Marine submicron aerosol gradients, sources and sinks

Ceburnis, Darius; Rinaldi, Matteo; Ovadnevaite, Jurgita; Martucci, Giovanni; Giulianelli, Lara; O'Dowd, Colin D.

doi:https://doi.org/10.5194/acp-16-12425-2016

Articles | Volume 16, issue 19

https://doi.org/10.5194/acp-16-12425-2016

© Author(s) 2016. This work is distributed under
the Creative Commons Attribution 3.0 License.

Special issue:

BACCHUS – Impact of Biogenic versus Anthropogenic emissions...

https://doi.org/10.5194/acp-16-12425-2016

© Author(s) 2016. This work is distributed under
the Creative Commons Attribution 3.0 License.

Articles | Volume 16, issue 19

Research article

|

04 Oct 2016

Research article |

| 04 Oct 2016

Marine submicron aerosol gradients, sources and sinks

Darius Ceburnis, Matteo Rinaldi, Jurgita Ovadnevaite, Giovanni Martucci, Lara Giulianelli, and Colin D. O'Dowd

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Final revised paper (published on 04 Oct 2016)
Supplement to the final revised paper
Preprint (discussion started on 16 Sep 2014)

Interactive discussion

Status: closed

AC: Author comment | RC: Referee comment | SC: Short comment | EC: Editor comment

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- Supplement

SC C7181: 'Diurnal Analysis', Michael Long, 17 Sep 2014
- AC C12987: 'Reply to short comment', Darius Ceburnis, 10 Apr 2015
RC C11616: 'Review', Anonymous Referee #3, 27 Jan 2015
- AC C12988: 'Reply to reviewer 3', Darius Ceburnis, 10 Apr 2015
RC C11942: 'Review', Anonymous Referee #4, 06 Feb 2015
- AC C12989: 'Reply to reviewer 4', Darius Ceburnis, 10 Apr 2015

Peer-review completion

AR: Author's response | RR: Referee report | ED: Editor decision

AR by Darius Ceburnis on behalf of the Authors (10 Apr 2015) Author's response Manuscript

ED: Referee Nomination & Report Request started (29 Apr 2015) by Tuukka Petäjä

RR by Anonymous Referee #4 (15 May 2015)

Suggestions for revision or reasons for rejection

I cannot support publication of this manuscript in ACP in its current form. There are many issues raised in the first round of comments that have not been addressed. I still have major questions about the uncertainties of the measurements (concentrations, gradients, K and fluxes), the data analytical approaches employed (particularly those concerning WIOM), and consequently, the strength of the papers conclusions. I have tried to restrict these further comments to the authors responses to my first set of comments and the additional material that has been added to the revised manuscript (e.g. abstract and section 3.5). However, now that I've looked at the Stull (1988) reference, which was missing from the ACPD paper, there are also some questions about the gradient transport theory underlying this work that I believe should also be addressed.

Gradient transport theory:
- In the chosen parameterisation for K, please clarify in the text what value was used for the timescale, t.
- The turbulent transport coefficient, K, is different for different variables. E.g. K for heat and moisture transport is a factor of 1.35 times greater than the K for momentum transport under neutral conditions (Stull, 1988). Please clarify which K is considered to apply here.
- A number of other paramerisations exist for calculating K. With the sonic anemometer data it should be possible to use some of these other parameterisations. This is another source of uncertainty that may need to be represented in the uncertainty of the reported fluxes. To know this, please indicate how sensitive the calculated fluxes are to the chosen parameterisation of K. This is important because the true fluxes of any of the chemical species are not available to validate these measurements (the sea salt fluxes compared against in Fig. 8 and discussed in section 3.3 each have their own set of problems). Nor were they available in the 2 earlier studies of Ceburnis et al., (2008) and Valiulis et al., (2002), which relied on the same theory and parameterisation of K. I.e. this approach for calculating fluxes has not been rigorously validated yet.

