From the journal Environmental Science: Atmospheres Peer review history

15-Sep-2021

Dear Dr Hayes:

Manuscript ID: EA-ART-07-2021-000053
TITLE: Evaluating SOA formation from different sources of semi- and intermediate-volatility organic compounds from the Athabasca Oil Sands

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Reviewer 1

This study used a box model and evaluated potential sources of secondary organic aerosols (SOA) from the Oil Sands, namely Oil Sands ore, bitumen, and excavated Oil Sands deposits heated at 20 and 60°C, based on their published volatility distributions. Although, given the complexity of the oxidation chemistry of different species, changes in chemical and physical properties that may impact the particle formation, and uncertainties of model inputs, it is not easy to draw a very convincing conclusion that the primary semi- and intermediate-volatility organic compounds (P-S/IVOC) are mainly from active mining and hot-water extraction of the Oil Sands. Nonetheless, this work is interesting, and future studies including more other aspects of SOA formation and evolution can help us to understand Oil sands operations as an important source of SOA. I will recommend the acceptance of the manuscript by Environmental Science: Atmospheres. However, there are some major and minor comments I would like the authors to address.

Major comment:
There are many different parameterizations to estimate logC* from the molecular formula. Many studies have shown that there are big uncertainties between different parameterizations. I wonder, whether using other parameterizations rather than Donahue et al. (2016) will bring differences in numbers of oxygen atoms, molar mass, and further to the final conclusion.

Minor comments:
Figure 2 please also add labels to the x-arises for A, B, and C and the number of carbons for primary VOCs and Primary IVOCs.
Figure 9 please give the unit of the x-axis.
Any subtitle of the figure on Page 44?
Supplement information:
Line 161 “n0 = -11.7”, is it a typo?
Table S3 though it is similar, it is better to use the same temperature, either 297 K (Figure 4) or 300 K.

Reviewer 2

Sommers et al. report on a modeling study that simulates the emissions, formation, and evolution of organic aerosol (OA) in plumes downwind of an oil sands facility(ies). The model is initialized and informed based on ground- and aircraft-based measurements and evaluated against aircraft-based measurements of OA mass concentration and O:C. Although they do not find a single model configuration that best explains the observations, the model provides insight into the aerosol process that might be more important that others.

The manuscript clearly outlines the need to understand the air pollution formation impacts from the Athabasca Oil Sands and hence the work is well motivated. The manuscript is long but generally well-written and easy to follow. The findings follow from the presented results and data analysis. This is high quality modeling work but it was a little disappointing that the model application did not result in more conclusive findings. I have a few major and minor comments (listed below) that the authors should consider before final submission. I generally recommend this paper for publication in ESA.

Major comments:
1. Volatility distributions: Although the volatility distribution of the emissions can have a significant influence on its potential to form SOA, this work over emphasizes the notion that the volatility distribution that best explains the observations is most likely to be the appropriate choice while discounting differences in the composition of the emissions. As the authors probably already know, SOA precursors with the same volatility but differences in composition could result in large differences in the formation rate, magnitude, and volatility of the oxidation products, all of which would drive differences in SOA mass yield and its composition (e.g., O:C). I recommend that the sections that describe both the model inputs and the appropriate outputs be updated with this composition lens in mind. My sense is that the previous work where the volatility distributions have been developed, comment to some degree on the composition of the organic compounds in P-S/IVOCs. Another related note then is, given the differences or lack thereof in composition, does that provide justification that the same scheme be used to model the oxidation chemistry of P-S/IVOCs?
2. Presentation of the OA mass evolution (starting with Figure 5 and elsewhere): Does it make more sense to present the OA evolution as an ‘OA NEMR’ with respect to a tracer (e.g., ideally BC or some other (see minor comment #1)) to show that it may be increasing in the plume with photochemical aging? Without information for the extent of dilution in the plume, it’s hard to internalize where the OA mass is increasing substantially (in case of high dilution) or only marginally (in case of low dilution). It may also become easier to explain the decrease in OA mass concentrations with time (which strangely isn’t accompanied by a change in O:C over the same duration), which I have attributed to dilution from a loss in OA mass loading rather than oxidation chemistry (e.g., fragmentation reactions). I don’t recollect this being discussed specifically in the manuscript. I was also wondering given the similarity in the model predictions across the ensemble of whether the relatively constant observed OA mass and O:C with time pointed to (i) rapid oxidation chemistry before the first transect that slowed down significantly after the first transect, (ii) mostly low-volatility OA by the beginning of the first transect that was resistant to chemical oxidation, (iii) semi-solid/viscous OA by the beginning of the first transect , or (iv) some combination of (i)-(iii). The larger point I am making is that some of these competing hypotheses may need to be stated earlier (in addition to the POA evaporation with dilution is balanced by SOA formation) in the manuscript and then revisited in the conclusions section.
3. Line 458-476: The authors seem to discount the O:C comparison here and elsewhere. If the background O:C is much higher than the plume O:C, simple dilution of the plume OA with background will tend to increase the O:C and ultimately reach the background O:C after the plume OA has diluted sufficiently. The fact that the O:C is flat suggests that there are interesting dynamics (linked to partitioning and oxidation) that the model captures and gets right. This should be discussed when describing the model results of OA O:C.

