This is an excellent paper on the chemistry of BrCN, which previously has never been reported to be present in the atmosphere.  Detected by two chemical ionization mass spectrometers during the ATom flights, this molecule appears to form in regions where active bromine chemistry is especially prevalent, i.e., in the polar springtime boundary layer when ice/snow is present.  The paper presents the measurements, does an excellent job at working through likely BrCN formation and loss pathways, and is well written.

An interesting observation is that high amounts of CHBr3 (relative to CH2Br2) correlate with BrCN. Given that HOBr is believed to form CHBr3 from reactions with DOM, this is indirect support for abiotic formation of BrCN via the multiphase reaction of HOBr with HCN. This makes sense given that this reaction (Reaction S4) has such a large rate constant (close to diffusion limited) in water. HCN is also measured to help constrain the chemistry but an open question, as usual, is the pH of the surface where the multiphase chemistry is occurring.  The paper also lays open the potential for there being a biotic source of BrCN (and HOBr).

The main point raised in the paper is that HOBr/Br- chemistry is required for bromine recycling and so, if HOBr is instead reacting to form BrCN, the ozone and mercury loss chemistry shuts down.  To my knowledge, this is a new suggestion.

The vertical gradient of the BrCN mixing ratio implies a fairly short lifetime in the atmosphere on the order of days, which is argued to be due to some type of aerosol loss process.  Given the high reactivity of BrCN with a range of organic functional groups, it is not unreasonable to hypothesize that complex organobromine compounds are forming as a result.

Questions:

1. Were the calibrations for both CIMS instruments performed with mixing ratios close to the ambient values? That point said, a factor of two agreement between different instruments, ionization schemes, and calibration procedures is pretty darn good for a molecule of this type.  
2. Has anyone ever reported measurements of cyanide ion in ice/snow?
3. Was there any evidence of BrCN in heavily biomass burning impacted regions, where the HCN mixing ratio would be very high?
4. It is reasonable to assume that HCN is the reactive species for this multiphase chemistry. That said, is it possible that acetonitrile may also be reactive? Probably not, but just wondering.
5. My main question: The paper presents data of active bromine species, such as BrCl and BrO. Presumably the CIMS also measured signals for HOBr and Br2.  Why were those signals (even if not calibrated) not shown? It would have been interesting to see HOBr/BrCN correlations.
6. We know from (unpublished) experience that the AMS shows signal for aerosol bromine during ozone depletion events in the Arctic. To my knowledge, these signals have never been calibrated, but it might nevertheless be fun to look at the AMS signals to see if there is any evidence for where some of the Br is going, if indeed it is getting lost via irreversible reactions of organics with BrCN. For example, are there organo-N-Br ion fragments detected in the particles during ozone depletion events?

My recommendation is to publish this paper after the authors decide whether they want to address the above questions.

This manuscript describes the first observation of BrCN in the atmosphere, during the global NASA ATom mission. Measurable BrCN was found within polar (Arctic & Antarctic) boundary layers, and was found in the presence of decreased O3 (relative to background) and increased reactive Br species BrCl and BrO. These measurements are highly novel and provide new understanding of polar bromine chemistry. Detailed comments are provided below and primarily focus on data quantitation, additional experimental information needed, and needed clarifications.

In Section 2.3, the authors state that only m/z 190 (and not the second isotope at m/z 192) was used to quantify BrCN (Line 193). They say that they divided the signal by its isotope abundance (0.51) “due to the calibration method employed”. Please provide additional details about the calibration described on Lines 195-198. It is confusing then that the calibration was “compared to the sum of…m/z 190 and 192” Page 6, Line 198). It is quite a coincidence that the “slope of the correlation of the CIT-CIMS vs I-CIMS is 0.52 +/- 0.01” (Line 207) (i.e. within error of the isotope ratio), when the CIT-CIMS m/z 190 signal was divided by 0.51. Perhaps there was a simple mistake in the data processing? This calibration is critical to the results presented because this slope led to correction factors being applied to the BrCN data from both the CIT-CIMS and I-CIMS.

