Rate coefficients for the reactions of OH radical with C3-C11 alkanes determined by the relative rate technique

Xin, Yanyan; Lun, Xiaoxiu; Xie, Shuyang; Liu, Junfeng; Liu, Chengtang; Mu, Yujing

doi:https://doi.org/10.5194/egusphere-2023-2802

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https://doi.org/10.5194/egusphere-2023-2802

Preprints

05 Dec 2023

| 05 Dec 2023

Rate coefficients for the reactions of OH radical with C3-C11 alkanes determined by the relative rate technique

Yanyan Xin, Xiaoxiu Lun, Shuyang Xie, Junfeng Liu, Chengtang Liu, and Yujing Mu

Abstract. Rate coefficients for the reactions of OH radicals with C3-C11 alkanes were determined using the multivariate relative rate technique in various bath gases (N₂, Air, O₂). A total of 25 relative rate coefficients at room temperature and 24 Arrhenius expressions in the temperature range of 273–323 K were obtained. Notably, a new room temperature relative rate constant for 3-methylheptane that had not been previously reported were determined, and the obtained K_OH values (in units of 10^-12 cm³·molecule^-1·s^-1) in different bath gases were N₂, 7.90±0.25; Air, 7.93±0.33; and O₂, 7.36±0.11. Interestingly, whilst results for n-alkanes agreed well with available structure activity relationship (SAR) calculations, the three cyclo-alkanes and two trimethylpentane were found to be less reactive than predicted by SAR. Conversely, the SAR estimate for 2,3-dimethylbutane were approximately 22 % lower than the experimental value, highlighting that the limited understanding of the oxidation chemistry of these compounds. Arrhenius expressions (in units of cm³·molecule^-1·s^-1) for the reactions of various cyclo- and branched alkanes with OH were determined for the first time: methylcyclopentane, (1.62±0.14)×10^-11exp [-(256±25)/T]; 2-methylhexane, (1.22±0.04)×10^-11exp [-(206±9)/T]; 3-methylhexane, (2.27±0.31)×10^-11exp [-(559±42)/T; 2-methylheptane, (1.62±0.37)×10^-11exp [-(265±70)/T, and 3-methylheptane, (3.54±0.45)×10^-11exp [-(374±49)/T]. In addition, the rate coefficients for the 24 previous studied OH + alkanes reactions in different bath gases were consistent with existing literature values, demonstrating the reliability and efficiency of this method for simultaneous investigation of gas-phase reaction kinetics.

Received: 23 Nov 2023 – Discussion started: 05 Dec 2023

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11 Oct 2024

Rate coefficients for the reactions of OH radicals with C₃–C₁₁ alkanes determined by the relative-rate technique

Yanyan Xin, Chengtang Liu, Xiaoxiu Lun, Shuyang Xie, Junfeng Liu, and Yujing Mu

Atmos. Chem. Phys., 24, 11409–11429, https://doi.org/10.5194/acp-24-11409-2024,https://doi.org/10.5194/acp-24-11409-2024, 2024

Short summary

Yanyan Xin, Xiaoxiu Lun, Shuyang Xie, Junfeng Liu, Chengtang Liu, and Yujing Mu

Interactive discussion

Status: closed

RC1:
'Comment on egusphere-2023-2802', Anonymous Referee #1, 22 Dec 2023
Xin and co-workers present a new set of kinetic measurements of the oxidation of a variety of aliphatic hydrocarbons by the OH radical. This work was performed using a temperature controlled reaction chamber in which the kinetics were determined using the relative rate method and the relative decays of hydrocarbon reactants were tracked using a GC-FID instrument. As the authors point out, the oxidation of hydrocarbons is a subject that is relevant to atmospheric chemistry and the publication of new kinetic measurements is of fundamental importance if we are to assess the effects of these reactions upon atmospheric chemistry. Therefore (in principle) I am in favor of the publication of papers such as this in Atmospheric Chemistry and Physics. However, I do have some serious comments to make, and I would insist that the authors address each one of them to the fullest extent, only then would I support publication.
Major comments:
The authors assessment of the kinetics literature is currently incomplete. This is made clear by the fact that they take credit for making the first temperature-dependent measurements in cases where measurements are clearly available, as well as the incomplete literature data presented in Table 2. I would suggest that the authors make use of the database paper of McGillen et al. (2020), and download the accompanying database. This will achieve two things: 1. It will give the authors a more comprehensive knowledge of the kinetics literature for OH + hydrocarbon reactions. 2. It will provide these authors with critically evaluated rate coefficients for many of the species that are contained within their paper. Regarding the latter, I would strongly encourage the authors to use these recommendations as their reference rate constants where applicable and reanalyze their data accordingly, and if not, I would expect the authors to justify why they do not accept these recommendations.

