the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
20 Jan 2021
20 Jan 2021
Dynamics of gaseous oxidized mercury at Villum Research Station during the High Arctic summer
- Department of Environmental Science, iClimate, Arctic Research Center, Aarhus University, Frederiksborgvej 399, 4000 Roskilde, Denmark
- Department of Environmental Science, iClimate, Arctic Research Center, Aarhus University, Frederiksborgvej 399, 4000 Roskilde, Denmark
Abstract. While much research has been devoted to the subject of gaseous elemental mercury (GEM) and gaseous oxidized mercury (GOM) in the Arctic spring, during atmospheric mercury depletion events, few studies have examined the behavior of GOM in the High Arctic summer. GOM, once introduced into the ecosystem, can pose a threat to human and wildlife health, though there remain large uncertainties regarding the transformation, deposition, and assimilation of mercury into the ecosystem. Therefore, to further our understanding of the dynamics of gaseous oxidized mercury in the High Arctic during the late summer, we performed measurements of GEM and GOM along with meteorological parameters, atmospheric constituents, and air mass history during two summer campaigns in 2019 and 2020 at Villum Research Station (Villum) in Northeastern Greenland. Five events of enhanced GOM concentrations were identified and investigated in greater detail. The origin of these events was identified, through analysis of air mass back-trajectories, associated meteorological data, and other atmospheric constituents, to be the cold, dry free troposphere. These events were associated with low RH, limited precipitation, cold temperatures, and intense sunlight along the trajectory path. Events were positively correlated with ozone, aerosol particle number, and black carbon mass concentration, which were interpreted as an indication of tropospheric air masses. This work aims to provide a better understanding of the dynamics of GOM during the High Arctic summer.
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Jakob Boyd Pernov et al.
Status: final response (author comments only)
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RC1: 'Comment on acp-2020-1287', Anonymous Referee #3, 03 Feb 2021
The manuscript by Pernov et al. describes the measurement of mercury species and ancillary chemical and meteorological parameters at a site of great importance and interest in the high Arctic at 81°N in Greenland. Unlike many studies which concentrate on Spring when mercury depletion events are common, this study describes two measurement campaigns which were performed in the Summer, which is a relatively less well studied period of the year at these kinds of latitudes.
The manuscript is well written and mostly clear. There is one point however which I think could improve the clarity of the presentation and that is making it more clear when the authors are referring to the free troposphere, the planetary boundary layer or the troposphere in its entirety. As a large part of the discussion revolves around the height of origin and transport of the air masses arriving at the measurement site, it would be useful if the authors were explicit in their descriptions. For instance when they refer to the surface (see for example line 183), does this literally mean the soil or snow, or the surface layer, that is the boundary layer? Still on the same subject, it would be useful for the reader if in the Introduction, the authors could provide a brief description of the typical characteristics of the boundary layer. This would help the reader later on in the Discussion section.
I have a few more specific comments, which are listed below.
L19 does tropospheric in this sentence refer to the free troposphere?
L24 I think it should be artisanal rather than artisan and in the list of ‘natural’ emissions, many would include re-emission of legacy mercury, perhaps the authors could make this clear.
L29 Hg(P) could include elemental mercury adsorbed (strongly) to soot particles as well maybe, which could be important in some instances.
L34 references for the specific cases mentioned where rapid oxidation occurs would be better, the Angot et al. paper refers only to polar regions.
L39 my curiosity here, to which type(s) of aerosol are the authors referring?
L42-44 I was very surprised that none of the work by Dibble or Saiz-Lopez and their co-workers was included in the references here. Is there a reason for this? They would seem pertinent to me.
L50 Again, I think the references should be more inclusive here.
L53 Some recent work by Gustin and her co-workers seem to be making progress on this front, see for example, Development of an Understanding of Reactive Mercury in Ambient Air: A Review MS Gustin, SM Dunham-Cheatham, J Huang, S Lindberg, SN Lyman, Atmosphere 12 (1), 73.
