This manuscript presents measurements of XO2 (=RO2 + HO2) at a ground site influenced by biomass burning plumes. The measured XO2 is used to evaluate box modeling with different mechanisms. It is shown that model results are consistently greater than measured [XO2] by ~30%. The influence of biomass burning on ozone formation is also studied. The ozone formation is only slightly impacted by smoke because of low NOx, indicating the O3 chemistry is NOx-limited. Overall, the measurement is valuable and I recommend publication with major revisions noted.

Major Comments

1. In the manuscript, the discrepancies between measured and modeled [XO2] are noted, but not fully explained. Namely, what causes the over-estimate of XO2 in models? Any recommendations to the chemical mechanisms? Or the difference is within the measurement uncertainty, which undermines the valuableness of the XO2 measurement? Looking at Figure 6, model sometimes is 50-60% higher than measurement. Why? The difference shown in Figure 6 seems larger than the 31% noted in the abstract. In fact, how is the “31%” calculated?
2. The effect of HO2 heterogeneous uptake on the radical budget is likely over-stated. As the authors noted, the HO2 uptake coefficient is highly uncertain. A relatively large value (i.e., 0.2) is chosen. In dense BB plumes, organic aerosol is the dominant composition with mass fraction up to 80%. As discussed in Abbatt et al. 2012 and George et al., the HO2 uptake coefficient to solid organic particles is < 0.001 and to liquid organic particles is < 0.01. If applying the small gamma values, the HO2 heterogeneous is negligible even in dense BB plumes.
3. Missing HONO as model input is invoked in several places as a possible reason for the model vs measurement difference, but this reasoning is questionable. First of all, the delta_HONO/delta_CO after 3hr aging of BB plume, as shown in Peng et al., is 0.1 ppt/ppb, rather than 1 ppt/ppb as quoted in the manuscript (Line 377). In addition, Peng et al. clearly stated that after 3hr the [HONO] is near or below the instrument detection limit and they refrain from interpreting what it implies in terms of potential HONO steady state in aged plumes. Lastly, HONO can be added to the box model (using delta_HONO/delta_CO = 0.1 ppt/ppb and measured CO), to directly test the effect of missing HONO on the modeling results.
4. Figure 5 is interesting and related discussions should be expanded. For example, what does the lack of correlation between P(O3) and NO when P(ROx) is small suggest. Does it suggest O3 formation is VOC-limited? More information can be distilled from the figure, or from the four variables in the figure (PO3, PROx, NO, and HCN).
5. In the manuscript, some metrics are from direct measurement (e.g., [XO2]), some metrics are calculated from measures species (e.g., P(Ox) from Eqn. (3)), and some metrics are purely based on box model. These need to carefully worded in the discussion to avoid confusion. For example, Line 460 and others use the term “measured OH reactivity”, which the reader believe is the calculated OH reactivity based on measured VOCs. Then, Line 477 refers to Eqn. (3) as measured P(ROx), which makes the reader confused for a bit, as it is calculated, not measured. Such subtleties hinder the readability of the manuscript.
6. Line 482. Are there any constraints or independent verification on the contribution of photolysis of methyl glyoxal and glycoaldehyde to the P(ROX)? Their contributions seem much larger than expected, based on measurements of these two species in previous wildfire studies.

Minor Comments

1. Line 26-28. The reader suggests to rephrase the sentence to “the model over-estimates the XO2 by 30%”.
2. Line 29-30. Suggest rephrasing to “likely due to the presence of an unmeasured HOx source that is not included in models”. The whole sentence may need to be rewritten after investigating the role of HONO as mentioned above.
3. Figure 5b. P(O3) is used in the y-axis, but P(Ox) is used in the figure caption. Be consistent.
4. Line 387-397. The negative delta_O3/delta_CO on 8/16 is likely a result of inaccurate O3 background and mixing, rather than depletion. It is because as the authors noted, the [NO2] is much smaller than [O3], suggesting that [Ox] ~= [O3], which rules out the possibility of depletion.
5. Be consistent with which model results are presented. For example, why is MCM-BBVOC-het presented in figure 8, but MCM-BBVOC in figure 6?

General Comments:

The manuscript by Lindsay et al. presents ground-based measurements of total peroxy radicals (XO2) within biomass burning smoke in McCall, Idaho in Aug 2018. The authors examined the diurnal profiles of radical concentration and ozone production rate in multiple smoke events with a unique set of measurements, and employed a 0D box model with different mechanisms to evaluate HOx radical chemistry. Overall, the paper presents useful results with detailed observational and model analysis, and are of interest to the atmospheric chemistry community. However, the paper would benefit from some additional model simulations and clarifications detailed below before it is acceptable for publication.

