Impact of Drought on Isoprene Fluxes Assessed Using Field Data, Satellite-Based GLEAM Soil Moisture and HCHO Observations from OMI

Round 1

Reviewer 1 Report

Review of “Impact of drought on isoprene fluxes assessed using field data, satellite-based GLEAM soil moisture and HCHO observations from OMI”

 

This paper attempts to use high frequency and reliable measurements from flux towers and surface measurements to improve a modeled isoprene emissions database. This improvement is done using measurements of HCHO from OMI as a proxy. The idea is interesting and the results, when carefully analyzed and properly accounted for, will yield a worthwhile result. However, at the present time there are too many assumptions made in this paper, too many missing factors which may have a larger impact than the modeled results presented, and a quite poor mis-match with the OMI observations at day-to-day temporal scales and grid-to-grid spatial scales. I strongly encourage the authors to make major improvements, and look forward to see their improved results in a re-submission.

 

Major points:

 

A first question about the setup of the study is related to other species which would have a high or higher correlation with the HCHO in your experiment. During your study, how many fires were spotted in the area or within a wind-transported upwind distance? How have you accounted for these upwind fires, which also would produce a large amount of direct and secondary HCHO emissions under drought conditions? What about urban direct emissions of HCHO? What about urban VOCs which also lead to rapid HCHO formation? Noting that urban areas tend to have a strong measurement-based disagreement in terms of magnitude and even sign from your own results (see general points comments below), this leads me to believe that the underlying assumptions of this paper may be flawed.

 

A second question is related to how representative your specific flux site is (radius of 1km) when compared with a single OMI pixel in size (or an average unit of 20km radius as you use)? A similar question with respect to the specific day-to-day scales? Can such really be representative regionally or globally?

 

A third question has to do with the uncertainties in the measurements of LAI, NDVI, and HCHO. You have not specifically mentioned how you deal with these uncertainties, or demonstrated if the differences over your regions of study are larger than the remotely sensed measurement errors.

 

Fourth, the emissions factors that you have used are based on GFED and EDGAR. There are ten of papers indicating that emissions from these datasets when run in models from global through regional strongly underestimate column loadings of BC, CO, and NO2, all based from remotely sensed column measurements. It is great that you are investigating HCHO. However, just randomly scaling up or down emissions is flawed. It is clear from your monthly average maps over the USA that your models have major issues representing the spatial variability of the HCHO columns. This is a process that will require higher emissions in some regions and and lower in other regions, or perhaps an entire new a priori emissions dataset. Please do more research into previous work on this topic, so that you may have a better starting point.

 

There is a very large impact of absorbing aerosols on measurements from OMI in the UV spectrum. I do not see these citations. It is also well known that models being used in your work grossly underestimate absorbing aerosols with respect to column loadings, which have been documented as far back as 2014 by multiple authors (including some of my own papers, which I will not cite here). How are these corrections accounted for? This is particularly important since the same oxidation processes from isoprene that form HCHO will also form biogenic OC, which may be at least partially absorbing in the UV. Especially so if there is any biomass burning smoke in the regions co-emitted and mixed.

 

General points:

 

In Figure 2, while the R2 looks good, the RMS error is very large. Why is this the case? It looks like either the model is not very trustworthy, or the measurement site is not very representative of the larger conditions.

 

From Figure 3, it is clear that your day-to-day and week-to-week variability are most essential. Your R2 statistic looks fine, but your RMSE statistic does not do justice at all. In July and August, it seems on some days, your estimates are very far off. This shows that all analysis with respect to HCHO must be performed at day-to-day or at most week-to-week scale. This is completely consistent with the results of the missing CO and NO2 sources respectively from MOPITT and OMI measurements observed globally in Lin et al. 2020 and regionally by Wang et al. 2021, and the missing feedbacks between extremes in observed NO2 from OMI and meteorological factors (including drought) measurements observed globally by Deng et al. 2020. In all cases these results were made at higher temporal frequency. Therefore, to make the results even reasonably new, I would strongly encourage you to perform all analysis at higher frequency.

 

Figure 4 should be done at a day-to-day or week-to-week level. And normalization would make more sense if it corresponded with the satellite overpass time, as compared to the mid-day time.

 

Figures 5d,5e demonstrates clearly that the variability from day-to-day data is much higher, leading to even some of the monthly-average values, under certain conditions being off. This result must be analyzed much deeper, and at higher temporal resolution. Ideally, you would also show the spatial distribution, since you are claiming that the measurements are representative of a 1km forested area in all directions, yet OMI is already being used to average over a 20km radius.

 

Figure 6 shows that you have many issues to overcome. As mentioned in the general comments, you have not yet satisfied me that HCHO under these conditions is a proxy of isoprene at all. Yes, there is HCHO produced from isoprene oxidation. But there is also HCHO produced from anthropogenic VOC oxidation. There is also HCHO directly emitted from biomass burning and other industrial processes. In fact, this latter most source is much larger in general, and has a kinetic time which is far more consistent with the 20km distance around the source site in which you use to build your models. Here are some specific things that you must do relating to these results before I will be convinced:
(a) June has very large positive differences in Eastern Texas, Western Nebraska, and Pennsylvania, New York and New Jersey which your models do not capture. Your model also has a very strong negative difference in Eastern Georgia which is not found in the observations.

