This manuscript describes the properties of soot generated by a mini inverted soot generator in terms of optical and physical properties, such as particle size, EC/TC mass fraction and absorption coefficient. The soot particles were generated by combustion of propane and ethylene.

The paper is written in clear language and is technically sound. However, there have already been several papers published that characterize the MISG soot properties under various operating conditions (both with ethylene and propane combustion), and which are cited in this manuscript. The results of this paper are largely consistent with these prior papers (which is good), but the novelty of the results presented in this paper is not clear. No attempt was made to further develop the MISG or the atmospheric simulation chamber. Moreover, the link to atmospheric sciences is missing (for instance, an intercomparison of aerosol measurement instruments using MISG soot as test aerosol, validation of new measurement techniques or data analysis procedures etc.). In this sense, I believe that this manuscript does not fit so well into the scope of AMT.

I would suggest to streamline the discussion on the soot characterisation (some of the results can be shifted to Supplemental Information) and add new results related to atmospheric sciences (e.g. interactions of soot with gaseous pollutants and bio-aerosols as suggested in Section 4 "Conclusions"). This would enhance the novelty of the paper. Another option would be to submit the manuscript to another journal, which is focused more on laboratory instrumentation.

Technical comments:

Line 46: The authors state that "The Inverted-Flame Burner (Stipe et al. 2005) is often considered as an ideal soot source (Moallemi et al., 2019 and references therein), due to its capacity to generate almost pure-EC particles and for the stability of the flame and of its exhaust (Stipe et al. 2005). To such category belongs the Mini-Inverted Soot Generator (MISG) used in this work". I find this sentence somewhat misleading. The MISG is known to suffer from poor day-to-day reproducubility for particle sizes below 150 nm (Moallemi et al.). This might be the reason why in the current manuscript the authors only generated soot with mode diameters larger than 170 nm (Figure 4). Considering that most engines emit ultrafine soot particles (with GMDmob from about 20 nm for aircraft engines up to about 90 nm for diesel vehicles), it is not clear to me how the MISG can generate realistic soot size distributions. Particles with mobility diameter <100 nm could potentially be size selected, e.g. with a DMA, but this was not investigated in this study. Moreover, it is not clear whether the number concentration of the size-selected particles (after being diluted in the chamber) would be sufficiently high for most type of experiments.

Review of 10.5194/amt-2021-345, Characterization of the MISG soot generator with an atmospheric simulation chamber, by Vernocchi et al.

The authors characterized an Argonaut MISG (Model MISG-2) using measurements of size distribution, elemental carbon, and light absorption. These measurements are thoroughly described. Measurements were repeated for a number of fuel/air flows using ethylene and propane, and also with/without a cyclone to remove large particles. Size distributions were measured using mobility measurements (SMPS; up to about 800nm) and an optical particle sizer (OPS; up to about 8 um). The results are presented clearly and the authors have observed an important supermicron soot mode that has not been reported by the 3 previously published literature studies on the MISG-2, which is by itself a strong reason for publication. 

The title and abstract should be modified to emphasize that conclusion, but at the same time the abstract must also mention that this study uses different fuel flow rates than earlier studies. A new title might be "Characterization of supermicron and submicron soot produced by a miniature-inverted soot generator". (Current title uses an acronym with 2 words which are part of the acronym.)

I have a few major comments which should be addressed before publication.

Major comments

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The observation of supermicron soot would suggest that future studies should never use ethylene fuel in the MISG (and perhaps also other inverted burners) as a surrogate for atmospheric soot. This is an important conclusion, and although an earlier study using ethylene in the MISG (Kazemimanesh et al., 2019) noted the supermicron soot, its importance was not emphasized. That study also used a different flow rate. Given this emphasis I would like to request one additional experiment is made before publication. The authors should directly test their hypothesis that "super-aggregates...are likely formed directly in the exhaust line where particles density is very high" (lines 498-499). If this is the case, then could the issue be solved simply by diluting immediately after the MISG? The experiment would be simple. The authors need only to run the MISG with 3 line lengths. Very short, normal (as used previously), and very long. For each line length, measure with the OPS and SMPS.  The results should be reported as combined OPS-SMPS size distributions in mass and number weighting.

Second, and continuing from above, a discussion of the physical properties of the supermicron aggregates is missing. For example, if super-aggregates are formed in the exhaust lines, then they should have the same MAC as the particles they are formed from. If they do not, then they must have a different morphology. Chakrabarty et al. (https://doi.org/10.1038/srep05508, 2014, Fig S3) predict a similar MAC for supermicron aggregates as for smaller aggregates. So, the authors might be observing aggregates that are more compacted than expected. This is supported by the trends in Figures 9 and 10. The authors should discuss their data with reference to this and other literature on superaggregates.

