General Comments:

In this paper, Andersen et al. use an AirCore UAV system to quantify CH4 and CO2 emissions from coal vent shafts in Poland using two different methods. These quantified results are compared with directly measured (in stack) emissions, both hourly and aggregated by vent/day. Andersen et al. then use various techniques to upscale the quantified emissions in order to obtain regional emission estimates.

Overall, this work has important implications in the field of methane quantification from coal vents. However, there are non-negligible gaps in the science presented here. Most notably, the authors do not adequately explain the effect of and error introduced by flights when the maximum detected concentrations are on the edge of the “curtain”, indicating that the peak plume concentrations may not have been sampled. Furthermore, the manuscript lacks an important figure which directly compares each flight-based quantification with direct (in stack) measurements. The manuscript can also be improved with a clearer, more coherent argument for the potential impact the manuscript will have on the state of this science. With these changes, this manuscript will be a valuable addition to the literature surrounding methane quantification, AirCore viability, and upscaling procedures. I was glad to get to read this manuscript and provide (hopefully) helpful feedback.

Specific Comments:

I believe there is a lack of explanation in the methodology section regarding the quantification procedures. For the inverse gaussian approach, what point(s) are plugged into the equation? Are multiple points used and compared/averaged? Is the maximum concentration used and assumed to be the center of the plume? How are the dispersion parameters determined (what method), and how do they affect results? Are concentration peaks dampened by the AirCore method due to mixing in the sampling tube before analysis, and how does this effect quantification?

A critical issue is how you address those flights where the maximum concentration is at the edge of the curtain. How are these flights interpreted? It is hinted at in section 3.2, but I’m confused as to how you are calculating either the IG or MB if the majority of the plume is outside the curtain. This may be clarified by some of the questions in the above paragraph. It would also be nice to see some type of error analysis for each quantification method; that is, how do things like wind variability, peak dampening, dispersion parameters, etc. introduce error and how is this error quantified.

In the same vain, I think there is some issue with how error is represented in the aggregate data. For example, in the aggregation of quantified flux from Pniowek IV (Figure 5c) you claim an error of +-0.2kt/y due to the standard deviation of averaged points. However, in the individual day data for this vent (Figure 6c), the inherent error in each measurement is on the order of 3kt/y. A more robust error propagation analysis would make the aggregate numbers more defensible.

A plot I’d really like to see is the hourly emissions compared with the flight quantified emissions (basically combining Figures 6 and 7). There is a bit of a roundabout comparison in the “hourly inventory” vs UAV quantified analysis (Figure 8b), but the critical representation is missing. The direct comparison is a key figure as it validates your UAV quantification approaches with real, empirical vent emissions data. As you state, emissions vary both intra and interday, so comparing UAV measurements at specific times with the directly quantified vent emissions instead of relying on aggregate data (like that presented in Figure 9) is an important distinction.

In section 2.1, you describe the del13CH4 data collection, but I am confused as how this is conducted. Are you capturing the outlet air of the Picarro upon measuring CH4/CO2 from the AirCore in a bag then analyzing? Some clarification would be helpful.

In my opinion, the argument of “weekends/holidays” does not add any value. If anything, it is confusing, as you postulate a reduction of emissions on these days then go on to show otherwise.

Finally, I think there could be some added discussion about lessons learned and recommendations for future use of AirCore technology to quantify vent emissions. Specifically, expanding beyond why the hourly emissions data and individual flight quantifications may not align well and describing how the methods may be improved would be helpful. Similarly, some discussion of the recommendations for best practices to achieve a certain level of accuracy for quantifying vent/regional emissions using AirCore flights would be helpful; such as, how many flights are needed over how many days…etc.

Technical Corrections:

16: Insert (CH4) after methane.

23: Delete “have”

28: Delete “though”

28-29: Rephrase “As an alternative…” sentence. Make sure verb tenses match and phrasing is clear.

34: Is methane the second “most abundant” or just second most important in terms of climate forcing?

49: Citation for coal being 12% of methane emissions?

52: Change “part of” to “some”

54: Change “releases” to “is released”

56: Insert comma between “mines” and “the”

58: Citation for data loggers lacking accuracy and temporal resolution? It seems that your data shows otherwise… high resolution and temporally resolved fluxes from vents.

64: Sources for other studies using UAVs for methane monitoring?

