the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 06 Aug 2024
Isomer Molecular Structures and Formation Pathways of Oxygenated Organic Molecules in Newly Formed Biogenic Particles
Abstract. Oxygenated organic molecules (OOMs) formed from oxidation of anthropogenic and biogenic volatile organic compounds (VOCs) are essential ingredients for atmospheric new particle formation (NPF) and secondary organic aerosol (SOA) formation, and thus impact air quality, human health, and climate. There is a large variety of OOM compounds, but currently, for the vast majority of OOMs, their molecular structures and formation pathways are still unknown. In this study, we identified isomer-resolved molecular structures and reaction pathways for dimer OOMs formed from ⍺-pinene ozonolysis, using an ultrahigh-performance liquid chromatography-electrospray ionization Orbitrap mass spectrometer (UPLC/(-)ESI-Orbitrap MS) tandem analysis and a high-resolution time-of-flight chemical ionization mass spectrometer (HrTOF-CIMS) attached to the filter inlet for gas and aerosol (FIGAERO), combined with explicit chemical modeling simulations using the Generator of Explicit Chemistry and Kinetics of Organics in the Atmosphere (GECKO-A). In general, each OOM identified in the newly formed biogenic particles contains 2–8 isomers with distinctive MS/MS fragmentation ions. For C19H30O5, which is one of most abundant dimers identified from the boreal forests and laboratory biogenic NPF studies, one isomer forms in the gas phase from a stabilized Crigee Intermediate (sCI) peroxy biradical and aldehyde, followed by subsequent gas-to-particle conversion; and another isomer forms in the particle phase via the Baeyer-Villiger reaction from a cyclic acylperoxyhemiacetal and ⍺-pinanediol. Two isomers of C16H26O6 form in the particle phase via decarboxylation from two different isomers of C17H26O8 after the condensation from the gas phase. Thus, our results show that biogenic OOMs can also form from particle-phase reactions and have different isomeric structures than in the gas phase. Our study represents the first molecular-level chemical analysis to identify particle-formation pathways for OOMs in the newly formed biogenic nanoparticles. Currently, parameterizations of NPF (e.g., biogenic NPF) are based on the gas-to-particle conversion of extremely low-volatility OOM dimers that form in the gas phase alone (e.g., via RO2 + RO2 reactions). Our study demonstrates that additional, independent particle-phase formation pathways should also be considered for predictions of the formation and growth of new particles in the atmosphere.
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RC1: 'Comment on egusphere-2024-2454', Anonymous Referee #1, 10 Oct 2024
The study utilizes a flow tube to generate aPinene SOA formed from oxidation by both O3 and OH radicals. The authors used 2 mass spectrometers (FIGAERO-CIMS and LC-MS) to evaluate the composition of the formed SOA and species present in the gas-phase. The manuscript is broken down into sections describing the measured composition by the mass spectrometers, a comparison of the log C* measured by the FIGAERO and a (undefined) volatility parameterizations, and LC-MS analysis of specific molecular formula which were thought to be associated with particle phase reactions. The authors desired to connect their measurements to the need to have isomer resolved C* measurements and the need to take into account particle phase reactions into new particle formation parameterizations.
I did not find the manuscript framed and connected the disparate sections effectively. I believe this draft is still very preliminary and the manuscript at this stage needs clear work to use correct terminology, connect their C* results to those of others, and provide adequate evidence of the mechanisms proposed.
