This work presents novel measurements of the d¹⁵N and D¹⁷O of gaseous NO₂ and total nitrate (HNO₃ + particulate NO₃^-) and utilizes the measurements to quantify the nitrate formation pathways based on the assumption that local chemistry determines the isotopic composition of the nitrate collected. This is the first study to present simultaneous isotopic observations of both NO2 and nitrate at a sub-daily scale. This type of work can push forward the field in important ways, better constraining the oxidation processes involved and testing our understanding as depicted in atmospheric chemistry. It is highly relevant for the readership of ACP. Overall, the quality of the writing and presentation is good/fair. The overall work and conclusions drawn would benefit from some revisiting and rewriting. This work needs to be presented as the case study it is. The measurements are extremely limited - 2 single days of sample collections in February in a fairly unique location (valley surrounded by mountains). In the end, the work is an important demonstration of what could be done with this novel approach, but we do not learn anything new about urban atmospheric chemistry and rely heavily on a priori assumptions of what is already known and then conclude that this chemistry indeed does predict the isotopes. Still, the dataset is novel and represents a step forward in these types of studies. The manuscript needs necessary revisions to improve the scientific understanding and expression in the work – there are a lot of areas where clarity is needed.

General comments:

#1) Two new works that should be digested/interrogated by the authors and incorporated into the work here are listed below. These should provide fodder for discussion of seasonal difference as well as additional datasets that may be more useful to compare with than is currently in the manuscript since this is also a mid-latitude site with significant diurnal variability.

Bekker, C., Walters, W.W., Murray, L.T., Hastings, M.G. (2023), Nitrate chemistry in the northeast US part I: nitrogen isotope seasonality tracks nitrate formation chemistry, Atmospheric Chemistry and Physics, 23(7), 4185-420, https://doi.org/10.5194/acp-23-4185-2023.

Kim, H., Walters, W.W., Bekker, C., Murray, L.T., Hastings, M.G. (2023), Nitrate Chemistry in the Northeast US Part II: Oxygen Isotopes Reveal Differences in Particulate and Gas Phase Formation, Atmospheric Chemistry and Physics, 23(7), 4203-4219, https://doi.org/10.5194/acp-23-4203-2023.

#2) A few aspects related to methodology – evidence needs to be provided that under the conditions in this study that both HNO3 and particle phase nitrate are quantitively collected. The references cited do not actually prove this, but rather suggest that conditions are alkaline enough that this “should” be true. This can have an important impact as there is large fractionations between the gas and particle phase nitrate. This is ignored in the current study, presumably because of the assumption that total nitrate is collected. But if the particles are decoupled from the gas upon collection, or upon transport, then this could indeed be making a difference in the dataset here. This topic should be better addressed in the manuscript (see general comments below tied to line/section numbers). See for instance Geng et al. (2017) treatment of this (this work is already cited in manuscript) and Li et al. (2020) (citation below).

Also, how is it ensured that there is no exchange of water with the analyte nitrite (ie NO2)? And are the oxygen isotopes scaled to the nitrate reference materials or only the nitrite reference materials? Exchange is relatively fast for nitrite in solution (even in frozen solutions) and has been the subject of corrections and difficulties in several studies (see for instance Casciotti and McIlvin, 2007; Wankel et al. 2009).

Casciotti, K. and M. McIlvin (2007), Isotopic analyses of nitrate and nitrite from reference mixtures and application to Eastern Tropical North Pacific waters, Marine Chemistry, 107(2), 184-201, https://doi.org/10.1016/j.marchem.2007.06.021.

Li, Z., M.G. Hastings, W.W. Walters, L. Tian, S.C. Clemens, L. Song, L. Shao, Y. Fang (2020), Isotopic evidence that recent agriculture overprints climate variability in nitrogen deposition to the Tibetan Plateau, Environment International, 138, https://doi.org/10.1016/j.envint.2020.105614.

