From the journal Environmental Science: Atmospheres Peer review history

17-May-2022

Dear Dr Patanen:

Manuscript ID: EA-ART-03-2022-000035
TITLE: Surface composition of size-selected sea salt particles under the influence of organic acids studied in situ using synchrotron radiation X-ray photoelectron spectroscopy

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Reviewer 1

The manuscript "Surface composition of size-selected sea salt particles under
the influence of organic acids studied in situ using synchrotron radiation X-ray photoelectron spectroscopy" reports the spectroscopic characterization of sea-salt aerosols having different sizes, in the presence/absence of organic molecules. The authors show good quality data and the results are interesting. The manuscript is well written. Below is a list of comments to address before the manuscript can be considered for publication in Env. Sci. Atmospheres.

1) Section 2.4 (page 2). What is the reason for such a large pass energy with low kinetic energy photoelectrons (70 eV)? Was 200 eV chosen in order to maximize the photoemission signals?

2) Page 4, right column (section 3.2). The authors claim that "...in all cases () the polydisperse particles show the smallest enrichment.". In the case of "inorg. sea salt + phenylalanine" the Mg enrichment in polydisperse, 250 and 350 nm looks almost identical.

3) Page 4, right column (section 3.2). "While the error bars for size-selected measurements are large, the observed trend indicates that the surface enrichment is larger towards the lower end of sub-micron size range,...". Here it is difficult to follow what the authors mean. Do they mean Mg or C enrichment? I don't see a clear trend in the surface enrichments, at least it is not clear in Figure 4. A trend would show that the enrichment is larger for smaller particles than for larger (decreasing trend passing from 150 to 350 nm and polydisperse).

4) Page 4, right column (section 3.2). "These binding energy shifts are
smaller than observed for gas phase phenylalanine." Based on reference 37, the shift between the carboxylic and the main peak in Phe is around 4.5 eV. The intensity of the carboxylic function in this work is weak (on both samples, and especially in the C 1s spectrum of aerosol particles containing octanoic acid). Based on this and on the resolution achieved during measurements, can the authors really exclude the presence of carboxylic groups (COOH)? As mentioned later in the text, at a pH of 7.8, Phe should be Zwitterionic. What is the driving force for a complete deprotonation of COOH?

5) Page 5, right column (section 4.1). "...Mg and Na are the most abundant cations, and their chloride salts are likely to be the most abundant species in the dried sea
salt particles.". The authors mention that the signal of Na 2s could not be clearly detected. However, sodium should be abundant. Na 2s is not the main core-level, however the cross section at 70 eV kinetic energy is quite high. Why isn't the signal of Na 2s detected in this study (bulk preference of Na+/signal attenuated by species at the surface)?

6) Page 6, left column (section 4.1). "This speculation needs verification by experiments using electron microscopy or preferably in-flight single particle imaging available at Free Electron Lasers (FELs).". The authors could carry out a depth profile analysis by means of XPS. The PLEIADES beamline should reach 1 keV photon energy. Why did not they vary the kinetic energy of Cl 2p, Mg 2p and C 1s?

7) Page 6-7, section 4.2 (addition of organics). Have the authors checked for possible beam-induced effects? If the surface is not permanently renewed, the beam may induce some decomposition of organics. Is there an evolution of the C 1s signal with time while scanning the C 1s signal?
I suggest the authors to show the ratio between different functionalities calculated from the C 1s fitting. This might give interesting information about the preferential orientation of the molecules (octanoic acid and Phe). As an example, if octanoic acid formed a "micelle-like" structure, exposing the aliphatic chain to vacuum, the (COOH)/(aliphatic C) ratio should be lower than the expected. If, as postulated, Phe does not form a monolayer, I would expect a COOH/aromatic C ratio closer to the expected.

8) Conclusions - GENERAL COMMENT. As suggested in the text, I believe that electron microscopy may help the authors to better characterize particles having different sizes (dispersion, shape and chemical composition). Having some microscopy data in this manuscript would increase the level/impact and justify some conclusions drawn by the authors.