Minor comments:
1. Line 197: In wildfire plumes, Sedlacek et al. (ACP, 2018) have found evidence for formation of light-absorbing carbon with photochemical evolution. If this process were relevant for emissions from oil sands, BC wouldn’t be a good tracer to use account for dilution. Are there other tracers to use instead of BC and does their use result in the same level of dilution as BC?
2. Table 2: There are issues with reporting of significant figures for the uncertainty. Please fix.
3. Figure 5 and elsewhere: If PMF data are available, can the model results be compared to the factors directly?
4. Figure S5: How is the plume O:C calculated? A simple average won’t work and the O:C will need to be approximately weighted by mass. For a relevant reference that calculates O:C using background-corrected molar concentrations of oxygen and carbon, see Hodshire et al. (2021).
5. Line 489: Mention units for RMSE?
6. Line 514: Can the off-road diesel fleet at the facility be characterized in terms of their emissions? Are the engines equipped with emissions controls and, if yes, what emissions standard do they comply to? If there is heterogeneity in the diesel fleet with age, can this fleet mixture be specified. Answers to these questions might influence the SOA precursor emissions with respect to BC and CO.
7. Line 530: BIT seems like it has the most volatile distribution and not the least volatile as mentioned. Please clarify.
8. Figure 6: Results from which model are presented here?
9. Line 577: My understanding is that WLC yields are only marginally higher in the case of high NOx conditions; see Table 1 in Zhang et al. (PNAS, 2014). Are the modeled trends consistent with Zhang? Also, some detail needs to be provided on how the WLC parameterization was developed. The current version of the paper has little to no information on this aspect.
10. Line 593: ‘based on’ instead of ‘based due’?
11. Line 640: I disagree that particle-phase reactions are slow enough to be discounted in this work. Oligomers in biogenic VOC-SOA systems are formed quite rapidly.
12. No Figure S8(b)??
13. Conclusions: The opening paragraph does not provide any citations for the big claims made here. I should admit that I had to read the paper in more than one sitting and had forgotten most of what was discussed in the introduction.
14. Line 765: One doesn’t necessarily need a multi-layered model to simulated phase-state-influenced gas/particle partitioning. See for example, Zaveri et al. (ES&T, 2020) and He et al. (ES&T, 2021).

Response to Referee 1

General Comment: This study used a box model and evaluated potential sources of secondary organic aerosols (SOA) from the Oil Sands, namely Oil Sands ore, bitumen, and excavated Oil Sands deposits heated at 20 and 60°C, based on their published volatility distributions. Although, given the complexity of the oxidation chemistry of different species, changes in chemical and physical properties that may impact the particle formation, and uncertainties of model inputs, it is not easy to draw a very convincing conclusion that the primary semi- and intermediate-volatility organic compounds (P-S/IVOC) are mainly from active mining and hot-water extraction of the Oil Sands. Nonetheless, this work is interesting, and future studies including more other aspects of SOA formation and evolution can help us to understand Oil sands operations as an important source of SOA. I will recommend the acceptance of the manuscript by Environmental Science: Atmospheres. However, there are some major and minor comments I would like the authors to address.



Response: We would like to thank the reviewer for their thoughtful feedback on the manuscript. We have responded to the comments point-by-point directly below, and we believe that the manuscript is now greatly improved. For clarity, the referee comments and our comments are separated by three line breaks.



Major Comments: There are many different parameterizations to estimate logC* from the molecular formula. Many studies have shown that there are big uncertainties between different parameterizations. I wonder, whether using other parameterizations rather than Donahue et al. (2016) will bring differences in numbers of oxygen atoms, molar mass, and further to the final conclusion.



Response: In the box model, the Donahue et al. parameterization is used to estimate the O/C and molecular weight (MW) from C*. The reviewer is correct that this parameterization does introduce uncertainty into our study, but we do not think this substantially impacts the OA model results. Specifically, the sensitivity of the model to estimated MW is explored in the sensitivities studies of the fragmentation parameterization, and it is found that the model is relatively insensitive to the modeled MW compared to other inputs. Furthermore, the O/C is a diagnostic output of the box model, and we have compared O/C from the model against measurements of O/C. The model and measurements are consistent, which indicates that the Donahue et al. parameterization can reproduce observed O/C.

We have added the following text to the final paragraph of section 3.3.3:
“Additionally, this sensitivity study indicates that the model is relatively insensitive to the uncertainty in the calculated molecular weight, which is obtained by the parameterization of Donahue et al. (2011).”



Minor Comments:
Figure 2 please also add labels to the x-axes for A, B, and C and the number of carbons for primary VOCs and Primary IVOCs.



