The manuscript “Estimation of OH in urban plume using TROPOMI inferred NO2/ CO” presents an analysis of OH derived from urban plume information using TROPOMI satellite observations combined with WRF model simulations.  Analysis focuses on the city of Riyadh, and assumptions regarding plume decay away from the city center, background conditions, and emissions are used to optimize the model to best match the TROPOMI products.  Optimization of both the NO2/CO ratio and individual components (i.e., NO2 and CO separately) produce similar results for the OH derived for the two seasons examined.

General comments

This paper describes an interesting analysis and a potentially useful technique, enabling inference of NO2 lifetime (and OH) from a single TROPOMI overpass.  This more instantaneous view could have benefit over previously used Exponentially Modified Gaussian function fit methods, which require substantial temporal averaging.  However, the analysis relies on many assumptions, the implications of which are in some cases discussed, in other cases not.  Some larger context is missing, regarding how the work might be applied on a wider scale, or else used for case studies of interest.  Many metrics and side analyses are presented, and the main analysis has many “moving parts,” (i.e., TROPOMI, WRF, CAMS, the main least squares optimization vs. the EMG optimization, etc.), making it difficult to interpret the results and muddling the main messages.  As a result, there is opportunity to streamline the writing and improve the presentation quality.  Since the analysis appears to be robust, given the convergence on OH from the two optimization methods (ratio vs. component wise), I would consider this work suitable for publication in ACP and of interest to its audience once the following comments are addressed.

For presentation quality, I usually try to stay away from commenting on writing style, but I do think some re-organization would be beneficial to the reader.  Instances that could help clarify confusion are noted under “Specific comments,” but I might also suggest reframing the results in an “easier to digest” way.  Currently, Section 3 follows the steps of the analysis quite closely, which gets quite overwhelming when discussing model vs. TROPOMI differences, then ratio optimization vs component wise differences and those differences vs. CAMS or EDGAR, then those differences vs. EMG, etc., each with an emissions, a background, and an OH component.   Perhaps an easier to follow organization would first discuss emissions only, in terms of the evolution of the emissions over the course of the optimization, then OH, then background?  This is only a suggestion, but I think it would improve the readability of the paper.

In terms of providing more context/motivation for this work, I would interested in seeing discussion on topics such as: how difficult would it be to apply this method to other cities?  What are the limitations that might make this hard to do for some locations?  How do these findings influence our understanding of urban pollution, or what role could they play in better quantifying emissions?  Etc.

Specific comments

L19: From the one-sentence description of the method in the abstract (that OH concentration, NOx and CO emissions are iteratively optimized), the referencing to “NO2/CO ratio optimization” and “XNO2 optimization” is unclear without having read the full paper.  I would suggest clarifying further the concept of ratio and component-wise optimization.  Also, aren’t background conditions also optimized?  This could be included in the method description.

L20: Again, on first reading of the abstract, the mention of CAMS comes as a surprise; I thought WRF was being used.  Further elaboration on the method could help clarify.

L30: Air pollution from cities doesn’t just threaten the health of those living in the cities, but also populations downwind; this statement seems overly general.

L82: Please provide the months used in Fig. S1 (i.e., is summer the average of June-July-Aug?)

L100: I believe the newer v.2.2.0 of the retrieval should help with the bias in NO₂ seen in the analysis, according to the statement here: http://www.tropomi.eu/data-products/nitrogen-dioxide.

Is it feasible to try this analysis with the newer products?  It is understandable that results cannot always be published immediately after they are produced, but if an update to the analysis cannot be undertaken, at least a discussion of how the analysis might be affected by newer data products or a suggestion for future directions should be included.

L102: I’d be curious if the WRF-chem model does a better job of simulating urban NO2, in general, compared against TM5?  So, is it fixing the bias issue for the right reasons?

L111: The authors assessed NO2 data quality vs ground-based measurements from prior studies; is there a similar analysis that can be done for CO?  Or is there reason to believe that the reference CO profile from TM5 is more reliable than it was for NO2?