Wankel, S.D., et al., (2009) Sources of aerosol nitrate to the Gulf of Aqaba: Evidence from d¹⁵N and d¹⁸O of nitrate and trace metal chemistry, Marine Chemistry, doi:10.1016/j.marchem.2009.01.013.

#3) The crux of the interpretation and conclusion rely on NO2 having a short lifetime such that production of nitrate from NO2 is controlled by local chemistry. The lifetime of NO2 photolysis is calculated, but the lifetime of NO2 loss (as nitrate) is not. The calculation of D17O-nitrate relies on D17O-NO2. At each time step (3 h interval) the nitrate is calculated from the NO2. A weighted average of the D17O-NO3- values is then taken and compared to the daytime average after the first 3 h interval. This 3 h offset is suggested to take care of the time to convert NO2 to nitrate. The weighting of each 3 h interval for NO3- is based on [NO2]*J(NO2) as a proxy for OH production. These values also represent a time when NO2 is being photolyzed, not converted by OH to nitrate. When the nitrate D17O calculated values match with the observations it is taken as proof that the short lifetime is robust. When they do not agree, there has to be another (non-local) source of nitrate. But the authors started with the assumption that at each time interval the D17O-NO2 is relevant to the D17O-NO3- collected. This all ends up a bit messy (albeit complex). It seems that it might make more sense to calculate an average (weighted) daytime D17O-NO2 and then calculate an average D17O-NO3- from this weighted NO2. There is not a direct link between the simultaneously collected NO2 and NO3- -- in other words, the NO3- collected in that time interval cannot be from the NO2 that was also collected in that time interval. So really what can be tested is whether there is diurnal variability in the signals and then for the comparison purposes use the average D17O-NO2 to predict average NO3- and see how that compares with the observations. If the authors disagree, then the approach they are currently taking needs to be better justified.

#4) The presence and photolysis of HONO is used in the discussion of the oxygen isotopes to infer a major source of RO2 radicals in wintertime. HONO, however, is not brought at all into the interpretation of the d15N. Both the d15N and d18O are impacted by the oxidation processes because of the fractionations detailed by the authors. So an explanation for one isotope necessarily impacts the interpretation of the other when that species can also be source of N.

Major comments:

(some of the correction suggested here are minor but change the meaning of the sentence or question the meaning of the phrasing so is scientifically relevant versus the minor technical corrections below)

Abstract:

Lines 17, 23-24: add n= # of samples when reporting on the deltas measured

Lines 16 and 24-25: the meaning of “important diurnal variabilities is unclear, please rephrase to be quantitative or use a better description than just “important”

Line 19: rephrase “NO3- local mass balance equations” --

Line 30: “particularly in urban environments in winter” – measurements represent winter only

Introduction:

The introduction well covers most of the important literature on the topic, but is really too expansive for the purposes of this case study. The introduction should focus on atmospheric chemistry in urban regions under the conditions in this study. It would also be useful to refer directly to the reactions as they are being described to keep readers following the text and the series of reactions.  All of the chemistry presented as “the important reactions” are based on global studies and may not be representative of chemistry in urban areas. It should also be noted that only one of the reactions includes a phase (e.g., HNO3(g)) and this should be made more consistent throughout the reactions. Furthermore, the titration of ozone should be explicitly discussed in the introduction as this is a major aspect of the nighttime chemistry in regions where there are continuous, fresh NO emissions at night (ie urban areas).

Line 60: be more specific quantitatively about what “the lowest temperatures” means

Line 75: “…NO3- is usually investigated in light of its 17-O excess” – there are many studies that utilize d18O AND d17O because there are uniquely enriched in ozone, in addition to a focus on D17O. It is important to also incorporate the two studies mentioned above, one of which includes D17O and d18O observations in both urban and suburban areas of the US. Please rephrase this line.

Line 87-88: The mention of ice cores and the lack of definition of AOC here is strange. This is not connected at all to the current study or the conclusions that can be drawn from the 2 days of measurements in France. Suggest removing this line and any discussion of ice core related data/conclusions.