Response: We have added the x-axis labels as requested. As for the number of carbons for primary species in A, B, and C, the initial oxidation step is not affected by the initial carbon number of the VOC and IVOC species. However, all the VOCs used in the model are identified in table S2, where one can determine the carbon number if needed. We have added the following to the caption in Figure 2:
“The carbon numbers for primary VOCs and IVOCs in (A), (B), and (C) are not included as they have no impact in the model.”



Figure 9 please give the unit of the x-axis.



Response: This has been done



Any subtitle of the figure on Page 44?



Response: It is not clear to us which figure the reviewer is referring to. However, we have checked the captions for all the figures and all the captions are placed below the figure. We will attempt to confirm this during every proofing phase.



Supplement information:
Line 161 “n0 = -11.7”, is it a typo?



Response: If this is referring to the formatting issue where the solved nO is placed in line 161 instead of 162, we have worked to ensure this conversion error in formatting does not carry over in the next draft.
If this is referring to the strikethrough of -11.7, This is not a typo, it is the mathematically accurate solution to the quadratic equation in line 159, though it is disregarded for being negative, which we denote by using strikethrough text.



Table S3 though it is similar, it is better to use the same temperature, either 297 K (Figure 4) or 300 K.



Response: We thank the referee for spotting this error. The calculations were done using 298K (as in Figure 4), and Table S3 has been corrected to account for this.


 
Response to Referee 2

General Comment: Sommers et al. report on a modeling study that simulates the emissions, formation, and evolution of organic aerosol (OA) in plumes downwind of an oil sands facility(ies). The model is initialized and informed based on ground- and aircraft-based measurements and evaluated against aircraft-based measurements of OA mass concentration and O:C. Although they do not find a single model configuration that best explains the observations, the model provides insight into the aerosol process that might be more important that others. The manuscript clearly outlines the need to understand the air pollution formation impacts from the Athabasca Oil Sands and hence the work is well motivated. The manuscript is long but generally well-written and easy to follow. The findings follow from the presented results and data analysis. This is high quality modeling work but it was a little disappointing that the model application did not result in more conclusive findings. I have a few major and minor comments (listed below) that the authors should consider before final submission. I generally recommend this paper for publication in ESA.



Response: We would like to thank the reviewer for their very useful comments on the manuscript. We have responded to the comments point-by-point directly below, and we believe that the manuscript is now improved as a result. For clarity, the referee comments and our comments are separated by three line breaks.



Major Comments:
1. Volatility distributions: Although the volatility distribution of the emissions can have a significant influence on its potential to form SOA, this work over emphasizes the notion that the volatility distribution that best explains the observations is most likely to be the appropriate choice while discounting differences in the composition of the emissions. As the authors probably already know, SOA precursors with the same volatility but differences in composition could result in large differences in the formation rate, magnitude, and volatility of the oxidation products, all of which would drive differences in SOA mass yield and its composition (e.g., O:C). I recommend that the sections that describe both the model inputs and the appropriate outputs be updated with this composition lens in mind. My sense is that the previous work where the volatility distributions have been developed, comment to some degree on the composition of the organic compounds in P-S/IVOCs. Another related note then is, given the differences or lack thereof in composition, does that provide justification that the same scheme be used to model the oxidation chemistry of P-S/IVOCs?



Response: The model setup does take into account a certain level of compositional heterogeneity by treating SOA from VOCs, IVOCs and SVOCs using different VBS schemes. In addition, the VOCs are almost fully speciated. To some extent, the impact of composition differences is explored in the manuscript through the inclusion of a composition dependent P-S/IVOC aging rate coefficient. Nonetheless, we agree that caution must be used when evaluating different volatility distributions because the performance of a given distribution depends also on the composition of SOA and its precursors. We have added the following paragraph to the end of section 2.5.2:
“Generally, in this work, we use a VBS to explore the oxidation and partitioning of P-S/IVOC species from the Oil Sands. This has both inherent advantages and disadvantages. As an advantage, we have documented volatilities of P-S/IVOCs from Oil Sands sources available in previous literature.1,2 Additionally, a VBS approach can be simplified and portions of this model can be incorporated into chemical transport models in future work. As a disadvantage, a VBS approach has limited chemical detail, which may be better described by a more chemically speciated SOA model. However, there is a lack of detailed speciation of P-S/IVOCs from the Oil Sands currently available in the literature to facilitate a more complex approach. The VBS approach has been successfully developed for urban sources. For the Oil Sands, the VK diagram (Figure S3A) has a slope similar to urban settings, as previously stated in section 2.4, which suggests that the VBS approach can also be successfully applied to modeling Oil Sands SOA.”



