|Reviewer #2 Response:|
Response to Major concerns:
1. In response to the concern that no standard reference material is used during the
R2 – The reviewers have adequately addressed this concern
2. In response to concerns about pyrolyzer efficiency:
R2 – The authors response is inadequate in regard to the pyrolyzer. The authors attest to the pyrolyzer working at 500 C for GOM by referencing other papers, but their own data shows that there is a rather large discrepancy between the Tekran concentrations and the GOM concentration in this dataset of which the authors acknowledge. This could be (1) inefficient reduction of all GOM to GEM for subsequent Tekran analysis or (2) some other artefact in the experiments. Using the Tekran was a clever way to QA/QC check the concentrations being sorbed to the CEMs. But there was substantial discrepancies in the recoveries. To simply say “the pyrolyzer was inefficient” and then argue in response to my criticism of this by showing references stating that the pyrolyzer should work under at the tested temperatures is inadequate when clearly something was array in the experiments in terms of these recoveries. The authors could have and should have EASILY re-tested the experiments at the pyrolyzer temperatures they themselves suggest. It is my opinion that this simple, additional experimental treatment needs to be included in the study. This relates to point 5 below.
3. In response to concerns over removal of first in-series CEM filter during GEM permeations:
R2 - Here I feel the authors have adequately addressed the concern by listing both the proportion of sorbed GEM with and without inclusion of the first filter. It is still my preference that the first filters be included and as they authors state this is still a very small amount. This would also reduce the length of the manuscript and discussion on this could easily be moved to the SI without affecting anything, which would help with the suggestion I make in point 5 below.
Nonetheless, one concern that is still yet to be addressed is why is the uptake of GEM on the first filter not linear with increasing GEM concentration? It is exponential. I brought up this concern in the previous round of comments and it was ignored.
4. In response to the concern over unheated Teflon sample tubing length between Line
1 and Line 0:
R2 - Indeed another factor that may be contributing to the poor recovery results and another part of the experiments that could have easily been adjusted and retested. Possibly not a big issue as the authors suggest, but I imagine it also could have been adjusted easily.
5. “The authors agree that more experimentation is both welcome and necessary, and
indeed is now ongoing within the scope of an expanded and fully funded NSF research
project. However, our original and primary concern within the more narrow scope of this
manuscript was with GEM uptake and HgBr2 breakthrough at high loading rates.
These questions were of particular importance to a companion manuscript, also currently
submitted to AMT.”
R2 – What the authors are attempting to do here is manuscript quantity over manuscript quality. These experiments show useful data, but as I have suggested they appear rushed and too many questions and concerns have been left unanswered and unaddressed, when they could have easily been rectified by simply re-running experiments making slight adjustments to the existing conditions. This is THE STUDY addressing “GEM uptake and HgBr2 breakthrough at high loading rates” it should not need “companion” studies or “follow-up" studies to comprehensively answer the research question it set out to do. That is the role of this manuscript. It is my suggestion that this study be combined with this “companion study” to make a more complete paper. There is a lot of over-elaboration in the discussion and many points could easily be moved to an SI without loss of information to combine this study with complimentary work. This study definitely has merit, but it needs to be more polished.
6. In response to concerns about high CEM filter blanks:
R2 – This concern was brought up here because it has been inadequately addressed in previous studies. Take the Huang et al (2017) study for example:
“The bi-weekly MDLs (336 h) for active systems with cation-exchange and nylon membranes were 2–68 pg m−3 (mean: 24 pg m−3) and 0.01–14.6 pg m−3 (mean: 2.1 pg m−3), respectively. Biweekly MDL was calculated from 3 times the standard deviation of bi-weekly blanks. The MDL was calculated for each period of sampling, due to the fact this can vary based on treatment of the membranes, the time samples are prepared for deployment, deployment at the field site, and handling once returned to the laboratory. The membranes may also vary by material lot. All samples were corrected by subtracting the blank for the corresponding 2-week period.”
