slightly higher compared to those from the base
simulation. Similarly, if we assumed that the lower OH concentration after the first transect was also
relevant to the time period before the first transect (OH-Low; 9.7×10
5 molecules cm-3
), the model
predictions of OA NEMR and O:C were slightly higher than those from the base simulation. When using
a constant OH concentration of 1.5×10
6 molecules cm-3
(OH-Ambient) or the higher OH concentration
from before the first transect (OH-High; 8.9×10
6 molecules cm-3
) for the entire evolution, the model
predicted a higher OA NEMR compared to predictions from the base, OH-Power Fit, and OH-Low
simulations. This was because the OH concentrations after the first transect in both of these instances
were larger than those used in the base, OH-Power Fit, and OH-low simulations and these higher OH
concentrations, which were ~50% larger in OH-Ambient and a factor of ~10 larger in OH-High, promoted
SOA formation.
For the OH-High simulation, the increase in OA NEMR was found to be relatively consistent
with the evolution in the observations indicating that the OH concentrations may continue to be elevated
even after the first transect. However, the OH-High simulations overestimated the OA NEMR compared
to the observations for the other Fires (Figure S11), where the base, OH-Power Fit, and OH-Low
simulations produced results that were more in line with the observations. As the Taylor Creek Fire
dataset is the most Lagrangian amongst all Fires, the OH sensitivity simulation results presented here
provide some evidence that our OH concentration estimates after the first transect (Table 1) may be biased
low and would need to be revised in future work to be consistent with the higher OH concentrations
estimated in earlier work (see Section 2.2 for a longer discussion). Interestingly, a higher OA NEMR in
the OH-High simulation did not change predictions for OA O:C presumably because the additional SOA
formed had an O:C similar to the existing OA’s O:C. Overall, the model predictions appeared to be
somewhat sensitive to the OH concentration inputs that produced a significant spread in the OA NEMR
and POA-SOA splits but not so much in the OA O:C.”
6. In this paper, the moment the plume reaches equilibrium height is set to t=0. No discussion for
t<0 was made in the paper. I believe that the period of the plume rising is significantly long and should
also be considered. Higher temperatures of the plume at lower heights may drive faster reactions. If BB
emissions in field measurements and laboratory experiments are assumed be similar, substantially lower
VOCs at t=0 than laboratory values may indicate Signiant VOC losses in the plume at t<0.
The t=0 point for our simulation was determined by extrapolating the VOC and OA measurements from
the first transect, knowing the OH exposure between t=0 and the first transect. Hence, t=0 represents our best estimate for VOC and OA back to the point of emission, regardless of the time required for the plume
to reach the equilibrium height. In Section 2.3, we made the assumption that the simulation started at the
equilibrium height primarily because it was unclear how we would model the vertical plume rise and the
temperature-dependent evolution between the point of emission and equilibrium height. We have made
the following edits to the relevant text in Section 2.3 to clarify this assumption: “For each wildfire plume,
the SOM-TOMAS model was used to simulate the OA evolution from the time just after emission up to
the last measured transect. While this should include both vertical plume rise and horizontal plume
transport after reaching the equilibrium height, we do not explicitly model the change in the pressure and
temperature of the air parcel during vertical plume rise.”. Assumptions about the pressure and temperature
for the air parcel are explained later in that paragraph: “While the pressure and temperature values
changed modestly between wildfire plumes, they were found to be in a relatively narrow range within
each individual wildfire plume (Figure S2). Hence, an average pressure and temperature value was used
for the entire wildfire plume. Model predictions and measurements of concentrations and mixing ratios in
this work were expressed at the plume pressure and temperature.”.
7. SOM-TOMAS includes OA microphysics. Regrettably, I see no results about it. For instance, size
and phase state evolution of wildfire plumes can be interesting results. I believe that OA microphysics
results should be included in the paper, or at minimum briefly discussed. Otherwise, why was
SOM-TOMAS instead of SOM only was used?
SOM alone does not simulate coagulation of particles and assumes instantaneous partitioning of organic
compounds into a liquid-like OA (Cappa and Wilson, 2012). In contrast, TOMAS when coupled with
SOM simulates the coagulation between particles and phase-state-influenced kinetic gas/particle
partitioning of OA. As the reviewer correctly points out, both of these microphysical processes strongly
influence the size- and composition-resolved aerosol distribution and hence SOM-TOMAS was used in
this work instead of SOM. The OA microphysics results were not showcased in this paper primarily
because there were few if any observations from the WE-CAN campaign that could have helped to inform
the microphysical properties of OA (e.g., phase state) and or support model-measurement comparisons of
OA microphysics (e.g., evolution of the particle size distribution). We have the following text in Section 5
that comments on the use of TOMAS to study microphysical processes in wildfire plumes in future work:
“Future work could certainly benefit from leveraging an extended set of measurements gathered during
WE-CAN and similar field campaigns focused on studying biomass burning emissions (e.g., BBOP101,
LASIC102, FIREX-AQ (https://csl.noaa.gov/projects/firex-aq/). For example, model predictions could be
compared against measurements of the evolving composition (e.g., oligomers), size distribution, and
thermodynamic (e.g., volatility), optical (e.g., scattering, extinction), and climate (e.g., cloud
condensation nuclei) properties.”.