Sections 2.2, 2.3, and 2.4.1: Describe the aircraft inlets (lengths, flows, materials, temperatures, etc) used for the two CIMS instruments and chemiluminescence instrument, as many of the compounds being measured can be impacted by line losses. I expect that BrO could have significant line losses, which is why the high flow Eisle-type inlet is typically used on the ground (Liao et al. 2011, JGR, A comparison of Arctic BrO measurements by CIMS and LP-DOAS); this, in particular, is not addressed.

BrCN backgrounds were conducted by scrubbing the ambient air (Line 143). Please describe the scrubber (material, temp, etc) and its measured efficiency for removing BrCN and BrCl.

The authors state concern for sampling inlet reactions, previously reported by Neuman et al. (2010), as the reason why Br2 and HOBr were not quantified. However, the presence of Br2/HOBr, while impacted by sampling inlet reactions, is another clear indicator of active bromine chemistry. Neuman et al. (2010) previously reported Br2 as a lower limit of the sum of HOBr + Br2. I believe that it would be very useful for the authors to report their Br2 and HOBr data, even with high uncertainties, since observations of these species are limited and their presence would provide further support for the current work, especially since the authors propose that HOBr is a precursor to BrCN formation.

The authors discuss the potential for BrCN formation from reactions on the sampling lines. Is there any evidence of the presence of reduced nitrogen compounds on the sampling lines, or is there a simple test that could be done to evaluate this? Were the Br2 and BrO calibrations (noted on Lines 175-176) done using the aircraft inlet or just the instrument, as currently implied? If both HOBr and HCN flow through the inlet, is BrCN formed?

The methods section (Lines 163-165) states that “clear signals for ICN were observed in ambient air” but were not quantified. Yet, there is no mention of ICN in the Results. It would be useful to learn if ICN was observed concurrently with BrCN, or under different conditions, even it is not quantifiable.

For the ATom-2 Arctic flights on Feb. 18 & 19, 2017, the authors assert on Lines 293-294 that “There was essentially no photosynthetic activity at the Northern latitudes during this time”, and state Lines 296-298 that “there was Br activation initiated by O3-Br- chemistry…because there was insufficient photochemistry to carry the gas phase catalytic Br chemistry”. This is again repeated in the conclusions on Line 593. Yet, no observational support or reference is provided for these statements. These flights include MAs over BRW and SCC, where Polar sunrise occurs in late January, and by mid-February there are several hours of sunlight. Further, Raso et al. (2017, PNAS) and Custard et al. (2017, ACS Earth & Space Chem.) previously showed photochemical snowpack Br2 and I2 production at the beginning of February to mid-Feb in Utqiagvik (BRW). In addition, Pratt et al. (2013, Nat. Geosc.) showed that ozone reaction with bromide is far less efficient than snowpack photochemistry, and this is supported by the results presented by Custard et al. (2017). The authors should re-evaluate their explanation.

In Figure S4, BrCN increases up to ~40 ppt below 600 m and O3 decreases to ~15 ppb in this same altitude range, but this anti-correlation is not clearly described in the text on Line 297. The text also rules out a bromine explosion without O3 below 10 ppbv; yet, BrCl and BrO data from ATom-3 and ATom-4 are discussed without this full ozone depletion, which is inconsistent. Please clarify the text. Also, is information about the boundary layer height available for these data points?

Abstract: It would be helpful to expand the abstract to briefly explain how the conclusions presented on Lines 26-29 were obtained, including mentioning that box modeling was conducted. Further, it would be helpful to also mention the observed seasonality of the BrCN and its relationship to the other compounds measured that currently missing from the abstract but are key to the study (O3, CHBr3/CH2Br2, BrCl, BrO; also mention in the abstract that these were measured).

Both the abstract (Line 29) and conclusions (Lines 615-616) refer to condensed phase loss of BrCN resulting in either Br- or C-Br bonds. What is this based on, and where is it shown in the text?

