Review of Burgeois et al. “Comparison of airborne measurements of NO, NO₂, HONO, NO_y and CO during FIREX-AQ”

Thank you for giving me the opportunity to review this manuscript. I hope my input will be useful to the authors.

I appreciate this paper very much. The paper describes results from an intercomparison of different measurement techniques for what many would call “basic” photochemical tracers but the validity and precision of these tracer measurements are in fact critical for the success of any atmospheric chemistry mission.

This paper is a timely and very relevant contribution at a time during which measurement capabilities are expanding rapidly. It is well structured and clearly written using precise language. The scientific methods are sound. The content is entirely appropriate for publication in AMT. The reference list is appropriate. I recommend accepting the manuscript for publication after considering the following suggestions.

HONO:

I have a bit of a hard time wrapping my mind around the HONO comparison numbers and illustrations.

1. How can the distribution of the factional errors be so tight around a value of 2 (Figure S1)? When plugging into the equation CES/CIMS values mentioned at various places in the manuscript (1.36, 1.8, 2.48 and 3.9) I calculate values for FE between 0.3 and 1.2. This should center the gaussian somewhere in the middle of that range and show a much broader distribution.
2. Figure S4e shows that the CES measures anywhere from zero to 25 ppb while the CIMS measures between 0 and 3 ppb. How does this reconcile with the gaussian distribution shown in Figure 5 and the mean difference plots in figure S9?

This might require a bit more explanation than what is currently presented in the text.

While I can appreciate that the IMR temperature may have an influence on sensitivity I’d be curious to know why this would only affect HONO and not also other analytes. Other readers might be left wondering about this.

Was there an attempt made to correct the HONO values for IMR temperature, and how does the comparison look like then?

NOy:

For lack of a better word, I find the assessment of the NOy measurements somewhat sugarcoated. In my view there are too many uncertainties to make these measurements ultimately useful, at least for fire smoke research. The facts I gather are the following:

1. Particulate nitrate makes up the largest fraction of total NOy in western wildfire smoke and a significant fraction in the eastern fires.
2. The sampling efficiency of particulates is highly dependent on airspeed but the real airspeed at the inlet tip (and the dependency on type of aircraft, banking and attack angle, or install location on the aircraft) is unknown.
3. Particulates used in the model described are assumed to be ammonium nitrate. The exact composition of the nitrates contained in fire smoke particulates is not known. There could be a significant fraction of organics, in particular nitroaromatics, but their volatilization behavior and conversion efficiency in the gold converter is unknown.
4. In the best case of sampling efficiency, 25% of the nitrate could be unaccounted for. Looking at the graph in Figure 10a, that fraction could be more than 50% in the worst case.

I’d agree with the authors if you call this a devil’s advocate assessment, but at the end of the day my impression is that NOy measurements and “oxidized nitrogen closure” calculations based on these measurements or their use as photochemical clocks, etc. still need to be taken with a (fairly large) grain of salt. Just like they had to in the past.

What would a comparison of plume dilution calculated using CO versus a similar calculation using NOy look like?

Minor suggestions:

Section 2 intro: Maybe a figure with a plumbing diagram of the manifolds described in the manuscript could be helpful

Section 2.2.1.: What was the conversion efficiency of the photolysis converter?

Line 134: Suggest replacing “minimal” with “least possible”

Line 169: NOy is missing in the list

Section 2.2.3.: What is the inlet material? What was is shared with?

Line 305: How can the addition of 1% flow of saturated nitrogen stabilize the I- / I-*H20 clusters to such a precise ratio?

Line 401: should be CH3NO2

Line 511: If this uncertainty is based only on the spread of the trajectory ensemble, does this mean that there is additional uncertainty arising from the plume rise time, calculated using a fixed vertical transport speed?

Line 575: I am not certain what the logic is behind putting some figures into the supplement and others into the main manuscript. Maybe this could be revisited.

Line 633: Could the positive artifact in the CL instrument be caused by thermal decomposition of peroxynitrate species inside the photolytic converter cell (which might be warmed by the heat output of the LEDs?)

Line 699: Suggest starting the paragraph with “The interpretation of literature….”

Line 733: If there is an obvious problem with the CIMS HONO measurements, why are these being used here?

Line 749: one or more ?

Line 757: see NOy discussion. How is this known?