Reviewer 2

This is a well-written paper on the effect of adding two organic acids on the surface enrichment of several elements for inorganic sea salt particles. I have the following comments that I think will improve the paper and hope authors can address. Overall, really nice study!
1. I suggest expanding on the selection of inorganic sea salt aerosols in relation to sea spray aerosols. This is important as at the selected size range, i.e., 100s of nanometers, it is now well established that real sea spray aerosols have very high organic enrichment, often with predominantly organic content, thus the selection of inorganic salts is problematic in terms of modeling sea sprays at these sizes. However, for larger sizes, sea spray certainly become less organic and predominantly inorganic.
2. Given that the authors determined that the particles formed after addition of acids are in carboxylate form, this likely indicates that chloride depletion took place as a result of an acid (HA) displacement reaction below, which is driven by high volatility of the HCl product: NaCl (aq) + HA (aq)  NaA (aq) +HCl(aq,g). Thus, for example, results shown in Fig. 3 b should also be discussed from the prospective of Cl depletion and corresponding C enrichment as a result of the displacement reaction above. I suggest authors add discussion on that + update the text where relevant as Cl clearly not a constant reference.
3. There is some interesting size-dependent trends and authors mention that could be in part due to formation of domains of organics on the particle surface. I think to test this hypothesis, one could do an additional experiment with different concentration of the acid, since for example increase in concentration should presumably lead to full coverage and thus similar results across sizes. I recognize that this would require extra measurements, which may not be directly relevant to the scope of the present paper; if authors decide not to do such experiments, then at least provide some additional discussion on the plan to carry out such experiments (in addition to SEM work authors already proposed to test the hypothesis).

Dear Editor,

we hereby submit a revised manuscript titled Surface composition of size-selected sea salt particles under the influence of organic acids studied in situ using synchrotron radiation X-ray photoelectron spectroscopy. We want to thank the reviewers for providing constructive feedback on our manuscript. Point-by-point responses and modifications to the manuscript are provided below. We also provide a separate marked-up version of the
manuscript, where all the changes are highlighted. It should be noted that the reference numbers in this letter differ from the revised manuscript (see the References-section below).

Reviewer 1
The manuscript "Surface composition of size-selected sea salt particles under the influence of organic acids studied in situ using synchrotron radiation X-ray photoelectron spectroscopy" reports the spectroscopic characterization of sea-salt aerosols having different sizes, in the presence/absence of organic molecules. The authors show good quality data and the results are interesting. The manuscript is well written. Below is a list of comments to address before the manuscript can be considered for publication in Env. Sci. Atmospheres.

Authors’ response: We thank the reviewer for the constructive comments and we are glad that the reviewer found our results interesting.

1. Section 2.4 (page 2). What is the reason for such a large pass energy with low kinetic energy photoelectrons (70 eV)? Was 200 eV chosen in order to maximize the photoemission signals?

Authors’ response: Yes, we used a big pass energy in order to maximize the signal while keeping the resolution still reasonable. We wanted to use a curved entrance slit, and the largest available is 0.8 mm, so a reasonable compromise with a transmission and a resolution was achieved with a 200 eV pass energy.

Changes to the manuscript: The second paragraph in section 2.4. is changed to: ”The spectrometer’s contribution to instrumental broadening was always 400 meV during the experiments, determined by a pass energy of 200 eV and 0.8 mm curved entrance slit of electron analyser. These settings offered a
reasonable compromise between the resolution and the transmission.”

2. Page 4, right column (section 3.2). The authors claim that "...in all cases () the polydisperse particles show the smallest enrichment.". In the case of "inorg. sea salt + phenylalanine" the Mg enrichment in polydisperse, 250 and 350 nm looks almost identical.

Authors’ response: The reviewer is correct, in the case of phenylalanine, 250 nm, 350 nm, and polydisperse are all within the error bars. We have now pointed this out in the text.

Changes to the manuscript: Page 4, right column, section 3.2.: ”However, in the case
of pure inorganic sea salt and pure inorganic sea salt + octanoic acid, the polydisperse particles show the smallest enrichment. This is also true for pure inorganic sea salt + phenylalanine, but in this case the ER values of monodisperse 250 and 350 nm particles are also very close to the polydisperse result.”