(b) In July the measurements show very large extremes in Colorado, Wyoming, and Northeastern Mexico which your models do not capture at all. Your models show perturbations in Louisiana, Missouri, and Tennessee which are completely spatially mis-placed with respect to the perturbations found in the observations.

(c) In August, significant perturbations observed in Colorado, Wyoming, Iowa, Wisconsin, and Central Texas are observed which do not show up in your models at all. The perturbations in your models in Pennsylvania are too small and geographically mis-placed with respect to the observed perturbations. Your models show a consistent huge decrease throughout the gulf-coast states, yet the observations do not show this consistent and negative value. While there are negative pixels, there are also positive pixels, in particular in urban areas, in particular in Mississippi and Alabama, which are not at all observed in your findings.

 

With respect to figure 7, the results to me, while slightly improved in the regions you mention (with respect to the R2 value, since there is no analysis of the RMSE or other magnitude error to make a comparison upon), are very worrying. Very large isoprene emitting regions in Yunnan China, Northern Thailand, Myanmar, and Eastern India. It further seems there are many areas which have a large signal in your map which are not significant sources of isoprene to start with, and this makes me wonder if there is any physical check on the mass fluxes computed? For example, the mechanisms actually leading to HCHO production via isoprene, as compared to mere correlation over a small area, which is then extrapolated in a way which is not physically consistent.

 

When talking about changes in climate, one must talk about anthropogenic induced effects. How have anthropogenic changes altered the BVOC emissions balance? Is it really so significant? How does this compare to changes in emissions of CO and HCHO, both of which are mostly anthropogenic and also impact ozone and methane. It seems like the statements in your first paragraph overstate the importance of BVOCs. Yes, this is an important topic, but not as much so as the reader is made to believe.

 

Furthermore, in the introduction, you claim that drought induced stomatal closure is related to isoprene emissions. However, I recall reading an article in science or nature 10 years ago or more, showing how ozone pollution induced as much or more stomatal closure as drought. Given that there have been significant changes in the ozone over your regions of study, please expound more on this.

 

https://doi.org/10.1029/2021EF002167

https://doi.org/10.1016/j.rse.2021.112573

Author Response

Dear Reviewer,

Thank you very much for your comments which have helped to substantially improve the revised manuscript. Please find a detailed point-by-point response to your comments in the attachment.

Regards,

Beata Opacka

Author Response File: Author Response.pdf

Reviewer 2 Report

the paper proposes an improvement on the parametrization for the isoprene emission flux in the MEGAN model in order to better capture the role of droughts by comparing field campaigns, satellite derived measurements and model retrievals; the aim is to reduce the model uncertainty on flux estimates both at local and global scale, in order to better  understand the role of  biogenic emissions for a better model interpretation of the evolution of BVOC atmospheric composition and chemistry. I have just some minor points and questions that are not clear enough and would like be clarified:

• 164,165: a table with the parameter values and ranges used in the models would hel the reading or a reference for the evaluation of the 'ypt' to support the sentence
• 187 'gamma'*sm estimates depend on parameter (alfa) derived from the same measurements data set - same site, so it's characteristic of that particular environment/emission: this could be a limitation on extending the discussion on a larger area/global coverage?
• 212,218: the choice of the (€=8.6) is based on the assumption that mild drought for 2011 has no effect on measured emissions: could this bias the results? I know that any modellistic approach need to start at some point with some approximation, but the actual measurements for 2011 should be affected by the droughts for that year.
• 300: we know Edgard db -even though the last revision - still has large uncertainty for NM-VOCs, specially for the anthropogenic sources; on the other end, the contribution of anthropogenic VOCs to HCHO is on average/at global scale negligible compared to BVOC's; moreover CH4 is not mentioned, whose contribute to HCHO is other than negligible. Have you test the results taking into account those uncertainties on the precursors?
• 333- do you think that the comparison between the Global simulation over a so long period (2006-2015) and the Regional MAGRITTE simulation that cover a shorter time period (30months) is appropriate? could be biased by the huge differences on the averaging time and space ? I can't figure out clearly the intention of this comparison
• Moreover the contribution of different sources of VOCs is strongly affected by spatial distribution of sources and emission factors could change dramatically, especially on areas strongly modified by anthropogenic activities . Is this taken into account?
•  figure 3b the gray plot is missing (or is underneath the blue one?)
• 430-434: the authors drawn conclusions apparently in contrast with the conclusions of the paper by Jiang, X.; et al 2018 -almost the same authors-: could you discuss at bit what are the differences and why come to different results?
• 496: the text is referring to "run 1 " and "run 3": it's meant for "'gamma=1' and "gammaOPT/SM'? or what else?
• 518 the discussion is centered on the relation between isoprene flux and total column HCHO: it doesn't mention the possible bias induced by the anthropogenic contribute to VOCs flux to the HCHO formation, whose emissions have a completely different spatial pattern. Could be the model improved in order to take into account also this factor? or if it's somehow included in the complex model chain, could be clarified in the text?
• 552: same as before: could be the role of non biogenic emissions of HCHO precursor the leading factor on the worsening performance of the 'gammaOPT/SM' on a global scale? i.e the derive optimized parameter can not be generalized to be used in a complete different -anthropogenic-environment?

Author Response

Dear Reviewer,

Thank you very much for your comments which have helped to substantially improve the revised manuscript. Please find a detailed point-by-point response to your comments in the attachment.

Regards,

Beata Opacka

Author Response File: Author Response.pdf