Line 787: “…higher than…”

Line 936: see NOy discussion above

Conclusions point 6: Averaging data always results in less scatter. How useful really are instrument comparisons when averaging data spanning orders of magnitude?

Bourgeois et al. report aircraft measurements made on board the NASA DC-8 during the FIREX-AQ campaign in 2019. In this paper, the authors compare duplicate measurements of NO mixing ratios by chemiluminescence and by laser-induced fluorescence (LIF), of NO₂ by photolysis coupled to CL (P-CL), cavity-enhanced absorption spectroscopy (CES), and LIF, HONO by chemical ionization mass spectrometry (CIMS) and CES, and of CO by tunable diode laser absorption spectroscopy (TLDAS) and integrated cavity output spectroscopy (ICOS). The authors also attempt to close the NO_y budget by comparing NO_y measured by CL with a sum of individually measured components, ΣNO_y, calculated by adding NO, NO₂, HONO, HNO₃ (measured by another CIMS), pNO₃ (measured using an aerosol mass spectrometer, AMS) and acyl peroxynitrates (APNs) that were quantified by a third CIMS.

This is a well written manuscript though perhaps a bit too long. There is a lot of interesting results, for example, a great validation of the new LIF instrument and excellent agreements for NO and NO₂, but there were also a few questionable items (see below) that the authors will hopefully be able to address in the finalization of this manuscript.

General/Major comments

(1) Tables are, strangely, absent from this paper. Having tables would have helped consolidate this rather long manuscript. Specifically:

Please add a table of measurements/instruments.

Please also add a table of the flight schedule(s), indicating time of day and whether there were nighttime flights analyzed here.

Please add a table which summarizing statistics on the mixing ratios observed (e.g., median, average, percentiles, max and min etc.).

Please consolidate the various correlation slopes/intercepts in one or more tables as well.

(2) Please clarify if the comparisons made here were "blind" or if kibitzing was allowed/possible before individual PIs reported their data.

(3) Some instrument descriptions are very thorough (and thank you for that!) yet important details are missing for others. For example, APN data presented, but it is unclear which individual compounds were actually quantified (PAN, PPN, MPAN, APAN etc.) and included in the sum. There was also no statement as to how good or uncertain these data are. HCN and NH₃ concentrations were quantified (Figure S14) but their measurement is not described at all.

(4) Measurements of HNO₃, APNs, ClNO₂, N₂O₅, pNO₃, C1-C5 alkyl nitrates were made but sample time series of those data are not shown, which is an odd omission considering that some of these compounds contribute the most to NO_y (judging from Figure 10).

(5) The definition and choices/explanations as to what species to include in ΣNO_y in this manuscript (abstract line 14; equation 2, line 339) would benefit from some polishing.

(a) Definitions.

Please add (to the introduction - see comment on lines 95-98) a comprehensive definition of what species contribute to NO_y (e.g., equation (1) of Fahey et al., J. Geophys. Res., 91, 9781-9793, 10.1029/JD091iD09p09781, 1986), if only to provide a contrast to equation (2) of this manuscript.

Many components of NO_y are omitted from equation (2). Please note more prominently the (many) omissions from ΣNO_y in the abstract, such as higher molecular weight alkyl nitrates ("total alkyl nitrates", line 846), coarse nitrate, peroxynitrates (HO₂NO₂, RO₂NO₂), and the nocturnal nitrogen oxides NO₃, N₂O₅ and ClNO₂.

Since the expression given here for ΣNO_y is a simplification, the right-hand side of equation (2) only approximates ΣNO_y and an equal sign should not be used (use ≈ instead).

Further, since the expression for ΣNO_y omits nocturnal nitrogen oxides, the definition of ΣNO_y as in equation (2) should perhaps be referred to as the sum of daytime nitrogen oxides, and the time of day of the measurements should be added to the title.

(b) Organization.

It is clear from the outset that several components of NO_y were measured by multiple instruments, yet the reader is kept in the dark for far too long what the authors included in this sum and what they mean by ΣNO_y (e.g., line 14 and 339). If I counted correctly, there are (at least) 36 different ways ΣNO_y could have possibly been calculated for this data set (NO from either one of two instruments or average NO which gives 3 possibilities, NO₂ from one of three instruments or average NO₂ to give 4 possibilities, HONO from one of two instruments or average HONO to give 3 possibilities, 3×4×3 = 36 possible combinations). The reader is only told on line 732 which measurements were actually used.