71: Perhaps add a line describing the Merlin mission and how CoMet ties in?

78: Change “strong ties to hard coal mining” to “ containing extensive hard coal mining” or similar.

83: Period after PRTR

83: Remove “the” after “quantify” and before “emitted”

Paragraphs 70-100: Ensure consistent verb tense. Example: 71 – “goal of CoMet is to provide”, 76 – “CoMet campaign was to quantify” etc.

86/89: It goes from 59 flights to 34 quantifications – consider adding a line about filtering and what section you discuss this, otherwise it is confusing why these numbers don’t match.

89: The quantified emissions are of the shafts using the aircore, not quantified emissions of aircore flights.

95-100: Consider removing the “Section 2 presents …, section 3 contains…” and instead replacing with a strong statement about what your results convey and why they are important.

123-124: The names of the vent shafts have not yet been introduced and I did not know what these names meant. Consider revising to introduce the region and vent shafts before this section (maybe move section 2.3 to beginning of methodology).

126: “First few”: specify how many.

126: What meteorological parameters were collected?

129: Add “Meteorology for flights #5 through …”

Section 2.2: Add details about the height of the meteorological sensors.

135-137: “The CSAT3 has an operating temperature … small changes in wind direction” is unnecessary.

144: Give some highlights about what the sampling criteria were to consider a “good flight”

144: The intro said 34 flights were used for quantification, this line says 36 fulfilled the criteria – why the discrepancy?

146: Add “technique” between “this” and “effectively”

153-154: Add the altitude range for the flight to go with duration and downwind distances.

Figure 1: Is there any reason for the different colors for each vent shaft? If so label.

179: How do you account for plume rise? In the gaussian equation, I believe h is typically the “effective stack height” which accounts for advective or buoyancy rise effects of the plume.

Section 2.4: How is the local/regional background accounted for?

196: Add “estimate” after “annual emission”. Also, a source citing the E-PRTR inventory would be helpful.

202: Add comma after “active shafts”

210-211: How do you account for the fact that the operating range of the sensors is <100% RH, but the conditions are often over 100%?

215: Should “concentrations” be changed to “fluxes”?

243-244: The sentence “All the isotopic….” Does not make sense.

Figure 6: I’m confused by the color differences – did different flights use different approaches (MB or IG)? I thought each flight was analyzed in both ways? If not be more clear in section 2 about this. Label what the error bars represent. Consider making the x axis on (b), (c), and (d) so that there isn’t so much white space (restrict to sampling time period). Put in caption what the “N:7-5” means. Overall, I think there may be a better way to represent this data, consider reframing.

298-299: “The Borynia VI inventory ‘may therefore not represent…’” I’d think it clearly does not, given the intra and inter day variability in your other data.

Figure 8: Many of the labels are obscured, overlapping, or otherwise can’t be read.

356: “Best statistics” – do you just mean the most flights? If so say that, if not clarify what “best statistics” means.

363: Wording is confusing

366: Again, is “lowest statistic” just fewest flights?

370: “All over”? Confusing

421, 424, others: Replace “linear curve” with “line”

421: Comma between “rate” and “calculated”

450-456: Instead of “comparing” to estimates then talking about how the estimates don’t include coal, perhaps introduce this idea earlier. In reading, it is confusing why the numbers are so different until I realized that the EPTR estimate really doesn’t represent coal emissions at all.

462: Add “method” after “upscaling”

466/471: These lines contradict one another. “does not accurately represent emissions of the whole region” vs “a useful tool for regional emission estimates”. Best to clarify.

500: Delete “have” between “we” and “used”

S.I.: The color scale makes it so that the peak (and most critical part) of each plume is invisible (white).

Review of “Local to regional methane emissions from the Upper Silesia Coal Basin (USCB) quantified using UAV-based atmospheric Measurements”

General comments:

The authors present a manuscript following a measurement campaign in the Upper Silesian Coal Basin in Poland, where they used an AirCore attached to a UAV in order to measure CH₄ and CO₂ concentrations from several individual coal mine shafts.  They make the case that a regional estimate derived from shaft-specific measurements will be superior to those that assign a single number to each mine, which broadly takes an average number across all shafts at any mine.  They find good agreement between their methane measurements and high-resolution hourly inventory data in some of the shafts, whereas their flights were not able to reproduce well the coarser inventory numbers based on yearly estimates.  They also claim that their CO₂ measurements have found that coal mines may be an overlooked source in the region that is not insignificant.