2. Presentation of the OA mass evolution (starting with Figure 5 and elsewhere): Does it make more sense to present the OA evolution as an ‘OA NEMR’ with respect to a tracer (e.g., ideally BC or some other (see minor comment #1)) to show that it may be increasing in the plume with photochemical aging? Without information for the extent of dilution in the plume, it’s hard to internalize where the OA mass is increasing substantially (in case of high dilution) or only marginally (in case of low dilution). It may also become easier to explain the decrease in OA mass concentrations with time (which strangely isn’t accompanied by a change in O:C over the same duration), which I have attributed to dilution from a loss in OA mass loading rather than oxidation chemistry (e.g., fragmentation reactions). I don’t recollect this being discussed specifically in the manuscript. I was also wondering given the similarity in the model predictions across the ensemble of whether the relatively constant observed OA mass and O:C with time pointed to (i) rapid oxidation chemistry before the first transect that slowed down significantly after the first transect, (ii) mostly low-volatility OA by the beginning of the first transect that was resistant to chemical oxidation, (iii) semi-solid/viscous OA by the beginning of the first transect , or (iv) some combination of (i)-(iii). The larger point I am making is that some of these competing hypotheses may need to be stated earlier (in addition to the POA evaporation with dilution is balanced by SOA formation) in the manuscript and then revisited in the conclusions section.



Response: Prior work (Liggio et al. 2016) showed that BC decreases rapidly between the 1st and final transect. Thus, the fact that OA is not rapidly decreasing to background levels shows that there must be rapid SOA production that is countering dilution. To illustrate this point the OA/BC ratio is plotted in Figure 1 in the submitted version of the manuscript, where the reader can clearly see increases in OA/BC with photochemical age. (Note that age increases with each transect.) Additionally, we have added OA/BC ensemble plots into the SI, and are referred to in the text (Figure S5 in the revised text).

We have added the following to the main text at the end of the first paragraph of section 3.1:
“Additionally, Figure S5 details OA normalized to background-subtracted BC to demonstrate the continued formation of SOA during a photochemical day, once the impact of dilution is accounted for.”

Regarding (i), yes, there is indeed rapid formation of SOA before the first transect but it continues after the first transect. This is demonstrated in the plots of modeled OA versus photochemical age, in Figures 6, 7, and 9 - as well as the current Figure S9 (Figure S7 in the previous draft). For additional clarity to this point, and to follow up on the referee’s 3rd major comment below, we have expanded on the growth and evolution of O:C and OA as the plume ages. We have added Figure S7 to the supplemental information (while other figure numbers have been adapted to account for this change) to show how O:C from the different components of OA contribute to the total modelled O:C.

We have split the final paragraph of section 3.1 into two paragraphs, as below:
“The variation of the O:C and H:C ratios inside and outside the plume is demonstrated in Figure S3 (B). Within the plume, the H:C ratio is higher than the out-of-plume background, while the O:C is lower within the plume than in the background. This pattern occurs as fresh, less oxidized, Oil Sands SOA is mixed with the more aged background SOA. In Figure S6, the ensemble model particle-phase O:C are plotted versus measurements taken within the plumes. Generally, the 20D volatility distribution exhibits the largest variation in O:C versus photochemical age within the ensemble, followed by the 60D volatility distribution. The larger range of predicted O:C in the 20D and 60D volatility distributions relative to ORE and BIT is caused by the larger concentrations of I-SOA and S-SOA. The low O:C ratios of POA, S-SOA, and less aged I-SOA, which are more prevalent in the model ensembles using the 20D and 60D volatility distributions, drive the lower average O:C versus the model ensembles using the ORE and BIT distributions. In most cases, the 50th percentiles of the ensembles lie within the measurement uncertainty, except at short photochemical ages for the model ensembles using the ORE and BIT distributions in Flight 19.

In Figure S7, the components which constitute the combined O:C ratio are described for the base case study (AGE + SLOW + 1P + F_ON + FIXED) with the 60D and BIT volatility distributions. In both cases, the high O:C background is mixed with the rapid formation V-SOA, which also has a high O:C. While the O:C ratio of POA, S-SOA, and I-SOA is very low at short photochemical ages, the concentration of those combined sources is also very low. In the 60D case, the POA + S-SOA + I-SOA fraction becomes more important as an OA source at longer photochemical ages, but this is coupled with the increased O:C ratio of the POA + S-SOA + I-SOA source. Meanwhile, in the BIT case, the POA + S-SOA + I-SOA fraction is never the dominant source of OA. As a result, the combined O:C ratio stays relatively flat for both the 60D and BIT cases (and the same pattern holds for 20D and ORE), and within the measurement uncertainty of reported O:C ratios. Therefore, while O:C predictions are not a very useful diagnostic for evaluating model parameterizations, they are still useful for developing other aspects of the model parameterizations. The largely accurate O:C ratio from the model adds confidence to our ability to use modelled O:C compared to measured background O:C to drive two-phase partitioning when applying the two-phase partitioning (2P) parameterization. The modelled O:C is also used in calculating the VAR multi-generational aging rate constant for S/IVOCs.”



