Exploiting stagnant conditions to derive robust emission ratio estimates for CO<sub>2</sub>, CO and volatile organic compounds in Paris

Ammoura, Lamia; Xueref-Remy, Irène; Vogel, Felix; Gros, Valérie; Baudic, Alexia; Bonsang, Bernard; Delmotte, Marc; Té, Yao; Chevallier, Frédéric

doi:https://doi.org/10.5194/acp-16-15653-2016

Articles | Volume 16, issue 24

https://doi.org/10.5194/acp-16-15653-2016

© Author(s) 2016. This work is distributed under
the Creative Commons Attribution 3.0 License.

https://doi.org/10.5194/acp-16-15653-2016

© Author(s) 2016. This work is distributed under
the Creative Commons Attribution 3.0 License.

Articles | Volume 16, issue 24

Research article

|

20 Dec 2016

Research article |

| 20 Dec 2016

Exploiting stagnant conditions to derive robust emission ratio estimates for CO₂, CO and volatile organic compounds in Paris

Lamia Ammoura, Irène Xueref-Remy, Felix Vogel, Valérie Gros, Alexia Baudic, Bernard Bonsang, Marc Delmotte, Yao Té, and Frédéric Chevallier

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Final revised paper (published on 20 Dec 2016)
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AC: Author comment | RC: Referee comment | SC: Short comment | EC: Editor comment

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RC C7600: 'Review of “A new method for estimating emission ratios in the urban atmosphere: examples of ratios of CO2, CO and volatile organic compounds in Paris”', Anonymous Referee #2, 05 Oct 2015
RC C7967: 'Review of Ammoura et al', Jocelyn Turnbull, 13 Oct 2015
AC C10340: 'Author answer', L. AMMOURA, 10 Dec 2015

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

AR by L. AMMOURA on behalf of the Authors (15 Jan 2016) Author's response Manuscript

ED: Referee Nomination & Report Request started (31 Jan 2016) by Jennifer G. Murphy

RR by Jocelyn Turnbull (12 Feb 2016)

Suggestions for revision or reasons for rejection

I previously reviewed an earlier version of this paper, and this review addresses the revised draft.

As I said in my previous review, this is a nice study with a good dataset that has been carefully collected. The authors develop a clever data analysis method to determine emission ratios between trace gas species that biases the result towards periods of stagnant air when enhancements in trace gases are high. They thus avoid the problem of spurious emission ratios during periods of low signal-to-noise. The analysis shows a strong seasonal cycle in the CO:CO2 ratio which is most likely (although not conclusively demonstrated to be) due to wood burning in winter.

General comments:
The revisions relative to the previous version are modest, mostly addressing the minor points of clarity. The largest revision was to further discuss the reasons for the seasonal cycle in the CO:CO2 ratio and compare with the AirParif inventory – this is a very nice improvement to the paper. Many of my other comments have been very well addressed in the response to reviewers but have not been incorporated in the paper itself. To be clear, a question or comment in the review is meant to imply that it needs to be addressed in the paper itself unless the authors are able to justify why it should not be addressed. I’ve listed changes that still need to be added in my specific comments below.

My main concern with the paper was and remains that the title and abstract imply a discussion of VOCs, but they are mentioned only briefly in the substance of the paper. In their response to reviewers, the authors make a case that there is insufficient data to make a useful comparison with other VOC emission ratio studies. Fair enough (although I disagree), but the authors need to make a choice here: either remove the VOC component from the paper altogether, or use the VOC data to draw some conclusions. The current state – with VOCs highlighted in the title but not really addressed at all – is not acceptable.

My second general issue was that the paper highlights the “new method” rather than the results. I appreciate the authors comments in response to the second reviewer that their “new method” refers to the data analysis technique to derive the emission ratios, rather than that the tracer:tracer method is new, but the title and abstract remain misleading. Some rewording to make this distinction is needed.

Overall, this paper is a nice contribution and is suitable for publication in ACP, but still needs some significant revisions to address the concerns previously raised as well as some additional more minor comments.

Specific comments from previous review that require follow-up:
Section 2.2.2. Is this the same Picarro unit as used for the MEGAPOLI campaign?
This was answered in the response to reviewers, but needs to be added in the paper text.

Section 3.1. Second paragraph. What VOC species were analysed? The only place they are listed is in table 1. A fleshed out discussion of the VOCs, their sources and sinks, etc should be added.
The authors say in the response to reviewers that they will add this information, but I don’t see it in the paper text.