Major comments:
- There is no specific volatility basis set parameterization. The volatility basis set is a simplification to be able to reduce the 1000s of molecules formed into discrete C* bins and to use that as a way to estimate partitioning of organics between the gas and particle phase. This reduces the 1000s of molecules into 3-10+ volatility bins. There are many volatility parameterizations that exist1-5 and they are correct in the description of how they work, because this is a simplification to take molecular formula measurements to extract C* values. Therefore, in the labels of “VBS” in Figures 2B and C are incorrect (and the corresponding discussion around it). What should be included is what actual parameterization is used (and cite it in the main text), and to note that in the figures. Further, there needs to be a discussion about the inherent uncertainties of the parameterizations, at the moment they are presented as base truth (hence no error bars in parameterization extracted C*), which is not the case. There is a discussion in Donahue (2011) about what the uncertainties are on the parameterization.1
- Regarding the implications that such particle phase processes are needed to understand new particle formation (NPF) and growth, I would agree with only one of the two statements. For growth I would agree, while for NPF I would not agree. My reason for disagreement comes from what is required to have new particle formation, which is a supersaturation of organic vapors because no pre-existing particle exists. Meaning, the important components are formed in the gas-phase. Also, the prerequisite for a particle-phase reaction is not present (i.e. particles). Therefore, I don’t believe the abstract and implication sections are framed correctly.
- Given the loading dependent and thermal decomposition effects in the thermogram of the FIGAERO, how did the authors take care to mitigate against these effects when extracting C* values? Related to this, please compare the C*s extracted here to those from other papers because these values are very low and to be quite honest are not realistic. For instance, these results would suggest that all monomers observed are basically LVOCs. (see other minor comments related here below)
- In the discussion surrounding the mechanisms proposed, my feeling is there is lack of basis for the proposed mechanisms without citations providing rationale for why things like the SOZ are the likely species formed, especially when another study proposed a very different structure with similar fragmentation pathways (as the authors discuss). The importance of the stabilized Criegee Intermediate is based on previous work which found this to be true, but there is no directly evidence to be able to assess if that is also true within this study for these specific molecules without experiments specifically designed to test this hypothesis or standards to demonstrate this. Other measurements used a Criegee and/or OH scavenger to elucidate the dimers forming from the stabilized Crigee Intermediate and found that the C19H30O5 was specifically not impacted by the presence of the Criegee scavenger.6 Other dimers were impacted (e.g. C20H30Ox dimers). This leads me to question the proposed reaction mechanism.
- Lines 423 – 424: Why is isomer resolution needed for volatility estimation? I think that there would need to be a discussion focused in this direction.
Minor comments: (some of which are used to generate the major comments)
CHO-1 and CHO-2 (I don’t understand their graphical abstract at a first look, and after the reading the manuscript, I see it applies to label present in the manuscript. I would recommend improving this.)
Line 43: This is the first molecular level analysis??? This paper cited many other papers that have done a similar thing.
Line 117: Does GECKO-A actually verify the molecular structures? In my mind it helps suggest possible pathways, but does not provide a ground truth.
Lines 125 – 136: What fraction of α-pinene reacted with O3 vs OH?
Lines 150-151: I agree with this statement, what was done to take this into consideration?
Methods 2.1: Were any background desorptions performed to determine the “noise” associated with the FIGAERO measurement? (i.e. is 0.1 #/s in Figure 1 really statistically significant?) (the same can also be asked for the LC-MS analysis)
Line 227: shouldn’t the full sentence on this line go after the next sentence. How much does 50% of the most abundant species make up of the total signal for each of the instruments?
Lines 226-242: It would be helpful to report fractions of “monomers” and “dimers” rather than relying on qualitative statements.
Lines 243 – 255: Perhaps there should be a discussion about the comparability between the FIGAERO-CIMS and the LC-MS data, because there are clear differences in sampling collection time between the instruments. What artefacts can this result in?
Line 254-255: The species in Table 2 (which refers to specific isomers and their distinct RT and MS/MS) were chosen because of their reproducibility in the FIGAERO thermograms? Is this different from the 50% mentioned on line 227?
Lines 266-269: I would argue the teeth-like shape references is really only apparent for the C15+ molecular formula.
Figure 2a and b are missing the units on the x-axis.
Figure 2c where do the error bars come from? I don’t believe the units on the y-axis are correct. μ / cm3???
