The separation of the paper into a paper mainly reporting the measurements and a paper on modelling of the exchange has made this paper more accessible. However, the revised paper now covers much of the same ground in the discussion as the paper by Zoll et al. (2019). I found it rather disingenuous that the paper does not point out right at the beginning that it presents a continuation of the time-series of Zoll et al. (2019), taken at the same site, which is not spelt out until line 651. There is little point in re-iterating the findings of Zoll et al. to the extent done here and much of the Discussions section is rather speculative. I suggest that the analysis and discussion gets more focussed on the presentation of the annual budgets, cutting the paper by about 1/3. This is particularly the case as I do not believe that either the present paper nor the analysis by Zoll et al. provides insights into the mechanistic controls. Whilst the neutral network analysis (and the correlation analysis of the present papers) can identify associations, they cannot identify causality.
1. At several places (starting with the opening two sentences and final sentence of the abstract) the paper overstates the utility of the Nr measurements for the development of model improvements / parameterisations. Because it is unknown which Nr compounds dominate the flux during any particular 30-minute flux period, any parameterisation of the net exchange is not transferable to other situations subject to another compound mix. I am not saying the analysis of the Vd and Rc of the net exchange is not worth doing but the paper should point out more clearly (e.g. lines 60-66) that the main utility of the TRANC is to quantify net dry deposition inputs of Nr with a single instrument (rather than a suite of instruments for each compound individually) and that the analysis of the net exchange parameter is a by-product.
2. As mentioned above, the paper does not sufficiently clearly distinguish between associations and correlations on the one hand and causes / drivers on the other. Radiation, turbulence and temperature (and sensible heat flux) are highly correlated with each other (Figure S7) and it is impossible to decide which is the mechanistic driver and I am not convinced that vd is controlled by the plant activity rather than u* (Line 435-436) and other drivers that correlate with Rg. From what we know of the exchange of the individual Nr compounds, stomatal exchange will be important for NO2 and its importance is highly variable for NH3 as pointed out in the paper. However, it is not so important for HNO3 and NH4+/NO3-. However, Rg will change Nr composition over the day with HNO3, a particularly fast depositing compound, typically peaking at midday (again related to Rg, this time via photochemical production), and it will produce a diurnal pattern on the effect of NH4NO3 volatilisation, which deposits fast only during daytime when temperature gradients are large. I therefore can’t see that the measurements prove that stomatal conductance is the main controller of the Nr flux (Section 4.2.1). Stating that u* does not affect the flux would be saying that Ra and Rb do not exist. If this analysis were done on Rc or 1/Rc at least the influence of turbulence would have been removed.
3. In this context I do not find the analysis of the controlling factors for the flux very helpful. The flux would be expected to be affected by u* (Fig. 7, Table 1 and associated text) as it still contains the control via Ra and Rb. Also, the authors seem to try to convey that the slope changes with u*. Except for the possibility of a non-zero intercept, the slope is actually vd. Thus, the authors should either plot vd vs Nr concentration or the ratio Vd/u* against Nr concentration. They might also want to consider binning data according to y-values rather than showing raw data to convey a clearer message. This has implications for the discussion in Section 4.2.1. I fail to see why the lack of correlation between flux and concentration within a u* class suggests that u* is not a driver (line 645ff). Surely, it would suggest that the concentration is not the driver.
4. Although it theoretically provides more insights, the Rc analysis is quite uncertain due to the calculation of Rb. On the one hand the authors attempt to calculate an Rb that is weighted by the different compounds, on the other hand they set Rb for particles to 0 so that their full interaction with the canopy enters Rc. This is a crude approximation because the authors only have long-term information on composition (rather than half-hourly) and, numerically, the weighting should be done according to the compound contribution to the flux rather than the concentration. Moreover, the statement that particles are not subject to an Rb term (line 285) is incorrect. Rb describes the resistance posed by the laminar sublayer resistance and this is in fact larger for particles than it is for gases. However, the concept behind the terminology of Rb is that of Brownian diffusion, whilst particles have other mechanisms (interception, impaction, gravitation settling) to overcome this boundary layer in addition to diffusion (which is very ineffective for all but the smallest particles). Thus, for particles, the concept of Rb is usually replaced with that of Vds = Vd(z0) = 1/(1/Vd-Ra). The current approach followed in the paper therefore derives an Rc that is a combination of different elements that mean different things for different compounds. This highlights again the limitations of the total Nr flux for mechanistic analysis (point 1 above).
