This study deploys an AMS and a FIGAERO-CIMS to investigate the sources and formation mechanisms of oxidized organic nitrogen (OON) species in an urban site in Guangzhou, China. By applying a tracer based method to FIGAERO-CIMS measurement, the contributions from biomass burning and secondary production to OON have been quantified. Further, the production rate of secondary OON is estimated based on the measured VOCs concentrations and literature values of ON yields. Overall, this study presents an interesting dataset and conducts comprehensive analysis. It improves our understanding of the concentration and speciation of OON in diverse environments. However, the conclusions on the source apportionment and formation mechanisms of OON are speculative as outlined below. I recommend accept with major revisions noted.

Major Comments

1. The mass closure analysis on particle OON measured by CIMS and by AMS is valuable. It is shown that pOrgNO3,CIMS only accounts for ~30% of pOrgNO3,AMS (Line 228). In other words, CIMS only captures a small fraction of total pON, if the AMS measurement is reliable. Thus, the majority of the analysis in this study only focuses on a small fraction of total ON. A more important question is what the rest 70% of particle OON are. The reviewer understands this question is beyond the scope of this study, but this measurement limitation should be stressed more throughout the manuscript, to avoid the fallacy that the OON measured by I- CIMS, such as figure 7, represents the composition of all OON in the atmosphere. Similarly, the conclusions like half of particle OON originates from biomass burning and the rest from secondary production should be discussed under the frame that the OON measured by I- CIMS are considered in the calculation, not total OON in the atmosphere.
2. Using C6H10O5I- as a tracer for biomass burning is not adequately justified. A major piece of evidence that biomass burning contributes to OON is figure 2a and 2c, which show the relationship between OON and C6H10O5I- is bifurcated. However, the same relationship is not observed between OON and other BB tracers including AMS mz60, methoxyphenol, and vanillic aicd. The contrasting observations are suspicious. The manuscript claims that BB tracers other than levoglucosan have all sorts of issues, such as non-biomass burning emissions, low concentration, or larger background. These issues could certainly be true. However, an obvious issue with C6H10O5I- is that it is not solely levoglucosan, but has interference from other isomers! Thus, it can be easily argued that C6H10O5I- is not a perfect tracer either. One should not rely the analysis solely on this single chemical formula. Let’s imagine, among all the CIMS ions, one ion, which is a tracer for VCP for example, exhibits similar correlation relationship with OON as C6H10O5 does (i.e., bifurcation as in Figure 2a). Then, the conclusion will easily become that VCP is a large contributor to OON. In conclusion, more evidence is required to support the contribution of biomass burning to OON. The authors mentioned that there are some episodes when pOON and levoglucosan peak coincidently (Figures S11a and S12a). Again, the figures only show pOON has some relationship with C6H10O5I-, not with levoglucosan, because the C6H10O5I- could be some other isomers.
3. The production rate of secondary OON is estimated based on measured VOCs, but the usefulness of this analysis is limited. First, as the OON concentration depends on both production and loss, which is clearly pointed out in Line 369-371, the correlation between OON concentration and product rate is not very meaningful. As a result, there is no clear correlation between two terms as shown in this study. Second, the calculated production rate is not tied to the I CIMS measurement, which degrades the importance of such analysis. In other words, both methods do not validate each other. But it is at the authors’ discretion regarding whether to keep this analysis.
4. Even though some analysis methods have been used in the literature, they still should be briefly explained to guide the readers who are not familiar with the methods. For example, Line 155 – 158 mentioned that three methods are applied to estimate the ON concentration based on AMS measurements. The basic principles behind each method should be briefly discussed (i.e., one or two sentences). For example, the NO2+/NO+ ratio method is based on the fact that inorganic and organic nitrates have different fragmentation patterns. Another examples include Line 232 and seasonal decomposed analysis (Line 348). Please briefly discuss the methods. Lastly, Line 431, please explain how the lifetime of gON is estimated.
5. Issues regarding CIMS quantification. Does the calibration account for the temperature-dependence? A recent study shows that the I- CIMS sensitivity has a strong dependence on temperature¹. This issue could be significant for particle-phase measurements, which have a higher IMR temperature. Line 134 mentioned that a voltage scanning procedure was used to estimate the sensitivity. However, neither detailed procedures nor calibration results are shown. Please describe the procedure, show the calibration curves, and show the accuracy of this method to the 39 compounds calibrated with authentic standards. Please discuss how the calibration curve is applied to estimate the sensitivity of individual compounds. Also, two recent studies have quantified the uncertainty of the voltage scanning method^{2, 3}, which should be cited and discussed in the manuscript.