L55 The sentence beginning Recently would be better at the end of the paragraph, where it is it interrupts the flow
L63 … thus posing a threat to … ?
L154 Here is a point where a little more description of local boundary layer dynamics would help the reader.
L163 to be honest I haven’t checked all the references, but Greene 2020 is definitely missing.
L168 In this section would it be possible to have a small summary table with the parameters listed simply as High or Low, when compared to the averages?
L232 The reference list is rather scarce again.
L263-4 Are there not any more recent studies which support or further clarify the results from these studies?
L284 mixed layer height which is how high exactly and how does it vary over time, see introductory remarks
L291 the characteristics of the trajectories for 2019 and 2020 seem very comparable, give or take a few hours, I would have emphasised this point, I think.
L312 Could the authors add a reference to Section 3.5 and or just include a short explanation of why fires might be important, otherwise the reader is at a bit of a loss as to why they are mentioned here.
L325 troposphere, all of it or just the free troposphere?
L330 This article might be useful in the discussion of free tropospheric Hg dynamics/reactions Weiss-Penzias, P., Amos, H. M., Selin, N. E., Gustin, M. S., Jaffe, D. A., Obrist, D., Sheu, G.-R., and Giang, A.: Use of a global model to understand speciated atmospheric mercury observations at five high-elevation sites, Atmos. Chem. Phys., 15, 1161–1173, https://doi.org/10.5194/acp-15-1161-2015, 2015.
L355 and 358 both parentheses refer to median O3 from August 2010-2018 but the numbers are different, should one be July?
L380 Good point, it is unlikely that small decreases in O3 would be noticed in the FT. But as we seem to be lacking oxidants
(Photochemistry of oxidized Hg(I) and Hg(II) species suggests missing mercury oxidation in the troposphere, Alfonso Saiz-Lopez, Oleg Travnikov, Jeroen E. Sonke, Colin P. Thackray, Daniel J. Jacob, Javier Carmona-García, Antonio Francés-Monerris, Daniel Roca-Sanjuán, A. Ulises Acuña, Juan Z. Dávalos, Carlos A. Cuevas, Martin Jiskra, Feiyue Wang, Johannes Bieser, John M. C. Plane, Joseph S. Francisco, Proceedings of the National Academy of Sciences Dec 2020, 117 (49) 30949-30956; DOI: 10.1073/pnas.1922486117)
Can we really ignore the possibility of O3/OH being an Hg oxidant, maybe through heterogeneous reactions? Just a thought.
L390 common source as in emission source? Or do you mean source region or regions?
L405 surface level, is this literally ground level or within the boundary layer?
L411 sources or source regions?
Section 3.6
In this discussion of possible halogen sources it would be useful to understand the dynamics of the mixing between the boundary layer and the free troposphere. The authors mention a number of surface sources and suggest that these are unlikely to play a role given that Hg oxidation seems to be occurring in the free troposphere L487.
However it is then postulated that biogenic halogen compound emissions and cycling on coarse mode aerosols are a potentially widespread source in the Arctic.
I would have thought that the coarse mode aerosol was less likely to reach the free troposphere than gaseous halogen containing compounds.
Some clarification of the reasoning behind the last two paragraphs of this section is required
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RC2: 'Comment on acp-2020-1287', Anonymous Referee #1, 14 Feb 2021
Review of Dynamics of gaseous oxidized mercury at Villum Research Station during the High Arctic summer by Jakob Boyd Pernow et al.
This manuscript presents original data regarding atmospheric Hg species during summertime in the high Arctic. The authors suggest that the GOM peaks (so called “ events”) that are measured are explained by the influence of free tropospheric production of GOM and transport to the sea-level site.