5. It is similarly incorrect that the flux pattern of “nitrogen aerosols … is driven by Ra” (line 317). In fact vd for particles tends to be more reduced compared with 1/Ra than that the vd of gases.
Other scientific comments
6. Throughout the manuscript it is not clear to me which results / figures are based on u* filtered data and which not. Please clarify throughout. For deposition u* filtering introduces a bias to the remaining data, removing preferentially small fluxes.
7. I cannot fully follow the alternative implementation of the MDV in which you consider temperature, humidity and precipitation (lines 485ff). The introduction of the approach is not very clear and should probably be moved the methods section anyway. Could you please go through the English. “Dry deposition without restriction” (line 485) is not very meaningful. You probably mean “agreed within +/- 3C” rather than “varied by”. It would probably make the section more readable if you gave this implementation a name. What about “stratified MDV” or “conditional MDV”. Overall, I wonder whether it would make more sense to apply the MDV gap filling to vd rather than fluxes as it is the exchange mechanism that is impacted by the meteorology rather than the concentration. Clearly, this would only work for periods for which you have concentration data.
8. Line 17ff and line 826. Ra and Rb do not make a contribution to vd, but to Rt=1/vd. Alternative reword to say that Ra and Rb make a negligible contribution to limiting vd.
9. It is well established that closed path sensors lead to a dampening of the fluctuations and thus the fluctuations induce the artificial flux due to quantum mechanical quenching are reduced compared with the true latent heat flux and as a result Eq. (1) will overestimate the correction by analogy to the impact on the density correction (e.g. Ibrom et al., 2007). Because the relative correction is small this is not a major issue, but the authors should acknowledge the uncertainty and clarify that the correction is an upper estimate.
10. The paper incorrectly states that the aerosol detected by the TRANC is NH4NO3 (line 46; line 144). In fact it detects the sum of NH4+ and NO3-, with the former also representing ammonium sulfates and the latter also sodium and calcium nitrate. Figure 4 very clearly demonstrates the presence of excess NH4+ over NO3- at this site.
11. The review of previous studies (lines 45 to 91) is incomplete and inconsistent. Firstly, it is worth mentioning that other micrometeorological methods do exist, beyond EC. In fact the references in line 69 refer partly to flux gradient measurements although the paragraph starts with “Prior EC studies of …”. Secondly, there are not as few flux studies of Nr compounds to remote sites as stated. I could probably easily list 30, but many only cover short campaign periods. I therefore suggest starting the sentence in Line 67 with “Only a few long-term studies have been conducted to derive annual inputs at remote locations.” and then focus on listing the long-term studies which can be done more exhaustively. This is also consistent with the true benefit of the TRANC system and this dataset as outlined above.
12. Section 2.2. Please add horizontal and vertical displacement between TRANC inlet and anemometer, as well as the pressure downstream of the critical orifice and the turbulent Reynolds number in this low-pressure region.
13. Some more information on how the DELTA denuders were operated would be helpful without having to look up the quoted references. What filters were used and which coating for the denuders? The use of paper filters has been found to result in an aerosol underestimation of about 30%, which is not an issue for PTFE filters. K2CO3 coating results in a positive artefact on HNO3 from other NOy compounds, while NaCl coating is more selective. It is only in Section 4.1 that the paper seems to imply that K2CO3 coating was used. It is also worth stating that the cut-off of the DELTA denuder is approximately PM4.5 (see Tang et al., 2015; https://uk-air.defra.gov.uk/library/reports?report_id=861 ). The implications should be discussed also when comparing the TRANC and the sum of the Nr compounds (line 353). Mention also that the APNA-360 NO2 measurement was (presumably) made with a thermal converter and is therefore cross-sensitive to other oxidised nitrogen compounds.
14. Lines 189-192. I suggest you state already in this context that you were not able to calculate NH3 fluxes.
15. Please add some details or reference with respect to the wet/bulk deposition measurements. Was a biocide used to avoid denitrification?
16. Line 305ff. Strictly speaking a “compensation point” is defined at the concentration at which (biological) consumption equals production. Thus, when talking about compensation points in a context other than “stomatal compensation point” it may be better to use the term “emission potential” or “equilibrium concentration”, depending on context.
17. Line 315. It is worth noting that the evaporation of NH4NO3 during the deposition process also implies that some of the NH4 and NO3 measured as aerosol does not reach the surface as aerosol but as NH3 and HNO3 and can therefore deposition faster than particles.