Third, I would also request that the authors try harder to reproduce exactly the conditions used in previous studies. As it is, the authors have used higher fuel flow rates (equivalence ratios) than all previous studies (Kazemimanesh et al., 2019; Moallemi et al, 2019; Bischof et al., 2019). It is unclear to me why the authors have not reproduced previous measurements exactly, to allow for comparable results. Is it because the authors used long line lengths and changed the pressure downstream of the flame? Is it because the authors used an "MISG-2" and not an "MISG-1"?  Also, as mentioned above, the abstract should emphasize this difference in flow rate.

Fourth, the authors should present SSA from the PAX instrument, to allow for a direct comparison of their measurements with the SSA reported by Moallemi et al. On line 386 the authors write "the comparison with previous literature (Moallemi et al., 2019) ... reported the Single Scattering Albedo instead of the absorption coefficient". The authors cannot change how Moallemi et al. presented their data, but they can match their presentation to Moallemi et al's. The authors have SSA data and should present it. 

Minor comments

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The absorption coefficient divided by the number concentration is the absorption cross section. Please use this definition in Figure 11.

What exactly is the difference between the MISG-1 and the MISG-2? Previous MISG characterization studies used the MISG-1.

Please specify the line length used between MISG and chamber. Obviously, this is important (see first major comment above). Please also specify the exhaust line length and i.d. (ideally pressure in the line would be reported, if that is not available then reporting these parameters will help).

Table 4. The dark red and dark purple look the same in a black-and-white printout. Use e.g. a lighter red.

The authors first mention Bischof et al. (2019) at line 292. The paper should be mentioned in the introduction; it is a characterization of the same MISG.

Line 79, the air flow is not internally split between combustion and carriage. This makes it sound like there are 2 divided flows. In fact there is one air flow, and some of the air is consumed for combustion.

Line 93, consider writing m^3 air / m^3 fuel (the unit m3/m3 is confusing.)

Line 104, Moore et al. demonstrated the relationship of stoichiometry with particle size for the miniCAST only. The miniCAST is unique from the MISG, because it is a quenched flame. The quenching height is fixed. In the MISG, the open tip can move up and down with fuel flow. Use a difference reference, or change the statement.

Line 248. This is repeatability, not reproducibility.

Line 248, is the repeatability measured day-to-day? Between scans?

Figure 3. Missing error bars.  Same for similar figures.

Figure 4 and line 292. The discussion of size vs. stoichiometry compares this work with prior work which was not performed at the same fuel flow rates. The comparison is not fair. It is more reasonable to conclude that the relationship changes at high fuel flow rates (if all data were plotted together, a trend might be observed). The authors need to reproduce earlier measurements to confirm their discussion, or change the discussion.

Line 307-316. The discussion compares "2 um" particles with "4 um" particles but the units are not the same. The 2 um was measured by TEM maximum dimension (or projected area?) and the 4 um was measured optically. Was the optical size corrected for the refractive index and shape of the particles? Please specify "projected diameter in an electron microscope" and "optical equivalent diameter". And please describe the calibration of the TSI OPS 3330 in Methods.

Figure 6. At what MISG flow rates were these data taken?

Figure 7 and 8. Why not use units on the y axis if units are reported in the text? Please change to units. If the authors argue against units, then specify the maximum in the caption.

Figure 9 and 10. Please combine into Panel A and B of the same figure, to avoid repeating a long caption twice. The important point is that one used a cyclone.

Figure 9 and 10. Please change from "Relative EC concentration" to "EC:TC ratio" to make it clear what the EC is 'relative' to. The discussion mentions OC:EC as well, which is confusing. Please always use EC:TC and OC:TC.

Line 366-373. Blank and backing filters should be mentioned in Methods so that the reader is not surprised at the discussion here. The authors should also mention that about 1000 ug/m3 EC was collected on the filters, which means that gas-phase VOCs become less important. Anyway, is the discussion of OC correction relevant if only EC concentrations are reported? Isn't "PC" more relevant, since that is where biases can come in? (In other words, how difficult was it to determine the split point?)

Figure 11. The authors normalized b_abs to N_SMPS. But in Figure 6 the authors showed that N_OPS was important. Why did the authors ignore the particles that the OPS couldn't see? Was a cyclone used? Clarify the text and figure please.

Table 6. Was the AAE calculated using a power-law fit? A fit to 3 points would not be reliable. I recommend reporting 2-wavelength calculations of the AAE, for blue-green and green-IR, (and optionally also blue-IR) which also allows the reader to observe the consistency between the individual PAX instruments.