8. Line 140: discussions are needed on the impacts of the true Lagrangian assumption for the
pseudo-Lagrangian sampling.
In Section 2.1, we have described the pseudo-Lagrangian nature of the aircraft measurements and the
Lagrangian assumption used for the model: “Multiple transects (4 to 14 per fire) were executed along the
length of the wildfire plume over multiple hours (2 to 6 hours of physical age) and several hundred
kilometers from the source of the fire (10 to 220 km). We should note that near-Lagrangian sampling was
accomplished for only a few of the wildfire plumes (e.g., Taylor Creek, later transects for Sharps) and, in
most cases, the sampling was pseudo-Lagrangian. As shown in Figure S1, the aircraft sampled much
faster (twice as fast, on average) than the physical age of the plume for four out of the five transect sets
studied in this work. The modeling and analysis undertaken in this work assumes that the fuel and burn
conditions and, therefore, the emissions remained constant during the measurement time period. In other words, we assumed that the measurements represent a true Lagrangian dataset and this assumption should
be considered while interpreting the results.”. We think this description is sufficient to inform the reader
early on of the Lagrangian assumption. As another point of reference, we have included the physical
(smoke) age versus sampling time plot from FIREX-AQ, which shows that the aircraft was sampling
much faster than the physical age (four times as fast, on average). Thus, the WE-CAN sampling was
relatively much more Lagrangian than that during FIREX-AQ.
9. Line 188: why is nitrogen in BBOA neglected in this study? N is a major of BBOA. A justification
is necessary.
We thank the reviewer for this comment. We would like to respond to this comment by first stating the
assumptions made in calculating the OA mass concentrations and elemental ratios, some of which are
used as inputs to the SOM-TOMAS model as well as used to evaluate model predictions. NO
+ and NO2
+
fragments in the HR-AMS, regardless of its origin (i.e., organic or inorganic), are classified as inorganic
nitrate. Hence, the oxygen-to-carbon (O:C) ratios estimated from the HR-AMS data are expected to be
slightly lower than reality in the presence of organic nitrates (Aiken et al., 2008) since the elemental ratio
calculation only includes oxygen atoms in carbon-containing ions. Similarly, the hydrogen-to-carbon ratio
is calculated only from ions that contain carbon. This is consistent with how HR-AMS data have been
analyzed in the past and used to report O:C and H:C ratios in the literature (Aiken et al., 2007, 2008;
Canagaratna et al., 2015). The nitrogen-to-oxygen (N:C) ratios were ~0.020 +/- 0.005 in the Bear Trap
and South Sugarloaf Fires, which are consistent with historical N:C ratios reported for wildfire OA
(Aiken et al., 2007, 2008; Sun et al., 2011; Kim et al., 2017). While N:C ratios were not quantified for the
other Fires, we do not expect the N:C ratios to be very different between Fires. We should note that since
the N:C calculation excludes the NO and NO2 fragments arising from organic compounds, the reported
N:C ratio is also likely to be biased low. However, as only a fraction of the organic nitrate is likely to be
misclassified as inorganic nitrate, the low N:C ratios and small nitrate aerosol mass (<5%) mean that accounting for nitrogen should have little effect on the OA mass concentrations and elemental ratios
reported in this work.
We have added the following text to Section 2.1: “While wildfire OA is likely to be composed of
nitrogen-containing organic compounds, the low N:C values measured during WE-CAN (~0.02) meant
that accounting for nitrogen had a negligible impact on the reported OA mass concentrations and O:C and
H:C values.”.
10. Line 211: how are the 106 VOCs weighted in the fitting? Normally, they can have very dif erent
concentrations and measurement errors.
The VOCs were not weighted in the fitting. Weighting was not required since we only studied the
normalized decay of these VOCs and hence differences in the VOC concentrations was not an issue. We
do agree that the VOCs had different measurement errors but this was not considered in our analysis.
11. Line 220: this sentence is not accurate. For instance, with 60 ppbv O3 and 4e6 molec/cm3 OH,
the rates of the ozonolysis of a-pinene and limonene would be ~40% of those of their reactions with OH.
The reviewer makes a good point. However, we are confident that reactions of VOCs with OH would still
dominate photochemical aging early in the wildfire plume. At 45 ppbv of O3 (lowest value for the O3
measurement at the first transect) and an OH concentration of 3×10
6 molecules cm-3
(lowest value for the
OH estimate at the first transect), 96%, 63%, and 95% of the isoprene, -pinene, and catechol,
respectively, would react with OH with the remainder reacting with O3
. More of the isoprene, -pinene,
and catechol would react with OH at 90 ppbv of O3 (highest value for the O3 measurement at the first
transect) and an OH concentration of 9×10
6 molecules cm-3
(highest value for the OH estimate at the first
transect). Taking the reviewer’s comment into account, we have updated this sentence as follows:
“Isoprene, monoterpenes, and catechol can also react with O3
in addition to OH and were excluded from
the analysis, although including these VOCs did not appear to change the estimated OH exposure (not
shown). This result was partly because the O3 mixing ratios in the wildfire plume were low enough (45-90
ppbv) that these VOCs still preferentially reacted with OH rather than O3
.”.