3. Page 4, right column (section 3.2). "While the error bars for size-selected measurements are large, the observed trend indicates that the surface enrichment is larger towards the lower end of sub-micron size range,...". Here it is difficult to follow what the authors mean. Do they mean Mg or C enrichment? I don’t see a clear trend in the surface enrichments, at least it is not clear in Figure 4. A trend would show that the enrichment is larger for smaller particles than for larger (decreasing trend passing from 150 to 350 nm and polydisperse).

Authors’ response: We agree that this sentence is not easy to follow, but we meant exactly the same trend which the reviewer describes. We have rephrased the sentence.

Changes to the manuscript: Page 4, right column, section 3.2.: ”While the error bars for size-selected measurements are large, the observed trend indicates that the surface enrichment decreases towards the larger particles, since the polydisperse particle stream contains a significant amount of surface area from micron-size particles. ”

4. Page 4, right column (section 3.2). "These binding energy shifts are smaller than observed for gas phase phenylalanine." Based on reference 37, the shift between the carboxylic and the main peak in Phe is around 4.5 eV. The intensity of the carboxylic function in this work is weak (on both samples, and especially in the C 1s spectrum of aerosol particles containing octanoic acid). Based on this and on the resolution achieved during measurements, can the authors really exclude the presence of carboxylic groups (COOH)? As mentioned later in the text, at a pH of 7.8, Phe should be Zwitterionic. What is the driving force for a complete deprotonation of COOH?

Authors’ response: We agree that the conclusion about the complete deprotonation of COOH can hardly be made based on XPS due to the very low signal in the COO−/COOH region. Related to the reviewer’s question 7, we have checked the intensity ratios of the COO−/aromatic and COO−/aliphatic carbons, and we found that they are much smaller than expected from the stoichiometric considerations (see answer 7 for more details). Thus, it is possible that the COO−/COOH signal forms a broad feature due to partial deprotonation and different chemical environments. Both seem feasible considering that the aerosol particles contained very little water during the measurement and thus protons could be replaced by inorganic cations. Our fits reflect this variety of carbon species not to the fullest extend. We have modified the text so that this uncertainty related to the deprotonation is better taken into account. There was also a confusion about the form of the phenylalanine, which is most likely zwitterionic and not completely deprotonated anionic form. We have modified the text and refer to literature binding energy shifts found for zwitterionic form.

Changes to the manuscript: Page 4, section 3.2., right column: ”Concerning the particles formed upon addition of acids, we can use binding energy differences between the aliphatic or phenyl carbons and carboxyl carbons to deduce whether they were in acid or acetate form in the aerosol particles. In polydisperse sea salt particles with phenylalanine, we found that the α and carboxyl carbons were shifted 1.3 eV and 3.9 eV towards higher binding energies compared to phenyl carbons. These binding energy shifts are smaller than observed for gas phase phenylalanine (1.6 and 4.55 eV[1]) and closer to measured values of solid state zwitterionic form (approximately 1.2 and 3.4 eV[2]). Similarly, the binding energy difference between aliphatic and carboxyl carbons in sea salt particles with octanoic acid was about 3.8 eV, which is lower than expected for acid indicating a carboxylate form. Thus, we have an indication that it was mostly COO– groups that were present on the particle surface. However, it has to be noted that the signal of the carboxyl carbon is very small, and the integrated intensity of the fitted peak is only about 4% from the aromatic carbon signal, whereas 17% would be expected based on purely stoichiometric arguments. Thus, it is possible that the carboxyl peak is very broad since the group can have many different chemical environments and our fits do not reflect this variety of carbon species to the fullest extend. On the other hand, variation from the stoichiometry has been observed before in different systems[4–8] and can be explained by various factors, e.g. a preferred orientation of molecules combined with scattering effects. Radiation damage which can similarly alter the stoichiometry[2] can be ruled out in our study due to a continuously renewing beam of particles which spend less than a 1µs in the photon beam (approximately 4·10^7 photons·s^−1 · µm^−2)[9] so that the probability for multiple ionization of the same molecule is very low.”