18. Section 3.1. Figure 3 actually conveys the relative contribution of NH3 and NOx to total Nr more clearly than Figure 2. Maybe refer forward to Figure 3 when you discuss Fig. 2. In my mind Figure 3 does two things: (a) it shows the best estimate of the relative breakdown of Nr into the different species and (b) it acts as a quality control of the total Nr measurement. However, to interpret the figure in terms of (b), the reader would need to know which stacked bars are fully based on real data and which rely on gap-filling and also the % coverage of the Nr measurement for each data period. Could both pieces of information be added to the figure? With this additional information February 2018 could then be re-added to the figure: it reflects real data, but the gap filling does not work well on this data point. It would also indicate the years to which the sampling periods refer.
19. Line 335. No systematic difference in NH3 between 20 and 30 m would indicate that NH3 showed no flux. Or is the uncertainty just too large to resolve gradients?
20. I have some comments regarding the assessment of the limit of detection and positive and negative fluxes (lines 371 to 390). The Finkelstein and Sims (2001) algorithm returns a different random error (and hence detection limit) for each 30-minute flux value. It is fine to state the average / median of this detection limit, but does it not make more sense to evaluate the fraction of data points for which the LOD is exceeded against individual LODs rather than the average LOD. For a near-zero flux below the LOD one would expect about half of the flux values to be positive and half to be negative, but this does not really carry much information on the actual contribution of emission events as many of the positive fluxes would not be significantly different from zero. It would therefore be useful to add what fraction of the flux values above the LOD shows emission and deposition. The LOD is a function of instrument signal-to-noise, but also of turbulence and would be expected to be larger over forest. This needs to be taken into account when comparing LODs between studies (lines 538ff). As with other parts of the manuscript it is not very clear whether the median deposition figures (lines 381ff) refer to the filtered or the gap-filled data.
21. Figure 9: Fluxes scale with gc = 1/Rc rather than with Rc and thus mean values of Rc should be calculated by averaging 1/Rc values and then turning back into Rc (or presenting as gc). The resulting pattern can look quite different. Was a filter applied for maximum that was allowed for Ra+Rb? At large values of Ra+Rb, Rc potentially becomes a small difference of two large numbers and thus quite uncertain.
22. It would be worth discussing the annual N input (line 507) in relation to the Critical Loads for woodland.
23. Line 549. Did February 2018 stand out in any other way? Was the wind direction unusual? Do the reports of the federal and state measurement networks report anything unusual?
24. Lines 562-565. I am not convinced there is a threshold NH3 concentration for ammonium sulfate formation. I thought any free NH3 would be pulled into the aerosol phase by the presence of sulphuric acid or bisulfate. Also, I am not sure this analysis works well with monthly data. The high concentrations could have been due to a short event during which no NH3 was present.
25. Lines 566 to 598. It is fine to point out the difference in flux during the winter periods 2016 and 2017, and their relationship to snow cover. However, it would be prudent to show in Fig. 12a the fluxes during periods with snowfall as dotted lines as they are highly uncertain (it could be argued they should be removed completely) and I find the section overly lengthy and speculative. I am highly sceptical that NH3 would be able to diffuse through a 60 cm snow layer without being re-captured. Is there literature evidence that this might be possible? Also, please select colours to be readable by people with red/green blindness (Figure 12).
26. Line 604f. I don’t understand this sentence. Are you trying to say that the DELTA measurements suggested that gaseous compounds made a significant contribution to the Nr concentration?
27. Line 605. Which slight increase in HNO3 and decrease in NH4+?
28. Line 610ff. The NOx analyser was likely a thermal analyser and cross-sensitive to other NOy compounds? Worth mentioning here also the likely difference in cut-off diameters between DELTA and TRUNC for aerosol.
29. Line 614f. What is your evidence that the DELTA suffered break-through at high concentration peaks? Or are you just speculating that this might be a possibility. Maybe the use of the word “could” is not quite right? Also, a key uncertainty originates from the TRUNC measurement likely not covering 100% of the DELTA sampling time. See comment 18 above.
30. Lines 617-624. Deposition velocities of NH3 are highly variable and would be expected to decrease for semi-natural forests that are subject to high Nr input (because the stomatal compensation points would go up; see Massad et al., 2010) and with decreasing ambient concentration (away from sources). The importance of the NH4NO3 evaporation effect that likely affected the summer measurements of Wolff et al. (2010) would likely be much smaller during cooler periods resulting in smaller deposition rates at other times of the year. So I am not sure the conclusions hold.
