Reviewer #1

  • Overview: Review of “Constraining methane emissions in Utah’s Uintah Basin with ground-based observations and a time-reversed Lagrangian transport model” by Foster et al. Foster et al. use in situ measurements from four surface sites in the Uinta basin in conjunction with the WRF-STILT model to evaluate two different methane emission inventories. They find that the basin-specific inventory compiled by Ahmadov et al. performs better than the US EPA inventory for this basin. This also lends support to the large leak rates derived in Karion et al. obtained from one day of aircraft-based massbalance flights. Overall, the manuscript it good. It’s well written and the meteorological evaluation is quite rigorous. My only major concern is on the use of Fruitland as a background site. I think this manuscript should be publishable with major revisions.

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  • Major comments: Using Fruitland as background? From Figure 1, it looks like there is fairly complex topography at Fruitland. As such, does this site have the same PBL height as the rest of the basin? It seems like a damped diurnal cycle here could lead to erroneous diurnal cycles at the enhanced sites (since they are getting the background concentration from Fruitland). Additionally, is the flow at Fruitland always from the west? It seems that any flow from the east could lead to an enhanced concentration due to emissions in the basin. Extending Figure 4 to include Fruitland would be quite useful. I think the paper needs to expand the analysis of the Fruitland data since this site is providing background concentrations for all other sites. So it seems critical to demonstrate that this site is (1) only sampling background concentrations and (2) that those concentrations are representative of background concentrations for the basin.

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  • Page 3: The authors seem to cite the Turner et al., 2016 paper a number of times in the second paragraph. It’s my understanding that this paper didn’t actually do an inversion, so it may not be the best reference for that paragraph.

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  • Page 3: Similarly, the Zavala-Araiza et al., 2015 reference at the end of the 3rd paragraph doesn’t seem to fit with the statement. The Zavala paper showed that top-down and bottom-up methods can agree quite well when the bottom-up methods used basinspecific inputs.

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  • Page 13, first paragraph: Is the vertical mixing the same at FRU as the rest of the basin? Seems like a critical point if it’s going to be used as a background site for the basin (e.g., if the PBL height is higher in the basin then the concentrations would be higher at the background site because the well-mixed region is smaller).

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  • Page 13: First paragraph of Section 3.2 The authors mention that the PBL extends well above 1000 m AGL and point to Fig. 5a and d but Fig. 5 only extends to 500 m, so this statement is confusing.

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  • Figure 9: What exactly is plotted here? Is this a Hadamard product of the footprint and the emissions?

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  • Page 23: The two paragraphs at the end of Section 3 are identical, delete one of them.

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Reviewer #2

Summary/General comments:

  • …This is an important advance to the field, in particular because these results extend further to other basins as it is indicative that daytime mass balance estimates can be representative of the full diurnal/annual flux, highlighting concerns brought up by Schwietzke et al., 2017 are likely overstated. My major problem with the manuscript is the introduction is not really appropriate for the paper and is riddled with misconceptions and inappropriate citations. I strongly recommend publication, but first the authors need to rewrite the introduction (and other small portions) to more accurately focus on what this manuscript studies and the importance to the field, and highlight the implications of this work in validating the midday mass balance estimate.

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Major comments:

  • The lack of page numbers and line numbers makes review comments much more challenging - these should be added in the revision.

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  • Introduction/importance of paper: The first sentence of the abstract and of the introduction are both false statements. Oil and gas activities have increased greatly in the US in the last decades, but whether this has corresponded with a correlated increase is controversial and unproven. Turner et al., 2016 claim this, but Bruhwiler et al., 2017 directly contradict this finding. Further, global methane has only been increasing in the last decade (since 2007)-it was stable the previous period and it is unclear if the recent rise is attributable to sources or sinks (Turner et al., 2017 or Rigby et al. 2017 PNAS). This speaks to a larger introduction problem - I would recommend deleting everything before the final paragraph on page 2 of the introduction ("Oil and natural gas exploration, production..."). There are many inaccuracies in the above section (for example the section on leak rates misses some important citations and highlights some papers that have since been shown to have problems), and much of this is not really relevant for the paper. The introduction should focus on the Uintah basin and it's unique role. Further the introduction should invoke the Schwietzke et al., 2017 paper that presents daytime mass balance estimates as possibly biased. The contextualization of the Uintah basin in the US should really refer largely to the top-down estimates made from the Peischl et al., JGR 2015, Peischl et al., JGR 2016, Karion et al., GRL 2013, Karion et al., EST 2015, Petron et al., JGR 2014, Smith et al. EST 2017 for mass balance and Turner et al., 2016; Millet et al., PNAS 2013 for regional. The Schneising et al., 2014 paper should not be referenced as this has been shown inaccurate (actually almost directly contradicted by Peischl et al. 2016 airborne results, illustrative of the need of the space-based approaches to have ground based validation as was done in Four Corners). Ren et al., 2017 should not be referenced (major problems with the attribution to oil/gas and leak rate, with papers coming out soon to illustrate this). The final paragraph of the introduction should expand on this studies ability to comment on the accuracy and representativeness of the mid-day mass balance approach.