12. Line 325: no documented evidence of HOM or oligomer in wildfire plumes is not equivalent to
evidence of no HOM or oligomer. I think that they can exist in wildfire plumes. Stolzenburg et al. (PNAS,
2018, 115, 9122) showed that a-pinene autoxidation can still occur relatively rapidly at ~0 C, leading to
HOM formation. Also, accretion products from highly oxidized RO2+RO2, which can be regarded as
dimers, should form more easily at ~0 C than under laboratory conditions. So a more appropriate
justification is needed for this simplification.
We thank the reviewer for this comment. We agree that no documented evidence for HOMs or oligomers
in wildfire plumes does not mean that they are not formed in wildfire plumes. We have revised our
assumptions as follows: “The SOM-TOMAS model also accounts for formation of highly oxygenated
organic molecules (HOMs) and formation/dissociation of oligomers (He et al., 2021). The SOM-TOMAS
model was also updated recently with the diffusive-reactive framework described in Zaveri et al. (2014)
to model the influence of phase state on the kinetic gas/particle partitioning of OA (He et al., 2021).
Although SOA precursors found in biomass burning emissions (e.g., monoterpenes) are known to form
HOMs (Ehn et al., 2014; Stolzenburg et al., 2018) and oligomers (D’Ambro et al., 2018; Zawadowicz et
al., 2020) and certain biomass burning particles can be viscous, neither HOM nor oligomer formation was
modeled and the OA was assumed to be liquid-like with a diffusion coefficient of 10
-10 m2 s
-1
. These assumptions surrounding HOMs, oligomers, and phase state will need to be examined in future work.”.
13. Line 418: it is unclear to me how to realize the iterations. What outputs were used as inputs of the
next iteration? How robust is this iterative process? Does it lead to some extent of indeterminacy or
multiple solutions depending on initial guess?
As described in Section 2.5, we start with an initial POA guess at t=0 that is larger than the OA mass
concentration measured at the first transect. This is to account for dilution between t=0 and the first
transect and evaporation of POA linked to dilution. If the simulated OA with this initial POA guess was
larger (smaller) than the OA measured at the first transect, the POA guess at t=0 on the second iteration
was reduced (increased). This process was repeated till there was agreement in the simulated and
measured OA at the first transect. The iterative process was performed numerically, and we did not
encounter numerical issues that the reviewer is alluding to.
14. Line 430: why is there a separate bar specifically for EPISuite in each volatility bin? What is it?
The POA+SVOC speciation of Jen et al. (2019) was translated into a volatility distribution by first
assigning each of the 150 species a c
* and then combining the information to be represented in a
logarithmically-spaced VBS. The c
*s were calculated either using the EPISuite or by using the
formulation from SOM. The EPISuite-based volatility distribution was only used for reference to compare
against the SOM-informed volatility distributions. As the EPISuite-based volatility distributions are not
used in this work, we have removed those from Figure S4 to avoid confusion; see revised Figure S4
below.
15. Line 651: I cannot find Monte Carlo results in (c), (f) or (i).
The figure caption has been revised as follows: “Model predictions are shown for sensitivity simulations
performed with varying assumptions for the (a,d,g) SVOC oxidation chemistry, (b,e,h) POA volatility and
SVOC oxidation chemistry, and (c,f,i) POA+SVOC mass distribution in the SOM grid (Monte Carlo).”.
16. Line 712: I disagree with this sentence. OH-High scenario also seems to be within the scatter of
OA NEMR. It also looks acceptable in terms of O:C and POA fraction.
We agree with the reviewer’s assessment of the OH-High results. We have significantly revised the
interpretation of the model-measurement comparisons for the OH sensitivity simulation results in Section
3.2:
“Results from simulations performed to assess the sensitivity to the OH estimates are presented in
Figure 7(a,d,g). The use of a power function fitted to the OH exposure data to determine OH
concentrations (OH-Power Fit) produced results that were slightly higher compared to those from the base
simulation. Similarly, if we assumed that the lower OH concentration after the first transect was also
relevant to the time period before the first transect (OH-Low; 9.7×10
5 molecules cm-3
), the model
predictions of OA NEMR and O:C were slightly higher than those from the base simulation. When using
a constant OH concentration of 1.5×10
6 molecules cm-3
(OH-Ambient) or the higher OH concentration
from before the first transect (OH-High; 8.9×10
6 molecules cm-3
) for the entire evolution, the model
predicted a higher OA NEMR compared to predictions from the base, OH-Power Fit, and OH-Low
simulations. This was because the OH concentrations after the first transect in both of these instances
were larger than those used in the base, OH-Power Fit, and OH-low simulations and these higher OH
concentrations, which were ~50% larger in OH-Ambient and a factor of ~10 larger in OH-High, promoted
SOA formation.