Line 95-104: This section should include an overview of the work of Albertin et al, 2021. The fact that lower values were found at night challenges previous understanding based on Morin et al (2011). This is not discussed in the current work, but should be presented here or summarized based on what appears in Albertin et al, 2021 to better set up the expectations for diurnal variability in the urban sampling site.

Line 109-110: This line does not include the fact that nitrate is also highly susceptible to large fractionations between the gas and particle phases. Why is that not included here and never discussion in the discussion? (see General comment and citations above)

The “during transport of NO3- in the atmosphere” should be a #3 here as it represents different process/processes than the prior 2 examples.

Line 113: remove or rephrase “which seemingly ignore the potential impact of post-emission fractionation” or find better references. The Hastings et al 2009 paper does not seem relevant here (it is based on ice core reconstruction – not at all comparable measurements to those taken here). Altieri et al. 2022 does not simply ignore this.

Methods:

Line 141: Given that the area was partly covered in snow, and Savarino’s rich literature on the impact of photolysis on snow nitrate and the release of NOx from this source, with very depleted isotopic ratios. Why is this snow-sourced NOx not included in the discussion here?

Lines 141-145: Evidence must be provided to support the assumption that total nitrate is collected (HNO3 gas and particulate nitrate). The studies cited do not prove this. This is an assumption made, and under the conditions in those studies, the alkaline quality of the aerosols was suggested to scavenge the HNO3 onto the filters. Is this true in the case study here?

It should be made clear here also what is being collected – i.e. total suspended particles or PM10 or ?

For the preservation of samples prior to isotopic analysis, how is it ensured that there is not exchange between the nitrite analyte (for NO2) and water? This has been shown to be extremely important and would yield incorrect results since the samples would no longer be representative of the atmosphere (see General comment and citations above)

Line 155: This first sentence is difficult to understand. What does “corrected by the arithmetic mean” mean? Was it subtracted from all results? It is stated that is represents 8% -- 8% of what? The average total nitrate collected? Or is this the average of the average based on comparison of the blank concentration to each sample’s concentration? It would be better to state the average concentration of the blanks here, perhaps compared against the overall average nitrate concentration, and more clearly state how this was “corrected” for to make this explicitly clear.

How many field blanks were collected? How were they collected? The impact of a high blank on one collection period is discussed several times later in the manuscript so clarity is needed here.

Line 177: Table S4 should be Table S3. What are the average measurement uncertainties based upon? Repeated measures of reference materials? And how many times were run? Additionally, it should be made clear here in the methods whether both nitrate and nitrite reference materials are necessary to be included in the separate runs for NO2 (as nitrite) and NO3- (as nitrate).

Line 183-184: Please clarify the “blank” here. Is this the field blank? Above it is stated that the blanks represented 8+/-9% so how is the mean here now 4%? Or is the previous blank about nitrate instead of nitrite? Were nitrate blanks also tested and what were the results?

Section 2.4.1: Please make it clear that D17O is only conserved in processes that are fractionating…i.e., this would not be true if exchange were to occur.

Line 224: What is the lifetime for NO2 during the day against loss? Why is this not also calculated? The table states that the lifetime against photolysis is 5 min, what is the lifetime against conversion to nitrate? The case for daytime comparison with a three-hour difference (i.e. NO2 now, compared to NO3- that was collected three hours later) needs to be better justified. If the NO2 lifetime is only minutes (Table B1) than the time frames should be the same for comparing NO2 and NO3-.

This is very important. The lifetimes calculated are based on chemistry alone and do not seem to include wind speed or direction. For nighttime, it is stated that NO2 has a 10 hour lifetime against loss (via deposition or chemistry). Therefore, the authors compare a single average nighttime measurement of NO2 to NO3-. In a closed system this would absolutely make sense. But in an open system, how can we ensure that the NO2 collected during that time represents THE NO2 that was converted to the sampled NO3-? The authors make the assumption that this is true, then prove it by saying they can calculate the NO3- based on the measured D17O-NO2 – this seems circular.