(c) Closure.

Having so many choices (data from several instruments to choose from, and which compounds to include in ΣNO_y) is great, but ultimately undermines the conclusion that NO_y budget closure was achieved (lines 22/23).

Even though I know this wasn't the case, the manuscript somehow gave me the vibe that data were cherry-picked and the authors stopped adding compounds to ΣNO_y once the slope relative to NO_y,CL reached unity. Can you be more convincing - for example, why not add all components that were quantified - surely, there would have been times when all instruments were operational? Please add such a plot (and use the larger NO_x and HONO data from the LIF & CES instruments).

And please discuss the elephant in the room: The unquantified components of NO_y. If closure was indeed achieved, it would imply that those unquantified components were negligible, which in my opinion is doubtful.

It is stated on line 846, that FIREX-AQ did not include a measurement of total alkyl nitrates, but the thought is left hanging. What if the suite of instruments had included such a measurement? Would the NO_y budget have blown up? I'd be surprised if the Cohen group had not quantified ΣAN in fire plumes at some point to help constrain this "known unknown" and to guide this discussion.

Also, if submicron pNO₃ constituted ~40% or so of NO_y in wildfire plumes (Figure 10a), surely there would have been coarse nitrate as well, which would have consequences on closure. More discussion is needed. There were measurements of coarse mode size distributions (Schoeberl et al., Coarse mode aerosol in biomass burning aerosol layers during FIREX-AQ, TBD, in prep, 2021 - listed on https://csl.noaa.gov/projects/firex-aq/science/pubs.html and Noyes et al., Remote Sensing 12(22), 3223, https://doi.org/10.3390/rs12223823) that may provide some constraints here.

(6) Carbon monoxide

The sections on CO seem like an afterthought and do not add much to the remainder of the paper. I'd recommend splitting this off into a separate to reduce the size of this already very long paper.

Specific/Minor comments

line 21. a slope of 1.8 - yikes!

line 72. Please add a table summarizing this large suite of airborne instruments.

lines 95-98. Please insert an equation here, defining NO_y (similar to equation (1) of Fahey et al., J. Geophys. Res., 91, 9781-9793, 10.1029/JD091iD09p09781, 1986).

line 112. There have been other papers from this campaign (e.g., Decker et al.) that would be worth calling out here.

lines 159. Pollack et al. describe two converters with LEDs at 365 nm and one converter at 395 nm, but not one at 385 nm. Is this a new system? If so, please provide relative data such as make/power of the LEDs, NO₂ photolysis frequency, temperature etc.

line 160. Pollack et al. - the Journal of Atmospheric Chemistry lists this citation as a 2010 paper (even though it was only accepted in 2011). Please update.

line 180. "5% HONO interference". The magnitude of this interference will depend on the ratio of HONO to NO₂ in ambient air. Please clarify what is meant by 5% (stated on lines 615-617: 5% of the HONO sampled converts to NO).

line 209. please provide an uncertainty estimate for the NO-LIF instrument similar to lines 183, 220 and 280.

line 247. please state how the zero air was generated (cylinder or scrubbed air).

line 259. Please state how often the Teflon filters were changed.

line 271. a 0^th order polynomial - interesting way to say "offset".

lines 270-276. Please comment on errors introduced from using reference absorption cross-sections are measured at near 1 atm pressure and near room temperature to fit absorption spectra collected at reduced pressure and ambient (I am guessing) temperature.

line 281. What is the effective optical path of this instrument?

line 307. What is the linear dynamic range of this instrument?

line 310. "normalized by the iodide signals" - I^- or I^-·H₂O or both? The Pratt group has recently used the water cluster to normalize.

line 313-314. "Calibrations with Cl₂ and HNO₃ permeation sources ... to diagnose the stability of instrument sensitivity" - please comment on how stable that response turned out to be (perhaps further down in the results section).

line 321. background typically equivalent to 40 ppt - what was the range of backgrounds observed? Does the background increase after sampling high concentrations of HONO?

line 339. Data from which instruments were used to account for the species in equation (2)?

line 372-373. Can you speculate how much coarse nitrate there might be in a biomass burning plume?

line 393. please provide an uncertainty estimate for the CIMS measuring APNs instrument similar to lines 183, 220 and 280 (see also comment for line 209).

line 404-415. Are the N₂O₅ data presented anywhere? If these data are from the same instrument that underestimated HONO by a factor of 1.8, how confident can one be in the N₂O₅ data and stated ±(15% + 2 pptv) accuracy?

line 431. "at approximately 4.6 μm" Since these types of instruments monitor a specific absorption line and derive mole fractions based on that particular line's line strength, please be more specific here.