For the OH-High simulation, the increase in OA NEMR was found to be relatively consistent
with the evolution in the observations indicating that the OH concentrations may continue to be elevated
even after the first transect. However, the OH-High simulations overestimated the OA NEMR compared
to the observations for the other Fires (Figure S11), where the base, OH-Power Fit, and OH-Low
simulations produced results that were more in line with the observations. As the Taylor Creek Fire
dataset is the most Lagrangian amongst all Fires, the OH sensitivity simulation results presented here
provide some evidence that our OH concentration estimates after the first transect (Table 1) may be biased
low and would need to be revised in future work to be consistent with the higher OH concentrations
estimated in earlier work (see Section 2.2 for a longer discussion). Interestingly, a higher OA NEMR in
the OH-High simulation did not change predictions for OA O:C presumably because the additional SOA
formed had an O:C similar to the existing OA’s O:C. Overall, the model predictions appeared to be
somewhat sensitive to the OH concentration inputs that produced a significant spread in the OA NEMR
and POA-SOA splits but not so much in the OA O:C.”.
We also revised the following paragraph in Section 5: “We acknowledged a significant discrepancy in OH
concentrations in the wildfire plume based on techniques used in this work and OH concentrations
estimated in earlier work. In addition, model predictions were found to be somewhat sensitive to the OH
concentrations assumed in the wildfire plume. Hence, ongoing and future work needs to focus on
developing and applying analytical and modeling techniques to better estimate and evaluate OH
concentrations in wildfire plumes. For instance, recently, Peng et al.
74 calculated HOX (OH + HO2)
production rates in wildfire plumes sampled during WE-CAN from the photolysis of nitrous acid
(HONO), O3
, and other smaller aldehydes (e.g., formaldehyde) and ozonolysis of alkenes. These HOX
production rates could be used to inform OH concentrations. Similarly, OH concentrations could be constrained by applying explicit gas-phase chemical mechanisms to reproduce the time-dependent
evolution of VOCs and their oxidation products in wildfire plumes.”.
17. Line 349: a- or b-pinene? I cannot the first character correctly on my computer.
It should be -pinene. This could likely be a Mac to PC issue but will hopefully be dealt with in the
copy-editing phase.
18. Line 512: y axis label of Fig. 4c needs to be “normalized” or “relative” OA composition. There
is the same issue in other relevant figures.
The y-axis label has now been changed to ‘Normalized OA Composition’ for Figures 4 and 5.
19. Line 719: the legend is not clear. For example, what does “Post-1st transect” really refer to?
Also, (c,f,i) are not properly referred to in the caption.
We are sorry about the confusing legend in Figure 7 and for not using consistent legends in Figures 7 and
11. This was likely an issue with version control. The legends are now consistent in the updated
manuscript (see below).
Reviewer #2
Comments to the Author
This manuscript investigates the evolution of primary and secondary organic aerosol (POA/SOA) in
wildfire plumes by integrating results from field observations, laboratory experiments, and model
simulations. Results showed that the rapid SOA formation from photochemical oxidation of volatile and
semi-volatile organic compounds (VOC/SVOC) could compensate the aerosol mass loss due to
evaporation of POA in the wildfire plumes during transport. The mass loading of aerosol remained
similar over the course of the evolution, while its physicochemical properties altered significantly with
SOA contributing to >30% of total aerosol concentration a few hours after emissions. Based on
laboratory-normalized and reactivity-dif erentiated VOC decay, the authors reported significantly lower
OH concentrations after the first hour of the plume evolution, as compared to those observed in the
literature. Several insightful implications and directions were provided in the manuscript. Overall, this is
a comprehensive study regarding aerosol evolution in wildfire plumes. The manuscript is well written, and
the results are quite interesting and valuable to the literature. I would like to recommend its publication in
Environmental Science: Atmospheres, subject to minor revisions:
We thank the reviewer for making the time to read through our paper as well as the positive comments.
1. Lines 188-189: The O-to-C and H-to-C ratios were calculated by assuming that OA was only
composed of C, H, and O. However, wildfires also emit a significant amount of reactive nitrogen species
that can contribute to the production of nitrogen-containing organic species. Please discuss how the
presence of nitrogen-containing organic species will af ect the estimation of O-to-C and H-to-C ratios in
this study.
[Response similar but not identical to that made for reviewer 1, #9] We thank the reviewer for this
comment. We would like to respond to this comment by first stating the assumptions made in calculating
the OA mass concentrations and elemental ratios, some of which are used as inputs to the SOM-TOMAS
model as well as used to evaluate model predictions. NO
+ and NO2
+
fragments in the HR-AMS, regardless
of its origin (i.e., organic or inorganic), are classified as inorganic nitrate. Hence, the oxygen-to-carbon
(O:C) ratios estimated from the HR-AMS data are expected to be slightly lower than reality in the
presence of organic nitrates (Aiken et al., 2008) since the elemental ratio calculation only includes oxygen
atoms in carbon-containing ions. Similarly, the hydrogen-to-carbon ratio is calculated only from ions that
contain carbon. This is consistent with how HR-AMS data have been analyzed in the past and used to
report O:C and H:C ratios in the literature (Aiken et al., 2007, 2008; Canagaratna et al., 2015). The
nitrogen-to-oxygen (N:C) ratios were ~0.020 +/- 0.005 in the Bear Trap and South Sugarloaf Fires, which
are consistent with historical N:C ratios reported for wildfire OA (Aiken et al., 2007, 2008; Sun et al.,
2011; Kim et al., 2017). While N:C ratios were not quantified for the other Fires, we do not expect the
N:C ratios to be very different between Fires. We should note that since the N:C calculation excludes the
NO and NO2 fragments arising from organic compounds, the reported N:C ratio is also likely to be biased
low.