Section 3.2. The 5th percentile baseline method does not take into account changing wind direction. For example, the lowest values could be when the wind comes from a clean air sector. When the wind comes from a sector with significant sources upwind of the city, the urban background could be much higher. How might this impact the results?
I am not convinced of the argument presented in the response to reviewers (and in any case, it should be addressed in the paper itself). You say that wind from the continental sector gives a background of 410.2 ppm whereas from the oceanic sector background is 402.4 ppm. So if the wind varies between these two sectors over the three day moving window, wouldn’t the background be too low for the times during that window when the wind was from the continental sector?

In interpreting these results, the authors should consider that Miller et al (2012) showed that using total CO2, the CO:CO2 ratio can be much lower than the CO:CO2ff ratio, since even in winter there can be a significant biogenic CO2 source. How would the seasonality in the biogenic CO2 source/sink impact the CO:CO2 ratio? Could this be important to the overall seasonal cycle observed?
The explanation in the response to reviewers is a reasonable justification – put it in the paper!

As I said in my general comments, this section is weak and would really benefit from a comparison of the observed VOC:CO2 ratios with inventories and/or studies from other urban areas. There are a number of urban and regional studies that have looked in detail at the ratios of VOCs:CO that would make useful comparisons, as well as several that have looked at VOC:CO2 or VOC:CO2ff ratios.
See my general comment in this review. This section remains very weak and needs to be expanded to give meaningful interpretation of the VOC ratios OR the VOC component should be removed altogether.

New specific comments:

Lines 44-47. See also Turnbull et al 2015 for discussion of how choice of background can strongly influence the calculated emission ratios.

Lines 62-66. Does AirParif account for biogenic and/or natural sources? Surely they must be important at least for some species.

Section 2.1. Please add something about the footprint of the sampling sites.

Line 115. Remove word “continuously”.

Lines 135-137. Please provide references to justify that the VOC sources are shared with CO and CO2.

Lines 160-169. Please provide references for justification of the lifetimes of the various species.

Section 3.2. Please also see Turnbull et al 2015 for discussion of background choice and how it influences emission ratios. They show that measurements from sites far afield and/or from the free troposphere can give misleading emission ratios since they implicitly incorporate emissions from a large area rather than just the urban area of interest.

Section 3.2. I’m still not convinced about the CO2 background choice, particularly in summer. In summer, drawdown will result in low CO2 values during the afternoon, whereas at night, the effective background might be expected to be higher, but the 3 day moving window doesn’t account for this. Presumably the MACC background with its 3 hourly data addresses this issue, but I don’t see any mention of it in the paper.

Section 3.3.1. r2 is not really a good way to evaluate goodness of fit in this case when there are errors in both species. Please justify the use of r2 vs chi-squared or other statistic.

Section 4.1. As is clearly pointed out in the paper, the method of calculating ratios biases the results to periods of stagnant air. How might the footprint of the sampling site vary between stagnant air and periods of strong mixing, and would it change the interpretation?

In the text, references to figures point to the wrong figure numbers in several cases.

Jocelyn Turnbull
GNS Science, New Zealand

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RR by Anonymous Referee #2 (14 Mar 2016)

Suggestions for revision or reasons for rejection

Review of revisions for “A new method for estimating emission ratios in the urban atmosphere: examples of ratios of CO2, CO and volatile organic compounds in Paris”

Overall, I am rather disappointed by the revisions made in response to feedback from myself and the other reviewer. The author’s made interesting, valid measurements, and have conducted interesting analyses, but there remain issues that need to be addressed (some larger than smaller) in order for me to recommend publication. Concerns raised by myself and the other reviewer need to be rigorously addressed—given the substantial feedback raised the modification of a couple sentences and addition of 2 paragraphs really isn’t sufficient.

“new method” issues. Both of the reviewers raised the point that the ‘selling’ of the manuscript in the title, abstract, and body as a new method was not accurate and misleading—and this has not been addressed by the authors. The authors may feel they are presenting a new method, but this needs to be accurately conveyed by the manuscripts language, and as both reviewers have taken issue it would seem the current language is inappropriate. Relatedly, the number of references is still light, in part because prior with CO/CO2 emission ratios is still not very well cited.

