The authors present multiple years of measured CH4 and CO concentrations from New York City, and combine the results with Lagrangian model output to infer emissions for both species. They compare the derived fluxes with inventory predictions and draw conclusions regarding patterns of variability and drivers of emissions.

The topic is well-suited to ACP and the findings are broad interest. I have listed comments below that I feel should be addressed prior to its publication.

Scientific comments

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A general question has to do with spatial representativeness. It seems likely that the inventories being examined have biases that vary in space, whereas the results from this particular rooftop are discussed as reflecting the NYCMA. How can we assess the representativeness of these findings? For example, does the inferred emission disparity for a given inventory vary with wind direction?   

Abstract: “The estimates of methane emissions correlated with those of carbon monoxide (CO) emissions, determined from coincident measurements, suggesting a common city-scale incomplete combustion source for both methane and CO.” And line 554, “The afternoon observation-informed methane and CO emissions rates for the NYCMA were well correlated over our study period (Fig. 6c, R2 = 0.59). Unlike the observed ΔCH4:ΔCO comparison in Sec. 3.1, this relationship between methane and CO emissions accounted for variability in atmospheric transport.”

But to what degree could this correlation reflect footprint effects? E.g., if there is more developed infrastructure in upwind direction A than B, we would expect both CO and CH4 to be enhanced when winds are from A and not when winds are from B. This could drive a correlation that doesn’t necessarily reflect a mechanistic source connection. Can you test the reasoning here using your model simulations? Your inventories segregate emissions by sector. So one can track the modeled CH4 and CO concentrations at the receptor that arise from different source sectors. If the reasoning above is sound, then we would not see a correlation between the modeled CO concentrations and the modeled non-combustion CH4 concentrations.

Lines 449-456: I am not totally sold by the reasoning in this section, in two respects. First, “Accounting for the varying atmospheric transport and mixing throughout the study period, which drives nearly all variability in the simulated ΔCH4, we found that meteorology only explained 30%–43% of the variability in observed ΔCH4, depending on inventory comparison, based on the calculated R2 between the observed ΔCH4 and simulated ΔCH4”. To me, “meteorology” as used in this context implies dilution/ventilation/mixing effects. But there is also the fact that changing wind directions also change the portion of the city that is being sampled. So the wording should be more precise here.

Second, based on the argument that the variability in simulated concentrations is entirely due to transport effects, and the fact that the model and observations correlate to ~ R2 0.3-0.43, the authors infer that meteorology explains 30-43% of the variability in the CH4 observations. Since the models correlate more strongly with CO, the authors then posit that “Therefore, methane emissions vary more than CO emissions on a 10-day time scale.” But the footprint issue is relevant here as well. For example, if the spatial distribution of CO emissions in the inventories were accurate, and the spatial distribution for CH4 was not, then the model-measurement correlation for CO will be higher than for CH4, independent of any potential temporal variability.

Lines 110-120: separation of local-scale vs. city-scale influences. Hours with SD(CO) < 200 ppb will still be influenced by (albeit slightly smaller) local sources. It seems that the threshold choice here is fairly arbitrary. I recommend including a sensitivity analysis varying this threshold to demonstrate (hopefully) that the specific choice does not have a major effect on the findings.

Line 281: “Interaction between the surface flux and atmospheric mole fraction (the surface influence) happens when particles are present within the lower half of the mixing layer.”

Same comment, this choice is also somewhat arbitrary. I have no objection to the particular choice, and I think it is a standard value used in STILT work. But can we demonstrate what the impact of this assumption is via the sensitivity analyses?

Eq. 3. I agree that we expect the relative concentration disparity to correspond to the relative emission disparity. But you also have a nice opportunity to demonstrate that to the reader rather than just asserting it… i.e. if you scale emissions by X do your HRRR-STILT concentrations at the receptor increase by the same factor X?

Line 483: “Since there was no diurnal variability in the inventory methane emissions, the diurnal variability in the simulated ΔCH4 was entirely due to changes in the surface influence footprint (i.e., transport meteorology) throughout the day. The differences in the variability between the observed ΔCH4 and simulated ΔCH4 were therefore due to changes in the methane emissions which were not included in the inventory”

and

Line 595: “The consistent difference between the afternoon and 24-hour emission rates suggests a diurnal cycle in emissions, which is well-known for CO emissions (traffic, human activity), but had not been, to our knowledge, previously inferred for urban methane emissions.”

