The manuscript "Urban inland wintertime N2O5 and ClNO2 influenced by snow covered ground, air turbulence, and precipitation" describes a set of measurements taken during winter in southern Michigan (USA). Observations of N2O5 and ClNO2 are needed in order to achieve a better understanding of the chemistry of these species, especially during winter, a known undersampled season. The focus of this paper on the effects of micrometeorology provides a novel, and very interesting, look at the ClNO2/N2O5 system. The paper is generally well written and the subject is within the scope of ACP. I recommend publications of the manuscript, after the authors have addressed the following points.

MAJOR COMMENTS

Most of the analysis presented in this paper uses 30 minutes averaged data. Is this appropriate for this type of study? For example, the periods of fog and snowfall discussed on pages 14-16 are of the order of 1 hour, so maybe higher frequency data would provide more accurate information. I think the authors should comment on this point early on in the paper.

In section 2.2 the authors say that Cl2 and HNO3 were being measured. However these species do not seem to be mentioned in the rest of the paper. If the reason is that they were not observed, I suggest this part of the method is removed. If they were observed, I wonder why they were not used in the subsequent analysis.

In section 3, it would be good to better define the conditions encountered during the campaign. From figure 1, it seems there was only 1 case of clear sky, 1 of snowfall, 1 of fog and 1 of rain during the entire period, but I suppose these are only selected case studies. What were the conditions on the other days? How were the case studies selected (i.e. are they truly representative of the respective conditions)? Related to this point, it should be clarified how are the statistics in the first part of section 3.1 - including table 1 - calculated: do they refer to the 4 case study nights only, or include other similarly classified periods? This is important to understand how representative are the numbers and how robust is the analysis.

I find the discussion in section 3.2 (effects of turbulence) a bit lacking, in the sense that it is not immediately clear what the authors think is the effect of turbulence on N2O5 and ClNO2. Sure, high or low turbulence results in higher or lower concentrations, but why? Is it due to deposition, advection or some other physical process? Likewise the first part of section 3.4 (page 21) can be a bit expanded: how do all the factors (turbulence, ground conditions, etc...) tie together and relate to the observed values of N2O5 and ClNO2? A short summary at the end of each section would help driving the point home.

MINOR COMMENTS

line 161: do these times correspond to sunset and sunrise?

lines 202-203: doesn't this introduce a bias? Isn't it better to exclude these data from analysis?

lines 215-220 (and elsewhere in section 3.1): are the 18:00-8:00 averages discussed here?

lines 365-367: if there is no significant difference between high and low turbulence, I think it is a bit misleading to say that values are on average a bit higher with high turbulence. More in general, can the authors speculate on why turbulence does not seem to affect N2O5 levels before 2:00?

table 1: maybe add bare/snow ground?

table 2: add the expected scavenging coefficient based on solubility? Otherwise a statements such as line 285 and 318-319 makes little sense.

Kulju et al. present measurements of N₂O₅ and ClNO₂ in Kalamazoo, Michigan, from January - February 2018. This paper follows up on earlier papers on the same data set (McNamara et al., ACS Earth and Space Chemistry, doi 10.1021/acsearthspacechem.0c00317, 2021 and Chen et al., ACS Earth and Space Chemistry 3(5), 811-822, 2019). In this paper, the authors focus on how meteorological events (fog, snow and rain) and turbulence affected N₂O₅ and ClNO₂ concentrations, which are interesting and understudied topics. Low mixing ratios of N₂O₅ and ClNO₂ during precipitation events have been observed before; this paper aims to extend these observations with simultaneous measurements of friction velocities using a sonic anemometer.

The paper is written well and thorough in citing related work and appropriate references. However, the analysis is not robust.

In general, concentrations of molecules in air change because of chemical production (P), chemical loss (L), and transport (E) terms. 