Section 2.4.2 – I suggest the authors consider moving up the discussion of the Freyer, 1971 study in discussing the framework for interpretation of the isotopes. This is the closest relevant study to the current work for nitrogen isotopes.

Why is the fractionation of HNO3(g) versus NO3-(p) ignored in this section? It should clearly be stated why this is not included. While the collection of total NO3- could mask this fractionation, this would only be the case if all of the nitrate gas and particles are locally derived. In other words, if gaseous nitrate is taken up on particles (e.g., see lines 326-330) transported to the observation site and collected as a sample, it will reflect fractionation of HNO3(g) versus NO3-(p) that may have not occurred locally. How is this accounted for? This seems like it could be particularly important in the SP 2 case.  

Line 268: what is the “daytime NO2 chemistry lifetime” used here?

Section 3.1 – This section is largely discussion, not just results. It is indeed important to characterize the general atmospheric observations but the section includes a lot of “likely” descriptions of how to explain the atmospheric observations, not simply a presentation of the results. The section title should be modified to Results and Discussion or the discussion points should be moved to the appropriate section.

Lines 305-310: As mentioned above, it would be useful to discuss ozone titration in the introduction with a more focused introduction around urban day and night NOx chemistry. Most of the section 3.1 is really discussion of the results, not results. This should be amended. Is it a hypothesis that O3 titration occurred at 16:00 LT or do you have evidence of this?

Line 318: “It turns out that a Saharan dust episode began on February 23 (Fig S3 in the Supplement.” This is simply stated as fact. What is the evidence for this? In the Fig S3 a more impressive dust event occurs on Feb 7^th and looks like a short term “event”. The time noted on the 23^rd does not have a clear start and end and looks more like a large background enhancement. No transport information is provided (e.g. back-trajectories or the like). So how is this event known to be of Saharan dust origin? It is stated that this should lead to increase in coarse materials and high concentrations of alumino-silicates and potassium and calcium  -- were these measured on these samples and can be shown as verification?

Line 329: “…the origin of NO3- during SP 2 at our site remains unclear…” – why is this case when line 318 stated as fact that it was Saharan dust? All of this needs much clarification!

Lines 352-365: Here it is stated that the conditions for Chamonix and Beijing are significantly different. But comparisons are made anyway. So this comes across as convenient. For seasonal considerations, this study is limited to only 2 days of wintertime observations. Suggest you include comparison with Kim et al., ACP, 2023 to suggest patterns of expected seasonal behavior for mid-latitude conditions.   

Line 372: The expectation that the d15N would be similar with Walters et al (2018) does not seem justified. Those measurements were made in a very different setting (ie not a valley surrounded my mountains) and during the summer. Comparing with Freyer et al would make a lot more sense. Commenting on the range and variability from different studies also makes sense, but a direct comparison with Walters does not seem appropriate unless it is justified.

Line 419: This is a bit hard to follow. Prior to Equation (4) RO2 is defined as RO2 = HO2 + CH3O2. Equation 4 thus does not include reaction with HO2 separately. But this line makes it appear as if RO2 is being calculated from HO2 alone. Please clarify.

Line 421: The calculated RO2 values are NOT consistent between cases A and B. This is even less true for SP2 than SP1. On average, and considering the variability one could argue they are not statistically significantly different, but at each time interval there are significant differences between case A and case B. This is noted in the following sentences, but this should be made clear from the start when you are discussing a mean versus a particular time period.

Then again on line 438 it is stated the “closeness between RO2 estimates using D17O(NO2) observations and those from empirical calculations…” – this is simply not true. The concentrations calculated for the different cases are very different so deriving conclusions based on their sameness is inappropriate. Further, the sensitivity of D17O-NO2 to the chemical dynamics is not surprising and here it is what is being both hypothesized/tested and concluded, which is circular.

Line 471: the sentence beginning with “To note…” does not make sense. Please rephrase as I am unclear on the scientific meaning here. The contribution of blank versus sample should be better stated again. Not sure what “pondered by the mean” means.