Since the N:C ratios measured during WE-CAN were quite small (~0.02), these are unlikely to have any
significant influence on the reported O:C and H:C ratios. We illustrate this by calculating the O:C and
H:C ratios for the Taylor Creek Fire with and without accounting for nitrogen, i.e., assuming OA is
entirely composed of organic compounds containing C, H, and O or assuming OA is entirely composed of
organic compounds containing C, H, O, and N. If the N:C ratio of the OA was similar between the plume
and the background (say, 0.02), accounting for nitrogen did not change the background-corrected O:C
ratio at the first transect where OA mass concentrations were larger than 300 µg m-3
. Accounting for nitrogen seemed to affect the background-corrected O:C ratios at subsequent transects where OA mass
concentrations were lower but the change was less than 1% even for the last transect (OA~30 µg m-3
).
We have added the following text to Section 2.1: “While wildfire OA is likely to be composed of
nitrogen-containing organic compounds, the low N:C values measured during WE-CAN (~0.02)
(Garofalo et al., 2019) meant that accounting for nitrogen had a negligible impact on the reported OA
mass concentrations and O:C and H:C values.”.
2. Line 207: The term “average VOC NEMRs” is confusing. Until reading the next few paragraphs
of the manuscript, I figured out that it means the average NEMR for each VOC, not an average value for
all the VOCs. Please be clear in the manuscript.
We agree with the reviewer. Two instances of ‘average VOC NEMRs’ were replaced with ‘average values
of the VOC NEMRs’.
3. Lines 223-224: Using the average NEMR values for VOCs emitted from lab-generated burns can
have huge uncertainties, which depends strongly on factors such as fuel type and burning condition in lab
fires and field fires. As the authors also mentioned in the later part of the manuscript, there could be
systematic kOH-dependent dif erences in emissions between the lab and field studies.
We agree with the reviewer that there are large uncertainties in using average values of VOC NEMRs
given that there may be systematic differences between the laboratory experiments and WE-CAN Fires.
But the average values of the VOC NEMRs from the laboratory experiments were uniquely used to only
inform OH concentrations between the point of emission and the first transect. The use of the average
values of the VOC NEMRs from the laboratory experiments to estimate OH concentrations after the first
transect produced results that were similar to those from the use of VOC NEMRs at the first transect,
highlighting, that despite the uncertainty, there was value in using averaged information from laboratory
experiments. Those results have been described in Section 2.2: “We also calculated OH concentrations
beyond the first transect by using the VOC NEMRs at the first transect as the reference instead of using
the VOC NEMRs from the laboratory. The concentrations so calculated and limited to the time period
beyond the first transect were found to be only slightly higher to those listed in Table 1 (0.67×10
6
-1.2×10
6
molecules cm-3
) but still lower than those in historical studies mentioned earlier. The VOC NEMRs at the
first transect, by definition, cannot be used to determine the OH concentrations prior to the first transect.”.
4. Do the authors have any information regarding tree species (e.g., family and type) at the wildfire
sites? How are these species similar to the ones used in the lab burning experiments? Instead of using the
average VOC NEMR values, what if the authors use fuel-specific VOC NEMR values? How do these
values change with burning conditions (e.g., flaming and smoldering)? Please discuss.
The dominant fuels for each wildfire are tabulated in Table 1 in Lindaas et al. (2021a) and cross
referenced in our manuscript in Section 2.1: “The location and dominant fuel(s) for each wildfire can be
found in Table 1 of Lindaas et al. (2021b)”. There was significant overlap in the fuels that burned during
WE-CAN (Lindaas et al., 2021b) and the laboratory experiments (Koss et al., 2018) performed during
FIREX since both studies were focused on fuels found in the Western United States. The primary
difference was that while only a single fuel was used for a given emissions experiment in the laboratory
campaign (for most experiments performed), the emissions sampled during WE-CAN were from the
combustion of a mixture of fuels. For instance, the Taylor Creek Fire involved emissions from the
combustion of douglas fir, jeffrey pine, ponderosa pine, tanoak, black oak, and madrone, with little information on the proportion in which these fuels burned. This made it non-trivial to use fuel-specific
VOC NEMRs to estimate OH concentrations (Figures 1 and 2 and Table 1) or assess differences in the
VOC composition between the laboratory experiments and WE-CAN (Figure 3). We have added the
following sentence to justify our choice in Section 2.2: “We decided to use the average VOC NEMR
across the 58 burns instead of using fuel-specific VOC NEMRs because the wildfire emissions sampled
during WE-CAN arose from the combustion of a mixture of fuel types.”.
VOC NEMRs are understood to vary with burn conditions (e.g., flaming, smoldering). The average value
for the laboratory-based VOC NEMR was calculated from experiments where the average modified
combustion efficiency (MCE), a proxy for burn conditions, mostly varied between 0.90 and 0.96
(Sekimoto et al., 2018). The MCE during the WE-CAN Fires varied between 0.87 and 0.92 (Lindaas et
al., 2021a) that indicated relatively higher smoldering conditions compared to the laboratory experiments.
We did not account for differences in the MCEs between the laboratory experiments and WE-CAN Fires
and acknowledge this limitation through this addition to Section 2.2: “Furthermore, we also did not
consider differences in the burn conditions (e.g., differences in the modified combustion efficiency)
between the laboratory experiments and wildfire plumes.”.