In Table 1, the term “XNO2(emis,OH)” is used in its own definition; I expecte it was intended to say “As XNO2(emis)…” – please check.

L181: I’m not sure I agree with this justification for not allowing XNOx,Bg to be lost by OH; NOx will continue to be oxidized, even if the plume it resides in was previously exposed to OH.  Is there any sort of sensitivity test that can be done to see how large an effect this would have on the results?

L194: Please explain why the lifetime of NOx is the more relevant quantity to this analysis than the lifetime of NO2.

Figure 1 caption: Please indicate “(right)” to describe the right panel, presumably after “wind direction” or “boundary layer.”

L248: Is it possible that the NOx/NO2 conversion factor may not hold for emissions, since all NOx emissions from combustion processes occur in the form of NO, strictly speaking?   While NO converts relatively rapidly to NO2, this still might be something to consider.  Please discuss any anticipated implications of this assumption.

Fig. 4c: It seems very counterintuitive that the optimization for XCO increases emis by so much, barely decreases Bg, yet you still achieve a decline in the XCO quantities such that TROPOMI values are well matched.  Am I interpreting this correctly?

Fig. 4 caption: How exactly are the f values shown here derived? It looks as though they are not simply the sum of f_1 and f_2 values shown in Fig. S17.  Please either explain or point to the location in the text where this is explained.

L345: I’m concerned that this test is more likely to work since you are dealing with an internally consistent system.  Using the model, it is easier to be sure that it can replicate a hypothetical scenario posed in the model with enough adjustments.  The real world and what TROPOMI are detecting could be very different systems, though, so if the model is missing underlying processes, there is less confidence that this optimization process is robust.

I suppose the pseudo data experiment is still worth doing, and I’m not sure what test I would suggest in its place, but perhaps some qualification should be added that the promising results of the experiment may stem from this being an ideal/consistent system.

L352: I was initially confused that the f values in Figs. S17 and S18 changed so much between the first iteration and the second.  I later realized that the second iteration values represented adjustments made to the first iteration values (i.e., f_emis doesn’t go from being +158.5 to –1.3 from iteration 1 to 2 in Fig. S17a; it goes from 158.6 to 157.2, or however you derive the 155.1 f_emis in Fig. 4a).  It may be worth describing this more fully, so other readers aren’t confused.

Also, for Fig. S17c, please place the values of f_emis1 and f_Bg1 on the left side, 2nd iteration f’s on the right, to avoid confusion.  And, why is there not a green line in this panel corresponding to XCO_WRF,1st iter?

L371: It would be helpful to state the value from Lama et al. (2020) here.

L417: Looking at Fig. S19, if this is done by linear extrapolation from data that is present for 2000-2015, why does year 2016 CO emissions drop followed by increases in 2017 and 2018?

L426: Please state why this model simulation is well suited to evaluate emissions changes – how does it calculate emissions, if not by relying on the EDGAR inventory?

L447: What is CAMS-TEMPO based on? Is there a reason why its temporal emission factors for Riyadh should be especially trustworthy?

L464: Why give a range for summer but a precise value for winter?

L470: “Estimates” here means estimates of OH change, correct?  Please clarify.

L475: It’s not just sources, but also some sinks are missing (for NO2), right?

L500: Is it possible to give a title to Appendix B, as was done for Appendix A?

L504-505: Why not write this in its simplified form, XCO_emis*0.10? The same goes for the next line.

Technical corrections

L30: “threating” should be “threatening”

L65: Beginning “OH estimates from…” is not a complete sentence

L107: This URL returns a “Not found” message

L175: “save” should be “safe”

L310: “emission” repeated twice

L313: either “estimates” should be singular or “an” should be removed

L355: f_B should be f_Bg

L392: “a” should be removed, or else “days” should not be plural

L397: “compare” should be “compared”

L407: “it the solution” should be “at the solution”

L419: “yield” should be “yields”

L422: “has” should be “have”

L481: “allows” should be “allow”

L509: Again, the link to the TROPOMI data appears to be invalid.  The Zenodo link for the WRF simulations requires a login, so I could not access the data; I’m unsure if this is typical or not.