Lines 476-478: I am interpreting here that the emphasis is on “processes” meaning the same expected chemistry for both nighttime sampling times. This seems overly simplified given that SP2 was impacted by dust events and SP1 was not. Is there no impact of dust on the nighttime chemistry? This should impact the reaction rates for N2O5. But also note that not all reactions are included in the case study here – for instance NO2 hydrolysis, which could be impactful with heavier dust loading (see Alexander et al., 2020 for example). I think a bit more clarity is needed to separate the two case studies. If differences in conditions between the two sampling periods (i.e. gas and particle concentrations) are not being considered in the context of the chemistry then it challenges the conclusion that transported nitrate has to play a role in explaining the nighttime SP2 data. (Note that I think the additional nitrate from aloft is a good explanation for the higher than expected D17O, but this needs to be set up better).

Line 515-516: Needs clarifying. The nitrate does not represent “deposition” so this phrasing needs to be changed here and through the rest of the manuscript. The samples represent aerosol (+gas) loaded onto a filter – so this does not represent deposition. Perhaps rephrase to “…during SP 2 may have increased the NO₃^- loading aloft, in comparison to SP1.“

Section 4.3

The interpretation of the oxygen isotopic composition discussed the likely potential for photolysis of HONO to add significantly to the local oxidant budget. This is not mentioned at all as part of the nitrogen isotopic composition discussion, but this process would also produce NO with a very different d15N. Furthermore, vehicle emissions could also be adding HONO, given that they are concluded as the primary source of local NOx and NO3-. These pathways are neglected in the chemistry calculations and HONO impact on the d15N assumptions should be discussed or justified as to why be ignored.

Line 554-555: This result only holds for GP2, i.e. only EIE regime. This sentence should be more specific.

Line 588-589: In fact, Miller et al., (2017) in an on-road study showed no dependence on most of these factors (except heavy emitters, e.g. presence of diesel trucks). Heaton, 1990 only measured vehicles with none of the modern catalytic convertor technology. Felix and Elliott (2014) measurements were taken in a tunnel and are not representative of on-road traffic. Walters et al. represents tailpipe measurements. Miller et al. and Zong et al. represent on-road and near-road sites. Please use more consistent studies and/or justify the use of averaged values across studies that are not similar and/or not representative of the current environment being studied.

Line 598-602: Some care needs to be taken here. It only takes about 30-50 seconds for an engine equipped with a catalytic convertor to be “warm” – in fact in the Walters’ study Figure 2, the NOx emission plateaus after ~50 seconds. It is challenging to believe that this is having such a large impact on early morning versus later daytime values given the 3-hour time period over which the d15N values are collected. Perhaps the authors could do a back of the envelope type calculation to confirm whether this suggestion is valid. Cold engines will emit very high concentrations of NO for a very short period, so could potentially impact NOx loading – is there evidence of this in the gas phase measurements? i.e. given similar traffic conditions in the early morning and late in the day the concentrations should be much higher under “cold start” conditions.

Line 601: “removal” should be “replacement” (not sure how NOx removes NOx in this scenario?)

Line 662: add “local” as in “…independently of the local NO2 to NO3- conversion processes.”

Line 663: In the framework here, dry deposition takes NO3- out of the system so please rephrase. Do you mean that nitrate production is more likely or do you mean that the particle nitrate is heavy enough to sink and mix into the boundary layer?

Line 682: perhaps add “…to test the hypotheses raised here.” At the end of the line? It’s not clear that there is evidence for a vertical gradient (yet) though the hypotheses raised in this work are certainly compelling.

Technical comments:

Line 33: add () around NO and NO2, i.e. (NO) … (NO2) as they are being defined here

Line 49: the Leighton reference has a typo with the added “1961 citation”

Line 50: suggests adding in reaction #’s in text and () around HO2 and CH3O2. For example, “This cycle can be disturbed by peroxy radicals (via R4; RO2 = hydroperoxyl radical (HO2) + methyl peroxy radical (CH3O2)) leading to formation of O3 (via R2) (Crutzen, 1979).” Similarly R1-R3 should be called out in the text on lines 46-49.

