General comments

The authors present a study of size-segregated particle size-distribution (SDP) and flux measurements at a forest site in the Athabasca Oil Sands Region of Alberta, Canada. The measurements enabled to correlate the SDPs to different particle sources in the Alberta Oil Sands. The particle flux measurement system enabled to determine the particle deposition rates in the size range from 60 nm to 1 mm. The particle flux measurements, in particular the size-segregated measurements, always impose a challenge due to high variability of flux sources and sinks and resulting high uncertainty in fluxes. The observed size-dependence of deposition velocities was in a good correspondence with latest parameterization and therefore the manuscript is a great contribution to experimental research on particle dry deposition.

Whereas there are no major concerns, a few topics would benefit from additional clarifications and potentially improvements. First, the particle number concentrations and SDPs exhibit systematic variation with wind direction. This is attributed to the downwind sources of pollutants or background concentrations in extensive forested areas. However, within the identified sectors (i to vii) there is significant variation and the authors have not attempted to find explanation of this variation in terms of atmospheric mixing (determined by stability) conditions. Simplest would be to differentiate the measurements into day-time and night-time, or into a few stability classes and test the hypothesis that the variation within segments is related to hour of day (perhaps also the source activity is dependent on time) or atmospheric conditions. A more sophisticated tool could be the source concentration footprint modelling, but presumable the assumptions of such models would be strongly violated (such as the assumption of surface sources) and as such not worth of considering. It is possible that the authors have made such analysis and neglected from the manuscript because of not finding strong evidence of the dependence on stability or time of day. In that case it deserves short explanation in the manuscript.

The deposition velocities are analysed as aggregates over all measurements (section 3.3). There is considerable scatter (and this is natural) and probably hard to differentiate more the measurements. However, attempt to separate day-night and/or some wind directions according to sectors i-vii (grouped to few subsets) might give additional insights and separate the conditions with different deposition/emission patterns, perhaps even to reduce the scatter when differently behaving samples are separated. Did you try this? If yes and this did not produce improvements, please mention in the manuscript.

A topic of a concern is the EC system frequency performance. It was explained that the size distributions were sampled at 1 Hz frequency (L. 102) and that the attenuation of signal at frequencies >1 Hz was corrected. It is not evident how the particle EC system frequency response was determined. Sampling rate is not equivalent to the frequency response of the system. In addition, in case of EC flux measurements it is important to determine what are the frequency response characteristics of the complete system consisting of the spectrometer and the rather long (32 m) sampling line. Please provide additional explanations to this experimental detail.

The last part of the result, the particle mass flux inference from measured PM1 gradients raises the question on the applicability of the K-theory inside canopy. In general, the K-theory is poorly applicable inside the canopy and in case of more closed canopies might not be applicable at all (counter-gradient fluxes within canopy contradict the K-theory). This needs to be acknowledged in the manuscript. However, the forest at the study site was not closed and the reasons for large discrepancy are probably elsewhere. Within canopy deposition mostly occurs at the upper part of the canopy (in most canopies majority of leaf area is in the upper part of the canopy and deposition is more efficient at higher levels where more turbulence exists). Therefore, the average K evaluated for the height interval of the observations might be biased (the "resistance" equivalent to those K-parameterizations over estimated). Could this be partly responsible for discrepancy?

Detailed comments

1. Line 30 and 32, remove repetition: “is key to correctly modelling atmospheric aerosol concentrations”
2. 55, minimum located near 2 µm in diameter, presumably this was a local minimum at that large particle diameter?
3. 58, “free atmosphere”, this was meant to mean the air layers above the forest? Free atmosphere denotes in meteorology the layer above the boundary layer within the troposphere.
4. 125, “three passes removed all high-frequency data”, this is a bit bad wording, such processing had a purpose to remove unphysical spikes and not the high-frequency data, which should be retained for EC flux calculation.
5. 135 (and the concern above), how the frequency response 1 Hz was determined?
6. 155, 201 (and the main comment above), did you try to differentiate the measurements according to hour of day or stability as an explaining factor?
7. 205, 206, should there first be sets (ii, iii, iv, vii), than set (i)? not all sectors are correctly assigned here, please revise.
8. 209, “ranging from 200 to 400 nm” is confusing, not ranging but being 200 and 400 for vii and ii, respectively.
9. 236, the instrumental noise, if not correlated with wind measurements, should not appear in co-spectra. But the fact that signal to noise ratio is small affects determination of good co-spectral shapes.
10. 239, How diffusion in the sampling line would affect the flux? By affecting the frequency response of the system? What physical process is meant here, diffusion of aerosol particles to sampling line walls (this should not be significant for larger than 60 nm particles)? Or did you mean that the laminar flow (not sure what was the flow regime) caused high-frequency damping?
11. 245-248, might be matter of taste, but “strong spectra”, “strong/low flux measurements” seem loose wordings which might be better to replace.
12. 304, which stability function was used? The function applicable to the atmospheric surface layer? I doubt that it would work inside the canopy.
13. 500. Add to the caption of Fig 5 what is N (the aerosol number concentration for sizes between 60 nm and 1 μm).

