Peer review of “Vertical distribution of sources and sinks of VOCs within a boreal forest canopy”

A two-year data set, gathered from 2014 and 2016,  composed of micrometeorology and chemically reactive species measured in the Norunda station (ecosystem Boreal forest) is analyzed. The investigation focused to identify and attribute the emissions sources of Biogenic Volatile Organic Compounds (BVOC) during different seasons and their diurnal variability. The analysis and the data set are worth to be published since the study helps to advance our understanding on the characterization of these actively species in the boreal forest and for future modelling studies of the canopy-atmosphere interaction. The research presents very interesting results, but I found it a bit unbalanced towards the description and discussion of the vertical and evolution of the emission of the BVOC without connecting to the turbulent transport at the canopy-atmosphere interface.

Below my major and minor comments:

Major comments

1.- In my opinion, a fundamental part of the investigation is on how the canopy is interacting with the atmosphere (Figure 2) as well as the potential influence of non-local phenomena on the estimation of these emissions. Here my questions are:

a) What is the level of coupling between the canopy and the atmosphere? Does it depend on the diurnal boundary-layer dynamics? Is it seasonal dependent? Perhaps here they could give a characterization of the degree of coupling by including a quantification of this coupling using an index such as the decoupling factor (Goldberg et al., Annales Geophiscae 2001, 19 581-587)

b) Connected to the last remark: What is the relevance of processes of non-local phenomena like entrainment or advection on their analysis? For example, at lines 339-345 they described the diurnal variability of monoterpene concentration: Is this variability entirely determined by biophysical canopy processes or by other processes driven by the atmospheric-boundary layer dyrnamics. As described by Patton et al. (2016, Journal of the Atmospheric Sciences 73, 1621-1624) there might exert non-local processes that can an influence the mean and fluxes of atmospheric composition in and above the canopy.

c) Also connected with this, much more simple inverse models as presented here show that not only the local turbulent dispersion processes can be important in determining the inferred inversion, but entrainment or chemistry (see Vila-Guerau de Arellano et al., Atmospheric Chemistry and Physics9, 3629-3640). Do they need to take into account these processes in inferring the sources and sinks of BVOC?

d) Are the source layers (lines 205-210 or lines 357-359) influenced by the dynamics of the morning transition (see Figure 8 in Ouwersloot et al. Atmospheric Chemistry and Physics 12, 9335-9353). How much of the diurnal variability described in section 3 depends on biophysical processes and how much on the contribution of the boundary-layer dynamics?

e) In several section of the paper (see for instance Figure 11 and the discussion at line 490-500) dew is described as a main process that can influence the chemical transformation of water-soluble BVOCs in forest canopy. This is a relevant processes, but in my opinion, the characterization can be more complete. For instance, the relative humidity is measured a 36 meters which 8 meters above the canopy: Is this a dew situation or a fog situation? Are they measuring negative values of evaporation? Could the authors complete and better quantitation these relation between micrometeorology and BVOC?

2.- I found very interesting and complete the application of the Lagrangian dispersion matrix to estimate the distribution of sources and sinks. Here, I have the following questions:

a) Would it be possible to include in an appendix an evaluation of the main variables used in this Lagrangian dispersion matrix? For instance the s_w/u_* (line 211)?

b) I realize that this comment is beyond the scope of the paper, but perhaps it should be mentioned in the discussion. Equation (3) is valid for atmospheric tracers that have a time scale larger than the turbulent transport. As explained by Lamb (1973, Atmospheric Environment 7, 257-263) for chemical compounds with similar or shorter time scales, these theories might be violoted. Do Lagrangian dispersion matriz need to be adapted for compounds with similar Eulerian time scales (see Figure 6c).

Minor comments

Line 226: What sort of instability?

Line 231: What is the tension parameter?

Figure 4: Maybe it is conveninet to include zero-line to facilitate the visualization of the figure

Line 361: Acetic -> acetic

This is a very well written paper with a logical, quantitative, and consistent analytical approach to interpret the observations. The observations themselves are impressive largely because of the latest generation PTR instrument that the investigators have deployed. With the very low detection limits for select VOCs, the authors are able to quantify ppt level changes in concentration for many species. There is alot of data here and the authors do a pretty good job in highlighting some aspects of the data set, but there doesn't seem to be a unified scientific impact or conclusion that can be captured by the myriad presented analyses. This reviewer is led with the thought of, And so...what does it all mean?

Application of the met data (w) from the 6 sonic anemometers at heights 4-34m to the observed concentration profiles is an interesting way to get at emissions of the individual VOCs. I very much appreciate the correlation coefficients between CO2 EC flux measurement calculations compared to the model inversion results in Figure 3. The authors rightfully show the limitations of the inverse modeling approach. It does however also lend itself to the robustness of the vertical distribution of the emissions for various species, as shown in Figure 9 and 10. Prior to this generation PTRMS, those lines would pretty much be straight up and down. This leads to the question; what is the significance of the magnitude of the difference in flux throughout the canopy? With the exception of methanol, the other species are not so exciting, and seem to fall within the range of 0. The standard error in shaded purple in figs 9 and 10 does not take into account the uncertainty associated with the inversion model, just the error associated with observations, or cps/amu. Again, the measurements are pretty impressive. How does our understanding benefit from these very precise measurements?

One technical question; with a 3/8" OD teflon tube, that means the ID is at most 1/4", and possibly less, like 3/16"; very thin wall PFA or PTFE is fragile and easily kinked, so I am not sure what wall thickness the sample tubing is; but with a pumping speed of only 20 SLPM per line, that's an approximate residence time of 45 seconds per line. This is, as the authors note, long enough for chemical loss. Did the authors try to shorten the lines at the lower elevations to see if the responses changed? I note all sample lines were consistent in length at 45 m; so I assume also that the sample lines at the lower elevations were coiled up within the trailer/shed? Why was this presumed to be a better choice than minimizing sample line length, residence time, and pressure drop by shortening the lengths that could be shortened?

I would like to have read more about the repercussions of the methanol observations on canopy (and above) chemistry; the lifetime of methanol is long enough where it could serve as a dominant VOC player in the area.

The methodology and data set presented in this paper are very good and very sound. If the sampling site were more active, the results might be more interesting. To me the most interesting emission is methanol, but other than a description, not much thought is put in to the chemical impacts of such a flux. This reviewer is thus led to think that while robust, the paper is not super scientifically intriguing.