First, the authors find that the model was not able to reproduce the XO2 enhancement of 15 pptv during the Aug 17 smoke event, and suggested that HONO, which was not measured,may be the cause. This possibility is not really investigated in the paper. What magnitude of HONO would be needed to  achieve the necessary production of XO2? It would be useful for the authors to verify their assumptions by conducting sensitivity analysis of the modeled HONO (perhaps by applying a scale factor to CO or NO2).

Second, there is an inadequate amount of discussion of how the modeled radical precursors compare to measurements. The authors showed significant model overestimates in XO2, P(ROx), and P(O3) across all model mechanisms used, but did not discuss in detail the possible causes of model discrepancies. More discussion on the cause of the model overprediction and what might be pursued to reconcile the problem would be useful. Are there inaccuracies in the recycling within XO2 species? What does the diurnal profile of model-obs discrepancy look like? What possible mechanisms could bridge the gap between measured and modelled total XO2? Is the modeled NOx close to observation? How is NOx constrained in the model (e.g., kept NO/NO2 ratio the same as observation or not)? This kind of analysis may help better understand where the model-measurement discrepancy arises from.

Last, the ozone analysis could be better utilized to reconcile the calculated rate of production with measurements. For example, the authors could show the changes in measured-to-modelled ratio of PO3 and XO2 with different parameters(e.g., NOx concentration), colored by different BB events, to find plausible explanations of the discrepancy. 

Specific comments:

1. How does the wind speed, RH, temperature vary each day? A brief description of meteorological conditions would be helpful. Or you could add a panel for that in Fig 2.
2. It would be more clear if you move part of the key model description from the SI (Line S108-114) to the main text, mainly what and how the measurements were used to constrain the model and what values are used for unmeasured species. 
3. Line 376-377: Peng et al. showed HONO enhancement ratios decay to ~ 0.1 ppt/ppb instead of 1 ppt/ppb for aged (> 3h) plumes. What enhancement ratio is needed to resolve the model disagreement if you initialize the model with HONO that scales with CO (or NOx)?
4. In line with the previous point, given the importance of HONO as an OH precursor, how does PO3 change after including HONO in the model? And how does that affect NOx? Is the estimation of the missing HONO different across different BB events? 
5. Figure 8: Why is the modeled P(ROx) almost a factor of 2 larger than observed? Line 481-482 suggests that the greatest HOx contributors in the carbonyls group are unmeasured carbonyls - how are they initialized in the model? How does each modeled radical precursor compare to the observation? Where are the sources of discrepancy in P(ROx)? It is important to mention how the uncertainty of the carbonyls input could affect the results and conclusions.
6. Do XO2 measurements agree with the XO2 estimates derived from modified Leighton ratio calculated with measured ozone, NO and NO2 concentrations from the campaign? A scatter plot of derived XO2 versus ECHAMP observations could be made.

Minor Comments:

1. Fig 2: How is smoke presence determined? There seems to be no text descriptions.
2. Line 186: extra period and space
3. Line 187: missing closing parenthesis
4. Line 302, Extra space after “MCM-base”
5. Line 357, sentence incomplete: “Clusters of data points at HCN concentrations ARE….”
6. Figure 3: better have a legend for the bottom panel
7. Figure 5. Add legend for model vs obs in panel a for convenience of the readers; also specify the analysis is for Aug 17 event in the caption
8. Fig 6. Typo in the legend for the upper panel: ISOPO2 instead of Isoprene?
9. Line 471-472: Did the decrease in OHR happen upon smoke arrival? From Fig 6 it seems to be upon smoke exit?
10. Line 477-478: shall be “O(1D) reaction with H2O”
11. SI Line 151: fix typo “GOES-Chem”
12. Fig S10 and 11: fix caption placeholder (Fig X)

Review of Lindsay et al., “Ground-based Investigation of HOx and Ozone Chemistry in Biomass Burning Plumes in Rural Idaho”:

Summary: The authors measured total peroxy radical (XO2) concentrations in McCall, Idaho, as part of a recent biomass burning intensive field campaign, with the goal of furthering our understanding of ozone and HOx chemistry in biomass burning plumes. Five smoke plumes were sampled. The authors found that the ozone production rate, P(O3), was not affect much by smoke plumes. Measured and modeled XO2 concentrations were compared, showing reasonable agreement. The measurements are novel for biomass burning plumes, and the insights gained could be useful. However, I have major issues with the analysis used to justify whether or how much O3 was enhanced in the measured plumes. The regular diurnal cycle of O3 was not considered, and led to incorrect interpretations as detailed below. Major changes to that analysis would be needed prior to publication.  