Line 283: I believe that there should be a comma instead of a dash in the molecular formula, since a C8H13O6 is not a closed shell species. (same comment about commas on line 285)
Line 288: “make them more stable in the gas-phase” isn’t an important distinction then the activity coefficient (or effective saturation vapor concentration) not the C*.
Lines 291-295: Aren’t these also attributed to thermal decomposition of species on the filter? I would treat this with caution. On the note of thermal decomposition, how do the authors know that the C* extracted for a specific molecular formula is actually for that specific formula? For instance, when I see the C10H14O4 in Figure 2C (Log C* ~ -6) it has a C* similar to ‘dimers’. To me that would suggest this should be attributed to decomposition. Further, if there is thermal decomposition of dimers, how would that impact the extracted C* of dimers? Wouldn’t this be biased in someway?
Without any oxygen containing an OH functionality, is it reasonable for H2O loss to be a dominate pathway?
Isn’t it also possible to have an RO2 + RO2 pathway to form C19H30O5?
Are there citations for SOZ fragmentation pathways? Without providing some evidence for these fragmentation pathways, I do not see why this is reasonable. (e.g. do you have standards where these fragmentation pathways have been observed for model compounds?)
What is the organic aerosol mass concentration in the flow tube for all of the experiments?
Line 316-325: This section is pure conjecture since there is no clear evidence that the stabilized Criegee intermediate is actually involved in its formation. To prove that the stabilized Criegee intermediate is important experiments with a Criegee scavenger would be necessary.
Line 346-357: shouldn’t this change in oxidants also be reflected in the methods section? How do these changing conditions change the aerosol mass concentrations in the flow tube?
Line 386: the RO2+RO2 reaction proposed does not work because they are actually closed shell molecules. C8H14O6 + C9H14O4 (did they detect the radicals in the gas-phase?) I guess the authors mean C8H13O6 and C9H13O4. Have these radicals been reported elsewhere in the literature?
Lines 382 – 390: Is there specific evidence that the C16H26O6 comes from a C17H26O8, unique to this study, that would suggest this reaction pathway? Or is this solely based on a mechanism from Zhang et al (2015)?
Lines 391 – 398: Is this a bias in the fact the filters were collected for 24hrs and then allowed to sit for some amount of time allowing reactions to continue both during and after collection? When considering the Pospisilova et al. (2020) At short time scales (similar to the flow tube in this study) the dimers were dominated by C20 molecules so I don’t believe that this is necessarily a fair comparison.
References:
- Donahue, N. M.; Epstein, S. A.; Pandis, S. N.; Robinson, A. L., A two-dimensional volatility basis set: 1. organic-aerosol mixing thermodynamics. Atmos. Chem. Phys. 2011, 11 (7), 3303-3318 DOI: 10.5194/acp-11-3303-2011
- Mohr, C.; Thornton, J. A.; Heitto, A.; Lopez-Hilfiker, F. D.; Lutz, A.; Riipinen, I.; Hong, J.; Donahue, N. M.; Hallquist, M.; Petäjä, T.; Kulmala, M.; Yli-Juuti, T., Molecular identification of organic vapors driving atmospheric nanoparticle growth. Nat. Commun. 2019, 10 (1), 4442 DOI: 10.1038/s41467-019-12473-2