Additional comments:

• Lines 32-37, 42-46, 93-96, 99-101, 188, 329-330, 430-432, 560-565, 608-609: Add references to these sentences.
• Line 43: Note that Pratt et al. (2013, Nat. Geosc.) showed that Br2 does not form on sea ice because the surface is buffered (Wren & Donaldson et al 2012, ACP). Also, Wang et al. (2019, PNAS, “Direct detection of atmospheric atomic bromine leading to mercury and ozone depletion”) is an appropriate reference to include in this sentence.
• Lines 82-92: It would be helpful if this intro discussion could be clarified, as it connects to later discussion of results. The following papers may be useful to consider incorporating: Swanson et al. 2007 (Atmos. Environ., “Are methyl halides produced on all ice surfaces? Observations from snow-laden field sites”), Rhew et al. 2007 (JGR, “Methyl halide and methane fluxes in the northern Alaskan coastal tundra”), Macdonald et al. 2020 (ACP, “Consumption of CH3Cl, CH3Br, and CH3I and emission of CHCl3, CHBr3, and CH2Br2 from the forefield of a retreating Arctic glacier”).
• Lines 131-132: Please define “MA”, “level legs”, and other common flight terms here and elsewhere to make the text more readable to the non-aircraft audience.
• Lines 149-150: Please provide information about the PTR-ToF, including the ion(s) used to detect ClCN.
• Lines 153-154: Were the BrCN and ICN in N2?
• Lines 160-161: Please add these data showing the sensitivity as a function of IMR water vapor concentration to the SI. Also, were the analyte ions normalized to I- or IH2O- prior to calibration?
• Section 2.3: Describe how the HCN calibration and zero measurements were conducted. How frequent were the “periodic zero measurements”?
• Lines 197-198: Define “IR” and “MS” acronyms, and check that other acronyms throughout the manuscript are all defined at their first use.
• Figure 2b: Given the instrument sensitivity issues on several ATom-4 flights (Line 268), perhaps it would be helpful to distinguish data below the limit of quantiation in the figure, as it is more difficult to distinguish the polar enhancement from this figure due to the data points that appear to be below the LOQ.
• Lines 275 and 278: Please state the dates of these BRW MAs for improved clarity.
• Lines 290-301: It would be helpful to add a map of the ATom-2 flights to the SI for context.
• Line 333: Please refer to the section where these atmospheric lifetimes are discussed.
• Line 334, Figure 4 slope, Figure S2 slope: Fix significant figures (e.g., should be 26.5 +/- 0.2 ppbv).
• Add references for R4-R6, S1-S4, EqS2
• Line 328-329: Discuss altitudes and boundary layer heights here for context since the figure is in the SI.
• Lines 335-336: Define the “intermediate polar boundary layer” and “middle of the polar boundary layer”.
• Line 349: Clarify whether the Southern Ocean was frozen.
• Lines 356-360: Refer to where these data are shown. If not currently included, please add as a figure in the SI.
• Lines 380-381: The authors are encouraged to also consider the work of Halfacre et al. (2014, ACP, “Temporal and spatial characteristics of ODEs from measurements in the Arctic”) here.
• Lines 498-499: Note that this statement does not appear to consider aldehydes or ketones.
• Section 4.1: The modeling of the pH dependence of BrCN production (Figures S17 and S18) is noteworthy, and these results warrant more discussion in the main text.
• Line 513: It is stated that “there are often clouds in the vicinity of the inversion”, but no reference is provided for this statement.
• Lines 524, S61-62: Fix reference formatting.
• Lines 566-568: Describe the details of this laboratory experiment in the SI.
• Lines 596-597: Provide the date for context.
• Lines S55-S56: Are both [Cl-] and [Br-] assumed to be 16 uM? No reference is provided, and previous measurements by Krnavek et al (2012, Atmos. Environ.) suggests that this assumption is not appropriate.
• Line 598: Change “ice and particle” to “ice, and/or particle”.y
• Line 605: Note that the sea ice surface is buffered (Wren & Donaldson et al 2012, ACP).
• Figure 1: State in the caption that this was during ATom-3.
• Figure 3: In the caption, provide the full date ranges for ATom-3 and ATom-4 for context, and also provide the general locations for the highlighted flights. Since a significant fraction of the data are below LOD and LOQ, please state these in the caption for context, or perhaps draw lines in the figure.
• The data in many of the figures is below LOD and/or LOQ, it would be helpful to indicate these values in the captions or show more clearly in the figures.
• Figures 11, S7, S9, S11, S19: In the captions, state the location where these data were collected.
• Figure S2: Add error to the slope fit through 0.
• Table S1: Define abbreviations in the caption.
• Table S2: My understanding from Line 298 is that the LOD for BrCN during ATom-4 was higher. Please clarify that here. Also indicate the m/z used for quantitation of each compound.