5. Page 5, right column (section 4.1). "...Mg and Na are the most abundant cations, and their chloride salts are likely to be the most abundant species in the dried sea salt particles.". The authors mention that the signal of Na 2s could not be clearly detected. However, sodium should be abundant. Na 2s is not the main core-level, however the cross section at 70 eV kinetic energy is quite high. Why isn’t the signal of Na 2s detected in this study (bulk preference of Na+/signal attenuated by species at the surface)?

Authors’ response: The reviewer is correct, the likely reason for absence of Na 2s signal is the bulk preference, and since the electron escape depth is small, the signal is attenuated by the overlayers. We now state this more clearly in the manuscript.

Changes to the manuscript: Page 3, section 2.5: ”The enrichment ER of a given atomic species (i=Mg or C) relative to a reference species (ref= Cl or Mg) follows the definition by Duce et al.[10], except due to practical reasons, we cannot use the Na+ ion as a reference species since its spectral signature is too small. This is likely due to bulk preference of Na+ in sea salt aerosols[11].”

6. Page 6, left column (section 4.1). "This speculation needs verification by experiments using electron microscopy or preferably in-flight single particle imaging available at Free Electron Lasers (FELs).". The authors could carry out a depth profile analysis by means of XPS. The PLEIADES beamline should reach 1 keV photon energy. Why did not they vary the kinetic energy of Cl 2p, Mg 2p and C 1s?

Authors’ response: The reviewer raises an important point and we agree that a depth profiling study would have been useful. However, due to the quickly decreasing photoionisation cross-section, the already small XPS signals would have been extremely low at around 1 keV, and the measurement times
would have been impractically long. This could be of course compensated by a very high photon flux, but unfortunately, also the photon flux decreases towards the higher available energies at PLEIADES. From another perspective, in order to increase the signal from bulk substantially, one would need to use significantly higher kinetic energies. To our knowledge, gas-phase nanoparticle XPS experiments have not yet been performed at hard X-ray beamlines. However, if those beamlines would become available for this type of experiments, it would certainly shed light on the proposed layered structures.

Changes to the manuscript: On page 6, section 4.1 we now comment on the depth profiling and we added a general comment about hard X-ray beamlines since it fits the topic of this special issue: ”Furthermore, increasing the electron escape depth by using a substantially higher photon energy would be
beneficial in order to clarify the composition of surface and bulk layers. This requires a very high photon flux and high particle densities in order to compensate the quickly decreasing photoionisation cross section as a function of photon energy. We look forward to future development of high brilliance hard X-ray beamlines to accommodate gas-phase nanoparticle sample environments that would enable such depth-profiling experiments.”

7. Page 6-7, section 4.2 (addition of organics). Have the authors checked for possible beam-induced effects? If the surface is not permanently renewed, the beam may induce some decomposition of organics. Is there an evolution of the C 1s signal with time while scanning the C 1s signal? I suggest the authors to show the ratio between different functionalities calculated from the C 1s fitting. This might give interesting information about the preferential orientation of the molecules (octanoic acid and Phe). As an example, if octanoic acid formed a "micelle-like" structure, exposing the aliphatic chain to vacuum, the (COOH)/(aliphatic C) ratio should be lower than the expected. If, as postulated, Phe does not form a monolayer, I would expect a COOH/aromatic C ratio closer to the expected.

Authors’ response: When it comes to the beam-induced effects, one of the benefits of studying a free-flying nanoaerosol beam is that it provides continuously renewing sample and charging or radiation damage is avoided. The velocity of the nanoparticle beam is about 160 m/s[12] and each particle spends less than 1 µs in the synchrotron beam whose width is order of 100 µm. The photon flux at PLEIADES in similar conditions to us has been previously estimated to be order of 4·10^7 photons/(sµm^2)[9], and the 350 nm diameter particle would encounter on average two photons on its way across the photon beam. Thus, even if each photon-particle interaction would lead to a photoionisation event, radiation damage due to
multiple ionization of the same molecule can be neglected.
As suggested by the reviewer, we have now included the information about the intensities of C components. In both cases, phenylalanine and octanoic acid, the ratio is lower than expected from stoichiometric considerations. Like the reviewer suggests, this could in principle be used to determine the orientation of the molecules. However, a recent article by Dupuy et al.[8] points out various factors which contribute to the difficulty of deducing the orientation purely from XPS intensities. They show that photoelectron angular distributions can be used for more complete information. Thus, as we did not study the angular distributions, we cannot say anything certain about the orientation. However, as advised by the reviewer, we now report the intensity ratios and find that they are inline with the assumption that the carboxylate group would be closer to the bulk of the particle.