- Stolzenburg, D.; Fischer, L.; Vogel, A. L.; Heinritzi, M.; Schervish, M.; Simon, M.; Wagner, A. C.; Dada, L.; Ahonen, L. R.; Amorim, A.; Baccarini, A.; Bauer, P. S.; Baumgartner, B.; Bergen, A.; Bianchi, F.; Breitenlechner, M.; Brilke, S.; Buenrostro Mazon, S.; Chen, D.; Dias, A.; Draper, D. C.; Duplissy, J.; Haddad, I.; Finkenzeller, H.; Frege, C.; Fuchs, C.; Garmash, O.; Gordon, H.; He, X.; Helm, J.; Hofbauer, V.; Hoyle, C. R.; Kim, C.; Kirkby, J.; Kontkanen, J.; Kürten, A.; Lampilahti, J.; Lawler, M.; Lehtipalo, K.; Leiminger, M.; Mai, H.; Mathot, S.; Mentler, B.; Molteni, U.; Nie, W.; Nieminen, T.; Nowak, J. B.; Ojdanic, A.; Onnela, A.; Passananti, M.; Petäjä, T.; Quéléver, L. L. J.; Rissanen, M. P.; Sarnela, N.; Schallhart, S.; Tauber, C.; Tomé, A.; Wagner, R.; Wang, M.; Weitz, L.; Wimmer, D.; Xiao, M.; Yan, C.; Ye, P.; Zha, Q.; Baltensperger, U.; Curtius, J.; Dommen, J.; Flagan, R. C.; Kulmala, M.; Smith, J. N.; Worsnop, D. R.; Hansel, A.; Donahue, N. M.; Winkler, P. M., Rapid growth of organic aerosol nanoparticles over a wide tropospheric temperature range. Proc. Natl. Acad. Sci. U. S. A. 2018, 115 (37), 9122-9127 DOI: 10.1073/pnas.1807604115
- Peräkylä, O.; Riva, M.; Heikkinen, L.; Quéléver, L.; Roldin, P.; Ehn, M., Experimental investigation into the volatilities of highly oxygenated organic molecules (HOMs). Atmos. Chem. Phys. 2020, 20 (2), 649-669 DOI: 10.5194/acp-20-649-2020
- Li, Y.; Pöschl, U.; Shiraiwa, M., Molecular corridors and parameterizations of volatility in the chemical evolution of organic aerosols. Atmos. Chem. Phys. 2016, 16 (5), 3327-3344 DOI: 10.5194/acp-16-3327-2016
- Zhao, Y.; Thornton, J. A.; Pye, H. O. T., Quantitative constraints on autoxidation and dimer formation from direct probing of monoterpene-derived peroxy radical chemistry. Proceedings of the National Academy of Sciences 2018, 115 (48), 12142 DOI: 10.1073/pnas.1812147115
Citation: https://doi.org/10.5194/egusphere-2024-2454-RC1 -
RC2: 'Comment on egusphere-2024-2454', Anonymous Referee #2, 26 Oct 2024
Review report for “Isomer Molecular Structures and Formation Pathways of Oxygenated Organic Molecules in Newly Formed Biogenic Particles”
Summary
This manuscript investigated gaseous and particle phase molecular composition from ozonolysis of a-pinene in the absence of seed aerosols. The gas phase analysis is done by an iodide CIMS. The authors applied two complementary MS (FIGAERO CIMS and LC-Orbitrap MS) for particle phase analysis, which are usually not often when both are available. Therefore, it is expected to provide some promising new information of SOA molecular composition, especially LC-Orbitrap MS is likely to provide isomeric speciation as well as structural info from MS2, which is the key focus of this study. However, my feeling is mixed after fully reading the manuscript. I will try if my comments can help the authors to improve their work, but my conclusion is clear that the current form of this manuscript really needs substantial revision and there are many problems I found.
Major concerns
(1) The authors emphasize their study as the first identification of particle-formation pathways in newly formed biogenic particles. This gives me a first feeling that this could not be true actually. Of course, new compounds and new chemistry in SOA can always be identified and proposed, but I strongly believe some SOA particle phase chemistry are already known, and these proposed particle phase mechanisms (even very uncertain) in this study are based on existing knowledge. The below reference is just one of the review papers summarizing some oligomer formation pathways.
It is true that aerosol nucleation and SOA growth occur in this study because of no seed particle, but basically the authors investigate very traditional a-pinene SOA composition that have been done for decades. This manuscript is NOT a typical NPF and aerosol nucleation study and the focus is NOT on composition of very fresh aerosol nucleation processes, e.g. sub-10nm. Therefore, it should have very limited implication that able to extrapolate to the so-called new particle formation. These over extrapolations to NPF processes should be revised and toned down throughout the entire manuscript, to avoid overselling.