Minor Comments

1. Lines 50 and 78. Please cite Xu et al. 2015 ACP⁴ which also extensively discussed the NO2+/NO+ ratio method.
2. Line 60. Please cite Chen et al. 2020 ACP⁵ which also deployed FIGAERO-CIMS to measure organic nitrates. Please also discuss Chen et al. in related analysis, such as the comparison between AMS and FIGAERO-CIMS.
3. Line 125. Do all 339 compounds have signal significantly higher than the background? Or 339 refers to the number compounds that are fitted in the HR analysis?
4. Line 200. The underlying assumption of this statement is unclear. Does the fraction of organic nitrate in total nitrate increases with decreasing OA concentration?
5. Line 225-228. There are many acronyms in this paragraph, including pOON_CIMS, pOON_AMS, pOrgNO3_CIMS, pOrgNO3_AMS. Please better explain the difference between these terms.
6. Line 247-248. Please explain “high susceptibility influenced by temperature”.
7. Line 253. “photolysis rate” in this sentence is confusing, because reader may think it refers to the photolysis rate of OON. Replace “photolysis rate” with jNO2 or solar radiation.
8. Line 258. It should be figure 1d, instead of figure 1f.
9. Line 282. replace “NO/NOx concentration” with “NO and NOx concentrations”.
10. Line 312 and Text S4. If the reviewer understands correctly, the “seasonal decompose analysis” removes the seasonal variation from the diurnal variation. However, the data only include one-month measurement and it is not clear why this analysis is necessary. Also, text S4 does not clearly describe the method at all. This method section should be expanded.
11. Line 340. For the strong BB emission period, are VOCs from BB considered in the calculation of OON production rate?
12. Line 413. Please rewrite this sentence because RO2+NO produces either RONO2 or O3.
13. Figure S21. Please explain why ALWC (RH and others) is correlated with pOON/Ox, instead of pOON?

Reference

1. Robinson, M. A.; Neuman, J. A.;  Huey, L. G.;  Roberts, J. M.;  Brown, S. S.; Veres, P. R., Temperature-dependent sensitivity of iodide chemical ionization mass spectrometers. Atmos. Meas. Tech. 2022, 15 (14), 4295-4305.
2. Bi, C.; Krechmer, J. E.;  Frazier, G. O.;  Xu, W.;  Lambe, A. T.;  Claflin, M. S.;  Lerner, B. M.;  Jayne, J. T.;  Worsnop, D. R.;  Canagaratna, M. R.; Isaacman-VanWertz, G., Quantification of isomer-resolved iodide chemical ionization mass spectrometry sensitivity and uncertainty using a voltage-scanning approach. Atmos. Meas. Tech. 2021, 14 (10), 6835-6850.
3. Bi, C.; Krechmer, J. E.;  Frazier, G. O.;  Xu, W.;  Lambe, A. T.;  Claflin, M. S.;  Lerner, B. M.;  Jayne, J. T.;  Worsnop, D. R.;  Canagaratna, M. R.; Isaacman-VanWertz, G., Coupling a gas chromatograph simultaneously to a flame ionization detector and chemical ionization mass spectrometer for isomer-resolved measurements of particle-phase organic compounds. Atmos. Meas. Tech. 2021, 14 (5), 3895-3907.
4. Xu, L.; Suresh, S.;  Guo, H.;  Weber, R. J.; Ng, N. L., Aerosol characterization over the southeastern United States using high-resolution aerosol mass spectrometry: spatial and seasonal variation of aerosol composition and sources with a focus on organic nitrates. Atmos. Chem. Phys. 2015, 15 (13), 7307-7336.
5. Chen, Y.; Takeuchi, M.;  Nah, T.;  Xu, L.;  Canagaratna, M. R.;  Stark, H.;  Baumann, K.;  Canonaco, F.;  Prévôt, A. S. H.;  Huey, L. G.;  Weber, R. J.; Ng, N. L., Chemical characterization of secondary organic aerosol at a rural site in the southeastern US: insights from simultaneous high-resolution time-of-flight aerosol mass spectrometer (HR-ToF-AMS) and FIGAERO chemical ionization mass spectrometer (CIMS) measurements. Atmos. Chem. Phys. 2020, 20 (14), 8421-8440.