5. Lines 246-256: OH concentration was observed to be around six times higher before the first
transect compared to that after the first transect, leading to much faster SOA formation before the first
transect. Are there any clues about how much OVOC is primary and how much is secondary? If VOC
chemistry occurred so quickly and contributed significantly to SOA formation, should OVOC be excluded
in the plots in Figure 1, although I understand that this will lead to even lower OH concentrations
estimated for the period after the first transect?
[Response similar but not identical to that made for reviewer 1, #3] The SOM-TOMAS model used in
this work is not a mechanistic model and the SAPRC chemical mechanism coupled to SOM-TOMAS (He
et al., 2020) is not detailed enough to explicitly track a vast majority of the OVOCs considered in this
work. Thus, it was not possible to simulate the gas-phase oxidation chemistry that would have allowed us
to answer the reviewer’s specific question: what are the proportions of primary and secondary OVOCs
and, further, how do these proportions evolve with time and vary by species? There is limited evidence in
the literature on this point. For instance, Coggon et al. (2019) have found that in laboratory experiments
performed on biomass burning smoke, there was little to no production of phenol or furan for
photochemical exposures under a day, with abundant primary emissions for both species. Assuming this is
the case for the majority of oxygenated VOCs measured by the PTR-ToF-MS (i.e., primary emissions of
oxygenated VOCs are significantly larger than those produced through secondary reactions), the
assumptions made in our work towards estimating OH seem reasonable. We have added the following
sentence to share this finding in Section 2.2: “Although there is limited evidence, Coggon et al. (2019)
have found little to no production of reactive oxygenated VOCs such as phenol and furan in laboratory
experiments performed on biomass burning smoke that exceeded the primary emissions for the same
species.”.
As the reviewer points out, there are two approaches to dealing with OVOCs. One is to exclude the
OVOCs in calculating the OH concentrations, which is something we have already done and reported on:
“Since the OH estimates were developed based on the observed decay of all species including reactive
oxygenated VOCs, any chemical production of oxygenated species should bias our OH estimate lower.
Hence, based on the inclusion of the reactive oxygenated VOCs alone, our OH estimates potentially
present a lower bound estimate. When OH was calculated from hydrocarbon VOCs measured by the
PTR-ToF-MS to eliminate the influence from including oxygenated VOCs, the inverse relationship was
weakened and produced OH concentrations that were at least a factor of 2 lower than those listed in Table
1, both before and after the first transect.”. The other approach would be to run an explicit gas-phase chemical mechanism (e.g., Master Chemical Mechanism (MCM) (Jenkin et al., 2003; Saunders et al.,
2003), Generator of Explicit Chemistry and Kinetics of Organics in the Atmosphere (GECKO) (Aumont
et al., 2005) to simulate the oxidation chemistry in the wildfire plume and determine OH concentration
profiles that matched the time-dependent evolution of both VOCs and their oxidation products. Clearly,
such a task would require significant development of the gas-phase chemical mechanism, especially to
represent oxidation chemistry of oxygenated aromatics and heterocyclic compounds, VOC classes that
remain poorly characterized. To that second point, we have revised the OH-related text in Section 5: “We
acknowledged a significant discrepancy in OH concentrations in the wildfire plume based on techniques
used in this work and OH concentrations estimated in earlier work. In addition, model predictions were
found to be somewhat sensitive to the OH concentrations assumed in the wildfire plume. Hence, ongoing
and future work needs to focus on developing and applying analytical and modeling techniques to better
estimate and evaluate OH concentrations in wildfire plumes. For instance, recently, Peng et al.
74
calculated HOX (OH + HO2) production rates in wildfire plumes sampled during WE-CAN from the
photolysis of nitrous acid (HONO), O3
, and other smaller aldehydes (e.g., formaldehyde) and ozonolysis
of alkenes. These HOX production rates could be used to inform OH concentrations. Similarly, OH
concentrations could be constrained by applying explicit gas-phase chemical mechanisms to reproduce
the time-dependent evolution of VOCs and their oxidation products in wildfire plumes.”.
6. Compared to the literature values, the OH concentrations after the first transect estimated in this
study are significantly lower. I agree with the authors that using a large number of VOC species to
calculate OH concentration improves its accuracy. However, except for the approach provided in the
manuscript, have the authors tried any other methods? For example, OH concentration may also be
obtained by examining the relationship between ln(VOC NEMR_field / VOC
NEMR_lab) and k_OH*t for each VOC. The slope of the relationship yields an
ef ective OH concentration. A mean OH concentration (after the first transect) can be obtained by
average the values obtained for all the VOCs at a specific site. How will this OH concentration be
dif erent from the one estimated in the manuscript?