The scientific reasoning that is conducted here is presented in backwards order. The authors conclude on the influence of air masses from the free troposphere on GOM measurements. To my opinion, the supplementary data are not robust enough to support this very original but debatable hypothesis. Then the authors examine additional data to further explore the GOM origin including other GOM sources. From the data they show, it appears to me that the hypothesis of alternative GOM sources remain still valid awhile the authors clearly reject these sources since they do not support their initial idea. I think this is a biased way of discussing their data set, and that their initial hypothesis is not supported by clear evidence and data.
Demonstrating the direct influence of the free troposphere at an ocean-front site requires solid multiparameter measurements, on-site knowledge of the vertical structure of the atmosphere and probably vertical concentration profiles (aircraft). Although the hypothesis is attractive, there are many other possibilities to explain these peaks of GOM , which have been only partially studied in this manuscript, including local pollution sources (ships, airplanes), biomass fires, anthropogenic influence of European pollution, and transport of GOM species from the Greenland ice cap. The backtrajectory analysis is not deep enough and the statistics are not convincing.
Moreover, the introductory part contains too many approximations and requires an obvious reformulation work.
For these reasons, this work cannot be published in ACP . It could at least be requalified as a "measurement report" with however an important work on the formulation of the different hypotheses.
Details comments.
Line 9 : « GOM, once introduced into the ecosystem, »- GOM are not really introduced in ecosystems, these species are deposited. The link with « threat to human and wildlife » is exaggerated since there is no proven direct link between GOM and wildlife contamination. This need to be rephrased
Line 11 : « the ecosystem » is not appropriate.
Line 21 « an »
Line 21 : what is « relaxation time » ?
Line 24 : artisanal small scale gold mining
Line 28 : atmospheric particles or aerosol, not a combination of both
Line 31. A reference is missing for « depletion events », at least you should cite Schroeder et al 1998.
Line 31 PHg is not a fraction of total gaseous mercury.
Line 32. The link with the previous sentence is not straightforward. « in contrast » is not appropriate here.
Line 34 – reactive halogens would be better. And especially bromine radicals. There is no real evidence for other halogens reactivity. Why coastal regions? There are many coastal sites where no reactivity is observed (e.g Mace Head in Ireland).
Line 38-39 : This statement is only valid for Alert in Canada. Has it been observed elsewhere?
Line 40 : the peak of Hg in snow – This should be clarified. What kind of peak ? is it totalHg in surface snow ? « GOM is the main deposition pathway » does not mean anything.
Line 60 : Do Ariya et al really mention a ionic pulse ? there are better references for this .
Line 61. Are you sure that GEM can be directly methylated ? PHG ? Methylation does not occur at the « earth’s surface, this should be better explained.
Line 65. I do not understand why « it is pertinent to understand mercury oxidation in response to a changing climate » . There is no link with the preceding sentences.
Line 71 : GOM deposition does exist outside of AMDE since this is a major removal pathway for Hg on a global scale
Line 82-83 : I do not agree with this conclusion. Most of the studies report low GOM/PHG values.
Line 84-86 : this sentence is difficult to understand.
Line 87 – I don’t understand what « will help to infer the response of mercury in the context of a changing climate » mean
Line 88 : It does not make sense “is also important to understand the dynamics of mercury to assess the effects of abatement strategies on atmospheric concentrations in the framework of the Minamata Convention (UNEP, 2013) »
What is the link between abatement strategy and Hg dynamic in the Arctic ?
Line 125. You should be consistent with the numbers.
Line 128 : How is snow depth measured ?
Line 129 : What does « averaged to 30 - minute means » mean?
GOM data
Is the use of the GOM detection limit appropriate? Why not using the Quantification limit since we all know that these speciation instruments are quite difficult to manage? Event 2 is very closed to the detection limit and the first days of Event 1 and may be excluded.
There is no discussion on the quality of GOM data obtained with denuders while the authors may know that Tekran speciation unit underestimate GOM value as shown in recent studies (Marusczak et al 2017 – Gustin et al 2015 – Huang et al 2015, 2017)
Are the raw data available for all these events ? This is critical to make sure that all the blanks where correctly made.
