Net CO<sub>2</sub> fossil fuel emissions of Tokyo estimated directly from measurements of the Tsukuba TCCON site and radiosondes

Babenhauserheide, Arne; Hase, Frank; Morino, Isamu

doi:https://doi.org/10.5194/amt-13-2697-2020

Articles | Volume 13, issue 5

https://doi.org/10.5194/amt-13-2697-2020

© Author(s) 2020. This work is distributed under
the Creative Commons Attribution 4.0 License.

https://doi.org/10.5194/amt-13-2697-2020

© Author(s) 2020. This work is distributed under
the Creative Commons Attribution 4.0 License.

Articles | Volume 13, issue 5

Research article

|

27 May 2020

Research article |

| 27 May 2020

Net CO₂ fossil fuel emissions of Tokyo estimated directly from measurements of the Tsukuba TCCON site and radiosondes

Arne Babenhauserheide, Frank Hase, and Isamu Morino

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Final revised paper (published on 27 May 2020)
Supplement to the final revised paper
Preprint (discussion started on 05 Oct 2018)
Supplement to the preprint

Interactive discussion

Status: closed

AC: Author comment | RC: Referee comment | SC: Short comment | EC: Editor comment

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RC1: 'Referee comments - Babenhauserheide et al 2018, amt-2018-224', Anonymous Referee #1, 30 Oct 2018
- AC1: 'Replies to referees', Frank Hase, 17 Sep 2019
RC2: 'Review for “The Fossil Fuel Emissions of Tokyo estimated directly from measurements of the Tsukuba TCCON site” by Babenhauserheide, A, Hase, F. and Morino, I.', Anonymous Referee #2, 04 Nov 2018
- AC2: 'Replies to referees', Frank Hase, 17 Sep 2019

Peer-review completion

AR: Author's response | RR: Referee report | ED: Editor decision

AR by Frank Hase on behalf of the Authors (18 Sep 2019) Author's response Manuscript

ED: Referee Nomination & Report Request started (23 Sep 2019) by Helen Worden

RR by Anonymous Referee #2 (06 Oct 2019)

Suggestions for revision or reasons for rejection

Review for “Net CO2 Fossil Fuel Emissions of Tokyo estimated directly from measurements of the Tsukuba TCCON site and radiosondes” by Babenhauserheide, A, Hase, F. and Morino, I.

The manuscript presents an approximation method for determining greenhouse gas emissions from large cities close to a TCCON measurement station. A general algorithm is developed for Tokyo that the authors suggest can be applied to other cities. Comments from the first review round have been adequately addressed. In particular, the methodology description section has greatly improved. Also, the expanded conclusion section now has a stronger connection to the rest of the paper. I have some very minor additional comments below, to be addressed prior to the manuscript being accepted for publication.

MinorComments:
1. Pg 7, ln 1-3: I disagree that only enhanced concentrations are seen between 5 and 15 m/s between 170º and 240º. The left plot of Figure 3 shows negative ∆XCO2 of between -0.75 and -1.00 ppm. Additionally, Pg 7, line 1 explains that both positive and negative residuals are used. Figure 5 also shows negative and positive enhancements in the "Tokyo" influenced directions. Please clarify what is meant by "only bins with an enhanced concentration" means.

2. Figure 4: Please separate out the wind speed and wind direction plots into two plots 4 (a) and 4 (b). Also, the caption mentions 1000 m altitude, so please also show the altitude in meters as well as pressure levels.

3. I am confused about the height relating to the average column wind speed. On pg 10, ln 2, it states (0-2000 m). However, Pg7, ln 24 and ln 31 says the upper limit is 1000 m. Please clarify which it is or why it changes?

Technical Corrections:
1. Pg 9, ln 7: apriori -> a priori
2. Pg 11: Change A_aff in line 1 and Eq 5.

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RR by Anonymous Referee #1 (08 Oct 2019)

Suggestions for revision or reasons for rejection

The authors made a nice start towards going through my numerous initial comments. However, some of these were only glanced over or skipped - especially some of the more scientifically important comments (highlighted below with **). Sometimes good responses were given, but then changes were not reflected in the manuscript. In addition the updated manuscript and auxiliary material do not always match what is in the responses. Again, I will reiterate my initial review that I think this is a fair start to a difficult problem but needs work especially on comments I already made.