Changes to the manuscript: See changes made to Page 4, section 3.2. in the answer to the question 4. Additionally, we have added a comment about the ratios to the discussion of the micelles, page 6, section 4.2, right column: ”Aerosol particles with long-chain organic compounds have been suggested to be ”inverted micelles”, consisting of a highly concentrated aqueous core surrounded by a layer of organics with their hydrophobic tail pointing outwards from the particle core[13]. Such structures are expected here as well, and the octanoic acid layer may prohibit complete drying of the core. This is supported by
the lower than expected signal intensity from COO– compared to aliphatic carbons. However, it should be noted that deduction of the orientation of the molecules using only XPS intensities is not straightforward[8].”

8. Conclusions - GENERAL COMMENT. As suggested in the text, I believe that electron microscopy may help the authors to better characterize particles having different sizes (dispersion, shape and chemical composition). Having some microscopy data in this manuscript would increase the level/impact and justify some conclusions drawn by the authors.

Authors’ response: We completely agree with the reviewer, but unfortunately we did not have in place a procedure to collect the XPS analysed particles on electron microscopy grids. This is however doable and has been established in another study concerning gold nanoparticles[14] and can be implemented on future studies of sea salt particles. We agree that electron microscopy could clarify the particle morphology and when combined with e.g. X-ray analysis, also in the elemental analysis. However, especially when it comes to organic coating on particles, it is not very easy to analyse with electron microscopy, and the electron beam deposits quickly carbon on the particles. Deposition of particles on substrates may alter their morphology, so ideally, the structural analysis would be also carried out in-flight.

Changes to the manuscript: No changes.

Reply to reviewer 2
This is a well-written paper on the effect of adding two organic acids on the surface enrichment of several elements for inorganic sea salt particles. I have the following comments that I think will improve the paper and hope authors can address. Overall, really nice study!

Authors’ response: We thank the reviewer for a positive assessment of our paper and for the comments helped us to improve the paper.

1. I suggest expanding on the selection of inorganic sea salt aerosols in relation to sea spray aerosols. This is important as at the selected size range, i.e., 100s of nanometers, it is now well established that real sea spray aerosols have very high organic enrichment, often with predominantly organic content, thus the selection of inorganic salts is problematic in terms of modeling sea sprays at these sizes. However, for larger sizes, sea spray certainly become less organic and predominantly inorganic.

Authors’ response: The reviewer raises an important point concerning the composition of particles in this size range. The pure inorganic sea salt aerosols are a natural reference point for our study. The surface enrichment can be an interplay of inorganic and organic effects, and in disentangling these effects we found the pure inorganic reference to be important. Furthermore, we want to emphasize that diameters reported here for aerosol particles are diameters of dry particles. The XPS analysed particles contain only very little water due to the passage through the diffusion dryer. However, they were much larger directly after the atomisation. To provide a very rough reference for the size, we assume a dry NaCl particle with 150 nm diameter generated from a pure 0.6 M NaCl solution. This NaCl concentration roughly corresponds to the sea salt concentration we used during our experiments (and that of sea water). Before drying, this particle would have an estimated diameter of 1.2 µm and would thus correspond to larger wet aerosol particles. Furthermore, from more practical side, inorganic sea salt solution was known to produce high particle concentrations in this size range and as size selection reduces the particle density significantly, high densities were needed. While in general in nanoparticles the variation of certain properties as a function of size is largest in a few nanometer size range, and the organic enrichment is also expected to be higher the smaller the size[15,16], the used aerodynamic lens setup has largest transmission for particles with diameter above 100 nm.