Line 204 : yes but there is no evidence that there are open leads on the way ?
Line 218 : snow cover is not displayed in figure S2
By the way the color scale for the contour is quite difficult to read.
Line 230 : What is considered as high radiation and low RH ? How are those threshold defined ? Event 1 had some low radiation too (<200). Was there a snow/rain fall ? on august 21st ?
What is the dynamic of the boundary layer ? This is an important factor that can explain some variation in your concentrations.
Line 230 : your suggestion that cold temperatures are associated to mercury oxidation is not valid in volcanic plumes or in salt lake regions. To me, the temperatures are not a solid argument to reject in situ production. Halogen measurements could give a major evidence to demonstrate this -although I do not believe that this is likely to happen at this time of the year.
Line 249-253 : How are calculated those averages ? on the whole trajectory duration ?
Given the uncertainties of all these measurements and of the average, are these air masses statistically different ? Given the shown interval, I do not see any evidence of a robust difference. The Wicoxon test is used for comparing independant populations. Here you have an overlap on « event » and « non-event » trajectorie : for example the 28/08 -120h trajectories overlap and are supposed to be included with the one from the 26/08.
Where the test conducted on each separate observation? (ie RH in « event » with RH in « non event »). Btw, water mixing ratio if a function of temperature and RH ?
Line 276 : The meaning of this sentence is not clear. What does « these air masses » refer to ?
Line 280 : Figure 3d and 4d With this figure the author suggest that GOM event air masses spent more time at high altitude. The overall picture is not that clear. Event 3 and 4 are not very different from the non-event period (27/07-31/07). Regarding the strongest event in 2020 (on the 23/07) these air masses are not different from the day before and the altitude is close to what one can expect as a marine boundary layer. In summer time it can be several hundreds of meters thick, even more when passing over turbulent and convective areas.
Line 282 : for the 2019 campaign : what is the value show with the median height ? 1sigma ? min-max ? For this campaign, there are important overlap between « event » and « non event » periods.
Line 285 : how is retrieved the mixed layer height ? How robust is it in Hysplit ? Why is it no plotted on your figures ?
Overall with the presented data, I do not come to the same conclusion (line 286-289).
Line 295 : you mentioned earlier than cold temperature below -15°C are likely needed.
Looking at temperature along the BT ways, it is not the case here ?
In the free troposphere what could cause the formation of GOM is mainly the supposed abundance of Br concentrations ?
Line 298 what is the low surface resistance ?
Line 299 There are two verbs in the sentence.
Line 301 : survival is not appropriate for a chemical species
Line 31 – 5 days backtrajectories are clearly not long enough. For BC studies or aerosols 10 days are usually used (see Thomas et al 2017 in GRL). The life time of GOM is poorly known and could be of several days to weeks in dry conditions?
This approach is not relevant. CO data and BC may be a more straightforward approach to track fires. This whole paragraph does not bring any relevant information and fires may contribute to these GOM events, and/or GEM.
Line 325 : this first sentence has no meaning in atmospheric chemistry.
The Shah and Jaeglé study point sub-tropical areas and this is an important difference from mid-latitudes.
Line 340 : Why not using aerosols (check Uge et al in GRL 2017). The paragraph 3.3 is only a short review of FT measurements and is of no interest for the discussion.
Line 390 – and after. The authors make a confusion between the influence of free troposphere and a stratosphere intrusion Stratospheric intrusion would bring very dry air masses and very high ozone. It is likely that the Biomass burning may have an influence on ozone.
There is not ozone data presented in Jacob et al 2010. I don’t understand what do the authors find in Monks et al 2015 to support their statements. Monks et al suggest that European anthropogenic emissions may be important for lower tropospheric summertime ozone and that PAN reactivity may be a source of ozone.
