Review of “Characterizing emissions, chemistry, and health …”  by Jin et al:

In this manuscript, Jin et al describe observations and modeling for a one-month smoke influenced period in Missoula MT.   The manuscript covers a lot of ground.  Some of this is done well and is a useful contribution, but other aspects are not strong.   The areas that I found to be strong (or could be) are:

1. The range of VOC observations.
2. The smoke day identification scheme.
3. Cancer risk calculations (although this is not adequately described).
4. Role of rainout in removing PM₅ (barely described, but this could be a very interesting section). This last point was mentioned only briefly (line 450), but is potentially an interesting analysis.  There have been some prior debates over the possibility of “low PMsmoke events”, and these results seem to support this.  To my knowledge, there is almost nothing published on this, so a good analysis on this point would be a useful contribution.  

The aspects that I found to be weak or not useful contributions were:

1. The O₃ observations (possible bias?) and analysis.
2. The GEOS-Chem analysis.
3. The ER/EnR analysis.

Starting with the O₃ observations, the authors should know that the Thermo-Fischer 49i instrument used here is known to suffer from strong positive bias in smoke.  See these refs:

https://doi.org/10.5194/amt-14-1783-2021 and https://doi.org/10.5194/amt-15-3189-2022

It is possible that the operators have fixed this problem, but at minimum, the authors should describe the bias issue and what, if any, steps were taken to minimize this bias.    I recognize the results shown (low O₃) seem inconsistent with a positive bias, but nonetheless, the issue should get discussed. 

Regarding the O₃ analysis, the authors have too few observations to draw much of a conclusion here.  O₃ from smoke is tricky as it can be positive or negatively influenced by smoke.  One must also consider what O₃ would have been on the day without the smoke.   

 Regarding the CTM (GC) analysis, I am not sure what this adds to the analysis.  Using a coarse resolution model (25km) to model smoke transport and chemistry is well known to problematic.   First one has to get the emissions and transport correct and then the chemistry.   Neither is handled well in GC for smoke plumes.   The rapid OH chemistry in smoke plumes after emissions is another well known problem for models. The fact that CTMs often dramatically over-predict O₃ from fires has been shown previously:

http://dx.doi.org/10.1016/j.atmosenv.2016.06.032

https://doi.org/10.1016/j.scitotenv.2018.05.048

It seems fairly obvious that this is the wrong tool to apply to the problem.

Lastly, I have some concerns with the ER/EnR analysis.   First, its not clear what the authors have done nor what is the goal of this analysis.   Is it to show emission ratios (not emissions) or estimate photochemical age or what ?   In any case the uncertainties are very large and not discussed.  

So my summary recommendation is for the authors is for the authors to re-orient the paper towards the first four items mentioned above (VOC obs, smoke identification scheme, cancer risk and rainout) and remove or minimize the remaining items.

Detailed comments:

Line 46-48”However, analogous…” ??    Aren’t there lots of observations that could be used to evaluate CTMs?   

50:  I think the wildfire smoke in Missoula was actually worse in 2021.

L101:  “Based on climatology..” ??

130; Define ncps

146:   The Thermo instrument seems to have the strongest bias.   Please discuss data and any remediation that was taken.

150:  As noted above, I am not sure what is gained from the GC results here.

196: I don’t understand the 1.5x.    Does this mean for PM with (say) a bg of 6 ug/m3, the criteria is 15 (9+6)?    Similarly for CO, with a bg of 100 ppb, would the criteria be (approx.) 250 ppb (100+150)?   Please clarify.    This seems ok for PM, with a relatively low bg, but not CO, as it has a high bg.

215:  It seems you are looking for a yes/no answer, but in reality you are probably getting a range of smoke influence.

256:  Strongly recommend to  use local standard time or GMT.  

270: missing:  Does this mean horizontal or vertical?

275:  Rain removal is very interesting and should be elaborated on.

Figure 3:  Is time axis LST, or ??

Figure 4: Not clear what the two diff numbers in relative change by mean refer to.

For example for O3 +7% seems clear for the MDA8, but then what is 1.1?   This needs a statistical analysis.   I am convinced that the O3 MDA8 values are statistically different.

315/Section 5:  Its not clear what is the goal of this section.. In any case, the uncertainties must be huge.  For example how are you calculating photochemical age?   Even in an ideal case, this could give estimates of the ERs, but not the emissions without some other type of analysis.    I am guessing that all of the ER values are relative to CO (please state here).

368/Section 6:  I found this analysis to be weak.    There are too few points to make a significant conclusion on the PM-O3 relationship.  The large over-prediction in modeled O₃ has been shown.   It is very hard to model smoke O₃ and this has been shown by others.

399/Section 7:   This is an important section.  It needs a better description of the methodology.

408:   Please restate this,  not clear as written:   “If the BB impacted….”

416:  HI = 3.  Need methodology.

This manuscript documents the impacts of wildfires on air quality at a ground site in Missoula, Montana, in 2020. The study integrates both ground-based measurements and atmospheric modeling and clearly represents a substantial amount of work. While the manuscript has considerable breadth, it lacks sufficient depth. Both the ground observations and the disagreements between measurements and models are the same as already shown in the literature. My major comments are listed below.

1. Figure 3: Why does maleic anhydride exhibit such strong diurnal variation?
2. Emission ratio estimation: The approach used to estimate the emission ratios is confusing and appears circular. For example, the measured emission ratio from WECAN campaign is used to calculate the photochemical clock, and the photochemical clock is then used to infer the emission ratio. In addition, given that the lifetime of toluene is only about 2 days, the toluene/benzene ratio is not an appropriate tracer for inferring a photochemical age of ~7.5 days. In such an aged plume, primary toluene would be largely depleted, and background toluene concentrations would likely have a substantial influence on the toluene/benzene NEMR.
3. Figure 6B: There are insufficient measurement data points to support the proposed non-monotonic relationship between O3 and PM2.5. However, I agree with the broader conclusion that the model overpredicts O3.
4. Health risk discussion: The discussion of chronic and acute health risks is outside my area of expertise. I recommend that this section be carefully evaluated by reviewers with relevant expertise.