VOC’s: there has been some small addition of VOC results, but still far from sufficient. There needs to be discussion in the analysis and conclusion of these results! Are these results consistent with the hypothesis put forward regarding seasonality of CO/CO2? Do these ratios show the impact of wood burning as theorized for CO/CO2? As stated before, if VOC’s are to be included, then they need to be fully incorporated in the analysis. It isn’t even clear if Table 1 and Table 2 listed in the response to reviewer 1 made it into the paper.

Representativeness of sampling: The author’s has not expanded or explained the representativeness of sampling to my satisfaction. The authors assert in the comments to reviewers, wind speed was < 1m/s and they estimate the area of influence to be ~3.5 km. First—how is this estimated? Second—this would be considered by many to be a rather local signal, and not necessarily representative of the entire Paris urban domain. Could this region of influence be different seasonally and explain the seasonal signal seen?

Background selection/importance of dilution: The author’s assert that they need not worry about dilution since their sampling sites are at 30m or closer to the ground, and the entrainment layer does not extend this low (not this discussion is only in response to reviewer and not in the main text). This is not an accurate conclusion. Every urban observation of CO2 shows a strong diurnal cycle, with minimum value seen in the middle of the day and maximum value in early morning, completely due to boundary layer dilution/mixing dynamics, even though emissions peak during the day. See for example Figure 1 in McKain et al., PNAS. 2012. Emissions in the night accumulate in the shallow mixed layer, and are diluted as the mixing layer develops throughout the day. The fact that the observations in Salt Lake City were near the surface and not in the direct entrainment zone does not remove them from being impacted by this dilution—air mixes within the mixed layer.
So, the author’s assertion that they do not need to consider this dynamic needs re-assessment. As I indicated before, the author’s may be able to pursue and argument that these issues may not matter because the size of the signal they are working with is very large… I am not partial to how the argument is made, but the author’s must explicitly address this issue in the manuscript and explain why their background approach is robust to these errors. The also must address to what level their approach might be in error—a 10% bias may be significant.

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ED: Reconsider after minor revisions (Editor review) (13 Jun 2016) by Jennifer G. Murphy

The reviewers bring up several concerns that have not been addressed in the revised version of the manuscript. I encourage the authors to consider all of the comments brought forward by the reviewers, including the incorporation of some responses to the reviews of version 1 into the manuscript. Below I highlight the specific aspects that I agree need to be addressed/improved in order for the manuscript to be acceptable for publication:

1) More emphasis is needed in the title that the ‘new method’ refers to the selection of low wind speed data rather than the tracer:tracer ratios. For example, “Exploiting stagnant conditions to derive robust emission ratio estimates for CO2, CO, and VOC in an urban area”. Because the authors are emphasizing the development of this ‘method’ they may want to provide some guidance in the conclusions section to others who seek to apply this in different urban areas.

2) A more fully developed description of the VOC data is required. At a minimum, a list of each of the VOC that will be analyzed should be provided in the methods section. Furthermore, some information on the sources and sinks of the VOC is required to provide context for the results of the analysis. Are these VOC from similar sources to the CO and CO2? Are they expected to have seasonal cycles in their emissions? How might their sinks/lifetimes change with season? I find that the language used on Line 371 and in Table 1 describing a ‘satisfactory agreement’ between the two campaigns is confusing. Given that you have found strong evidence for a seasonal cycle in the CO/CO2 ratios, why is it expected that the VOC ratios would be consistent between campaigns? If you want to highlight ratios that remain consistent, I would recommend using that word, rather than ‘satisfactory’. A further question about the VOC analyses – presumably the ratio of VOC1/VOC2 should be the inverse of VOC2/VOC1 – is that really true for your analyses? It would be good to confirm since it could highlight situations where the two tracers have sources that are not in common.

3) Representativeness and footprint – given that the method emphasizes low wind speeds, it would be valuable to have a sense of the scale of the region impacting the measurements at each site. Especially given that a comparison is being made with the AirParif inventory, is it expected that the citywide totals or avera

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AR by L. AMMOURA on behalf of the Authors (11 Jul 2016) Author's response Manuscript

ED: Publish subject to technical corrections (12 Jul 2016) by Jennifer G. Murphy

AR by L. AMMOURA on behalf of the Authors (20 Jul 2016) Manuscript

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We propose a new approach to estimate urban emission ratios that takes advantage of the enhanced...

Exploiting stagnant conditions to derive robust emission ratio estimates for CO2, CO and volatile organic compounds in Paris

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Interactive discussion

Peer-review completion

Exploiting stagnant conditions to derive robust emission ratio estimates for CO₂, CO and volatile organic compounds in Paris