Comments 0n acp-2022-656

I am a fan of the field research activities of the teams at York and Guelph Universities. Working with the Environment Canada micrometeorology group, they have provided decades of revealing results regarding air-surface exchange, primarily involving forests. The present submission continues the progress. The experiments described were based on new sensors that permit extension of particle covariances into size ranges considerably smaller than previous studies. 

Line 18.  Please explain “PM1.”  Later on, we find PM2.5 PM4, PM10. Maybe define each at the outset.

Line 28.  My understanding is that the de minimis aspect of particle health effects remains contentious. I recommend softening this statement (attributed to Kappos et al., 2004).

Line 32.  Delete sentence. It repeats what has already been said. 

Line 45.  To help clarify the presentation, the terms “Aiken” and “accumulation size” might best be introduced earlier.  The text so far has concentration on numerical sizing.  These new terms are introduced without explanation.

Line 48 et seq.  I am quite unimpressed by the Finland work and wonder whether is appropriate to think of it as providing “experimental evidence.”  It seems to me that the major contributor to their conclusions is the model they use.

Line 53.  Watch the font change.  Here, and elsewhere.

Line 54.  OK.  I cannot resist.  As far as I am concerned, forests differ considerably from other vegetated surfaces, in that the subcanopy air space of a forest serves at a constrained chemical reactor is which all sorts of particle generation and growth processes flourish. The “deposition velocity” measured above the canopy is then the net consequence of an upflux of particles of recent origin and a downflux of aerosols from somewhere upwind.  All else follows.  But I like the 70 nm minimum point.  My own data indicate about 100 nm, but I figure this depends on the site and its surroundings and so I do not look for generalities.   

Line 70.  I suggest that it would be a good idea to squeeze this description of the chemical composition of the aerosols into somewhere earlier, so that people (like me) who automatically think in terms of pinenes and the like do not head down an inappropriate path.

Line 103.  At this point, I started reading some of the basic aerosol agglomeration/growth literature (my favourite Friedlander’s “Smoke, Dust and Haze”). After recognizing that I no longer understand much of what seems relevant, it occurred that you guys must have done the relevant tests.  My main concern is that the sample size spectrum at one end of the 32 m tube will differ from that at the other, due to particle processes occurring during transit.  If there is a change, how do you account for it?

Line 130.  I always wince when low-speed observations are rejected. To my mind, these are the most variable and hence the best to focus on.  There is also a tacit assumption involved – that the transport of particles is somehow associated with the flux of momentum. This is not the right time to look at this in detail, but if you have other covariances (e.g. c’T’, c’u’) and especially the partial correlations that arise, then a little exploration could be entertaining.

Line 153.  This seems to say that “While HYSPLIT could work better, in reality it doesn’t.”  No surprise here.  No local model constructed using mesoscale outputs can improve on what local eyeballs report.

Line 236 – 251.  I think that this discussion illustrates the complexities and insecurities of extending well verified flat-earth and conventional meteorological flux experiences to issues of local (and very practical) importance.  The discussion is along the lines advocated by micrometeorological purists of the Obukhov community, but to my mind the reference to power-law slopes of -1, -7/3, -4/3, -2/3 is sufficient for me to prefer a different approach, based on the confidence with which measured particle covariances represent the statistical distributions that are expected and as measured.  To this end, I would prefer to look at the details of the ,  and  analyses, and to examine these with consideration to the relevant correlation coefficients (mainly partials) derived from similar measurements of  and . This has been very informative in the past, but flies in the face of what micrometeorological convention and its perfect-site advocates recommend.  To my mind, the essence of air-surface exchange is statistics, and examination of the statistics is the only way to address many of the issues that arise.

I do not recommend changing any of the text now presented, but I request that the authors consider my views and examine how their data archiving could provide a more statistically satisfying quantification of uncertainties.  I suspect that there is a goldmine of relevant data ready to be mined.

Section 3.3.  A couple of things concern me.  In particular, Figure 6 appears to be of averages and standard deviations computed arithmetically but plotted on a logarithmic scale.  Why?  On first principles, the individual quantifications of V_d are ratios of covariances to averages, both quantities being subject to large statistical uncertainty.  The distribution of V_d should then be log-normal (or close to it), and the plots of Figure 6 should be of the appropriately transformed data (geometric means and relevant error bounds).

Section 3.4.  This is a very welcome discussion.  It is based on familiar flat-earth time-stationary Fickian stuff, that I have never accepted as appropriate for any sub-canopy environment.  I like the results presented in Table 1 and thank the authors for going through this exercise.  My interpretation of Table 1 is that none of the gradient-interpretation analyses yields results statistically different from zero, and hence none gets close to what eddy covariance indicates. However, I am nervous about the tabulation.  I suspect that a different conclusion could be drawn if the statistics were based on log-transformed results.

Lines 353 - 358.  Careful.  Compare what is said here with the my interpretation of Table 1 above.

Lines 358 – 363.  There is something unsatisfying about using a model to determine if another model needs to be changed.  My opinion is that the analysis yielding Table 1 has already shown that the sub-canopy use of conventional diffusivity relationships is not highly profitable. I have yet to find a counter example.

Figure 7.  Of the three lines plotted, only one is detectable.