Overall, the paper is well-written and their ideas are clearly presented.  The CH₄ analysis, in particular, is laid out in a straightforward manner that is easy to understand.  That said, I feel that there are some important elements that are missing and some important changes that need to be made to this manuscript before it will be ready for publication.  In particular, I have strong concerns about the CO₂ analysis, as I do not feel that there is enough data presented to support the conclusion that they have found a missing source of ~1% from the regional inventory, rather than it possibly being an artefact of upscaling.  This, combined with my concern about how there is no independent value to compare the CO₂ measurements against, and some other smaller concerns I detail later, means my inclination right now would be to recommend leaving the CO₂ analysis out of this manuscript entirely.  I also may have found an issue with the stated method of how the hourly methane emission rate is calculated, for those numbers that they later compare their UAV measurements against and find relationships with, which I would like to see clarified.  And I would also like to see further explanation/justification for the first of the three presented upscaling methods, which upscales the yearly inventory numbers using a relationship identified only with the hourly inventory.  Further, I would like to see an expanded discussion of the possible areas of uncertainty including: i) the dangers of upscaling with such a small population of data (which they already do acknowledge briefly), ii) the uncertainties and potential misquantifications inherent in their plume calculation methods (the inverse Gaussian and especially the kriging), iii) the possibility of difficulties introduced by sampling at different times of day and under different atmospheric mixing conditions, and iv) at least some discussion of how the background was defined when calculating the leak rates, along with other ideas the authors may think of themselves.  I am curious, as well, as to whether the experimental set-up may mean that the AirCore samples are taken downstream of the rotors of the UAV, and whether that may introduce some dilution into their measurements (which may also help to explain why the measured values tend to be lower than the hourly inventory numbers).  There are additionally smaller things that should be quicker to fix, but would also be essential, including double-checking the unit scale-factors on each figure that shows CH₄ mixing ratios (which often seem too high by a factor of 10) and the units on the CH₄/CO₂ ratios.  I believe that starting with these changes will make a substantial impact on the quality of the manuscript, and that by the time it is ready for publication, it will be a valuable manuscript to the broader community.

Specific comments:

Lines 47-49: Is there a citation for the numbers in either of these 2 sentences?  It’s a key statement towards the motivation of the study—even referenced in the abstract—so I think it’s important to show where those numbers come from.

Lines 109-110: I am wondering how the AirCore was exactly “attached” to the UAV.  I see that the AirCore is coiled up, and there is a reference a couple of lines up to “carbon fibre box housing”.  Is the AirCore contained within that housing, or is that just the housing of the electronics for the UAV?  It would help if there was a picture showing the set-up.  Particularly I am wondering how it was ensured that the AirCore was measuring from air that was undisturbed by the rotors of the UAV.  It looks like this UAV has 4 vertical rotors, and if the AirCore is taking air from underneath (or otherwise “behind” the rotors), then there may be a risk that the rotors are mixing the air (potentially pulling in more dilute air from the background) just before measurement, and therefore affecting the measured mixing ratios.  If so, I would be interested in knowing how much effect this may have on the ultimate measurements.  And along those same lines, I would wonder about what the effect on sampling rate is when the UAV is moving, considering the primary driver of intake is the ambient pressure.  (Is the AirCore exposed in a way that it would sample more when the intake is pointed towards the direction of movement, because of the higher pressure, and vice versa?  If so, how might that affect the results?)

Figure 2:  The units on these colorscales seem at least a factor of 10 too high.  Were the authors really detecting plumes of 150 ppm of methane?

Line 210: This methane sensor gives output as a percentage concentration?  Am I understanding that correctly?

Line 213: I might be misunderstanding this sentence.  It says “about 5% of the vented air to the atmosphere is from air inflow via the ventilation shaft closure”.  I understand that to mean that there is some quantity of vented air in this region, and that 5% of that total ventilated air comes from the shaft closure here.  That does not sound like the same thing as saying 5% of the total gas flowing through this shaft gets vented.  In order for it to contribute 5% of the total vented gas, we would need to know what the total vented amount is, then we take 5% of that number and use that to see how much of the gas flowing through the shaft would have to be venting.  So, have I misunderstood the statement here?  If not, then the “95% of the flow-rate” scaling factor would not work.