Please recheck:

2) The changes in the response do not match the changes in the manuscript.

There are 2 uncertainties on the fluxes, please provide a short description why in the abstract so people do not need to read the full article. I think most global inventory (e.g., ODIAC) developers would generally agree that comparing global inventories with local flux estimates is generally not an ideal comparison.

Pisso et al. (2019, doi: 10.1186/s13021-019-0118-8) should be referenced somewhere in this paper and compared with (does not need to be the abstract).

The authors should include a caveat in the abstract that matches 2.1 in the response. Namely this study was not designed to have the best accuracy using all possible measurements, but rather is just a starting estimate from 1 ground site and should not be interpreted as being unbiased with a high accuracy (e.g., for policy makers).

3) Again, I don’t know why Frey et al. 2015 (instrumental), Chen at al. 2016 (CH4 not CO2), and Butz et al. 2016 (not fossil fuel) are included as references here. If the authors insist on including these only marginally related citations, they should put them in a different location, for example in the conclusions section where mobile spectrometers are mentioned. In that case the authors may also consider citing Luther et al., 2019 (CH4 from coal mines, doi: 10.5194/amt-12-5217-2019), Frey et al. 2019 (also instrumental, doi: 10.5194/amt-12-1513-2019), Viatte et al. 2017 (similar to Chen, but used a different inversion method doi: 10.5194/acp-17-7509-2017).

5) I still don’t think “inexpensive” is a word that should be used here. Smaller satellites can have a cost of less than CAD 10 million (e.g., GHGSat Claire: https://spectrum.ieee.org/energy/environment/private-satellite-to-track-carbon-polluters). Besides, the scope of satellite missions and ground-based missions is often very different which makes a simple cost comparison difficult or not particularly useful.

12) I still think it strange to say the granularity around the end/beginning of the years where there is a sharp dip is the same as everywhere else in the fits.

13) a) It seems perhaps the original supplement was uploaded again, so I am unable to see the results of the ccgfilt. To me as a reviewer the current method with the multiple steps is actually more convoluted.

b) **Degrees of polynomials – but why 6? Why not 4, or 8? Or 15? I’m guessing you had some sort of adjusted R^2 you analyzed to reduce overfitting? Or was it more just qualitative as it sounds on page 5 of the manuscript? The beginning/end of year looks over fit.

c) **Could you comment on the very low R^2 for the diurnal fit in the manuscript?

d) **The claim that both “background” and “enhancements” can be measured from one site is one of the key requirements of this study. If the background values are not in any sort of agreement with those more removed from Tokyo (but at a similar latitude and not too far away) then the flux bias could be quite large.

19) I still think it would be nice for the reader to not have to turn to the auxiliary material to see the model used was GDAS 1 degree, and starting heights varied from 20-30 meters. That way those familiar with HYSPLIT will know it is just a basic estimate (coarse grid for scale of interest, and trying to model winds close to the ground), hence why the radiosondes were critical.
24) So low outliers are not clipped to the left? I do not understand why having a greater focus between 0 and 1 is less valid. If a linear scale is insisted upon, why not make the ratio the opposite way?

25) **This is better, but there are still major issues.

a) Please include a citation for your chosen notation. It seems almost arbitrary. See for example Chen et al., 2016.

b) Again, I’m concerned that units were not thoroughly checked or at least labelled. I may have been off on page numbering, but I don’t think that’s an excuse for units not working out or at least not matching. Units are not listed for all terms in the table. Please use kg instead of g for mass.

c) The 0.9975 factor from Bannon needs more of an explanation in this manuscript.

d) TCCON measuring a dry-air mole fraction was precisely my point. By not including a water correction term, the “unit air column mass” is now based on a whole or “wet” air fraction rather than a dry one, which will bias “CO2 column mass.” See Appendix A in Wunch et al. 2011 (doi: 10.5194/acp-11-12317-2011).

e) If you insist on using different units, why not also show the actual plots where you calculated “R”? Do you do the subtraction in ppm or in kg/m2? What is written in the text still does not agree with what is in the table.