Ref: Hall IV W A, Johnston M V. Oligomer formation pathways in secondary organic aerosol from MS and MS/MS measurements with high mass accuracy and resolving power[J]. Journal of the American Society for Mass Spectrometry, 2012, 23(6): 1097-1108.
(2) The structural characterization for some selected OOMs is the key focus of this study. Unfortunately, this is highly challenging but also highly uncertain based on MS2 alone. There are different levels of identification confidence for communication. I am not sure the authors are aware of this or not, but usually should be deeply discussed when interpret the proposed structures, e.g. see below reference. From my knowledge, the authors proposed four structures of four OOMs, which are all at level 3. This means that these are tentatively assigned structures and highly uncertain.
Ref: Schymanski E L, Jeon J, Gulde R, et al. Identifying small molecules via high resolution mass spectrometry: communicating confidence[J]. ES&T. 2014.
(3) These structures are proposed without designing targeted experiments to validate the proposed structures, e.g. introducing SCI and RO2 scavengers, which is one of my biggest concerns of this study. The authors mentioned they performed another experiment by varying ozone concentration (250-1000ppb, as shown in Fig. S5). It is not clear to me how many different expts involved, and are they normalized to same mass loading? Line 353-355 this is something vague, and this argument certainly does not convince me. A compound showing same peak area at different ozone concentrations does not justify that this compound is formed via particle phase reaction. By the way, the EICs of blank sample should be added. Again, the best way to test the proposed reaction is to introduce different scavengers rather than change ozone concentration.
(4) Do the authors first get the SOZ structure from MS2 analysis and then propose the SCI+C9 aldehyde reaction? Or in a reverse way that first assume there is such SCI+C9 aldehyde reaction occurring to get the SOZ structure and then interpret MS2 data following the pre-assumed SOZ structure? This is another concern regarding the structural analysis, especially the MS2 based structure is highly uncertain. I notice that the authors mentioned another study in line 324 by Witkowski and Gierczak [2014] that they showed similar MS2 and suggested the particle-phase aldol condensation route leading the formation of C19H30O5. It is not clear for me that how this possibility can be ruled out without other complementary experimental evidence?
(5) For Fig. 3d, there is a clear mistake of the structure of a-pinene SCI, as the C=O of a-pinene SCI is missing. There should be at least two SCI (I/II) structures (not considering cis- and trans-) due to the two decomposition pathways of a-pinene POZ. At the same time, C9H14O2 has two C=O bonds and therefore should at least result in four different SOZ structures of C19H30O5. Even though I do not believe this C19H30O5 at RT=15.3min is SOZ (see my later following comment 6).
In addition, in Fig. 3, there are two clear isomers at ca. 15.3 min, and why specifically chose the one eluting at 15.3min not the other one at ca. 15.5min? By contrast, two isomers found at ca. 20.2min and it seems both are chosen for MS2, which is a bit strange to me. It is not clear what collisional energy condition - HCD of the MS2 for these MS2 spectra in Fig. 3-4.
(6) I have a very close look at the two isomers of C19H30O5, as shown in Fig. 3, which is one of the two main OOMs in this study. Firstly, I strongly believe the isomer of C19H30O5 at RT=15.3 min is not SOZ, but might be the other dimer involving a-pinanediol (note that other possibility cannot be excluded here). Just simply looking at the proposed SOZ structure of C19H30O5, it is very unlikely to get a deprotonated ionization and result in a form of [M-H]-. The caption of Fig. 3 is not clear but I think the authors mentioned EIC of m/z = 337.2019 referring to [C19H30O5-H]-. Another reason is from Fig. S4, where the EIC of [C10H18O2+Na]+ shows two peaks, and the first one eluting at ca. 11.3 min, and the second peak eluting at 15.3 min. From my experience, this second peak at 15.3 min is an in-source fragmentation and likely from C19H30O5. The first peak eluting at ca. 11.3 min is almost for sure the ⍺-pinanediol because it should be eluting at similar monomeric region to these monomer compounds (e.g. pinic acid C9H14O4 at 9.28min, C10H16O3 at 10.98 min as I found Table S2). This means that the entire structural analysis for C19H30O5 is likely wrong and therefore the interpretation should be re-done and re-written. I did not have further close look at the two isomers of C16H26O6, but my assessment is that the proposed structures and reaction mechanism are highly uncertain, if no other evidence provided.