Paragraph 435 – 444 . The correlation of GOM and BC looks very interesting in 2019 so I do not understand why the conclusion is that combustion sources has no influence – As said earlier the 5 days trajectories are too short to reach this conclusion. For year 2020, event 3 and 4 may be as well related to combustion sources (the scale is different on figure 7a and b). Event 5 could be due to production of GOM over the Greenland ice cap (as mentioned in Brooks et al 2011 – although earlier in the season), or as proposed in Angot et al 2016 10.5194/acp-16-8265-201. This hypothesis would also lead to low BC.
Then I do not agree that this airmasses comes from the upper troposphere. The GOM peak on August 1st show trajectories around 1000-2000 m ? This could only be air masses leaching the Greenland icecap before arriving to VRS.
453-454 – This is not because a high BC is observed without GOM for a single event that biomass burning cannot influence artic GOM concentration. This is too speculative.
508-511 – This is a very vague speculation.
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RC3: 'Comment on acp-2020-1287', Anonymous Referee #4, 24 Apr 2021
The authors present data from two summer measurement campaigns at a high Arctic station. The presentation and discussion of the data is focused on the origin of the gaseous oxidized mercury (GOM). They arrive at the conclusion that high GOM concentrations during all 5 events are due to the transport from the free troposphere. At a very remote site this is almost always the case and, as such, too unspecific. This is a pity because the observed events display different patterns which would enable more specific conclusions.
The data are valuable and worth of detailed analysis. Unfortunately, the manuscript is difficult to read because GEM, GOM, PHg, O3, BC, H2O, and Ncoarse are all discussed in different chapters. A change of perspective in O3 chapter from the analysis of individual events to the whole campaign analysis does not make the understanding easier. Ideally, the air mass of each event would be characterised by all of the available data, including backward trajectories (the consideration of the latter would probably result in splitting the event 1 into two events). This would be followed by detailed discussion of GOM origin in each of the characterised events separately before making final conclusions.
I recommend the publication of the manuscript after a thorough reorganisation of the text along the lines proposed above. Some of the comments below are also to be considered:
Lines 12-13: „we performed measurements of ……air mass history”?
Line 24: Biomass burning is partly natural and partly man-made.
Lines 31-33: Wording: During depletion events… GOM and PHg can constitute large fractions of… In contrast,….. GOM and PHg can constitute large fractions of. ??
Line 41: “oxidation” instead of “oxidization”
Line 51: What does it mean “liable halogen reservoir species”?
Lines 56-57: Uptake by vegetation and soil in the high Arctic? Is there enough vegetation and soil not covered with snow for that in the high Arctic?
Line 65: “important” instead of “pertinent”?
Line 80: CA stands usually for California, not Canada.
Section 2.2: Duration of GOM and PHg sampling time should be given. This is important because the usual 2h sampling at 10 L/min usually provides too small Hg amounts for analysis unbiased by the internal Tekran signal integration routine (Slemr et al., Atmos. Meas. Tech., 9, 2291-2302, 2016; Ambrose, Atmos. Meas. Tech., 10, 5063-5073, 2017). This artefact applies also for 5 min GEM sampling time which probably leads to a small underreporting of the GEM concentrations.
Line 181: RH at a given H2O content of air is inversely related to temperature and as such provides a redundant information on temperature (as can be clearly seen in Figures 1 and 2). Consequently, it is not a suitable variable for the characterisation of the air mass. H2O content of air, as shown in Figure S5 and discussed elsewhere in the manuscript, should be used mostly through the paper. The use of RH makes sense only when discussing the GOM attachment to particles.
Section 3.1: Figures S1 and S3 show that local meteorological parameters essentially do not matter. What matters are the times of the air mass exchanges characterized more clearly by their specific chemical fingerprints and the question where they come from. As already mentioned, RH should be replaced by H2O content of the air.