3. Line 458-476: The authors seem to discount the O:C comparison here and elsewhere. If the background O:C is much higher than the plume O:C, simple dilution of the plume OA with background will tend to increase the O:C and ultimately reach the background O:C after the plume OA has diluted sufficiently. The fact that the O:C is flat suggests that there are interesting dynamics (linked to partitioning and oxidation) that the model captures and gets right. This should be discussed when describing the model results of OA O:C.



Response: We have addressed this comment in response to the previous comment.



Minor Comments:
1. Line 197: In wildfire plumes, Sedlacek et al. (ACP, 2018) have found evidence for formation of light-absorbing carbon with photochemical evolution. If this process were relevant for emissions from oil sands, BC wouldn’t be a good tracer to use account for dilution. Are there other tracers to use instead of BC and does their use result in the same level of dilution as BC?



Response: In previous work (Liggio et al. 2016), we noted that CO, which is often used as a dilution tracer, is a poor tracer in the Oil Sands, as the enhancement over the background is very small. Furthermore, Tokarek et al. (2018) demonstrated from Principal Component Analysis that total sulfur and individual VOCs are poorly correlated with some of the primary sources of IVOCs and lightly oxidized OA from the Oil Sands. For these reasons, we do not believe there is a more appropriate tracer for the Oil Sands than BC.
In the first paragraph of section 2.5.1, we have added the following sentences:
“In both flights, the enhancement and dilution of BC within the Oil Sands plume compared to the background concentration is demonstrated in Figure S2 (C, D). In this work, we assume the formation of light-absorbing carbon will not interfere with SP2 measurements of black carbon.”

Additionally, we added two graphs to Figure S2, demonstrating the temporal evolution of BC in Flights 19 and 20.



2. Table 2: There are issues with reporting of significant figures for the uncertainty. Please fix.



Response: We have updated the table and have fixed the significant figures in Table 2.



3. Figure 5 and elsewhere: If PMF data are available, can the model results be compared to the factors directly?



Response: PMF was done on one flight, from which two factors were obtained: the in-plume and out-of-plume factors (as described in Liggio et al. (2016)). For this work we are analysing two flights, so instead of using the PMF results, we are using the directly measured of OA inside and outside of the plume to separate the regional background from the Oil Sands emissions. We have added the following sentence to the last paragraph of section 2.2:
“In this previous work, the PMF separation was limited to in-plume and out-of-plume OA factors. We do not use them as a diagnostic for model performance since the PMF results do not provide any additional information about OA components within the plume.”



4. Figure S5: How is the plume O:C calculated? A simple average won’t work and the O:C will need to be approximately weighted by mass. For a relevant reference that calculates O:C using background-corrected molar concentrations of oxygen and carbon, see Hodshire et al. (2021).



Response: The modeled plume O:C is weighted by mass. The model extracts the number of oxygen atoms and number of carbon atoms from each OA component, then O:C is calculated from the total oxygen and total carbon atomic ratio. We have added the following sentence to the caption of Figure S5:
“The O:C is modeled using the total number of oxygen and carbon atoms for each component.”



5. Line 489: Mention units for RMSE?



Response: The units of RMSE (µg m-3) have been added to all descriptions of RMSE.



6. Line 514: Can the off-road diesel fleet at the facility be characterized in terms of their emissions? Are the engines equipped with emissions controls and, if yes, what emissions standard do they comply to? If there is heterogeneity in the diesel fleet with age, can this fleet mixture be specified. Answers to these questions might influence the SOA precursor emissions with respect to BC and CO.



Response: There are a few studies of the emissions from the diesel fleet at the Oil Sands facilities. The engines are designed to meet the EPA standard for off-road vehicles, which have also been adopted for Canada.(a) The fleet in 2013 was a mixture of Tier 1 - 4 vehicles. BC emissions for the vehicle fleet have only been measured for Tier 1 vehicles (b), and no tier specific emissions are available.

a) Evaluation of Vehicle Emission Reduction Options for the Oil Sands Mining Fleet, https://www.mjbradley.com/reports/evaluation-vehicle-emissions-reduction-options-oil-sands-mining-fleet, (Accessed October 15, 2021).

b) Characterization of Real-World Emissions from Nonroad Mining Trucks in the Athabasca Oil Sands Region during September, 2009, https://wbea.org/wp-content/uploads/2018/03/watson_j_g_et_al_2013_characterization_of_real_world_emissions_from_nonroad_mining_trucks_in_the_athabasca_oil_sands_region_during_september_2009.pdf, (Accessed October 15, 2021).



7. Line 530: BIT seems like it has the most volatile distribution and not the least volatile as mentioned. Please clarify.



Response: BIT has a slightly larger log(c*) = 5 volatility bin mass fraction than ORE, which make up the Li et al. (2019) volatility distributions. We have removed most of this sentence as it adds unnecessary confusion. We have changed the sentence to be clearer:
“Both BIT and ORE volatility distributions, from Li et al. (2019), are much more skewed to the highly volatile range than the samples measured in Liggio et al. (2016), as described in Figure 4.”