Kulju et al. present an analysis that essentially neglects the P and E terms and attributes observed rates in concentration changes entirely to L. It is inappropriate to neglect transport during precipitation events as a possible reason for concentration changes via rapid vertical mixing - see, for example, Winkler et al. Radiat. Environ. Biophys., 40, 115-123, 10.1007/s004110100096, 2001, who observed this effect for radioactive tracers. Further, the L term is, incorrectly, attributed in its entirety to scavenging by precipitation even though other reactions may contribute such as the indirect loss of N₂O₅ via NO₃ chemistry (see, for example, the 'steady state lifetime' approach pioneered by Brown et al., J. Geophys. Res., 108, 4539, 10.1029/2003JD003407, 2003, and J. Geophys. Res., 114, D00F10, 10.1029/2008jd011679, 2009 (equation 6)). It would have been useful for the authors to explore the use of box models to better constrain the precipitation loss term. Unfortunately, it does not appear that the necessary auxiliary data (such as concentrations of NO and NO₂) are available to extend the analysis in this direction.

As already stated, the data set has already been partially described elsewhere, such that this manuscript's value rests largely with its analysis, which is in poor shape. Considerable and major revisions would required to make this manuscript acceptable for publication. I hence recommend rejection of this article, though it would be acceptable imo for the editor to reconsider a revised version if the authors believe they can address the issues raised below.

Major comments

(1) One cannot simply compare N₂O₅ (and ClNO₂) abundances with meteorological conditions as presented in this manuscript (rain, snow, fog - Figure 2, lines 215-216; turbulence - Figure 4, line 360) unless the rates of NO₃ production, P(NO₃) = k₄[O₃][NO₂], the NO₃ loss rates to VOCs and NO, temperature and [NO₂] (which affect N₂O₅ concentration via equilibrium  K₃), and aerosol surface area chloride abundances were of similar magnitude for these events. It is not at all likely that all of these variables were identical. In fact, Table 3 shows that temperatures were very different, indeed.

(2) The calculation of "gas-phase scavenging coefficients" (Table 2) is questionable as one needs to assume the absence of production and transport terms that also affect mole ratios. The examples cited (lines 280-283) are for molecules (SO₂ and NH₃) that are relatively unreactive and are mainly primary in origin, but that is not the case for ClNO₂ and certainly not for N₂O₅. Furthermore, the analysis is not robust because vastly different values are obtained depending over what time period the scavenging coefficients are calculated. For example, the data in Figure 3d show an increase in ClNO₂ mixing ratios during a rain episode - does this imply that the scavenging coefficient would be negative, and the rain is a source of ClNO₂?

(3) A large portion of the analytical methods, data set and analysis have been presented elsewhere. The authors should avoid unnecessary repetition (e.g., line 128 - section 2.2. N₂O₅ and ClNO₂ measurements using chemical ionization mass spectrometry (CIMS)). Rather than restating everything here, please simply cite the earlier paper(s) where possible, briefly summarize and note deviations from the earlier work.

(4) Throughout the manuscript, there are statements such as "N₂O₅ was fairly stable" and "ClNO₂ increasing steadily", which is grammatically incorrect since molecules cannot be referred to in this way, only their abundances. Consider rephrasing to "Mole ratios of N₂O₅ ..." or "Mixing ratio of ClNO₂".

(5) The manuscript would benefit from more data as only one of each snowfall, fog and rainfall events were described in the main paper yet more were observed (Figure S2). It is thus unclear how representative the events selected in the main manuscript are.

Specific comments

lines 153-54. "N₂O₅ and ClNO₂ were calibrated offline relative to Cl₂ as described in McNamara et al. (2019b)." A better way to say this is "the instrument response for N₂O₅ and ClNO₂ was calibrated ..." as a compound cannot be calibrated.

McNamara et al. (2019b) did not describe a calibration "relative to Cl₂" which would not be accurate since Cl₂ does not convert quantitatively to ClNO₂ (and cannot be used to calibrate for N₂O₅); instead, they described a titration method for N₂O₅ and thermal dissociation method for ClNO₂.

Please clarify how response factors were obtained in this work and state how accurate the derived calibration factors were.

N₂O₅ is not quantitatively transmitted through inlets. What was assumed for its inlet transmission efficiency? How uncertain and variable is the inlet transmission efficiency?

line 164. "Cl₂ was monitored" appears under the heading "N₂O₅ and ClNO₂ measurements ..." Please address this (minor) organizational issue.

line 226 Table 1, caption "±95% confidence interval". These are very small confidence intervals, too small to be credible in my opinion. How were the CI calculated? Do the values in the table take uncertainties in calibration factors and inlet transmission factors into account, or are they were merely calculated based on (averaged?) measurement precision?

line 253 / Figure 3. One of the axis titles is missing an oxygen.