Summary:

The authors performed measurements of gas and particle-phase organic compounds using a FIGAERO-CIMS in a polluted urban location in China, with a particular focus in oxidized organic nitrogen species. Using C6H10O5 (levoglucosan) as a tracer, they estimated the contribution of biomass burning to the measured gas and particle concentrations. Calculations were done to estimate the contribution of different oxidants and precursors to secondary organic nitrogen production. Broadly, the measurements and analysis presented in this manuscript are useful for helping to understand sources of organic nitrogen gases and particles in urban areas. Before this work is published, I believe there are several major issues that should be addressed. If I understand the experimental setup correctly, I am worried about the impact of sampling through a nafion tube. I think the authors should consider how much that could affect their measurements in light of recent literature on the topic. I also want to see an uncertainty analysis of the measurements, especially of the voltage scanning technique that is still a relatively new method of CIMS quantification. Taken together, I think the authors should carefully discuss the strengths or limits of their conclusions in the context of these uncertainties.

Comments:            

Line 103: Have the authors investigated any artifacts that could result from sampling the CIMS through a nafion dryer? For instance, have you considered possible particle losses, or losses of compounds with particular functional groups that do not transmit well through nafion? This previous work from Liu et al. 2019 indicates that polar S/IVOCs do not transmit well through nafion (https://amt.copernicus.org/articles/12/3137/2019/). This could be a critical problem for this work, and needs to be addressed.

Line 132: I have some questions about the CIMS calibration. I suggest the authors provide the calibrations factors that they determined for the 39 species that were calibrated. Calibrating a CIMS is challenging, but if the authors provide their calibration numbers, then readers can place the resulting concentrations in context of other measurements with possibly different calibration factors (each instrument can be different). I do not see these numbers in Ye et al. 2021 either, but maybe they are published somewhere.

Line 134a: I also would like to see more information about how the voltage scanning procedure was done. I see that there is information given in Ye et al. 2021, but the reader of this paper would benefit from more information included here instead of having to search in other papers for it. Also, it is my understanding that the voltage scanning technique can have relatively high uncertainty.

Line 134b: When I look at Fig. S7c of Ye et al. 2021, the sensitivity values calculated from voltage scanning seem larger than I would expect. Perhaps this is normal for the instrument used here, and it would be useful to see the calibration numbers for more common compounds such as many of the 39 directly calibrated species (see my previous question).

Line 134c: My main comment about voltage scanning is that the authors should calculate the uncertainty for voltage scanning calibrations, and apply that uncertainty to the determination of gas and aerosol mass (especially organic nitrogen) measured by the CIMS. Section 3.1 compares AMS and CIMS masses in several ways, but I do not see any analysis of the uncertainties in calibration of the CIMS (or the AMS) and how that affects the comparison. In the Conclusions section Line 472, you say that the CIMS measured 28% of the total pOON, but how well do you know that number? Is it possible that the CIMS actually measured a much larger fraction, but the calibrations are just really hard to do?