8. Figure 6: Results from which model are presented here?



Response: The following text has been added to the caption of Figure 6:
“Each figure uses the base case study (AGE + SLOW + 1P + F_ON + FIXED parameterizations)”



9. Line 577: My understanding is that WLC yields are only marginally higher in the case of high NOx conditions; see Table 1 in Zhang et al. (PNAS, 2014). Are the modeled trends consistent with Zhang? Also, some detail needs to be provided on how the WLC parameterization was developed. The current version of the paper has little to no information on this aspect.



Response: Yes, the omission of the description of how the WLC parameterization was developed was a mistake. We now direct the reader to our detailed publication on this topic with the following text that replaces the second sentence of section 3.3.1.
“To evaluate the possible errors in SOA yields resulting from gas-phase SVOC losses, we have developed a SOA model parameterization, WLC, that accounts for such losses in Ma et al. 2017, (32) which is incorporated into our current box model. In the box model, the WLC parameterization results in an increase in both anthropogenic and biogenic SOA sources of VOCs (V-SOA) at short photochemical ages as shown in Figure 7 (B).”
Where 32 is the following reference:
32 P. K. Ma, Y. Zhao, A. L. Robinson, D. R. Worton, A. H. Goldstein, A. M. Ortega, J. L. Jimenez, P. Zotter, A. S. H. Prévôt, S. Szidat and P. L. Hayes, Evaluating the impact of new observational constraints on P-S/IVOC emissions, multi-generation oxidation, and chamber wall losses on SOA modeling for Los Angeles, CA, Atmos. Chem. Phys., 2017, 17, 9237–9259.

Also, another sentence has been added to the manuscript in the second paragraph of Section 3.1.1 to compare against the results of Zhang et al. 2014
“When comparing the AGE and WLC parameterizations, at short photochemical ages an increase in SOA concentrations of up to 50% is observed for WLC, which is consistent with the average biases of SOA yields from chamber experiments reported by Zhang et al. (2014) (63)”.
Where 63 is the following reference:
63 X. Zhang, C. D. Cappa, S. H. Jathar, R. C. McVay, J. J. Ensberg, M. J. Kleeman, J. H. Seinfeld and Christopher D. Cappa, Influence of vapor wall loss in laboratory chambers on yields of secondary organic aerosol., Proc. Natl. Acad. Sci. U. S. A., 2014, 111, 1–6.



10. Line 593: ‘based on’ instead of ‘based due’?



Response: This has been corrected.



11. Line 640: I disagree that particle-phase reactions are slow enough to be discounted in this work. Oligomers in biogenic VOC-SOA systems are formed quite rapidly.



Response: The first paragraph in section 3.3.3 has been changed to include the following:
“Only gas-phase oxidation reactions are considered in this work, as particle-phase and heterogeneous reactions are not included in this model. We do not explicitly include oligomerization in the model. However, as oligomerization increases carbon number, in a sensitivity study we conceptually added oligomerization as a counterbalance to the fragmentation effects in the model.”



12. No Figure S8(b)??



Response: This has been corrected, as this refers to Figure 8(b) in the main text.



13. Conclusions: The opening paragraph does not provide any citations for the big claims made here. I should admit that I had to read the paper in more than one sitting and had forgotten most of what was discussed in the introduction.



Response: We thank you for alerting us to this error. Citations, which were previously used in this paper, have been added to this paragraph to support the text.



14. Line 765: One doesn’t necessarily need a multi-layered model to simulated phase-state-influenced gas/particle partitioning. See for example, Zaveri et al. (ES&T, 2020) and He et al. (ES&T, 2021).



Response: We thank the reviewer for drawing our attention to these articles. We have updated the final paragraph of the conclusions to account for this additional work:

“Generally, the model predicts rapid formation of SOA, followed by a relatively rapid decline in OA concentrations, driven by dilution and evaporation. In this model, we do not account for the viscosity of OA particles, which may affect the ability for semi-volatile OA to evaporate, due to mass-transfer limitations.(70) Applying a more sophisticated gas-particle partitioning model to the gas-phase SVOC formation parameterizations in this work would be informative to evaluate this possibility.(71,72)”
Where 70, 71, and 72 are the following references:
70 T. D. Vaden, D. Imre, J. Beránek, M. Shrivastava and A. Zelenyuk, Evaporation kinetics and phase of laboratory and ambient secondary organic aerosol., Proc. Natl. Acad. Sci. U. S. A., 2011, 108, 2190–2195.
71 Q. Chen, Y. Liu, N. M. Donahue, J. E. Shilling and S. T. Martin, Particle-phase chemistry of secondary organic material: Modeled compared to measured O:C and H:C Elemental ratios provide constraints, Environ. Sci. Technol., 2011, 45, 4763–4770.
72 W. Hu, B. B. Palm, D. A. Day, P. Campuzano-Jost, J. E. Krechmer, Z. Peng, S. S. de Sá, S. T. Martin, M. L. Alexander, K. Baumann, L. Hacker, A. Kiendler-Scharr, A. R. Koss, J. A. de Gouw, A. H. Goldstein, R. Seco, S. J. Sjostedt, J.-H. Park, A. B. Guenther, S. Kim, F. Canonaco, A. S. H. Prévôt, W. H. Brune and J. L. Jimenez, Volatility and lifetime against OH heterogeneous reaction of ambient isoprene-epoxydiols-derived secondary organic aerosol (IEPOX-SOA), Atmos. Chem. Phys., 2016, 16, 11563–11580.