31. Line 639. A stomatal compensation point has only been shown to exist for NH3 and has in some studies been indicated for NO2. There is no such thing as a stomatal compensation point for total Nr. And there is also no canopy compensation point for Nr (Line 685). The concept of a canopy compensation point has not been introduced in the paper anyway.
32. Line 645. HNO3 is formed by reaction of NOx with OH not O3.
33. Lines 664 to 669. This paragraph seems to mix up the effects of concentration on the flux and vd. Clearly, for a depositing compound, the flux increases with concentration. For vd this may or may not be the case.
34. Lines 729 to 738. I am not sure the water holding capacity of leaves at intermediate relative humidity is governed only by NO3-/NH4- in air. Any hygropscopic aerosol from dry, wet and fog deposition could contribute to this. As the authors show their measurement site is by no means pristine. See also Sutton et al. (1998) and Flechard et al. (1999).
35. Line 801. What do you mean by ‘canopy outflow’? Do you mean “catchment outflow” or “throughfall”? How can those measurements distinguish between dry and wet deposition?
36. Line 803. Which two sampler types? Positive artefacts on bulk deposition gauges (if this is what you are referring to here) can also originate from dry deposition of gas phase NH3 and HNO3.
37. Line 834. I can see that inferential modelling would extrapolate fluxes mechanistically to low turbulence conditions, however I fail to see how this is possible with neutral flux networks if they are trained with u* filtered data.
The papers uses different units in different places. When discussing the Nr components these are in µg-N m-3, which is logical, but when referring to previous measurements (e.g. line 121, 512, 521, …) they change to ppb. I suggest adding values in µg-N m-3 in brackets here so the reader can compare more easily.
Line 10. “was observed for the contribution of NH3 …”
Line 15. “changes in composition of Nr and radiation”
Line 23. “During these periods, cuticular or soil …”
Line 38. Correct subscript on PM2.5
Line 45. The community tends to use “nitric oxide” over “nitrogen monoxide” for NO.
Line 74. “… radiation as the primary driver for …”
Line 76. “… as a secondary driver …”
Line 134. “the dominating Norway spruce is recovering”
Line 149. The sentence starting “The mass flow rate …” seems redundant.
Line 208. The sentence “Figures with the notation …” seems over the top. I suggest you just write “(see Fig. S1 of the Supplementary Material)”
Line 266. Missing parenthesis “2010)).”
Figure 2. I think the figures would be more readable if they all used the same y-scale, possibly capped at 15 ug N m-3.
Figures 2 and 5. The whiskers do not look like they scale with the IQR. Please state sampling intervals for both figures as the statistics depend on it.
Line 329. “reached values of up to”
Figure 5. Rather than the last sentence in the caption, the authors could use arrows with values to indicate the magnitude of the three points that fall outside the y-range.
Line 405. “shows the median vd for the corresponding fluxes.”
Line 416. Should this more accurately read “the deposition of total Nr.”?
Figures 8 and 9. I would find these easier to grasp if the plots of the first row were labelled (a), (b), (c) etc.
Line 443. “dry conditions (no precipitation) are associated with enhanced deposition”
Line 507. “In total, we derived a total”
Line 521. The word “who” cannot refer to authors in brackets.
Line 524. Change “expectable” to “to be expected” – it is highly unusual and not in all dictionaries.
Line 535. Change “phase” to “period”.
Line 542. “that the flux magnitude”
Line 559. Correct “SO42-“
Line 560. “is the dominant aerosol form.”
Line 599. “that NOx made the largest contribution”
Line 603. “NH3 had a strong presence”
Line 653. “may also be related”
Line 657. “as a primary controlling”
Line 705. “During periods of”
Line 723. “When the canopy gets drier”
Line 726. “than stomatal deposition”
Line 788. This acronyms were introduced in line 95 and not used since! Probably worth spelling out in full here.
Line 834. “to the use of friction”
Andreas Ibrom, Ebba Dellwik, Søren Ejling Larsen & Kim Pilegaard (2007) On the use of the Webb–Pearman–Leuning theory for closed-path eddy correlation measurements, Tellus B: Chemical and Physical Meteorology, 59:5, 937-946, DOI: 10.1111/j.1600-0889.2007.00311.x