Responses to the authors responses:
- Line 288: If this interpretation is based not on the actual range of values for the height of the internal boundary layer reported by Norton et al., (2006) but only on their statement that the effect is smaller at higher levels, then clarify this here.
- Section 2.5. The equations for calculating propagated errors are much clearer now, but the concentration uncertainty values are still not reported. What are the uncertainties for the normalised concentrations presented in Fig. 3? How do these compare to the variances? I disagree with the authors response. There is a decision to be made about whether the error bars in Fig. 3 represent the accuracy (uncertainty) or precision (variance) of the measurements. The error bars should reflect as best as possible the confidence one can place in these measurements. If the uncertainty is large this needs to be represented by the error bars in the Figure (especially considering that large uncertainty is the authors stated reason for the mixed nss-SO4 profile). Although the sea salt profile seems clear, given the questionable assumption of stationarity over the many hours required for sampling I am still far from convinced about the accuracy of the NH4, nss-SO4, WSON, MSA, WSOM and WIOM gradients.
- Line 380: How exactly were the nitrate and oxalate profiles 'distorted'. And 'systematically'. Need to be more specific.
- Line 396-419: This discussion still fails to mention wind speed, a factor which is later shown to explain as much variance in WIOM fractions as Chl a concentrations. Therefore, this discussion is not only speculative but also inconsistent with results presented later in the paper. It needs to be modified or removed.
- Line 434: The ambiguity supposedly responsible for the unexpected nss-SO4 profile is not reflected in the error bars in Fig. 3. As things stands the main text says don't trust the nss-SO4 profile, but the small error bars in Fig. 3 invite the opposite interpretation. This is one reason I suspect the error bars in Fig. 3 should represent the measurement uncertainties and not variances, to give a better sense of exactly how much confidence we can place in these measurements.
- Line 444: The definition of the calculated ammonium displayed in Fig. 4 is still not specific enough in the main text. Does 'full neutralisation' mean all the sulfate and nitrate was neutralised?
- Line 501: The SSS-oxalate relationship is not similar to the SSS-nitrate relationship in Fig. 5 so this discussion needs modifying or removing. In general, it is not ok to simply select a subset of points that would follow a positive linear relationship and conclude that all of the data does. If certain points are excluded from the analysis, sounds reasons need to be presented for doing so. The SSS-oxalate relationship looks far more similar to the SSS-MSA relationship.
- Line 550 (also applies to lines 314- 317): This is still not clear. Please indicate the actual values that were used for the relative uncertainties in G and K in the error propogation calculations. I am troubled by the authors response and the statement added to line 316 that deltaK will be small because it is an average of hundreds of values. To give an accurate sense of the uncertainties in the calculated fluxes, deltaK should reflect the large variance in K over the long sampling times (which can be seen for example in Fig. 1). K and therefore the calculated fluxes are likely to display substantial diurnal variation. Uncertainty in K and therefore flux will also arise due to the choice of parameterisation used to calculate K (as mentioned above). Since each F is an average over a number of days and nights the calculated delta F needs to reflect the variance and uncertainty in K. I suspect the true uncertainties in F are much greater than currently reported.
- Line 589: My original comment hasn't been addressed. Since the relationship is only fitted to the positive flux points the wind speed range the fitted relationship is valid over needs to be reported (this should also be done for the other fitted relationships in the paper). The negative flux points are still not included in Fig. 7. The discussion here is qualitative and vague and does not provide a strong enough basis for suggesting that the relationship between WIOM flux and wind speed would be linear and not some other function (e.g. power law). The phrase "..best fitted to the line" needs to be made more precise.
- Line 609: I agree with the authors decision to remove the physically-unsupported WSOM-wind speed parameterisation from Fig. 7. The problem is, the parameterisation is still discussed in the text and included in Table 3. If no confidence can be placed in the parameterisation than it should be removed from the paper entirely. A side point, the argument that the opposing signs of the WIOM and WSOM flux dependencies on wind speed suggests that a 'significant' fraction of WSOM is processed WIOM is not clear. It should be further expanded on or removed.
- Line 708: If the authors contend "...that a fraction of measured WSOM was associated with sea spray" then it is a simple exercise to check whether the OMss relationships with wind speed and Chl a concentrations would hold if it is assumed that, say, 25% or 50% of measured WSOM contributes to OMss.
- Lines 710 - 721: The fact that there is correlation between Chl a concentrations and wind speed (coincidental or not) is precisely the reason why a multivariate analysis is required to answer the questions asked here. I do not accept the authors response that "...multivariate analysis won't solve the condudrum which can only be elucidated." As it stands, the conclusion that the OMss dependence on wind speed is significant but weaker than the OMss-chlorophyll relationship is completely unjustified. No evidence is presented to conclude one factor is more important than the other. This conclusion should be removed or supported by further analysis.

New additions to the manuscript:
- Abstract lines 16-21: Sentence needs updating. Only chemical gradients, and not fluxes, are presented for the secondary components.
- Abstract line 27: What is the meaning of the sentence the "...observed seasonal pattern of sea salt production was mainly driven by wind action with the tentative effect of marine OM"? Sea salt fluxes are only examined as a function of wind speed in the main text. What is the 'effect of marine OM'?
- Table 1: Include headings for the columns
- Line 742: Please support this statement by providing, for example, the average sea salt concentrations in summer and winter.
- Line 749-758: I have tried hard but simply cannot follow this sea salt replacement argument. I suspect there is confusion between the terms 'sea salt' and 'sea spray'. Please confirm if some uses of the term 'sea salt' are actually referring to 'sea spray'. In any case, the argument is vague and needs to be outlined more precisely. What do 'somewhat diminished' and 'stronger sea salt and wind speed power law relationship compared to pure sea salt relationship' mean exactly? And how does this provide evidence of a sea salt replacement effect? I doubt these flux results are accurate enough to be able to detect such an effect.
- Line 762: Please support this statement by providing, for example, the average WIOM concentrations in summer and winter.
- Line 764-768: How is this possible? The fluxes are directly proportional to the chemical gradients (Eq. 1). Shouldn't both quantities display similar seasonal variations?
- Line 782: Why can the Yoon et al., (2007) study, which is based on satellite Chl a concentrations, be used to investigate the link between the sign of the WIOM gradient (production or removal) and coastal Chl a concentrations, but the same thing can't be done directly with this dataset because satellite Chl a concentrations aren't accurate enough?
- Line 784 (and Lines 145-152): Please state explicitly the 'open ocean' region that Chl a concentrations used in this paper were calculated over? What percentage of this region did the flux footprint region take up?
- Line 787: Where is it shown that "...WIOM fluxes were dependant on biological activity in the flux footprint area (0.2-10 km)"?
- Line 790: How is this conclusion arrived at? Specifically, how does it follow from the results presented and discussed here that the sea spray source function presented by Ovadnevaite et al., (2013) can be justifiably combined with the primary OM parameterisation of Rinaldi et al., (2013)? This conclusion should be further supported or removed.