Changes to the manuscript: Page 2, end of section 1.: ”We have concentrated on size-selected particles with dry diameters in the 150-350 nm range. Based on the studied 0.6 M sea water salt concentration, we estimate these particles to originate from droplets with their wet diameters in 1-2 µm range. This is an interesting size range for SSA where both sea salt and organic content are important[16]. While the organic content is found to become the more dominant the smaller the droplet size[15,16], the used aerodynamic lens setup practically limited the studied size-selected particles to sizes above 100 nm for dry particle diameter.”

2. Given that the authors determined that the particles formed after addition of acids are in carboxylate form, this likely indicates that chloride depletion took place as a result of an acid (HA) displacement reaction below, which is driven by high volatility of the HCl product: NaCl(aq)+HA(aq) → NaA(aq)+HCl(aq,g). Thus, for example, results shown in Fig. 3 b should also be discussed from the prospective of Cl depletion and corresponding C enrichment as a result of the displacement reaction above. I suggest authors add discussion on that + update the text where relevant as Cl clearly not a constant reference.

Authors’ response: We agree that enrichment of C can be also Cl depletion, and we have tried to make this clearer now in our modifications. We would like to point out that it is difficult to find a reference ion which would be constant reference, as in previous works it has been shown that also relative cation
concentrations change on the surface depending on the composition of the solution[11,17]. Cl depletion due to HCl formation in case of acid can take place, however, the observed size-selected vs. polydisperse trend is difficult to explain solely by this mechanism.

Changes to the manuscript: On page 4, section 3.2., right column: ”Compared to pure sea salt particles, the addition of octanoic acid increased the Mg enrichment while the addition of phenylalanine decreased it. This effect can be achieved in two ways: in the case of octanoic acid, Mg is enriched and/or
Cl depleted from the particle surface, and in the case of phenylalanine, either Mg was depleted or Cl enriched.”
Starting from page 6, section 4.2.,right column: ”One possible reason for increased Mg-enrichment upon addition of octanoic acid would be that Cl is expelled from the surface due to salt formation between cations and carboxylate. Cl can form HCl and as a volatile substance leave the solution. Thus, our method, where we compare the abundance of the ions to Cl signal instead of more commonly use Na reference[16,18] is not ideal, but stems from practical limitations of the method: the Na XPS signal is so small that such a comparison would introduce large errors to the analysis. Also, addition of organic acid was shown to change the relative cation ratio on the particle surface[11], and thus, it is difficult to find an absolute constant reference for the ER. ”

3. There is some interesting size-dependent trends and authors mention that could be in part due to formation of domains of organics on the particle surface. I think to test this hypothesis, one could do an additional experiment with different concentration of the acid, since for example increase in concentration should presumably lead to full coverage and thus similar results across sizes. I recognize that this would require extra measurements, which may not be directly relevant to the scope of the present paper; if authors decide not to do such experiments, then at least provide some additional discussion on the plan to carry out such experiments (in addition to SEM work authors already proposed to test the hypothesis).

Authors’ response: Varying the concentration of the organic would have been interesting and it is a very good idea for a future work. Unfortunately, due to limited availability of synchrotron beamtime, such measurements are not possible in relation to this manuscript.

Changes to the manuscript: Page 7, end of section 4.2, right column: ”XPS analysis carried out as a function of the concentration of the organic compound would be beneficial to shed light on the organisation of the organics on the particle surface. This is left for a future study, in which also the photon polarization could be varied for additional information on the surface layer orientation.”

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29-Jul-2022

Dear Dr Patanen:

Manuscript ID: EA-ART-03-2022-000035.R1
TITLE: Surface composition of size-selected sea salt particles under the influence of organic acids studied in situ using synchrotron radiation X-ray photoelectron spectroscopy

Thank you for submitting your revised manuscript to Environmental Science: Atmospheres. I am pleased to accept your manuscript for publication in its current form. I have copied any final comments from the reviewer(s) below.

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Environmental Science: Atmospheres
Royal Society of Chemistry

Reviewer 1

I am satisfied by the replies provided by the authors. The manuscript can now be accepted.

Reviewer 2

The authors addressed concerns and suggestions raised by this reviewer, I am happy to support publication of the manuscript in the present form.