The study by Drysdale et al. investigates NOx eddy covariance flux measurements in context of emission inventories in London. It presents a follow up study on previous campaigns at the same site. A main finding seems to be that NOx emissions are still underestimated by local emission inventories in London. The paper is well written and meets ACP quality criteria for research papers. I suggest publication after the comments below have been addressed adequately.

Line 85: Air was pumped through a 45 m sampling line. Obviously flowrates varied between 2.8 and 26 l/min due to clogged filters. What was the variation of delay time calculated by EddyRe through this line? The dependence of NOx flux vs Reynolds Number suggests a bias up to 50% for the first half of the measurement period. I understand that this would make the discrepancy between measured fluxes and inventory even larger (thus not change the major conclusion of the paper), but I wonder whether this large bias justifies the inclusion of the early campaign data without correction.

Line 100: The EC analysis is done with eddy4R aggregating the flux calculation into 60 min intervals. This is a non-standard flux averaging interval because stationarity can become an issue for longer time averaging intervals. It would be good to present a statistical measure that justifies a 60 min flux calculation interval. Why not simply apply spectral corrections as described by Massman et al. 2002 (doi: 10.1016/S0168-1923(02)00105-3) The cospectral analysis could give a good metric on flux averaging intervals - e.g. how long is long enough?

Line 149: Figure 7 is mentioned before Figure 3,4,5, and 6. It also appears that Figure 5 appears before figure 4 - Figure numbering should be consistent – i.e. in sequential order.

Line 135: This correction formula merits more discussion. For example what was the assumption for the concentration jump of NOx across the PBL?

Line 250: The temporal disaggregation methodology of the yearly emission inventories is not clear. Why would you still scale the LAEI hourly emission data by week and month?

Line 253: It is not clear what the open R package is really used for. The 2D flux footprint should already give you an appropriate weighing function that can be applied to bottom up fluxes. Using the along wind distance to the footprint maximum in conjunction with a polarPlot function seems an unnecessary (and rather semiquantitative) step here.

Section 3.1: NOx fluxes are reported in mg/m2/h – in my opinion molar units would be much more appropriate, since NOx is the sum of two species with different molecular weight. Reporting fluxes in mg/m2/h leads to an important loss of information. This is particularly relevant since most of NOx is emitted as NO from combustion processes. I therefore highly recommend to change from mass to molar units as is done for mixing ratios, which are all reported as ppbv and not ug/m3.

Line 273: It would be informative if the authors expanded their discussion here, comparing their results to NOx flux measurements elsewhere and previous studies at the location. Are NOx fluxes in London quite a bit higher or lower than in other urban areas? e.g. Marr  et al., 2013: doi: 10.1021/es303150y; Karl et al., 2017: doi: 10.1038/s41598-017-02699-9; Guidolotti et al., 2016: doi:  10.1016/j.agrformet.2016.11.004;  Squires et al., 2020: doi: 10.5194/acp-20-8737-2020; How similar or different are the results to Lee et al.,2015 (doi: 10.1021/es5049072), who published NOx fluxes at the same location? Have fluxes changed since then or rather stayed constant?

Line 280: what is meant be temporal upscaling?

The authors present eddy covariance measurements of NOx fluxes over London and interpret the results in terms of predominant sources and bottom-up predictions. The topic is of relevance to ACP and in general the quality of analysis is appropriate. I list some comments below that in my view should be addressed prior to acceptance.

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Main comments

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Section 2.2. Here the authors derive a 23-62% correction due to vertical flux divergence but then don't apply it as too uncertain due to issues with the model mixing height. What helps put the study on more solid footing is that this correction would only increase the measured fluxes, and the authors are already inferring an inventory underestimate. However a couple aspects of this are somewhat surprising, at least to me, and merit more discussion.

- The first is the size of the effect, and here it would help to give some information on the modeled boundary layer height values. Based on Eq 1, 23-62% corrections require heights of only be 500-1000m. If I'm reading it correctly, the observational comparison later in this section indicates that the modeled boundary layer heights are biased substantially low, so that the flux divergence influence as estimated is too big.

- I believe application of Eq 1 implies that the measurement height is always out of the constant flux layer, and further that there isn't actually a constant flux layer at all ... i.e. the correction begins at the surface rather than at the top of the surface layer. Some more physical justification is needed of its applicability.

- Another surprising aspect is the inconsistency between the entrainment-based correction approach (23-62%) and the single-point correction approach (0%). The authors attribute the latter to "attenuation of the concentration enrichments at this measurement height, rather than the lack of stored flux" but it is not clear to me how physically plausible this actually is. Some more information / discussion is needed.

2.2.1.3 The authors derive a 5% spectral correction due to high-frequency sampling losses. However there was large variability in sampling flow (3-30 L/min) and turbulent characteristics (Re 120-2300). Does the degree of high-frequency loss vary significantly across these conditions? Is it really only 5% for the low-flow / laminar periods?

Sampling took place on a 13m mast atop a 177m building. Surrounding buildings are all quite a lot shorter but to what degree might the BT Tower itself disrupt the sampled flow field in a way that would bias the fluxes?

2.2 I appreciate the discussion of eddy covariance QA/QC. It would also be helpful to show ogives and to give information about the range of sampling lag times.

2.3.1 please state the temporal resolution of NAEI in this section. Is it annual?

2.3.2 what is the spatial resolution of LAEI? Also 1km2?

L252, "Day of week and month of year factors were still applied". Unless I missed it, this is the first mention of temporal variability in the inventories. Such factors need to be more carefully described in the corresponding methods sections.

Conclusions. It seems that pinning down the uncertainty due to entrainment / storage should be an important priority for future work, as this term is similar in magnitude to the inventory bias inferred. Are there plans along these lines that can be mentioned in the conclusions?

Conclusions. The reader is left a bit unsatisfied by the lack of take home messages. The authors might consider discussing some implications of their findings; e.g. what do the derived emission errors mean for AQ predictions? 

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Technical/editorial comments

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some typos and grammatical issues throughout; please correct.

Lines 25-35, the narrative here as written is confusing and hard to follow.

67, "hitherto unreported sources" implies missing sources when it seems the problem is mainly underestimation of known sources. Perhaps "underreported"

Figures are not referred to in order

Table 1, I'm confused here because some directions the sectors add up to <<100% and others add to >100%. Please clarify what is going on.