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 |