17-Nov-2021

Dear Dr Hayes:

Manuscript ID: EA-ART-07-2021-000053.R1
TITLE: Evaluating SOA formation from different sources of semi- and intermediate-volatility organic compounds from the Athabasca Oil Sands

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

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

Reviewer 1

The authors have addressed the points raised in my previous review and publication of the manuscript as is recommended. One minor point: I think “The figure on Page 44” that I mentioned is the key figure. A better resolution will be needed for the final publication.

Reviewer 2

I read through the author responses and the revised paper. The authors seemed to have appropriately answered most of the reviewer’s comments, except a few which I have outlined below. My most major comment (#4 below) is that the authors are still using absolute OA concentrations to present their model-measurement comparisons. In my opinion, a casual reader may miss the significant chemical evolution that is happening in the plume and may [incorrectly] find the results uninteresting. I recommend publication in ESA.

1. I don’t think the authors responded appropriately to the major comment from reviewer 1. Reviewer 1 was asking about how the C* was estimated from the chemical speciation to build the volatility distributions used as model input.
2. For reviewer 2’s major comment #1, can the authors elaborate on the chemical composition data available from the primary references used to generate the different volatility distributions? Are there differences worth discussing between 20D, 60D, ORE, and BIT?
3. I do not think the authors responded carefully to reviewer 2’s major comment #1 in discussing the role of P-S/IVOC composition on SOA formation in other parts of the manuscript.
4. Figure S5 is fantastic and mind-blowing (!) and I think it should be how the data need to be presented in the main manuscript to make it clear that there is rapid SOA production in the plume. I am not sure why the authors haven’t shifted to this presentation style in the revised manuscript. A related question is why the OA goes down to nearly 0 at t=0? Are there no primary emissions? I would think that the combustion sources at the facility would contribute to some low-volatility POA that one would see at t=0.
5. Reviewer 2’s minor comment #4 is asking about measured (not modeled) O:C and details on how that is calculated.
6. I would recommend that the authors add some text around the diesel fleet (e.g., make-up, tier certification, etc.) at the facility in the manuscript (see reviewer 2’s minor comment #6).

In the following response to reviewers, we separate the referee comments with our responses with a series of three line breaks.

Response to Referee 1

Comments to the Author
The authors have addressed the points raised in my previous review and publication of the manuscript as is recommended. One minor point: I think “The figure on Page 44” that I mentioned is the key figure. A better resolution will be needed for the final publication.



We thank the author for their comment about our TOC figure, previously described as on “Page 44”. We have uploaded a higher resolution version of the TOC figure.



Response to Referee 2

Comments to the Author
I read through the author responses and the revised paper. The authors seemed to have appropriately answered most of the reviewer’s comments, except a few which I have outlined below. My most major comment (#4 below) is that the authors are still using absolute OA concentrations to present their model-measurement comparisons. In my opinion, a casual reader may miss the significant chemical evolution that is happening in the plume and may [incorrectly] find the results uninteresting. I recommend publication in ESA.

1. I don’t think the authors responded appropriately to the major comment from reviewer 1. Reviewer 1 was asking about how the C* was estimated from the chemical speciation to build the volatility distributions used as model input.



We address this comment by adding the following text to the manuscript, in section 2.5.2:



“In Liggio et al. (2016) and Li et al. (2019), the volatility distributions were determined by comparing the GC retention times of a solution of alkane standards to the unresolved complex mixture from the Oil Sands.1,2 The method for estimating c* from an unresolved complex mixture has been reported in the literature previously, in detail.59"

Where 59 is a newly added reference:

A. A. Presto, C. J. Hennigan, N. T. Nguyen and A. L. Robinson, Determination of volatility distributions of primary organic aerosol emissions from internal combustion engines using thermal desorption gas chromatography mass spectrometry, Aerosol Sci. Technol., 2012, 46, 1129–1139.



2. For reviewer 2’s major comment #1, can the authors elaborate on the chemical composition data available from the primary references used to generate the different volatility distributions? Are there differences worth discussing between 20D, 60D, ORE, and BIT?



The method for determining the P-S/IVOC volatility distributions, as described in comment #1, does not provide additional information about composition beyond volatility. This is one of the advantages of using a composition-agnostic Volatility Basis Set to model the oxidation of P-S/IVOCs. However, there is some indirect information about the composition of the P-S/IVOCs and their oxidation pathways in the atmosphere.