(7) Speaking of in-source fragmentation, it seems the authors are totally not aware of this issue, but this is a very common issue in LC-ESI Orbitrap MS and can result in misleading data interpretation. There are clearly many wrongly assigned monomer compounds that eluting at dimeric regions in Table S2, e.g. C10H16O3-2 eluting at 20.8 min must be a fragment from a larger molecular. By looking at Table S2, the monomer eluting region seems to be RT<12 min and dimeric eluting region is likely RT>12min. It seems that the authors need some basic HPLC knowledge and polar analysis to understand the eluting orders in reverse phase C18 HPLC. Otherwise, I would assume the authors are not yet ready to handle such complex LC-Orbitrap MS dataset for complex SOA composition. This is especially for non-targeted analysis where the authors cannot simply rely on the output of Compound Discovery software, which usually needs further refinement of post data analysis and manual adjustment. In addition, pos mode usually has better ionization for dimers than neg mode. Comparing both negative and positive LC Orbitrap data are usually helpful for more accurate formula assignment, especially for positive mode where [M+Na]+, [M+NH4]+, [M+H]+, [M+K]+ as well as H2O neutral loss are common adduct forms and usually can ionize some compounds that not easily being ionized in negative mode, e.g. the structure of the proposed C19 SOZs is likely observed in pos mode (but very hard to identify since other possible structures cannot be excluded). However, the study focuses on negative mode, and it would be better to have pos mode results in these EICs.
I think the authors need to spend a bit of efforts to re-analyze their entire data to make the results and interpretation as accurate as possible.
(8) For writing, the authors should spend some efforts to improve the writing and results interpretation of the entire manuscript, especially these text in results and discussion are not in good quality and some logics behind the interpretation are not clear.
Other comments:
Line 81-85: when refereeing CxHyOz, it is typically using MW= xxx rather than m/z of the same MW. If you are refereeing accurate m/z, it must be defined an adduct form. If you are referring one of the isomers of same formula, then RT must also include.
Line 162: Such long filter sampling of 28h is expected cause some evaporation of SOA, and not sure this is the same filter for FIGAERO CIMS? If not the same filter, then might have further concern with the comparability between LC-MS and FIGAERO CIMS
Line 166-175: after the filter extraction with methanol, do these extracts injected into LCMS immediately? Methanol extraction is known to creates artifact, e.g. usually leading methyl ester formation
Line 191-192: I do not understand why these conditions necessarily to be optimized by pinic acid, as these are quite normal HPLC setting
Line 214-221: I never used GECKO-A box model but I assume it is not designed to verify expt data, but rather, expt data should be the used to evaluate the performance and reliability of such mechanism box model. My understanding is that GECKO-A box model is only used help to interpret the MS data
Line 230-233 This part is vague. I cannot find higher intensity in dimer regions than monomer regions from LC-MS and FIGAERO CIMS.
Line 277: “We chose only the 50% most abundant OOMs in the present study”. This 50% is sorted by which measurements? This is also making me confused as in line 254-255 “These compounds were selected by considering the reproducibility of their desorption thermograms”. Are these same?
In Fig. 1, LC-MS has many isomers and is the m/z peak area referring sum of multiple isomers? Fig. 1 caption, c and d are from FIGAERO-CIMS, not e and f. Fig.1(g) should be LC-Orbitrap data, am I right?
Citation: https://doi.org/10.5194/egusphere-2024-2454-RC2
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