26) **No response?

28) **This choice of location seems somewhat arbitrary. Not to mention the calculations seem very sensitive to this arbitrary choice.

29) This looks like actually almost no change was made at all. I don’t see the necessity of dedicating 3 equations to a unit conversion.

30) ODIAC is on a 30 arc second grid (see page 545 of Oda et al. 2011 doi: 10.5194/acp-11-543-2011), not a perfect distance grid. To reduce any possibility of misinterpretation you could you specify these are angular degrees.

31) Why is this response not incorporated into the manuscript? Can you show the TIMES grids selected on a map?

32) But as you have admitted, the data you work with only makes measurements during daytime hours. This biases the result if daytime emissions are different from nighttime (which they almost certainly are).

33) a) Accuracy of background?

b) Why didn’t the rest of this discussion make it into the manuscript?

34) What about #2?

39) If this does not yet exist, then this claim should not yet be here. A better citation may be Frey et al., 2019 (doi: 10.5194/amt-12-1513-2019) which at least has a 3.5 year dataset.

The supplement does not actually appear to be updated.

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ED: Reconsider after major revisions (09 Oct 2019) by Helen Worden

AR by Frank Hase on behalf of the Authors (17 Feb 2020) Author's response Manuscript

ED: Referee Nomination & Report Request started (19 Feb 2020) by Helen Worden

RR by Anonymous Referee #3 (31 Mar 2020)

Suggestions for revision or reasons for rejection

The manuscript "Net CO2 Fossil Fuel Emissions of Tokyo estimated directly from measurements of the Tsukuba TCCON site and radiosondes" by Babenhauserheide et al. describes a study that tries to estimate the CO2 emissions from the Toyko megacity simply from column-averaged observations of the nearby Tskuba TCCON station. The idea is to calculate a difference between airmasses with enhanced CO2 when the wind is coming from Tokyo and a background that is derived from airmasses coming from other directions.

The method has its pitfalls and limitations which are described in the manuscript. In my opinion, the most critical point is the structure of the actual vertical wind field and the fact that the column observations are only available during day light. So it is is doubtful, if these observations could contribute much compared to the existing information from CO2 emission inventories. However, it is valuable to have done this study even if this is not the case.

The manuscript has already been reviewed in-depth by two other referees, so I do not want to ask for further minor changes. However, I have two general comments that the authors should consider next time:

- I also think that the presentation quality could be improved. The individual plates in the main Figure 3 are rather small. At some point, a sketch of the principal method would have been more illustrative. Also, I think that the structure of the manuscript is not ideal: sections 4-6 contain a mixture of method description and results instead of a clear distinction of these.

- There were also some interesting discussions going on in the review process that did not make it into the manuscript. For example, I agree with referee #1 that the term "inexpensive" on page 2 is not appropriate. Neither method, satellite nor TCCON instrument is "inexpensive". The actual costs are very hard to compare, even if they were applied to the same purpose. It is already wrong to compare instrument cost in the first place as the author does when he claims that 50 stations could be installed and run for the cost of a 10 M CAD satellite mission. That is actually ridiculous as the major cost factor personnel is not part of the figure and the rest would not cover the instrument and operational cost. The authors argue along the same line in the conclusion section. I think this whole cost discussion should be left out completely.

After considering all these points and the replies to the referees, I think the manuscript should be published after all. The authors are free to take my comments into account if the wish.

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ED: Publish subject to technical corrections (01 Apr 2020) by Helen Worden

AR by Frank Hase on behalf of the Authors (09 Apr 2020) Manuscript

Net CO2 fossil fuel emissions of Tokyo estimated directly from measurements of the Tsukuba TCCON site and radiosondes

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Interactive discussion

Peer-review completion

Net CO₂ fossil fuel emissions of Tokyo estimated directly from measurements of the Tsukuba TCCON site and radiosondes