In general, more detail (or a more appropriate citation) is needed in this section since the Baer et al. (2002) reference does not describe an instrument quantifying CO via its absorption in the mid-IR.

line 442 and 456-457 "dry air mole fraction". Is this correction made purely because the water vapour variability is sufficiently large to cause deviations to mole fractions, or are there other effects in play, too, such as spectral broadening or overlap with water lines in the IR? Please add an explanation and justification for this correction to the text.

In practice, how much of a correction was made, and perhaps most importantly, why were only the ICOS data corrected and not also the TDLAS instrument described in 2.2.8 which used an absorption line ~4.7 μm and whose data would have equally been affected by the presence of water vapor?

line 451. "precision" - is that for 1-second data?

line 533. Please cite a paper for orthogonal distance regression or describe the algorithm.

line 556. Figure 2a shows a slope of 0.98±0.00 whereas the text has 0.98±0.08. The meaning of the error is defined for the text (±combined instrument uncertainties) but not for the Figures since the values there are different. Please clarify.

Also, please state how combined uncertainties were calculated.

lines 554 - 577. Impressive performance by a new instrument! Well done!

line 609. "ranging from 0.88±0.12 to 0.90±0.11". This large difference is interesting. Wouldn't that suggest that the CL NO_y data may also be 10% - 12% too low, since it would have been calibrated using NO_x calibration standards?

line 609. "comparable" is probably not the best word in this context - suggestion: "on the upper end of the combined uncertainties" or similar.

line 618. how much HONO was there relative to NO₂?

lines 666-697. Sounds like the CIMS would benefit from an internal standard to track its HONO sensitivity, e.g., continuous addition of a calibrated amount of ¹⁵N¹⁸O₂H to the inlet.

If I understood this correctly, one HONO instrument sampled through a filter, the other did not. Please comment on what role, if any, the filter on the CES may have played? There are indications that NO₂ can convert on surface to HONO. Has the CES inlet transmission of NO₂ been tested using an "aged" filter?

line 720. "NO_y". Usually, NO_x constitutes the largest fraction of NO_y. Since there was good agreement between NO_x measurements, good agreement can also be expected for NO_y. Consider a section on NO_z = NO_y ‑NO_x.

line 723. Section 2.2.8 should be section 2.2.6.

line 817. How were HCN and NH₃ quantified?

line 817. "Here, we find no evidence for a potential interference of HCN or NH₃" - thats' good news! Is there an explanation as to why this instrument outperforms others in this regard?

line 846. "However, FIREX-AQ did not include a measurement of total alkyl nitrates." And if it had, would the result have been ΣNO_y >> NO_y,CL? I wonder ...

line 953. My browser displayed: "Hmm. We’re having trouble finding that site." Please verify the link to the archive.

Figures 2a, 9a, and 12a. Are all data included in these panels, or a selection? Please clarify in the caption(s).

Figure 3. Please clarify in the caption at what time of day these plumes were observed (>20 ppbv of daytime HONO would seem like a lot during daytime).

Figure 8. Since the CES data are likely more accurate, consider switching the axes (plotting CIMS vs CES data). Were photolysis frequencies quantified? Are these daytime HONO levels? If there was truly this much HONO in the daytime, more justification as to the suggested absence of other photolabile compounds (N₂O₅/ClNO₂) is needed.

Figure 10. Please state what percentiles are used of the box-and-whisker plots.

Supplement

The figures here are labeled SA, SB, SC, ...  and S1, S2, S3, but could have just been numbered consecutively to avoid unnecessary confusion.

Figure S12. I am surprised not to see a larger difference in the slopes of Figures S12a and 9c, considering NO_x (~30% of NO_y in background air judging from Figure 10) would have been increased by 10%-12% and HONO (which was abundant at times also - Figure 8) by 80%, yet the slopes are virtually identical (1.00±0.01 and 1.01±0.00). Since a distinction was made in Figure 10 between background air and "in smoke", please also make that distinction in Figures 9 and S12.