Figure 12-14. Consider using open/closed symbols to enhance readability in black-and-white printouts.

OVERVIEW

The present manuscript aims to characterize soot particles produced with a MISG. Overall the manuscript needs some rewriting and rethinking. Many sections appear to be a list of results which are scarcely interpreted, while many figures are barely described. Hence, some important results are shaded by many non-relevant information and figures. As final results, the conclusions and overall take-home message of the manuscript becomes extremely unclear. As mentioned in the second review, the authors show for the first time that MISG can produce large soot aggregates, which are not well characterized in other previous studies and cannot be generated, up to my knowledge, with the more traditional CASTburner. So, I suggest the authors to focus on this specific aspect of their research. Considering the presence of these large particles, PAX measurements must be corrected for truncation error. In its current form, the manuscript is not suitable for publication.

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SPECIFIC COMMENTS

ABSTRACT: The abstract is very generic and does not provide any real information on the performances of the burner. I suggest rewriting of the abstract.

INTROUDUCTION: Introduction does not provide a context and does not present the motivation for this study. At the moment is a list of references without a clear story behind it. It does need some rewriting.

L27-34: the definition of “BC” is mostly based on its non-null imaginary part of the refractive index. However, Petzold 2013 made it clear that the term BC is a qualitative definition of BC rather than operational. From your text I have the impression that absorption photometers will directly provide BC concentration. I think that, however, a discussion on soot nomenclature is not needed so early.

L43-50: This part needs to be developed further since it will create the right context for your work.

L51-63: This part provides some sparse technical details of burner and a very generic description of smog chambers. It is not clear what the author wants to communicate here.

L74: reference

L77-80: what are the consequences of the absence of quenching or carrier gas?

L84: give number to equation. Recurrent

L85-91: this occupy more space than needed. Put it as normal text. Recurrent

155-156: revise indent.

L166: size distribution measurements

L181-182: what refractive index was used to derive diameter from OPS?

L196-197: Considering the extensive use of PAX measurements in the paper I am genuinely surprised that truncation errors are disregarded.  I think it is important to show that truncation is not relevant in these conditions. As recently resumed by Modini et al. (2021) little is known on the dependency of scattering phase function on the particle morphology and how this might impact truncation for highly absorbing aerosol particles. Scattering correction for absorbing aerosol is investigated for the nephelometer instrument by Bond et al., 2009. The argument of the authors is valid, but it should be contextualized if not verified.

L246-251: If I understand correctly this is simply the relative standard deviation. It is not clear, however, in what conditions these values were calculated.

L301-302: does it mean that all size distribution are measured 3 minutes after injection. The ageing time in the chamber should be always specified, since concentration and dimeter of particles drastically change due to coagulation, especially at high concentrations.

L340-372: Describing both EC:TC and OC:EC is redundant. It is also hard to compare and understand the impact of large soot on the OC:EC fraction from the two figures. I would suggest to merge them or focus on the impact of large soot. To be honest, figure 9 could easily go in the supplementary. Is there any correlation between OC:EC and diameter mode, CO2, NO ?

Section 3.2.4 -3.2.5: These sections could be merged. Especially considering the length of Section 3.2.4. Figure 11 is barely described or discussed in the text. Hence, it can be moved to supplementary or removed.

L412-417: This part is very hard to read and follow. The authors are requested to build a discussion on their result, rather than list numbers in series. This problem appears in almost every section of the paper. As a consequence, Figure 12-13-14 become hard to interpret too. I would suggest move the figures to supplementary, summarise the result in a table and construct a separate discussion for ethylene and propane.

Figure 15: since you do not correct for truncation error, this comparison between PAX and MWAA is highly questionable, especially for the experiments without cyclone.

Review of “Characterization of the MISG soot generator with an atmospheric simulation chamber”

General comments:

This paper discusses the physical, chemical, and optical properties of soot produced by burning propane and ethylene in a miniature inverted soot generator (MISG). Although some aspects of this work (such as flame shape vs. fuel and air flows) have been discussed in previous studies, there are some novel aspects to the paper: combining the MISG with an atmospheric simulation chamber and studying the optical properties of soot in depth. The methodology used in the paper is sound and valid but the paper itself is cluttered and poor in terms of readability. I suggest that the authors streamline the paper by omitting the discussion on flame shape with combustion conditions or moving it to the supplementary material, and instead focus on aspects that have not been covered in similar other studies. The whole manuscript should be edited for grammar and proper academic writing too. There are also some discrepancies between the results presented in this paper and previous papers that characterized the MISG soot, which need to be discussed in more details by the authors (see my comments below). Overall, the paper is not acceptable in its current form and needs major revisions before it can be published.