Lama et al., "Estimation of OH in urban plume using TROPOMI inferred NO2/CO," presents a new approach to estimating OH concentrations using space-based measurements and model simulations, but without using a full chemistry scheme or formal data assimilation methods. Measurements of OH are sparse, yet OH plays a critical role in chemical reactions that govern air quality, therefore novel methods (such as the one presented here) are an important contribution to the atmospheric chemistry community. 

As in situ OH measurements are very sparse, validating new methods of inferring OH from other observations is difficult. The authors take a two-fold approach to address this by first showing that the optimization approach behaves self-consistently and second by comparing to both modeled OH concentrations and OH derived using the exponentially-modified Gaussian (EMG) approach. 

The method described here shows promise as a new approach to constrain OH concentrations, though with some notable limitations which the authors acknowledge in the manuscript. This manuscript is appropriate for ACP, and I recommend acceptance after the authors address the following concerns and suggestions.

Major comments

First, the model simulations used were WRF-Chem simulations with passive tracers only, without online chemistry. On line 162, the authors mention that they "account for the chemical transformation of NOx to HNO3 in the reaction of NO2 with OH." However, it isn't clear how this is done - whether a highly simplified mechanism was added to WRF-Chem or whether this was done offline. A more detailed explanation of this would be welcome, even if just in the supplement. The larger issue is the choice to use passive tracers with this simplified chemistry rather than one of the established chemical mechanisms in WRF-Chem. Line 180 states that such simulations are considered outside the scope of this paper, but does not explain this reasoning. I could see two reasons for such a choice:

1. To reduce computational cost, making this easier to apply at scale. If this is the case, some measurements of the relative speedup compared to a full chemistry simulation would help support this choice.

2. The framework used in this paper required a specified OH background to permit the calculation of d[NOx]/d[OH] in a straightforward manner. With a full chemistry simulation, I suspect it would be much more difficult to impose a constant increase or decrease in OH for this purpose.

Whatever the reason for the choice to use passive tracers, I urge the authors to explain their reasoning behind this choice, given (as they mention) the potential impact of other NOx loss pathways.

Second, at line 404, the authors state that "the optimization method can be used for a single TROPOMI overpass and does not require yearly averaged NO2 data." This is contrasted with the EMG approach, which does need a significant amount of data to generate reliable results. However, the ability of the optimization method described in this paper to estimate OH for individual days is not clearly demonstrated in this paper. Since this seems to be one of the main advantages of the authors' optimization method over the EMG method, this should be shown in more detail. At least a timeseries plot of daily OH concentrations obtained by this method would help by showing that we do get reasonable OH values with a single day of data. Further, I expect that there is a minimum amount of clear sky pixels over a city required for this method to work effectively. Assuming that clouds are uncommon over Riyadh, this could still be explored by withholding increasing percentages of the available pixels for a given day and testing how the estimated OH deviates with the reduction in data.

Third, the efforts to test this optimization approach described in the manuscript are a good foundation, but could be improved. My understanding is that there are three elements to the testing, covered in Sect. 3.3:

1. Tests in which NO2 and CO fields generated by varying the scale factors in Eq (5) are input to the optimization algorithm and it has to reproduce the scale factors used.
2. Comparing the NO2 and CO line densities and their ratio produced by the optimization against those from TROPOMI, in Fig. 4 and 5.
3. Comparing the OH concentrations, NOx emissions, and NOx lifetimes output by the optimization to those derived from the EMG method (Table 2)

These are important tests, but each have weaknesses. 

• For #1, because the framework that generated the synthetic NO2 and CO fields is the same framework used to match them, it cannot account for chemistry or other confounding factors outside that framework. 
• For #2, the optimization was given the goal of matching the TROPOMI NO2 & CO values and their ratio. Thus, showing that it can do so proves that the optimization has sufficient degrees of freedom and that the underlying model simulations include enough of the physics to reproduce the observations. It does not necessarily show that it obtains the right answer for OH.
• For #3, the EMG method makes a similar assumption to the optimization approach that the OH + NO2 pathway dominates NOx loss. This may well be true in Riyadh, but cannot give any information on errors from unsimulated chemistry.