This information is summarized in the following sentences in the manuscript, added in section 2.5.2, along with the paragraph addressing comment #1:

“While the chemical composition of the ORE and BIT samples was not fully speciated, their chemical oxidation was explored in an oxidation flow reactor (OFR) in Li et al. (2019).2 The OFR data suggest a similar oxidation pathway as cycloalkanes, according to the VK diagrams. The VK diagrams from ORE, BIT, and cycloalkanes were also very similar to those from the aircraft measurements.”



3. I do not think the authors responded carefully to reviewer 2’s major comment #1 in discussing the role of P-S/IVOC composition on SOA formation in other parts of the manuscript.



We have addressed this comment by further discussing the role of P-S/IVOC composition in the conclusion, adding the following paragraph to section 4:

“In addition, there is a lack of detailed information regarding the composition of P-S/IVOCs emitted from the Oil Sands, which would be very valuable for constraining SOA models. For example, the P-IVOC parameterizations of FAST and SLOW were based on studies of diesel combustion emissions, which are not a major source at the Oil Sands, and do not necessarily have the same composition as Oil Sands emissions.16,29 In previous work, we have explored a more detailed approach when speciated P-S/IVOC emissions are available.32”



4. Figure S5 is fantastic and mind-blwing (!) and I think it should be how the data need to be presented in the main manuscript to make it clear that there is rapid SOA production in the plume. I am not sure why the authors haven’t shifted to this presentation style in the revised manuscript. A related question is why the OA goes down to nearly 0 at t=0? Are there no primary emissions? I would think that the combustion sources at the facility would contribute to some low-volatility POA that one would see at t=0.



Respectfully, we disagree with the reviewer. We believe that normalizing the model OA to BC is problematic in our case study. Specifically, the OA concentrations at the longest photochemical ages modeled become dominated by the formation of biogenic SOA, including the background OA, due to the flight path over the boreal forest. Therefore, black carbon drops to very low concentrations while SOA remains (relatively) high, which causes the plots to curve upwards dramatically.

In responding to this comment, we also realized that we made a mistake in the revised manuscript with respect to Figure S5. We did not specify that the model results were only for OA sourced from anthropogenic emissions. This omission has been corrected in the text.

In response to the second half of this comment, in Liggio et al (2016), where these measurements were first reported, no POA was identified in the PMF analysis of aircraft measurements. While POA was reported at the ground level in Lee et al. (2019) and Tokarek et al. (2018), this was likely due to the proximity of their site to the Oil Sands operations and nearby roads. The volatility distributions in this work consider either the presence of no POA (BIT and ORE) or the presence of little POA (20D and 60D) in our model runs. Even in the latter runs the small amount of POA is imperceptible at a photochemical age of zero in Figure S5. In the case of a small presence of POA, the modelled concentrations of POA at the first transect are very small compared to total OA, which would explain why no POA factor was identified in the aircraft measurements which were analyzed by PMF.



5. Reviewer 2’s minor comment #4 is asking about measured (not modeled) O:C and details on how that is calculated.



We have addressed this comment by adding the following sentence to section 2.4, when describing Figure S3(A):

“The O:C and H:C of OA was determined using the measurements from Liggio et al. (2016), following the method described in Canagaratna et al. (2015).1,54”



6. I would recommend that the authors add some text around the diesel fleet (e.g., make-up, tier certification, etc.) at the facility in the manuscript (see reviewer 2’s minor comment #6).



We have adjusted the final paragraph of section 3.2 to account for this comment:

“In our study, we compare the calculated emissions of P-IVOCs from ORE to estimated P-IVOC emissions of the mine fleet. Unfortunately, there are few studies on the emissions of the diesel fleet at the Oil Sands. To meet NOx and PM2.5 standards, the fleet, as of 2013, is regulated using EPA Tier 1-4 standards for off-road diesel engine emissions.63 However, direct emissions from Oil Sands vehicles have only been studied with Tier 1 vehicles.64 Given this lack of information, it is reasonable to use published P-IVOC:ΔBC emission factors for off-road diesel vehicles in the United States, which have similar emission standards as the Oil Sands fleet.11,60,65 The P-IVOC:ΔBC emission factors from these previous studies of off-road diesel vehicles is 1.4 µg m-3 / µg m-3, which is two orders of magnitude less than the Oil Sands, which has a total P-IVOC:ΔBC emission factor of 196 µg m-3 / µg m-3. ”

06-Jan-2022

Dear Dr Hayes:

Manuscript ID: EA-ART-07-2021-000053.R2
TITLE: Evaluating SOA formation from different sources of semi- and intermediate-volatility organic compounds from the Athabasca Oil Sands

Thank you for submitting your revised manuscript to Environmental Science: Atmospheres. After considering the changes you have made, I am pleased to accept your manuscript for publication in its current form. I have copied any final comments from the reviewer(s) below.

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