Specific comments:

Article title: Avoid using an acronym in the title without fully defining it first.

Abstract should be written as one paragraph.

Abstract: MAC stands for mass absorption cross-section, not mass absorption coefficient.

Section 1: Combine paragraphs 2 and 3.

Line 45: List the “several other purposes” in those references more specifically.

Section 1: The introduction is written poorly and needs to be improved in terms of readability and transition between paragraphs. It should also clearly state the objective(s) and novelty of the study near the end of the introduction.

Line 69: Change “air and fuel flow in an opposite way to the buoyancy force” to “… in opposite direction to the …”

Line 70: Change to “The resulting diffusion flame is more stable by reduced flickering of flame tip”

Line 77: lpm and mlpm should be defined (it is better to use L/min or mL/min as units of flow rate).

Line 79: This statement is not correct. Kazemimanesh et al. (2019) states that part of the air flow is used in combustion and the rest is used to dilute the exhaust products.

Lines 81-101: The definition of equivalence ratio is based on fuel-to-air ratio, thus the reader would not be confused if you define the fuel-to-air ratio (instead of AFR) first. Also, all equations should be numbered.

Line 93: The units used for AFR are not clear to me. AFR is a unitless parameter, so just get rid of any units.

Line 103: Many of the in-text citations in this article should be in format of Author (Date). Please consider this whenever suitable during revision. For example: Moore et al. (2014) demonstrated that fuel-lean flames produce soot particles …

Line 144: Consider changing to “at the fuel tube nozzle”

Line 125: I cannot find Section 2.1.2 in the paper.

Line 179: It is known that the multiple charge correction algorithm in the TSI AIM software breaks when the median mobility diameter is relatively large (>200 nm). Can the authors show the uncorrected and corrected size distributions for 2-3 cases in the supplementary material?

Line 218: Change peculiar to a better adjective.

Line 236: “To our knowledge, no 237 literature information is available for the ethylene in the flow range of Table 4.” This statement is not true. Kazemimanesh et al. (2019) studied the MISG and its flame shape with ethylene and air flow rates (80-130 mL/min and 4.0-10.0 L/min, respectively) that partly cover Table 4.

Lines 241-251: The authors talk about various experiments that they did and the calculated repeatability (mistakenly noted as “reproducibility”) in mode diameter and concentration. However, it is not clear what conditions were tested and the results are not shown in the paper or the supplementary material.

Page 10 – Fig. 4 and the discussion around it: The particle mode diameter reported for ethylene flames is constant at ~175 nm. This is inconsistent with previously reported values of ~240 nm and up to 270 nm (Kazemimanesh et al., 2019). The same reference also reported an initial sharp increase in particle size and concentration with increasing ethylene flow rate, which eventually levelled off to a relatively constant value. This is in contrast to the trend seen in this paper. These differences must be noted and discussed in the paper.

Fig. 3 and 4: The authors should consider adding error bars to the data points. In addition, it is not clear why a linear fit is shown for the data points when the paper does not offer any evidence or support for trend.

Fig. 5: I suggest that the authors show and discuss figure 5 before figures 3 and 4, as this will enhance the readability and flow of the paper. I was completely lost about the results shown in figures 3 and 4 when I first read the paper until I saw figure 5. Figures 3 and 4 are essentially the size distribution parameters extracted from figure 5 and shown with respect to equivalence ratio.

Lines 307-316: Can you show the number and volume distributions side by side in Fig. 6? What is meant by “relative particle number concentration” in Fig. 6? [dN/dlog dp]/N_tot?

Section 3.2.3 (EC-OC analysis): The authors did not elaborate how they calculated TC (total carbon). OC can exist in gas-phase or as condensed semi-volatile particles and the authors need to distinguish between the two when calculating TC. The authors briefly mention the use of a second filter, which should help in determining the mass concentration of OC existing as semi-volatile particles.

Fig. 9 and 10: I do not quite understand why normalized EC concentrations are shown rather than the absolute values of EC concentration or the EC/TC ratio. The latter two parameters are more important for researchers when using a soot generator.

Line 384-385: Why is propane soot more light absorbing than ethylene soot at all three wavelengths?

Line 498: The formation of superaggregates is related to high particle concentration in the exhaust line. This means that by diluting the MISG exhaust, the formation of these large aggregates can be alleviated. Kazemimanesh et al. (2019) and Chakrabarty et al. (2012) suggest that these superaggregates are formed at the stagnation plane of the flame tip, which seems more plausible. The authors should note and discuss these differences in the paper (not in the conclusions section).