This manuscript presents mass spectrometric analyses of carbonaceous aerosol in long-range transported smoke from Siberian wildfires. The analysis is based on off-line analysis of filter samples collected at two sites in Northwest Siberia: Nadym city and Bely island, which lies 800 km further north. In August 2021, both sites were impacted by smoke transported from wildfires covering large areas in Yakutia, approx. 2000 km east.

Chemical analysis of the organic aerosol is comprehensive, with three different mass spectrometric methods applied to the samples. Furthermore, multiwavelength light absorption is included in the analysis. On the other hand, there are no supporting measurements such as trace gases (e.g. CO NOx) to augment the analysis. Also, the Hysplit back-trajectories accumulate rather large uncertainty for such long distance as covered here.

Overall, this manuscript offers a relatively rare picture of carbonaceous aerosol from Siberian wildfire emissions and I recommend it for publication after some minor comments have been addressed.

Minor comments

I do not think it is correct to refer to the smoke from the remote fires as one plume. Especially, interpreting the differences between the two sites through dilution / plume edge effects only seems oversimplification. Given that the sites are 800 km apart and wildfires were occurring over an area of several hundred km across it is quite possible that there were differences in the emissions as well as in the processing during the transport.

Based on Fig. 1, there is extensive gas and oil field flaring between Nadym and the wildfire area, but less so for Bely island. Here, more detailed air mass history analysis with higher resolution meteorological data (e.g. Flexpart with ERA5) would have helped to show if smoke observed at both sites had similar exposure to gas flaring emissions. Also, NOx from a trace gas analyser, had it been available, would have been useful. For instance, Table 1 shows that Nadym had higher CHNO fraction than Bely island. Is this due to higher NOx from the flaring, or due to different chemistry in a more concentrated plume?

Specific comments

P1, L37-38 “Owing to lower aerosol concentration in the plume periphery than in its center, it is demonstrated how dilution affects the chemical plume composition during atmospheric aging.” The sites are 800 km apart. As commented above, changes in the emission or effect of additional NOx from gas flaring have not been ruled out.

P3, L20-21 “the phenomenon of dry thunderstorms, which have been estimated to account for more than a half of the fire causes.” Please provide reference.

P3, L30-31 “differences in atmospheric aging of plume center and plume periphery.” Please see previous comments on other possible causes for the differences between the sites.

P4, L36 Please explain in more detail what the different OC and EC components (Table S1) from IPMROVE_A protocol represent and what are the assumptions and uncertainties related to determination of e.g. OCpyro.

P6, L4 “HYSPYT” do you mean HYSPLIT?

P6, L22-24 “The OMPS Aerosol Index (Fig. S2) suggests that the periphery (lower OMPS Aerosol Index, yellow) of the Yakutian wildfire plume was transported to Bely Island in contrast to the plume center aerosol transported to Nadym (higher OMPS Aerosol Index, red).” Please give numerical values for the aerosol index. Please also change Fig. S2 so that the colorbar is legible.

P6, L24-27 “This may have led to a gradient in photochemical processing of the plume, i.e., a lower extent of atmospheric processing by OH radicals, with the northern section containing more atmospherically aged aerosol and the southern section more fresh wildfire emissions, which were picked up on the way westward.” Previously, the effect of decreased OH concentration has been shown for fresh plumes (age some hours) only. In this case, is the difference in actinic flux large enough to have an effect after maybe a week or more of atmospheric ageing?

P7, L12-15 “Regarding biomass burning, spectral absorption obtained throughout the near-ultraviolet to near-infrared spectral region and high Angstrom absorption exponents (AAE) up to 4.4 are were found for smoke from smoldering combustion of pine debris in the wavelength regions from 370 to 670 nm.” Please provide reference.

P7, L37 Elevated NOx may increase BrC formation during atmospheric ageing. Thus, if there are differences in the gas flaring or other NOx mixing into the plume, that could explain part of the difference. Thus, it is not self-evident that the difference in AAE is due to photobleaching only.

P8, L25 “time period (21-07-31 to 07-08-21)” Please check date.

P9, L4-5 “The majority of compounds is found in the low to ultra-low volatility area, but there is a difference when comparing individual compounds classes.” Please discuss the uncertainty in the volatility parameterisation.

P9, L35-36 “This has been assigned to HU-HOM, which are produced from the photooxidation of larger PAHs on soot particles, thus indicating heterogeneous processing of wildfire aerosol particles.” Please provide reference.

P12, L36 – P13, L40 Please consider splitting the long paragraph into shorter ones.