Review report.

Bourgeois et al. presented comprehensive intercomparisons of airborne NO, NO2, HONO, NOy and CO in biomass burning plumes, each measured with differing techniques during FIREX-AQ in the summer of 2019. This study provides valuable dataset and the evaluation of accuracies of major techniques deployed in the challenging biomass burning plume conditions. Additional literature review on these species from major airborne field campaigns are helpful for understanding the accuracy of these measurements under different environmental conditions. The manuscript was written thoroughly, and the figures are made clear. Thus I recommend acceptance after revision. Below are my comments:

1. Line 204, hourly calibration of NO LIF was performed with [NO] 4-20 ppbv, did this concentration range apply for all the smoke conditions? How do you ensure the linear response beyond this range?
2. Lines 508-510, “Trajectories and ages that were grossly inconsistent with smoke transport patterns seen in geostationary satellite images were excluded from further analysis”. Whiich group should these data categorized into
3. Lines 648-649, what is the p-value of Figure S4 b and d, any explanation for the seemingly dependence of the difference on NO2 concentration?
4. Figure 3 and Figure 4, no letter label (e.g., a to e) was assigned to any of the panel.
5. In section 3.3.1, intercomparison between CES and CIMS measured HONO were presented. I have the following questions:       1) The slopes shown in Figure 8 suggests CES HONO was higher than CIMS HONO. However, it seems neither the flight averages of the absolute difference shown in Figure S9, nor the histograms of the absolute difference between the two methods suggest the CES-HONO > CIMS-HONO. Any explanation?       2) In Figure S9, why are there many missing points for intercepts (middle panel) and slopes (bottom panel), while the top panel (mean absolute difference) shows all the data on each sampling day?         3) it is interesting to see the measurement of HONO with CIMS are significantly affected by temperature, especially above 30°C, as is shown in Figure S10. Would the slope of CES-HONO vs CIMS-HONO be closer to 1 since it’s not shown in this figure?       4) Could the inlets for the two methods be an issue that cause the discrepancy during FIREX-AQ?
6. Do the measurements shown in Figure 10 (a) include both fresh smoke and aged smoke? If so, what if the fresh smoke and aged smoke were separately considered? Will the relative contribution of each NOy be significantly different? Are the large uncertainties associated with NO2, APNs and pNO3- driven by flight-to-flight difference, secondary processing, or environmental conditions (humidity and temperature)? What could be possible causes for the different contributions of major species (e.g. NO2, APNs and pNO3-) between western wildfires and eastern agriculture fires?
7. In Figure S11(a), from the slopes determined for fresh versus aged smoke, can we say the sum of NOy outweigh CL-NOy for fresh smoke and the CL-NOy outweigh the sum of NOy, although the difference is within the combined instrumental uncertainties? If so what would the explanation be?
8. Lines 732-734 described what different NOy measurements were used to calculate total NOy. While I understand the choices are based on precision, I wonder why CIMS HONO instead of CES HONO was chosen, as CIMS HONO underestimated CES HONO and its accuracy seems to be significantly affected by temperature variation as is discussed in 3.3.1?
9. Lines 747-779 are difficult to follow. Figure 12(a) should be well explained first followed by Figure 12 (b). The current order is reversed, and I don’t quite get the idea of Figure 12 (a). For Figure 12 (b), it is unclear how the missing NOy fractions (bottom panel) were calculated. My understanding is that fraction of each individual NOy to total NOy was calculated from the individual measurements and sum of NOy, then particle sampling fraction was calculated from the model. Combining the two pieces will enable the quantification of missing NOy (0-24%) resulting from the CL-technique, but how? Thus, further clarification will be needed. Also, in section 3.4.1, it is interesting to see the possible reasons that cause the negative and positive mode of the discrepancy between CL-NOy and sum of NOy. The authors separated the two modes and interpreted them separately. However, if one reason is important (e.g. pNO3- loss through the CL inlet), it should be important throughout the entire campaign, instead of certain period. I might miss something, but a clarification would be helpful.
10. In section 3.5.1, it was noted the cause of the discrepancy between ICOS and TDLAS measured CO was unclear. I am curious whether temperature plays a role? Additionally, Figure 14(a) shows when CO goes above 10 ppmv, ICOS seems to outweigh TDLAS; as CO is higher the deviation from 1:1 line is larger. What are the possible explanations?