Line 58: “Reaction R7” should be just “R7” (ie R implies the word “Reaction”)

Line 101: “Authors” should be “The authors” or given the overlap in authors perhaps “We” ?  

Line 129: rephrase “The first study case” to This case study is the first to carry out concurrent multi-isotopic….”

Line 133: “conduction” should be “conducted”

Equation (6) and (7) should contain the subscripts day and night for NO2 as well. i.e. make it clear that for the nighttime nitrate the NO2 comes from Eq. 5. Can you also clarify why equation 5 uses D17O-NO2 at night rather than D17O-O3? The only production channel at night is assumed to be NO+O3, with presumably 1 oxygen from ozone and 1 from NO. Is it just implicit that D17O-NO2 formed at night = D17O-O3? This seems weird to not make this explicitly clear.

Line 246: “later” should be “latter”

Line 246-247: This should be referenced to Li et al (2020) here. (it is not original to this work here)

Line 250: “of the fraction of NOx in the form of NO2” is awkward phrasing, please rephrase.

Line 286: “schematises” is not correct – rephrase.

Line 275: [NO2] in the denominator should be [NO], correct?

Line 309: suggest rephrasing to “…recovers and stay relatively low throughout the night…”

Line 344-345: rephrase here – D17O-NO2 is ONLY similar for two of the time periods, not during the whole daytime. The observations at 13:30-16:30 at SP2 are questionable, and then the 16:30-18:00 samples are 3 per mil different. So overall, they are more different than similar for these time periods.

Line 358: Is this Zhang et al, 2022a or 2022b?

Line 368: add “from” after “Aside” – i.e .”Aside from the intrusion…”

Line 385: “targeted” should be “found”

Line 392: Add “observed” in the figure caption to be sure reader follows that the D17O values here are observed not calculated.

Line 412: this could use some rephrasing – it sounds here as if ozone were high over the whole time period. Perhaps rephrase to make clear that ozone peaks at 16:30 LT but is not high through the whole time from 10:30 – 16:30 LT.

Line 420: The equations number in the text do not match those in the Table 1 footnotes.

Line 433: rephrase to “could be a significant source of VOCs….”

Line 423: “…could be due to the important blank associated with this sample.” The real issue here is the % contribution of the blank versus sample so perhaps rephrase to make that clear; currently it is not clear what “important blank” means.

Line 427: “The highest contribution of RO2…is correlated with the highest NO levels.” For this to be stated it must be shown to be true. The highest NO levels occur around 10:30-11am at both SP1 and SP2. This is not the time of the highest RO2 concentrations. This IS the time of the lowest T(NO+O3) which means that the relative contribution of RO2 is high, but this is not the time when NO levels are highest. Note too that nothing is shown in terms of the sensitivity of D17O to RO2 concentration – i.e. calculated D17O values are not directly compared with the calculated RO2 concentrations.

Line 440: rephrase to “be used to improve understanding of the oxidation processes …”

Line 458: D17O(NO2) should be D17O(NO3) here (with the subscript NO2+O3)

Line 471: the formatting for the D17O changes here

Line 497: “in” should be “on” average

Line 498: add were as in “values were more homogenous”

Line 499: “attitude” should be “altitude”

Line 525: “informations” should be “information”

Line 564: the overall mean value stated here does not match what is in the Table.

Line 585: Different papers seems to use different values for biomass combustion. Looking back at Fibiger and Hastings, 2016 the results indicate that latitudinal difference in d15N biomass exist and thus so should latitudinal difference in d15N-NO from this source. Is that how Martinelli et al., 1999 is being used here? Please explain the values used if they do not directly represent the citations.

Line 627: what is the meaning of “faction” here?

Line 635: rephrase to “associated with a KIE effect…”

Line 637: rephrase to “with the OH pathway”