Line 140: Instead of saying definitively that ONs were the dominant components of OON, I suggest you acknowledge the considerable uncertainty by saying something like this: “Some nitroaromatic signal may be detected as elemental formulas other than those listed above, and some of the signal at the elemental formulas identified here as nitroaromatic may have contributions from ON species. While uncertainty exists, it is likely that ONs dominated the OON observed during this campaign.”

Line 148: How was this photochemical age determined? Even if it is described in the Chen et al 2021a citation, it would be useful to briefly describe here.

Line 201: Since it makes more sense to compare the AMS pOrgNO3 with CIMS pOON when the AMS total nitrate is less than 5 ug m-3, I suggest you show remove the data points with greater than 5 ug m-3 from Fig. 1b. Then you can keep Fig. S5a as it is to show all the data. Also, I am not sure I understand the purpose of Fig. S5b and you can probably remove it.

Fig. 2 Caption: The letters you use in the caption do not match the letters assigned to the figure panels. Please correct this.

Line 278: I strongly recommend that when you refer to CIMS signals, that you always refer to the elemental formula rather than a specific isomer name. For instance, say C7H8O2 instead of methoxyphenol and C8H8O4 instead of vanillic acid. The iodide CIMS signal very likely comes from multiple isomers. Indeed, if you look at Fig. S12 of Palm et al. PNAS 2020, they show that the iodide CIMS signal at C7H8O2 is more likely to be methyl catechol rather than guaiacol. So here in the text, I would suggest changing to “Another two biomass burning tracers, i.e., C7H8O2 (methoxyphenol, methylcatechol, and isomers) and C8H8O4 (vanillic acid and isomers),…” You should also update the text when referring to C6H10O5 (levoglucosan and isomers) and anywhere else that is needed.

Table S1: Please indicate in the table caption that the data that was used to derive these slopes is also shown in Figs. S11 and S12.

Line 316: It seems reasonable to me that OON_bb would be an estimate of primary plus rapidly formed secondary OON from biomass burning emissions. I think that the OON_sec could also include slowly formed (i.e., next day) OON from biomass burning sources in addition to the other sources. That slowly formed OON would not correlate with the primary C6H10O5 tracer. If the authors agree, please update the text. If not, do you have evidence to suggest otherwise?

Section 3.2: I would like to see a discussion at the end of (or throughout) this section of the authors’ assessment of the uncertainties of this analysis. For instance, the iodide CIMS C6H10O5 signal is not a perfect representation of primary biomass burning emissions. That signal can have variability due to chemistry, variable emissions, etc. This should be discussed. Also I think a considerable source of uncertainty is that the OON_sec is defined just as the OON that is not biomass burning related, rather than defining OON_sec by some correlation with a secondary chemistry tracer. How could this affect your results?

Line 458: This correlation of 0.52 < R < 0.79 is not very high, so I would not agree that this means that C10HxNOy (y>=6) “indeed mainly” comes from biomass burning emissions. Correlation does not mean causation, and Fig. 7b shows that these C10 compounds are present during the whole campaign and not just during biomass burning periods. I suggest the authors remove this assertion or follow it up with other analysis such as correlation with a monoterpene SOA tracer.

Line 472: I mentioned this in a comment earlier, but I would like to see what your estimated error bars are for this 28% number of how much pOON the CIMS sampled relative to the AMS. But, if this number is your best estimate, then how does this affect your conclusions? If the CIMS only measures a small fraction of the pOON, then is it justified to conclude that about half of pOON is from biomass burning, or can you really only say that about half of the 28% of measured pOON is from biomass burning emissions? There are some uncertainties here related to not being able to measure most of the organic nitrogen that I believe the authors should explore further.