Lines 230-235: This is a lot of words to describe the math, and I think I got a bit lost.  Would it be possible to include the simple formulas for these 3 upscaling techniques?

Line 282: I’m not sure that I’m convinced that there is a potential difference between weekend/holiday and weekdays, given the mass balance numbers.  The inverse Gaussian numbers seem more like they could suggest that, but is there a reason to trust these more than the mass balance numbers?  Feels like one shouldn’t hint at a conclusion either way.  (I assume that the phrasing “this may indicate…” is maybe an attempt to stay neutral, but it still reads to me like it’s leaning towards the conclusion that there is a relationship.)

Figure 6: Maybe this shouldn’t be explained in the caption, exactly, but I’m not finding where in the text it explains why certain flights were deemed worthy of a mass-balance estimate but not of a Gaussian estimate?

Line 297:  Instead of assuming, is there anyone who could be contacted/referenced that would have more insight into why this period is missing from the inventory data?

Line 305: So the inventory seems to contradict the hypothesis that there’s a difference between weekend/holiday and weekday emissions.  To me, though, this seems consistent with the lack of conclusions we could have drawn from the data, anyway?

Figure 7: Looking at Pniowek V, for example because it has the longest timeseries, the inventory would lead me to expect higher measured values on the 19^th, 21^st, and 28^th compared to the 31^st and June 1^st, but that’s not exactly what was seen in Figure 6, which shows low values recorded on all of the flights of the 28^th and potentially high values on June 1^st.  Do we have an explanation for this discrepancy?  (I actually think it might have been nice to combine Figures 6 and 7, so that we see the overlay of the measurements against the reported inventory directly.)

Line 313: Wouldn’t we expect that the correlation between individual flights and yearly reported emissions would be very low, though?  Because day-to-day variability would be so high, in comparison?

Table 2: Could we convert this to a bar chart, maybe?  (One could mark the max/min values separately from the error bars, and include the N numbers at the tops or bottoms of the value bars.) 

Figure 8: It’s difficult to intuit where the 1:1 line would be with rectangular figures like this.  Would it be possible to make these figures square with identical limits on the axes, to really visualize the comparison?  Maybe with a dashed 1:1 line, for reference?  (I understand that this might necessitate dividing this up into 2 figures, in order to fit on the page.)

Figure 8: It also may be helpful to change the legends of each subplot to indicate that it’s the best-fit line from the inverse Gaussian approach, specifically, as is noted in the caption

Line 331: What is the justification for forcing the linear fit through 0?

Line 339: The hourly inventory is going to be used to scale up the UAV-measured concentrations?

Line 341: Of the linear fit from the multiple-days-averaged shaft-specific, inverse Gaussian case?

Figure 9: Is this all the same info from Table 2, it seems?  If so, maybe we can just get rid of Table 2 and refer to this instead?

Lines 358-9: Does this also imply that the sample size might not be enough to accurately quantify the other sites?

Line 362: It doesn’t look to me like there is overlap at Pniowek IV in the mass balance approach…?

Lines 374-5: I think here is where to mention the possible explanations for lower quantification in the air than what the hourly measurements within the shaft show, rather than lines 362-364, which was specifically talking about Pniowek IV

Line 382: One thing I don’t think I understand is, if CO₂ has been measured as well as CH₄ from the AirCore, then why not just calculate the emission rate of CO₂ in the same way as was done with CH₄?  Why introduce some linear dependence with methane and throw away the data that does not sufficiently have that linear dependence?  Is the thinking that, if there are enhancements seen with CH₄, then it’s presumed to originate from the shaft, but if there are enhancements in CO₂, they could also be from elsewhere nearby (are there other CO₂ sources nearby, like running engines?)?  So this is done in order to ensure that one only looks at CO₂ that is believed to be from the shaft?

Line 383: The authors probably should specify which is the numerator and denominator in “slope”, even if it seems obvious.

Lines 385-6: Would it be possible to include these scatter plots in the supplemental info, as well?  I’m curious to see what they look like.

Line 387: I’m assuming the units are supposed to be ppb/ppm and not ppm/ppm?  Additionally, this caused me to look at the figures in the supplemental info, where the flight tracks are provided, and it looks like the scaling factor on many of the colorbars is listed as 10⁴, but it should be 10³, since background methane should only be around 2ppm, not 20ppm.