Figures 1 and 2: I think that these figures should include all measured parameters, i.e. additionally O3, BC and Ncoarse . Measurements of BC and Ncoarse shown in Figure 7 are especially important because these species are specific tracers for anthropogenic activities and biomass burning. GOM and PHg below detection limit are plotted as zero concentration which is misleading because “below detection limit” does not mean zero. As mentioned above, their concentrations are underreported due to the internal Tekran integration procedure. I would plot only the measured GOM and PHg concentrations above the detection limit.
Figure 3: RH in panel b provides hardly any additional information to T in panel a. Water content could be more useful because it would reveal the precipitation along the trajectory as discussed in the related text. A comparison of panel a (T) with panel d (altitude) shows an inverse relationship which is not mentioned in the text.
Figures 1, 5a and S2 show that event 1 consists essentially of two events with different trajectories which should be perhaps treated separately.
Figure 5: The addition of trajectory altitudes, as in Figure S4, could provide support for the claim of GOM arriving from the free troposphere.
Line 325: “Influence of the troposphere on mercury concentrations” sounds like “water has influence on fish”. Please reword.
Lines 328-332: Measurements of GEM by Talbot et al. (2007) are subject to two experimental artefacts: a) with their specific inlet system they measured most likely GEM + GOM, not only GEM as they claim, and b) their reported concentrations are too low because they relied on internal Tekran signal integration procedure which was demonstrated to underreport Hg concentrations leading to numerous zero concentrations in the paper which are incorrect. With these problems, Talbot et al. does not provide any usable information about GOM. A reference to Lyman and Jaffe (Nature Geosci., 5, 114-117, 2012) and Slemr et al. (Atmos. Meas. Tech., 9, 2291-2302, 2016; Atmos. Chem. Phys., 18, 12329-12343, 2018) would be more appropriate.
Line 355: Do you mean O3 median at Villum station?
Section 3.4: Elevated O3 mixing ratios could be due to a transport from free troposphere but also due to O3 formation in polluted air masses. The latter applies clearly due to anthropogenic pollution during the events 1 and 3 and to a smaller degree to event 2 as indicated by BC and Ncoarse. A discussion of the elevated GOM concentrations during these events in terms of anthropogenic pollution would be more appropriate.
Figure 6: Putting all data for 2019 and 2020 campaigns into each GEM vs O3 and GOM vs O3 diagrams is inconsistent with the discussion of individual events 1-5 in other chapters and obscures the origin of GEM instead of revealing it. What would be the GEM vs O3 and GOM vs O3 correlations for each of the individual events 1 – 5?
Section 3.5: This discussion is muddled. GOM correlates well with BC and Ncoarse during the events 1, 2, and 3 but not during the events 4 and 5. Despite the different patterns, the authors conclude that emissions from biomass burning and combustion have little to no influence on GOM levels at Villum station. That may be true for events 4 and 5 but obviously not for events 1, 2, and 3. The discussion in lines 445 – 454 may be used as an argument against biomass burning being the source of GOM in some of the events but not in all.
Section 3.6: This section is highly speculative and confusing. As in the discussion of GOM vs O3 the different pattern of each of the five events is not mentioned. Especially that of event 5 with no relation between GOM and Ncoarse and BC, whatsoever. A weak correlation with of GOM with O3 in this event could be interpreted as transport from the free troposphere. A general problem is that the authors attribute high GOM to free troposphere in all events while the halogens claimed for GEM oxidation are produced more likely in the boundary layer. I would skip this section.
Line 491: The statement about “the positive correlation between GOM and Ncoarse observed in our study (Figure 7)..” is valid only for events 1, 2, and 3, not for the events 4 and 5. The statement is thus wrong without a qualifier.
Section 4: The conclusions are too unspecificl, they do not reflect on the different patterns of the individual events.
Figure S4: I could not find a reference to it in the manuscript.
Jakob Boyd Pernov et al.
Jakob Boyd Pernov et al.
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