This reviewer makes a good point. We did consider the method presented by the reviewer but it has one
major limitation. It assumes that the VOC NEMR in the laboratory and the VOC NEMR in the field are
identical at t=0 or that the VOC emissions are the same between the laboratory and field. Hence, any
emissions differences between the laboratory and field (at t=0) would erroneously lead to a negative or
positive OH that is not linked to the decay of the VOC in the field. To estimate OH after the first transect,
there isn’t a significant advantage in using the VOC NEMR from the laboratory to normalize the VOC
NEMR from the field. Rather one can calculate OH concentrations after the first transect simply by
normalizing the VOC NEMR at a given transect with the VOC NEMR at the first transect. We performed
this calculation and the OH estimates derived from this approach were similar to the basecase approach
outlined in Section 2.2: “We also calculated OH concentrations beyond the first transect by using the
VOC NEMRs at the first transect as the reference instead of using the VOC NEMRs from the laboratory.
The concentrations so calculated and limited to the time period beyond the first transect were found to be
only slightly higher to those listed in Table 1 (6.7×10
5
-1.2×10
6 molecules cm-3
) but still lower than those
in historical studies mentioned earlier. The VOC NEMRs at the first transect, by definition, cannot be
used to determine the OH concentrations prior to the first transect.”.
7. Line 256: “the first transect was estimated between 21 and 56 minutes of the physical age of the
wildfire plume.” Please add this information to the caption of Figure S1 regarding the calculation of
sampling time to show that this time is not long so that it does not af ect the conclusion about Lagrangian
sampling.
Thank you for pointing this out. To provide a more appropriate comparison, the sampling time in Figure
S1 was offset by the physical age of the first transect. The revised figure is shown below along with the
updated caption.
Figure S1: Physical age plotted against the sampling time for the five transect sets and four wildfire
plumes. Physical age was calculated by dividing the straight-line distance from the fire with the average
wind speed measured within a transect. Sampling time was calculated as the time of the day minus the
time when the first transect was sampled but of set by the physical age at the first transect.
8. Lines 540-543: The word slight seems inappropriate. It seems to the reviewer that OA NEMR was
significantly underestimated (by ~15%). What about revising the sentence to the following: The base
simulation that assumed a semivolatile POA and oxidation chemistry for both SVOCs and VOCs
(SV-POA+FullChem) underestimated the OA NEMR by around 15% compared to observations...
We agree that the word ‘slight’ is not justified and have revised the sentence as follows in Section 3.1:
“The base simulation that assumed a semivolatile POA and oxidation chemistry for both SVOCs and
VOCs (SV-POA+FullChem) underestimated the OA NEMR by 15% compared to observations
(MBE=-0.024, MAE=0.024; µg m-3 ppbv
-1
) but produced a large increase in OA O:C consistent with the
observations (MBE=-0.019, MAE=0.032; µg m-3 ppbv
-1
).”.
9. Lines 608-610: It does not seem that the contribution of VOCs to SOA was identical among
dif erent transect sets, except for the results between Sharps and Bear Trap 1. The results cannot lead to
the conclusion that VOC composition was uniform across fires. I suggest rewriting or removing this
sentence.
We agree with the reviewer. The sentence was revised as follows in Section 3.1: “The contribution of the
different VOC classes to SOA formation was similar between the different transect sets, although
oxygenated aromatics contributed much more to SOA formation in the Silver Creek Fire than in the other
Fires.”.
10. Figure 6: Results of Monte Carlo simulations are missing.
The results of the Monte Carlo simulations are in the rightmost column of Figure 6. The figure caption
was incorrect but has now been updated as follows: ‘Model predictions are shown for sensitivity
simulations performed with varying assumptions for the (a,d,g) SVOC oxidation chemistry, (b,e,h) POA
volatility and SVOC oxidation chemistry, and (c,f,i) POA+SVOC mass distribution in the SOM grid
(Monte Carlo).’
11. Lines 687-689: The reviewer is confused. Are the base simulation results presented in Figures 4
and 5 based on the volatility distribution observed by May et al. or based on the optimal results from the
Monte Carlo simulation? Please clarify.
The base simulations always assume a mass distribution of POA+SVOC emissions in the SOM grid that
is consistent with the volatility distribution of May et al. (2013). This is mentioned early in Section 2.5:
“... we fit a mass distribution for eight model species in the SOM grid that was able to reproduce the
average volatility behavior observed by May et al. (2013) for POA emissions (Figure S3a).”. The eight
model species in the SOM grid that were used to distribute the POA+SVOC mass, were determined from
the results of the Monte-Carlo simulations presented in Figure 6(c,f,i). In other words, the Monte-Carlo
simulation results were used to identify the eight model species in the SOM grid that were then used to
distribute the POA+SVOC mass. This aspect has been alluded to in Section 2.5: “The following species
were used to represent the POA/SVOC mass in the SOM grid: C5O7
, C9O2
, C9O5
, C11O2
, C12O2
, C12O3
,
C14O5
, and C15O6 (Figure S3c). An explanation for why this precise set of species was used is presented
later when describing results from the sensitivity (Monte-Carlo) simulations (Section 3.2).”.
12. Line 704: The figure legend in Figure 7 is confusing. For example, it took me a while to figure out
that “pre-1st transect” represents “OH-High”. Why not use OH-High, OH-Low, OH-Power fit,
OH-Ambient, just like Figure S11?
We uploaded the wrong Figure 7 before submission. It has now been fixed. See response to reviewer 1,
question 19.
13. Lines 709-711: It seems to the reviewer that “OH-High” provides the best fit, at least for the
Taylor Creek Fire, the most representative Lagrangian dataset. Does it suggest that the OH concentration
after the first transect was underestimated in this study?