Major Comments:

Line 387 etc: I understand that the dO3/dCO metric has been used before, but it seems to me that it is underconstrained here. Wouldn’t the derived slope be strongly dependent on the time of day when the measurements were taken? O3 has a strong diurnal cycle due to photochemistry, while CO does not. So across the several hours of measurements encompassing in-plume as well as pre/post plume background, the dCO term will likely be dominated by the addition of CO in vs out of the plume. However, the dO3 term will be a sum of the O3 added (or lost) from plume-specific chemistry plus any O3 that would have been added (or lost) during the several hour measurement period due to regular photochemistry. With this in consideration, it appears that the slopes in Fig. S6 are most positive for the 22^nd and 23^rd because those data were taken during the early part of the day when ambient O3 concentrations were increasing most rapidly, while the slope for the 17^th was smaller because the data came just shortly before peak daily O3, and the slopes for the 24^th and 16^th (not shown) were smallest because the data came from after the daily peak of O3 when mixing ratios were declining slowly. This might correlate with your calculated P(Ox), though it would depend on L(Ox) too I think. In other words, this method could work if it was using dO3/dCO data that came from a short enough time span that the daily O3 cycle was not a factor, for instance aircraft measurements spanning just a few minutes. But here, you’re deriving a slope between in-plume data and out-of-plume data that are separated in time by several hours, during which time the actual O3 in each airmass is changing (and changing in different ways depending on time of day of sampling). Therefore I do not think you can use this analysis to support your abstract-level conclusion that “During BB events, O3 concentrations were enhanced…” at line 23. That conclusion may still be accurate, but you will need to provide better evidence.

Fig. 4: The same analysis as my previous comment applies here; O3 has a prominent diurnal cycle that would exist with or without a wildfire plume, while HCN would not. Plume chemistry may enhance the O3 cycle, but it apparently doesn’t dominate it. Thus, the trends shown in this plot are driven by that underlying O3 diurnal cycle. The slopes are steep and positive for data taken when a plume arrived during midmorning when O3 is increasing due to ambient photochemistry, and shallow for data taken when a plume arrived after peak daily O3. If you had a plume arrive at ~midnight, O3 would be decreasing while HCN increased, giving a negative slope in Fig. 4. Therefore I do not think you are correctly interpreting the apparent positive correlation between O3 and HCN here. The proper correlation would be between only the O3 derived from smoke plume chemistry (i.e. subtracting the normal background photochemical diurnal cycle) vs. HCN. Obviously that’s really difficult to parse and would likely require a model, so I’m not sure what to suggest other than removing this part of the analysis.

Line 354: Also, can you state here what is the R^2 value for the correlation in Fig. 4?

Line 376: I believe j(HONO) was measured, or could be estimated. Can you do a rough calculation of how much [HONO] would be needed to account for the added XO2? That would be helpful for convincing the reader that it is reasonable to assume HONO is the missing factor.

Line 377: The fit line from Peng et al. 2020 (Fig. 3) suggests a value of more like 0.1 pptv/ppbv^-1 for average dHONO/dCO at 3 hours age, not 1 pptv/ppbv^-1 as stated here. However, the line is fit to all data regardless of in situ j_HONO, and some plumes did have elevated [HONO] at those ages, so it’s possible this plume also did.

Line 404: Here you say “…there is little correlation between P(Ox) and smoke tracers.” Then in the next sentences you discuss examples of how BB influences P(Ox). I would agree with the sentence at line 404. Also, Fig. 5a is not the correct plot to show to conclude that “P(Ox) is slightly higher during the afternoon and evening smoke influenced periods compared to non-smoke periods” as you say at line 408. I see the high [HCN] data covering a similar span of P(Ox) as low [HCN] data. Really to draw this conclusion you would need to split the green trace (diurnal cycle of measured P(Ox)) into two, one with high HCN and one with low HCN to show the difference between them. Please do that, and then alter the text to tell a consistent story that there either is or is not a strong effect of smoke on P(Ox) in your measurements.

Line 477: By plotting them together in Fig. 8, you’re directly comparing measured P(ROx) from a subset of sources with modeled P(ROx) from all sources. They don’t agree very well, nor should they agree, especially at night when alkenes+O3 dominates. But this just adds confusion, and it doesn’t help answer the real question of how well does the P(ROx) from measured sources compare with the P(ROx) modeled from the same subset of sources? I’d suggest maybe adding a dashed line for the P(ROx) modeled from that same subset for comparison, or altering the figure in some other way to help clarify so you’re not comparing apples and oranges.

Minor Comments:

Line 33: add a citation here for Brazil and Australia fires

Line 272: It would be helpful if you refer to a specific location in the SI, e.g. Sect. S4 here. Please check other references to the SI as well.

Fig. 5: The figure panels are labeled P(O₃), but should probably be P(O_x) to be consistent with the caption and rest of text (and be consistent throughout).

Line 384: I’d prefer if you labeled the green and blue traces using a legend in the figure, rather than having to dig through the caption to find that information. Same goes for the P(ROx) speciation in the bottom panel of Fig. 3.

Line 418: Model Evaluation should be Sect. 3.3, not 3.2.