Couldn’t a diurnally-dependent bias in the model met fields also be a plausible way to explain this? It seems likely that this occurs at least to some extent.

Technical comments

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Line 33: grammar, “highlighting the importance of accurately quantify”

Line 38: awkward, “identified atmospheric methane greater than expected”

Line 58: suggest “reduced THE ESTIMATED methane emissions

Lines 135-140: was this a simple boxcar average or something else?

Lines 167-169: I find the wording here confusing. Do you just mean you don’t average the same time period twice when computing averages? Please clarify wording

487: “When tested for …” this sentence is not very clear as written, can it be clarified?

In “Missing wintertime methane emissions from New York City related to combustion,” the authors analyze rooftop measurements of methane and carbon monoxide to investigate the variability of methane emissions and extend the time frame of a previous carbon monoxide study. The work presented is thorough and the paper is well structured, well written, and provides sufficient background and context for how the work fits into the broader field. Urban methane has received increased attention in recent years and many important scientific questions remain around temporal variability and source attribution. Accordingly, I find the presented work to be timely and of likely interest to the ACP reader.

I believe clarifications around some conclusions are required prior to publication:

• Influence of transport/spatial sensitivity

The authors use the STILT model run by HRRR met fields to calculate the surface influence (footprint) of their observations at the rooftop site. This method is well established in the literature. They also provide the footprints (both afternoon and 24-hours) in the supplement at the monthly scale. At the monthly scale (Figure S7), differences can be seen between the spatial sensitivity of the site between different months and different years. I would expect further differences in spatial sensitivities to emerge at shorter time scales, such as the 10-day and 2-hourly intervals used in this work (e.g., Figure 5). Are the conclusions drawn from these shorter time intervals robust to difference in spatial sensitivity from one interval to the next?

In addition, for the diurnal time series shown in Figure 5b the ratio of the observed/simulated is assumed to remove the influence of transport. But does that not require that the representation of the transport be completely accurate? Could there still be transport related signals in the ratio when HRRR-STILT does not capture the transport sufficiently?  Particularly at night.

• CO as a combustion tracer

In section 2.6, CO is described as a combustion tracer. However, this section goes on to discuss how the source of CO and methane are not co-located for typical city sources. Based on this section, I am not quite clear how CO can act as a methane combustion tracer at the city-scale.

When discussing the correlation between observed enhancements of methane CO (Lines 376-375), the authors note that “a large portion of the correlation is likely from the variability of atmospheric transport but could also indicate simultaneous emission sources of methane and CO.” I agree. Later, the correlation of methane and CO emissions rates (~Line 555) is used as possible evidence for a common city-scale incomplete combustion source. The reasoning is based on the use of HRRR-STILT to calculate both emission rates. Similar to my point (1), isn’t there the possibility that influences from transport could remain? Differences in the accuracies of spatial allocations in urban CO and methane inventories could also influence the emission rates due to their use in calculating the simulated enhancements. Perhaps there is a way to assess the sensitivity of the emission correlations to these influences.

• Uncertainty of 24-hour data

As the authors state, “Meteorological products (i.e., 3-dimensional wind fields) used to drive the atmospheric transport model are more uncertain at night, for mixing heights especially, ...” (Lines 518-519). It is not clear to me if this larger uncertainty in transport at night is incorporated into the confidence intervals for the 24-hour emission estimates or diurnal analysis.

It is stated that for 24-hours “Longer aggregation time resulted in much narrower confidence intervals….” (Lines 323-326) and “The combination of many hours to produce the 24-hour emissions estimates resulted in much smaller confidence intervals compared to the afternoon-only emission estimates, further supporting the possibility of diurnal cycle for urban methane emissions” (Lines 600-602). More data would likely lead to higher confidence in the estimates, but does this uncertainty approach consider the increased transport uncertainty in the non-afternoon hours?

Minor comments:

• Lines 113-120: Methane categorization as local- or city-scale. Variability in CO at an hourly timescale is used to remove near-field signals? Is this a typo, should it this methane instead of CO? In the near-field methane and CO might not be co-emitted.
• Lines 249-255: “… we chose to leave emissions constant throughout the day ...” It is not clear to what this statement applies. Is what part of the analysis are emissions assumed to be constant throughout the day? I assume it to calculated the simulated enhancements, but it is not clear from the text.
• Line 556: “CH4:CO emission ratio” of combustion appliances I assume?