[Response similar to that made for reviewer 1, #16] We agree with the reviewer’s assessment of the
OH-High results. We have significantly revised the interpretation of the model-measurement comparisons
for the OH sensitivity simulation results in Section 3.2:
“Results from simulations performed to assess the sensitivity to the OH estimates are presented in
Figure 7(a,d,g). The use of a power function fitted to the OH exposure data to determine OH
concentrations (OH-Power Fit) produced results that were slightly higher compared to those from the base
simulation. Similarly, if we assumed that the lower OH concentration after the first transect was also
relevant to the time period before the first transect (OH-Low; 9.7×10
5 molecules cm-3
), the model
predictions of OA NEMR and O:C were slightly higher than those from the base simulation. When using
a constant OH concentration of 1.5×10
6 molecules cm-3
(OH-Ambient) or the higher OH concentration
from before the first transect (OH-High; 8.9×10
6 molecules cm-3
) for the entire evolution, the model
predicted a higher OA NEMR compared to predictions from the base, OH-Power Fit, and OH-Low
simulations. This was because the OH concentrations after the first transect in both of these instances
were larger than those used in the base, OH-Power Fit, and OH-low simulations and these higher OH concentrations, which were ~50% larger in OH-Ambient and a factor of ~10 larger in OH-High, promoted
SOA formation.
For the OH-High simulation, the increase in OA NEMR was found to be relatively consistent
with the evolution in the observations indicating that the OH concentrations may continue to be elevated
even after the first transect. However, the OH-High simulations overestimated the OA NEMR compared
to the observations for the other Fires (Figure S11), where the base, OH-Power Fit, and OH-Low
simulations produced results that were more in line with the observations. As the Taylor Creek Fire
dataset is the most Lagrangian amongst all Fires, the OH sensitivity simulation results presented here
provide some evidence that our OH concentration estimates after the first transect (Table 1) may be biased
low and would need to be revised in future work to be consistent with the higher OH concentrations
estimated in earlier work (see Section 2.2 for a longer discussion). Interestingly, a higher OA NEMR in
the OH-High simulation did not change predictions for OA O:C presumably because the additional SOA
formed had an O:C similar to the existing OA’s O:C. Overall, the model predictions appeared to be
somewhat sensitive to the OH concentration inputs that produced a significant spread in the OA NEMR
and POA-SOA splits but not so much in the OA O:C.”.
We also revised the following paragraph in Section 5: “We acknowledged a significant discrepancy in OH
concentrations in the wildfire plume based on techniques used in this work and OH concentrations
estimated in earlier work. In addition, model predictions were found to be somewhat sensitive to the OH
concentrations assumed in the wildfire plume. Hence, ongoing and future work needs to focus on
developing and applying analytical and modeling techniques to better estimate and evaluate OH
concentrations in wildfire plumes. For instance, recently, Peng et al.
74 calculated HOX (OH + HO2)
production rates in wildfire plumes sampled during WE-CAN from the photolysis of nitrous acid
(HONO), O3
, and other smaller aldehydes (e.g., formaldehyde) and ozonolysis of alkenes. These HOX
production rates could be used to inform OH concentrations. Similarly, OH concentrations could be
constrained by applying explicit gas-phase chemical mechanisms to reproduce the time-dependent
evolution of VOCs and their oxidation products in wildfire plumes.”.
14. The caption of Figure 1: “Solid red lines represent the linear fit to the data and the red bands
capture the uncertainty in the fit (1).” There are three solid red lines. The bands are missing. I guess that
the first and the last (from up to down) lines give the uncertainty of the fit and the error “1” represents
one sigma deviation?
We apologize that the bands did not translate well to your version of our paper. We do see them on our
end. We will make sure that the bands are visible in the final version of the paper. The bands represent the
standard error: ‘Solid red lines represent the linear fit to the data and the red bands capture the standard
error.’
15. Line 449: Error for “-pinene”.
Some of the ‘α’s did not show up in the PDF version of the submitted paper. Again, this is likely to be a
Mac to PC conversion issue but will hopefully be dealt with during the copy-editing stage.
16. Missing label c in Figure 4, label i to l in Figure 5, label a to i in Figure 7.
The label (c) in Figure 4 was in a different color than the labels (a) and (b). The same is true for labels (i)
to (l) in Figure 5. Therefore no change is needed. We uploaded the wrong Figure 7 before submission. It
has now been fixed. See response to reviewer 1, question 19.

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11-Jun-2022

Dear Dr Jathar:

Manuscript ID: EA-ART-10-2021-000082.R1
TITLE: Dilution and Photooxidation Driven Processes Explain the Evolution of Organic Aerosol in Wildfire Plumes

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Reviewer 1

I think that the authors have adequately addressed all reviewers' comments. I recommend publication of the revised paper.

Reviewer 2

I do truly appreciate the time and effort that the authors put into both revising the manuscript and replying to my comments. The authors have sufficiently addressed my comments, especially for those concerns regarding VOC NEMR values and OH concentration estimation. This is a very interesting and comprehensive study investigating the evolution of organic aerosol in wildfire plumes. I would like to recommend its publication in Environmental Science: Atmospheres.