P13, L16-21 “According to RETprim/RETtot close to zero, samples N01–N02 (06 August 2021) contain biomass burning aerosol e.g. originating from fires at smoldering condition (Fig. S6). From 07 August 2021 to the morning of 08 August 2021 (N03–N07), the fires became more intense and turned over to more flaming conditions, suggested by increased OC and EC concentrations, lower ratios OC-to-EC being typical for higher combustion efficiency, and RETprim/RETtot between 0.15 and 0.26; on these days, the main plume by means of highest aerosol concentrations arrived Nadym city.” Did you observe any difference in the mass spectra that could be explained by the apparent differences in the combustion characteristics? For instance, Sekimoto et al. (2018, 2023) found distinct VOC profiles for the high and low temperature combustion.

P15, L29-30 “Also, AAE values are decreased, indicating degradation of chromophores by photobleaching (Liu et al., 2021).” Or then secondary BrC was not formed, due to e.g. lower NOx.

P18, L8-11 “Moreover, AAE405/808 from 1.5 to 3.3 suggested the presence of BrC in Nadym city, but the weekly average of AAE405/808 over a similar period at Bely Island accounted for 1-1.2, indicating more intense atmospheric aging and degradation of BrC chromophores from the same wildfire plume.” Please see previous comment.

References

Sekimoto, K., Koss, A. R., Gilman, J. B., Selimovic, V., Coggon, M. M., Zarzana, K. J., Yuan, B., Lerner, B. M., Brown, S. S., Warneke, C., Yokelson, R. J., Roberts, J. M., and de Gouw, J.: High- and low-temperature pyrolysis profiles describe volatile organic compound emissions from western US wildfire fuels, Atmospheric Chemistry and Physics, 18, 9263–9281, https://doi.org/10.5194/acp-18-9263-2018, 2018.

Sekimoto, K., Coggon, M. M., Gkatzelis, G. I., Stockwell, C. E., Peischl, J., Soja, A. J., and Warneke, C.: Fuel-Type Independent Parameterization of Volatile Organic Compound Emissions from Western US Wildfires, Environ. Sci. Technol., 57, 13193–13204, https://doi.org/10.1021/acs.est.3c00537, 2023.

Schneider et al. present a detailed assessment of carbonaceous aerosol in Siberia, commenting on topics such molecular-level characterization, plume aging, trajectory analysis, and optical properties. Their multimodal approach used allows for a broad range of molecular coverage, and the findings are well-supported by visuals throughout. While the investigation is well-written overall, I have several concerns detailed below that I believe should be addressed prior to publication.

Comments:

• Title: I don’t believe that the title of the paper is suitable, as ‘comprehensive’ and ‘unprecedented’ are both somewhat misleading. To this point, ‘comprehensive’ implies a complete characterization of the carbonaceous aerosol. And while the data interpretation herein is indeed detailed, it is largely limited to MS1 observations (i.e., lack of isomeric and structural resolution), and therefore should not be referred to as comprehensive. Use of the word ‘unprecedented’ is described in a later comment.
• Page 2 Lines 19 – 20: the authors cite a lack of studies on Siberia as motivation and provide a single 2007 reference. However, it appears that there has been more recent work characterizing similar types of samples, and should be cited accordingly (e.g., https://acp.copernicus.org/articles/23/2747/2023/; https://www.sciencedirect.com/science/article/pii/S1352231021000595; https://www.mdpi.com/2072-4292/14/19/4980)
• Page 2 Lines 33 – 37: Some more precise langue should be used here.
• Page 3 Line 5: Instead of using the word ‘different’, please briefly describe what exactly is different to better contextualize this statement for the reader.
• Page 3 Line 34: How high off the ground was sampling conducted? Were there any measures taken to minimize potential contribution from dust and/or ground soil particles?
• Page 4 Line 11: Expanding on the previous comment, it is imperative that the authors conduct HYSPLIT back trajectories ending with an altitude that correspond to the sample collection height. While it is great to understand the evolution of the plume at an altitude of 500m AGL, it becomes challenging to link these observations with samples that were (presumably) collected at ground level. As such, additional trajectories need to be simulated to better represent the actual sample that was collected (e.g., 10m AGL), especially since many of the authors conclusions/interpretations rely on the description of long-range transport.
• Page 6 Line 4: HYSPLIT typo
• Page 6 Line 6: The use of language such as ‘unprecedented’ should not be done lightly. If such a qualifier is to be used, then the authors should provide some context for why this plume is indeed unprecedented. My overall recommendation would be to soften this though, as there are plenty of other examples of extreme smoke events worldwide (e.g., 2023 Canadian wildfires that blanketed significant portions of USA and Canada in smoke).
• Page 6 Line 14-17: Instead of using qualitative words such as ‘almost’ and phrases like ‘clean artic air’, I recommend that the authors improve the precision in this observation my using an actual metric, such as PM2.5, to support these statements more concretely.
• Page 6 line 30 – 35: this language is much more clear, but a somewhat repetitive version nonetheless of what was stated on Page 6 lines 14 – 17. I recommend merging this information for a more concise story.
• Page 7 Line 18: The authors use sample identifies in the text (e.g., NO1), but dates in the figures. Please pick a consistent way to refer to sample to ensure easier comparison/interpretation between text and figures.
• Page 7 Line 20: Where is this data? If it is going to be presented and discussed, it needs to at least be shown in the SI.
• Page 8 Line 6 – 9: Now I have better context for the term ‘unprecedented.’ I would still recommend against its use overall though for reasons highlighted before. Again, an increase in concentrations by factors of ~10 is high, but likely not unprecedented given other worldwide wildfire aerosol observations.
• Figure 3: A few of these mass spectra, particularly those for CHNO and CHO detected by APPI, CHNO detected by ESI- and CHO detected by ESI+ look as if they might be contaminated in the ~m/z 500 – 800 range. Are these major peaks that otherwise don’t fit with the gaussian-like distribution separated by 44 Da? If so, there might be a significant PEG contamination issue. If yes, this is particularly concerning as PEG does not contain nitrogen – the authors peak assignments should be carefully inspected again. If these ‘outliers’ are instead fatty acids (high H/C, low O/C), the authors should consider manually removing them (while still describing it in the SI) as there is a strong likelihood that these are contaminant related, and not due to the sample. Further general info may be found here: https://beta-static.fishersci.ca/content/dam/fishersci/en_US/documents/programs/scientific/brochures-and-catalogs/posters/fisher-chemical-poster.pdf . This issue is perhaps further compounded/realized in Figure S5, most notably in the top center and top right panels. Biomass burning samples are generally expected to exist as a continuum of species (e.g., https://pubs.acs.org/doi/full/10.1021/acsearthspacechem.1c00141), and therefore, the large ‘gaps’ in data here suggest that further data critiquing/cleaning is needed to ensure that all shown peaks are truly representative of the sample.
• Figure 3-4: The authors show prominent entries for CHNOS peaks in Fig 4, but they are not shown in Figure 3. If the authors observed CHNOS, then a Figure 3-like representation of them should at least be added to the SI.
• Page 8 Line 35: while I understand that terms like ‘lipid region’ have been used historically to evaluate VK diagrams, it does not feel appropriate given the nature of the sample (i.e., it is not relevant to the sample or research questions to refer to detected compounds as ‘lipids’ or even ‘lipid like’). While I defer to the authors, my preference would be to avoid using such classifiers that aren’t particularly relevant to the sample at hand.
• Page 8 Line 39: While true, this statement in and of itself is not novel. To be fair, the authors aren’t saying it is novel either. Nevertheless, consider adding some references (such as https://pubs.acs.org/doi/full/10.1021/acsearthspacechem.1c00141, the same as referenced above) which have similarly shown the utility of a multi-modal assessment of wildfire particles.
• Page 9 Line 9-10: The authors should clarify that by ‘the highest abundant compound class,’ they are referring to the class with the most assignments. Although it is likely that the CHO class also has the highest actual abundance, it cannot be definitively stated using uncalibrated MS data.
• Page 9 Line 16: Point the reader to a particular figure.
• Page 9 Line 17-18: If a reference to ‘the literature’ is made, then it should be supported with appropriate references.
• Page 10 Line 21: What is meant by ‘most frequently detected’? Surely CHO compounds were detected in every sample too, so it isn’t clear what this statement implies.
• Section 3.3.4.: If the potential contamination concerns outlined in a previous comment are true, then the authors should very carefully consider whether the peaks discussed in this section are truly endogenous to the sample, or perhaps an additional contamination artifact.
• Page 12 Lines 11 – 22: Direct the reader to Figure 6 at some point here.
• Page 13 Lines 14 – 16: While the correlations shown in Figure 6 appear to indeed show a trend, I caution against using this data in the current tone. Again, the authors do indeed seem to show a trend. But given that uncalibrated MS data is inherently not quantitative, that there is likely isomer effects, etc., multiple additional caveats needed to be stated before this data can be shown. The authors state in the SI that ‘As REMPI is conducted under vacuum conditions, the intensity of an analyte is linearly proportional to its concentration in contrast to direct injection of samples and ionization under atmospheric pressure conditions, such as ESI or APPI.’ This is not entirely true in its current wording, as MALDI and LDI (both vacuum based techniques) are well known to exhibit matrix effects. In summary: while the authors present the data interpretation in a way that may be appropriate to the study at hand, the implications should be clarified to better include caveats and need for calibration.
• Page 14 Lines 22 – 23: This statement (the link to proteins) needs to be referenced.
• SI: The choice of a 1-1 methanol:dichloromethane mixture is interesting on the basis of comparison to other wildfire studies. The authors should comment in the manuscript that their chosen solvent conditions are more likely to bias the extraction to non-polar constituents. Can the authors also comment on their ESI spray stability after using such a high concentration of DCM?
• SI: were radicals allowed for in the APPI assignments?
• SI: Were blank mass spectra recorded? If so, how were they accounted for in data processing?