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  • Likewise, the final paragraph in the discussion section should be removed - it simply is not relevant to the study. The proceeding paragraph should be expanded upon as the results in this paper really illustrate even a single day midday mass balance assessment can prove to be robust and representative, and that the Schwietzke paper results may hold for the Fayettville basin on the days they flew, but is likely not extendable to other basins.

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  • Title: I would suggest re-writing the title. Something like "Confirmation of elevated methane emissions in the Uintah Basin with long-term ground-based measurements and a high-resolution transport model"

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  • Key point 3: The EPA inventory is not state of the science and should not be represented that way. There are much better ways to generate an inventory -- this simple is the EPA method and has now been gridded.

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  • Figure 2 and text/plots throughout: Methane should really be presented in parts per billion (ppb), not ppm. The variation is all on the ppb scale and that is more standard and would be more readable.

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  • Paragraph below Figure 3: remove sophisticated before "bottom-up approach based upon .." as the EPA inventory is really not sophisticated.

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  • Section 2: Should add here some discussion of how the background condition is derived for the model. I understand later you use one of the measurement sites, but it would be helpful for this to be explained here.

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  • Paragraph before section 3.3: How is the ceilometer being used? What approach to calculate pbl height? Ware et al. JGR 2016 show that the ceilometer using a log-transform approach will be statistically biased. Please expand on the discussion of how the ceilometer is used and compared with the model.

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  • Figure 7: I'm not sure what I should take away from this figure?

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  • Figure 9: I think this should likely not be plotted on a log scale. It also would be useful to have contours on this figure (say 50% and 90%).

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  • Figure 10: What is the role of background here? Is the distribution fully from variation from local sources/pbl depth? Would similar distributions of enhancements look the same?

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  • Last 2 paragraphs of section 3: The ceilometer becomes important here and I would like to better know how accurate it is in these comparisons.

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  • Discussion: Should we expect the same emissions as Karion? The measurements are for different years - have any practices changed? Are activities the same? Have the large venting problems been addressed?

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  • I'd like a more quantitative estimate of what the fluxes are with uncertainty derived from the modeling. It is very compelling that the Karion estimate derived inventory is consistent and the EPA is too low, but some clearer quantification of the flux and associated possible uncertainty would be critical here.

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  • Data needs to be made publicly available with reference to location in paper.

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Reviewer #3 (Scot Miller)

  • Holistic suggestions:Some of the references (particularly in the introduction) are not a great fit for the associated statements. I have pointed out all of the instances I noticed in the specific suggestions section below. In general, I would be vigilant on this point when revising the paper.

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  • Some of the figures look like they are from png or jpeg files, not postscript files, and they look pixelated when I try to zoom in. If postscript versions of the figures are available, I would consider submitting those for better figure quality.

Specific suggestions:

  • Have emissions increased? Are you referring to the US or globally? Recent studies from Lori Bruhwiler and Daniel Jacob's research group indicate that emissions increases from the US have been relatively modest in the past decade.

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  • Introduction: "Global methane (CH4) emissions have increased rapidly over the last few decades with satellite observations documenting a 30% increase in CH4 emissions over the 2002 - 2014 period [Turner et al., 2016].

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  • More recent papers from Lori Bruhwiler at NOAA and Daniel Jacob's group at Harvard have revised this estimate downward to about 10%.

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  • Introduction: The first page of the intro is framed relatively pessimistically. Based on the current text, one might think that natural gas extraction is horrendous for the environment. However, the air pollution impact of natural gas are still far less than coal and the GHG emissions are likely smaller as well. Instead, you might consider framing these paragraphs a bit less pessimistically. For example, you could point out that natural gas has the potential to be a 'bridge fuel' between coal and clean energy but that we really need to understand and mitigate the emissions in order to realize this potential. Furthermore, these emissions are due to leaks or inefficiencies and are arguably fixable or avoidable.