(a) A 2 week mean detection limit concentration of 24 pg m-3 is at or below typical GOM concentration even in industrial city sites (examples: Lyman and Gustin 2009; Huang et al. 2012; Choi et al. 2013).
(b) These are DETECTION limits. Not QUANTIFICATION limits. Attempting to provide high certainty, quantifiable results at concentrations at or below detection limits is simply erroneous.
(c) The purpose of averaging method detection and/or quantification limits is to prevent exactly what the authors are discussing here by smoothing out inconsistency in variable handling of materials, residual Hg, etc. By subtracting “the blank” (a single blank for a single sampling period; n=1) is again incorrect and based.
(d) This completely contradicts a statement the authors of the current manuscript have introduced in this round of reviews in terms of their attempting to caution the use of the term RM:
“a broad term that favors basic accuracy of measurement over determination of specific compounds”
How can this favour “accuracy of measurement” if attempts at field measurements at typical concentrations encountered in the environment are at or below detection (not quantification) limits. There is no confidence in such results.
As such these concerns do still need to be addressed for this sampling method.
R2 Other comments of this latest version:
Lines 39-40: This “cautionary” description of RM that was suggested by me previously is inadequate as decribed above. This research group attempts to use this same sorbent material to determine specific compounds of GOM in previous work (Huang et al. 2017). Thus, by making this statement here they are saying the results from this previous work are not accurate measurements.
Line 95: Once again here the authors should include a reference to the Marusczak et al. 2017 that describes how adding the zero flushes from GOM analysis to the actual GOM concentrations increases the derived concentrations to agree more closely with alternative measurement techniques and some modelled values. This was paper was specifically mentioned in the previous round of comments to be added to the literature review to balance impartiality but this comment was ignored.
Lines 128-131: Can the authors please reference where exactly in the Gustin et al. 2015 paper is the mention of PTFE/PFA producing zero sorption of GEM. Personally, I could not find this specific point within the reference.
Lines 220-222: Yes, the uptake was linear if the first filter was not included. But when the first filter is included it is exponential. Why? As yet this has not been addressed by the authors anywhere.
Line 232: Approximate not approximately.
Lines 236-237: “but it should be noted that the performance of the CEM filters at low concentrations could be slightly different"
This should be changed to:
“but it should be noted that these concentrations are 50-1000x above typical background concentrations and the performance of the CEM filters at low concentrations could be slightly different”
As was previously suggested.
Lines 263-266: Caution needed here. You would never use such a system that has been used in contaminated environments for background work. Even a small memory of the Hg would overwhelm the background signal. Lines would need to be discarded or thoroughly acid cleaned for background work. Please make a cautionary note on this here. A comment was made about this in the previous revisions, but ignored.
Lines 284-285: Oagain I ask is "photochemistry driven by room fluorescent
285 lighting." a process reported in the literature? If so please reference, if not this is just pure speculation.
Lines 340-343: Again, why speculate when this could have easily been determined by repeating the experiments at higher pyrolyzer temperatures?
Choi, H. D., Huang, J., Mondal, S., & Holsen, T. M. (2013). Variation in concentrations of three mercury (Hg) forms at a rural and a suburban site in New York State. Science of the Total Environment, 448, 96-106.
Huang, J., Miller, M. B., Edgerton, E., & Sexauer Gustin, M. (2017). Deciphering potential chemical compounds of gaseous oxidized mercury in Florida, USA. Atmospheric Chemistry and Physics, 17(3), 1689-1698.
Huang, J., Liu, C. K., Huang, C. S., & Fang, G. C. (2012). Atmospheric mercury pollution at an urban site in central Taiwan: Mercury emission sources at ground level. Chemosphere, 87(5), 579-585.
Lyman, S. N., & Gustin, M. S. (2009). Determinants of atmospheric mercury concentrations in Reno, Nevada, USA. Science of the total environment, 408(2), 431-438.
Marusczak, N., Sonke, J. E., Fu, X. and Jiskra, M. (2017). Tropospheric GOM at the Pic du Midi Observatory—Correcting Bias in Denuder Based Observations. Environmental Science & Technology 51 (2), 863-869