For the snowfall case (Figure 3b) there appears to be a sustained loss throughout the episode with a consistent loss rate coefficient, but for the other cases (fog - 3c and rain 3d) the mole ratios sometimes increase during the episode. Please explain why this might be and how this affects the subsequent analysis.

line 280-281. "one hour fog period". Where all scavenging coefficients calculated over 1-hr long periods? How did the authors decide over what periods the loss rates should be calculated?

line 289 / Table 2. Uncertainty estimates should be added to Table 2. Please indicate (in Figure 3) over what periods the scavenging coefficients were calculated, as the derived values depend on it.

line 300. "Although precipitation rates were used to inform time periods used for calculations during the rainfall case, a more thorough characterization of scavenging with respect to precipitation rate and intensity is beyond the scope of this discussion." This would have been useful, imo.

line 360. Here, N₂O₅ mole ratios are compared to turbulence conditions. However, this analysis is not sound as it is not clear if the production from oxidation (via reaction of NO₂ with O₃ to NO₃ and subsequent reaction with NO₂), sinks (e.g., aerosol surface area, VOC abundance) and temperature (which shifts the NO₂/NO₃/N₂O₅ equilibrium and has a large effect on N₂O₅ concentration and loss rates) are identical for the high and low turbulence cases.

line 464. The N₂O₅ mixing ratios observed were small; how much additional nitrate would be expected if all of it were taken up (i.e., if the production of N₂O₅ via NO₃, i.e., R4, were integrated)?

line 565 - strike "Received"

Figure S1 - please state uncertainty of the slope. What is the theoretical value based on? Note that the ³⁷Cl :³⁵Cl isotope ratio is known to higher precision than shown.

The manuscript by Kulju et al. presents CIMS measurements of N2O5 and ClNO2 made during a winter field campaign in a continental region. They compare mixing ratios during different weather, ground cover, and turbulence conditions. They calculate the first N2O5 and ClNO2 gas-phase scavenging coefficients for rain, snow, and fog. These measurements aid in our understanding of N2O5 and ClNO2 chemistry and their impact on air quality, particularly for the relatively understudied winter season. I have some concerns that should be addressed prior to final publication.

General comments:

Why did the authors choose to use 30-minute averages to analyze their data? It seems that faster data would be useful for this type of analysis. Please explain.

Generally, there is a lack of information about what criteria were used to classify the different conditions. This should be added. There is also a lack of information about the number of samples used to assess each condition. For example, in Section 3.1, mixing ratios for each type of weather condition are compared graphically and statistically, but the reader has no indication of how many events or 30-minute time points were considered for each condition. It would be useful to include this information throughout the manuscript: the overall clear/rain/snow/fog conditions (e.g. in Table 1), the low/high turbulence conditions (e.g. in caption of Figure 4), ground cover (e.g. in caption of Figure 5).

As I was reading Section 3.1, several questions arose about the impacts of meteorological conditions, many of which were addressed in Section 3.4. To reduce confusion, I suggest adding text to Section 3.1 indicating that the effects of RH and T will be discussed later. It would also help the reader to combine Tables 1 and 3 as I found myself flipping back and forth between the two. One of my questions in Section 3.1 that was not answered in the manuscript was the impact of wind direction (if any) on the observed differences in N2O5 and ClNO2 under different weather conditions. This should be added to the manuscript.

Specific comments:

Line 69: Define NOx at first usage (line 39)

Line 73: Should be equilibrium arrows (can be inserted in Word by typing 21cc, then pressing ALT and “x” simultaneously)

Line 187: Where was LiF added? Was it an internal standard for chromatography and/or particle sampling?

Figure 3: Check y-axis label in Figure 3a

Table 2: Present the scavenging coefficients in the table in the same order as they are discussed in the text.

Line 265: Is this different from the dimensionless Henry’s Law coefficient (or air-water partitioning coefficient, K(AW))?

Line 330: Would be clearer to define the trend (i.e. thickens with increasing temperature). Listing the average temperature during the snowfall case in the text here would help to clarify.

References: McNamara et al. 2020a and Sander et al. 2015 are missing from the reference list.