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  • Introduction: "Through a combination of in situ CH4 concentrations and meteorological transport modelling, emission rates can be inferred [Turner et al., 2016]."
    I don't think Turner et al. used meteorological transport modelling (or it was not a primary component of their analysis). I would pick a different example here.

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  • Introduction: "These activity rates are then multiplied by estimated emission factors (per unit activity) to determine an emission rate...."Consider adding a citation to an EPA inventory document or EDGAR inventory document here. I think those sources would be most relevant to this sentence. By contrast, Turner et al. is primarily a GOSAT-CH4 study and Miller and Michalak is a review paper.

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  • Introduction: "The leak rates in natural gas extraction and productions regions are generally much larger and more variable than those in urban natural gas distribution systems [McKain et al., 2015]."McKain et al. (2015) estimated leak rates for distribution pipelines in Boston. Boston is not an extraction or production region. I would use a different reference here.

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  • Section 2.2: Some people prefer the term "mixing ratio" over "concentration".

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  • Section 2.4: "The Thompson microphysical scheme and Mellor-Yamada-Janjic planetary boundary layer scheme were used in the simulations based upon the results of previous simulations in Utah basins [Neemann et al., 2015; Foster et al., 2017]."I think a lot of previous WRF-STILT simulations use a Yonsei University PBL scheme. Are these schemes used here better than Yonsei? I am mostly asking out of personal curiosity!

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  • Section 2.4: Paragraph starting with "The STILT-produced backward trajectories are used to calculate footprints...."If you are space-limited in this paper, you might consider cutting the equation and associated description and instead refer the reader to Lin et al., 2003 and Mallia et al., 2015.

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  • Sections 3.1, 3.2, 3.3, and portions of 3.4: All of these sections provide a really great and thorough diagnosis of atmospheric transport patterns and atmospheric transport errors. With that said, I think it would be ok to move some of this material to a supplement if you are space-limited in any way. That would allow you to more prominantly highlight the main take-away messages of the article.

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  • Figure 9: Would it be feasible to put this plot on a scale that is easier to interpret or has a clearer physical meaning? For example, you could color-code or contour the regions that contribute different percentages to the total overall footprint.

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  • Figure 10: What is the take-away message of this figure? It looks like the mixing ratios have a skewed distribution at all sites, but what does this distribution tell us about emissions, atmospheric transport, etc.? I would consider cutting this figure if it does not have a clear takeaway message.

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  • Discussion: A lot of the results (sections 3.1-3.3) analyze and diagnose atmospheric transport. I think you could include some high level take-away messages in the discussion. For example, what did you learn about modeling transport in a confined/mountainous basin like the Uintah? Do you have any recommendations for future, regional top-down studies that require accurate estimates of atmospheric transport? Overall, the results are very meticulous and detailed, and I want to encourage the authors to zoom out a bit more in the discussion and reflect on the broader implications or take-home messages of this work.

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  • Discussion: The EPA inventory is national in scope, so it does not surprise me that the inventory is not very accurate in a specific basin like the Uintah. This point could be worth mentioning. I wonder if Maasakkers et al. used natural gas leak rates that vary by basin and whether results in this paper (and other oil and gas studies) could be used to inform spatially-variable leak rates in national inventories. Furthermore, I am curious why the EPA inventory has what looks like an inaccurate spatial distribution for the Uintah (particularly in comparison to the NOAA inventory). Presumably the NOAA studied used better activity data. I think there are potentially some larger questions here about how basin-specific studies can inform national-scale inventories (i.e., how to bridge these different spatial scales).

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This is a good point. Maasakkers et al. did not use gas leak rages that vary by basin

  • Discussion, last paragraph: This paragraph sounds a bit dramatic (e.g., "public outcry"). Furthermore, the Aliso Canyon leak does not seem particularly relevant to this study; it was a catastrophic, once-off event and seems pretty different from business-as-usual leaks from the Uintah basin. Instead, you could close by reminding the reader that natural gas could be a really great bridge fuel, but that this potential could be undone by leaks. Furthermore, leak rates likely vary a lot by basin, so national-scale inventories are not sufficient for quantification and mitigation (at least not given their current capabilities). This study contributes to knowledge of oil and gas emissions by robustly quantifying emissions for one basin with a particularly high leak rate.