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ED: Reconsider after major revisions (29 May 2015) by Tuukka Petäjä

AR by Darius Ceburnis on behalf of the Authors (19 Oct 2015) Author's response Manuscript

ED: Referee Nomination & Report Request started (06 Nov 2015) by Tuukka Petäjä

RR by Anonymous Referee #5 (19 Nov 2015)

ED: Reconsider after major revisions (23 Nov 2015) by Tuukka Petäjä

AR by Darius Ceburnis on behalf of the Authors (12 Jul 2016) Author's response Manuscript

ED: Referee Nomination & Report Request started (29 Jul 2016) by Tuukka Petäjä

RR by Anonymous Referee #6 (02 Aug 2016)

Suggestions for revision or reasons for rejection

This paper has gone through substantial revisions and, based on apparently very critical earlier-round referee comments, the EC part of the analysis has been taken out of the paper. The current version of the paper is in a relatively good shape. I have a few, mostly minor, comments that should be considered before accepting this paper for publication.

Scientific comments

One thing that the authors did not consider when discussion the result was the potential influence of the coarse/submicron partitioning of a compound. This definitely affects the relations between two compounds (Figure 3) and might also affect concentration gradients. This could, for example, be one explanation for the odd relation between MSA and SS in Fig. 3. MSA is rather non-volatile, so the great majority of it is expected to be in the aerosol-phase in the marine boundary layer. When there is lot of sea-salt, a bigger fraction of MSA is expected be in coarse particles, lowering its lifetime and thereby its concentration. This might explain the relatively low MSA concentrations at high SS levels. Likewise, when SS concentration are moderate to low, one would expect more MSA in submicron particles with higher lifetimes, and thereby a higher MSA concentration. This is exactly what is seen in Figure 3. The authors might think of this partitioning issue and perhaps add something to the manuscript along with it.

The authors should be more careful when using statistical expressions. For example, what is statistical basis of stating “…were not significantly different” on line 359? What does “correlated at a significant level” on line 444 mean? The strength and significance of a correlation are two different things. On lines 511-522, should one say inversely related to… than inversely correlating with…?

Influence of partition between coarse and submicron particles 435

Technical comments

The first paragraph of introduction is very long. I suggest slitting it into 2-3 parts, e.g. on lines 46 and 62.

Section 2 starts with a general background of the approach and then introduces an instrumental set up. To make this clearer, I suggest adding 2 sub-section titles to this part before the current sub-section 2.1.

Sections 2.2 and 2.3, and elsewhere. It is a bit confusion that the authors use the same notation for both the name of compound and its concentrations. The authors could think of using e.g. brackets (i.e. [WIOC]) when meaning concentration (like in eq. 3) or writing explicitly WIOC concentration in the text. Compound names should not be italicized like on lines 239-249.

The same symbol should be used: H_BL in eq. 1 vs. H in eq. 2

line 139: 30-m height

lines 269, 271, 278, 579 and 642: there should be a space between the variable and unit

line 310: should it be oxalate rather than oxalic acid?

line 321: section 3.4 rather than chapter (the same on line 513)

line 366: here, one may get the wrong exression that ammonium is neutralized by sulphate, even though it is the other way around

Finally, the figures should be understandable by themselves. Therefore, I recommend moving some explanation given on calculated NH4 concentration explained in the main text (lines 364-370) to the caption of Figure 2 (By the way, the yellow circles in Figure 2 do not show up clearly, maybe some other colour would be better). In the caption of Figure 4, it could be added: …contribution of organic matter in sea salt particles (OMss).

Language issues (mainly suggestions)

line 144: …any particular wind speed
line 171: “did not have” correct tense?
line 184: sufficient at or sufficient for?
line 337, comma before “it should”
line 359, comma before “preventing”
lines 400-401: …were mostly below detection limit…
line 427: comma before “its”
lines 474-479: this is a complicated sentence, please reword.
line 515: comma after “range”
line 539: the comma should be after, rather than before, “that”
line 542: in the submicron particle range
lines 557-560: this is a complicated sentence, please reword.
line 604: the occurrence of
line 617: comma before following

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ED: Reconsider after minor revisions (Editor review) (18 Aug 2016) by Tuukka Petäjä

AR by Darius Ceburnis on behalf of the Authors (23 Aug 2016) Author's response Manuscript

ED: Publish as is (12 Sep 2016) by Tuukka Petäjä

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