One way to address these issues would be to repeat the first experiment, but using NO2, CO, and OH from a full chemistry simulation of WRF-Chem. Even if computational costs limit the runs to only a few days each in the summer and winter, comparing the OH returned by applying this optimization approach to the NO2 and CO columns simulated in the full chemistry WRF-Chem to the OH in that WRF-Chem run would be a useful metric of the error introduced from ignoring other NOx loss processes. Additionally, going back to my second main suggestion, this would be a useful way to demonstrate that this optimization approach works for individual days. 

Since the authors state that full chemistry simulations are beyond the scope of this paper, I accept that this specific approach may not be practical. However, something like this - effectively an OSSE experiment in which NO2 and CO columns simulated with more complete chemistry are ingested by the optimization framework proposed in this paper, and the optimum OH from this framework compared with known OH in the original simulation - would help quantify the uncertainty introduced by omitting VOC-NOx chemistry from this framework.

Minor comments

• Title should be "Estimation of OH in an urban plume" or "Estimation of OH in urban plumes" (singular/plural mismatch in the current title)
• Recommend defining XNO2 in the abstract, since it is less common to use column-average mole fractions for NO2 than for CO or CO2.
• At line 49, recommend mentioning that the EMG method assumes that OH+NO2 is the only loss route so that this is clear from the start.
• In Sect. 2.6, do you use the average pressure and temperature over the same time period as the EMG fit when computing the rate constant? Over what vertical distance?
• Recommend reiterating that f_emis, f_OH and f_Bg in Eq. (5) are the scale factors alongside the other variable descriptions following Eq. (10). Also please explain why they are divided by 10.
• Fig. 3 caption - I'm not sure "zonally" is the right term, that implies averaging along latitude lines. Should this be perpendicular to the wind direction?
• Fig. 3 caption - "with background as a function of distance" is ambiguous - does it mean that the background value depends on distance or is it saying that each of the quantities described previously (XNO2, XCO, WRF Ratios) are plotted versus distance?
• Line 357 - the OH uncertainties of 11% to 15% are probably underestimated because VOC chemistry is not accounted for. Please note that here.
• Lines 358 to 368 - the discussion here is difficult to follow because the results for OH, emission ratio, and background ratio vs. CAMS are very spread out and (in one case) given in different ways, e.g. the amount by which CAMS is overestimated and optimized value. It would help significantly to gather the results from the ratio-optimized and component-optimized tests into a table along with the CAMS values and provide the actual values. Describing the optimization results as percentages by which CAMS is overestimated is awkward to follow while reading.
• Lines 365 to 371 - the discussion of why the component and ratio optimizations yield different emissions ratios isn't convincing. Whether directly optimizing the ratio or the NOx and CO amounts, the algorithm has information on the ratio of NO2 to CO, so how can it come up with emissions ratios that vary from 0.38 to 1.05 (if I understood the ratio optimization result correctly)? If the component optimization matches TROPOMI NO2 and CO well, it should by definition match the TROPOMI NO2/CO ratio too. 
• Lines 371 to 376 - please provide the Lama et al. (2020) values for comparison.
• Lines 391 to 392 -  "Both methods result in higher NOx emissions and shorter lifetimes in summer; lower NOx emissions and longer lifetimes in winter." In summer, the prior values are within the EMG uncertainties. To claim that the EMG values are higher than the prior, given the uncertainty range, requires a t-test or other statistical test to determine if that difference is significant.
• Line 411 - the simplified OH + NO2 chemistry used here will also be a barrier to more general use. It would be good to acknowledge that any such simplified approach in the future will either need to (a) account for other paths for NOx loss, or (b) prove that neglecting those paths introduces an acceptable error in the OH concentrations. 
• Line 442 - this paragraph could use a stronger topic sentence. It's not clear what the main point of this paragraph is.