Summary:

This work uses emission factors from ~20 published studies across ~9 regions to estimate national methane emissions from active mid- and up-stream oil/gas production facilities for 2021. Using infrastructure inventories (Enverus, OGIM database), regional emission rates were modelled and validated with airborne surveys.

The manuscript is well written and the subject is of suitable content for EGUsphere. The subject is timely as there is active discussion regarding how mitigation funding can most effectively be used to reduce fugitive emissions from O&G. The figures are well designed and informative.

I have two main hesitations that together question the novelty of this work and the contributions that it provides. First, the chosen methodology, which is complicated and I am not convinced contributes to the authors results, discussion, or conclusions (see general comment 1). Second, the close similarity of this work prior work from this group (see Omara et al. 2022; 2024) questions the novelty of this manuscript. Specifically, the aggregation of emission factors is already published in Omara et al. 2018, 2022, & 2024. Scaling from emission factors to national budgets using Enverus is repeated from Omara et al. 2022 & 2024. Lastly, comparison of national/regional/basin-level emissions to airborne studies was previously done in Omara et al. 2022 & 2024.

General Comments:

1) Methodology: What is the benefit of using a bootstrapping approach? Is the bootstrapping solely to provide confidence intervals, or is there an additional benefit?

My criticism is that many of the same results and conclusions are achieved without this analysis or less complex approach. Conclusions 1 and 2 can be drawn solely from the prior EF distributions. Conclusions 3 and 4 require knowing the number of facility types and production rates (taken from Enverus, OGIM database) but also do not require the monte carlo bootstrapping. Same critique for sections 3.1, 3.2, and 3.3.

As an example, the main conclusion of the authors (Conclusion 1, L712) is that 72% (70% as stated in abstract, L22) of total emissions are from facilities that emit less than 100 kg/hr.  This is in fact buried in the last table of the supplement, which states the prior emission distribution and shows that 72.7% emissions facilities are from these “small” emitters. The posterior is unchanged from the prior, which is good since MC bootstrapping in this approach shouldn’t change the center value.

A MC bootstrapping technique may be more interesting if applied to randomly select which EF studies to include. For example, if 6 of the 11 studies of facility category “Well Sites” listed in Table S1 were randomly selected for each simulation, then we might assess dependence based on regional dependence of studies, sampling/analytical methodology, etc. Indeed, regional differences are maybe observed, e.g. loss rates of 0.90% for Appalachian and Greater Green River regions (Omara et al, 2018) compared to  >4.5% for San Joaquin and San Juan regions, but the variance within the regional populations precludes saying these loss rates are different (based on a Tukey test). Could the Tukey test be run on the log₁₀(loss %), given that these appear to be lognormally distributed in Figure 1?

2) What is the 95% CI for the total national CH4 emissions?

3) Data Availability: Data should be made available in a publically accessible, reliable repository and linked, preferably, through a DOI per EGUsphere instructions.

Ideally, I would also prefer to see a table or reference section in the supplementary that has direct links, references, etc to the data from other studies used in this manuscript. This would be the data references in Table S1, plus Lan et al. 2015.

Specific Comments:

Review of Williams et al., Small emission sources disproportionately account for a large

majority of total methane emissions from the US oil and gas sector

The paper examines the role of super emitters in the contribution of different midstream and upstream site categories in the oil and gas sector with regard to CH4 emissions. The authors use published data to create emissions distributions for the different categories as a function of daily gas production rate, using an algorithm that is very similar (identical?) to Omara et al. (2018). The novel aspect in the present manuscript comes from the framing: Previous papers have stressed that super emitters dominate emissions in a given distribution of emitters, where the super emitters where generally the relatively highest emitters in a given distribution. The new manuscript emphasises the large role of emitters below a fixed absolute emission rate of <100 kg/h, so with this absolute definition, the super emitter category contributes less to total emissions that smaller emitters. 

My biggest concern is that this (and the title of the manuscript) imply a discrepancy between previous and new analyses, which is in fact not the case, and this is not well communicated. I strongly encourage the authors to clarify the change in perspective/framing and where it originates from. It is very clear from Fig 6 of the manuscript that in the category Well sites (<15 boed) there are almost no super emitters according to the absolute definition (>100 kg/h), so it is no surprise that they don’t contribute much to emissions. And since this category contributes most to the annual emissions, (Fig 6b) the category strongly lowers the weight on super emitters to the national totals. This should be explained more clearly!

My second recommendation is to clearly explain the underlying concept of the model. I read Omara (2018) again, and if I understand correctly, the approach is the following: 

1)    you use as input i) daily average gas production data for “all” sites and ii) a correlation between production data and measured emission intensity (percentage of production) from a small sub-set of sites, divided into categories.  

2)    you use a Monte Carlo technique to assign to each site in i) an emission intensity from ii) based on the emission intensity distributions in each category, to calculate hypothetic emissions per site, and then sum sites up in the different categories. You do that many times randomly to get statistically robust data.

In the present manuscript the essence of the model concept is buried in a lot of information on input data. Please state it more clearly. 

Also, point 2 is making the method rather complicated, and I wonder whether one would not reach the same conclusions by deriving emission factors for the categories based on previous work, and using these emission factors per category for up-scaling. 

I strongly recommend using SI units, according to Copernicus guidelines (https://www.atmospheric-chemistry-and-physics.net/submission.html#math). I get confused by units like Mcfd, Mcf, boe, and cf3, in the text and in Eq. 1. I realize that these units are used in the O&G industry, but they should not be used in scientific publications. When common SI units are used, the rather trivial unit conversion factors can be omitted in Eq. 1, which would then read: 

Emission rate = Gas production * methane content * loss rate * methane density

Except for these general points, I find the manuscript well written, but I have a few suggestions to the figures, partly linked to my general recommendations: 

I find Fig. 2 complicated and it could be simplified in 2 aspects: 

1) remove the “loop over i” going back to the start, and simply state that you do this for all facilities, (then also remove the index i). 

2) show separate paths for categories 2, 1&3, and 4-9. I understand that this can be incorporated in an algorithm but this “high level” and rather trivial criterion makes the flow confusing. 

In figures 3,5 and 6 the cumulative percentage of emissions is plotted versus emission rate. In many previous studies the cumulative emissions were plotted versus fraction of total sites (ordered from high to low or low to high). These plots usually show the effect of the skewed distributions, namely that the highest emitters in a given distribution contribute most to the emissions. As I mentioned above, this apparent “discrepancy” should be explained, and it may help to also show the cumulative distributions versus fraction of total sites, at least for the category Well sites (<15 boed).

Technical points: 

L127: …. intermittent sources…..

L 185 and Eq. 1: It is not appropriate to use the chemical formula CH4¬ as the “methane composition”, in eq. 1. Refer to it as” methane content” of the gas and use a proper symbol

L188: Omara (2020) is not in the reference list, should this be Omara (2018), otherwise add reference

L534: reformulate