Line 392: Can the authors explain the NaNs again here?  If there’s not enough data to include an upper and lower bound, maybe it’s better just to state that than to present it as a NaN value.

Lines 407-412: I don’t think I’m following the logic here.  Figure 8 showed that there was no clear linear relationship between the measurements and the E-PRTR inventory, but that a relationship may instead be found when comparing against the hourly inventory.  Then, here, the linear relationship that was found between the hourly inventory and the measurements is used to scale the E-PRTR inventory?  What’s the rationale for that?

Lines 414-419: Might want to include an acknowledgement that the number of sampled shafts is small compared to the total number of shafts in the region (and among those sampled, those that have a large number of samples is even lower), so they may not be representative of the region as a whole.

Lines 421-2: My comment from the last paragraph should apply here, too.  Though I think this is a much more sound approach than the first approach (which I would be tempted to toss out altogether without a clearer justification for why the hourly linear relationship would be directly applicable to the E-PRTR estimates).

Line 441:  When saying that they aren’t statistically different when factoring in the uncertainties, should probably also acknowledge that the uncertainty bars are around 30%, which can be quite large.

Lines 448-460: This illustrates the danger of upscaling to a region from just a few measurements.  The authors note that coal mining activities are not a major source of CO₂ in the region, and that their measurements are also very low.  The flight paths for the CO₂ enhancements are not included, so it’s not apparent how clear or strong the CO₂ plumes really are compared to the background.  Although Figure 10 shows that, though many of the quantifications do not have error bars, the ones that do are often quite large (e.g. Pniowek IV and Zofiowka IV).  And since the E-PRTR inventory does not include coal mines in their inventory, there appears to be no way to independently check whether these values correspond to what would be expected or not.

Lines 475-476: I do not think that one can conclude that the CO₂ inventory is missing a source of about 1%.  Without having more information presented about the nature of the CO₂ plumes that were quantified, it seems within the realm of possibility that contemporaneous CO₂ data recorded with the CH₄ data displayed some stochastic variations (especially if the atmosphere is not well-mixed) that could mistakenly be quantified as small plumes with the inverse Gaussian or kriging techniques, especially if the corresponding background values are not well defined.  Then, by scaling up those small numbers to the size of the region, they become an apparently large number (~1%).  But this feels to me more like a potential artefact of the upscaling than a real missing piece of the inventory.  Would we otherwise have any reason to expect large amounts of CO₂ to come out of coal mines?  (If so, this is something that I guess should also be addressed in the introduction?)  Overall, it is starting to feel like it may be best to leave out the CO₂ analysis altogether.

Line 496: I thought it was only this large for 25 of the 36 flights?  And again I think these units are incorrect.

Lines 509-511: I really disagree with this conclusion without some compelling evidence that it’s not just an artefact of the upscaling.

Line 516: Maybe the authors should point out that their data indicated that at least 5—and probably more—good flights were needed for a decent quantification of a single shaft.

Lines 513-520: All of this (good) assessment of uncertainties should have, I think, belonged in the discussion section.  It’s fine to repeat it here, but it felt like it was lacking above.  Additionally, included in the discussion of uncertainties should be a discussion of the inherent uncertainties involved in the techniques applied (especially with kriging, which can be a very uncertain way to quantify a plume!).

Technical Corrections:

Figure 3: One of the labels is cut off—the one attached to the red marker.

Line 241: The isotope numbers should be in units of permil, not percent.  It’s correct in the figure, but not in the text.  (May need to be corrected throughout the manuscript.)

Line 300: “emitted emission” seems redundant

Line 328: “on an hourly basis”

Line 332-3: “not significant”

Line 338: “Our evaluations indicate”

Line 370: “all overlap with”

Line 374: replace “more than one flights” with “multiple flights”

Line 381: remove “emission” from “emitted CO₂ emission”

Figure 10: The caption describes these plots as “histograms”.  I do not believe that’s the case.

Line 403: “As many as”

Line 448: “linear curves” should be “linear fits”

Line 490: “show very low…”? agreement?  correlation?

Lines 526-28: This last sentence feels like a long fragment instead of a complete sentence, and should probably be reworked