The presentation of the data/ quality of the data is unsatisfactory. When I inspect the contents of Table 1, taking the reference rate constants as provided on page 7 of the manuscript, I am able to reproduce kOH for the first 3 entries (i.e. propane in N2 with n-hexane, cyclohexane and n-octane as references). Following this, the next 3 entries (propane in air) are inconsistent. I noticed that throughout this table there are many problems of this type. In my judgement, this is not acceptable for a paper whose principle subject is kinetic data and it undermines your experimental work. What is the purpose of this data, if your readers cannot trust it? For this reason, I insist that the authors return to their spreadsheets, remake this table correctly and triple check its contents.

The authors insistence on Arrhenius parameters for this selection of reactions in Section 3.3. is unjustified. With all the high-temperature data available for this collection of compounds, it is plainly obvious that the Arrhenius equation is insufficient to describe the temperature dependencies of any of these reactions. The only reason for using such an equation would be for datasets spanning a small temperature range (or where data precision is insufficient). I strongly encourage the authors to consider fitting their data within the context of the available measurements, because I don’t think these new Arrhenius parameters add any value to your paper.

Problems with general consistency. This is an example (but there are several others), Figure 6(a) shows temperature-dependent literature measurements for OH + methylcyclopentane. In the abstract, it states that “… Arrhenius expressions (in units of cm3·molecule-1·s-1) for the reactions of various cyclo- and branched alkanes with OH were determined for the first time: methylcyclopentane…”. I can interpret this in one of two ways: 1. The authors don’t appear to be aware that there is temperature-dependent data, even though they have presented it in their figures. 2. The authors are discounting the work of Sprengnether et al. because it is not presented in Arrhenius form. If the former, then the authors should organize their manuscript more carefully. If the latter, then I find this to be a strange idea (after all, if you don’t like their equation, just re-fit their data with an Arrhenius equation!)…

It is not clear to me why the authors chose to consider the bath-gas as an important aspect of these measurements. The literature has many examples of measurements that were conducted in a wide variety of bath gases (helium, argon, nitrogen, air etc.). As far as I am aware, no dependence on bath gas has been noted. In fact, a small amount of oxygen would be necessary in relative rate experiments such as yours, otherwise alkyl radicals formed from the hydrogen abstraction reaction would themselves abstract hydrogen from other alkanes in the system, re-forming the original alkane, consuming some of the other hydrocarbons and confusing your results. In practice, it is difficult to remove oxygen to such an extent, and I would therefore assume that your experiments are not affected by this anoxic chemistry. Either way, I suggest that bath gas is an irrelevance in this paper and can be ignored.

There are some advantages to studying so many compounds simultaneously, the main one being that it can save you some time. However, there are also some possible problems. The main one would be the formation of products which could interfere with some of your analyte peaks. I see no discussion of any sort regarding products of the reaction. Do you see any product peaks in the GC-FID? If not, why not?

Minor comments:
General: the symbol for rate constant in the kinetics literature is an italicized lower-case k. It is not to be confused with an upper-case K (which is reserved for units of kelvin), or an italicized upper-case K (which is normally reserved for equilibrium constants).
Abstract: revise according to suggestions above.
Introduction:
Line 44. why are you making comparisons with NO3? It is well known that the abstraction reactions are unimportant for the alkanes. Chlorine on the other hand may become important in some environments.
Line 44. “Dehydrogenation” of alkanes leads to alkenes. You mean to say “hydrogen abstraction”.
Line 46. I assume by “rate constants”, the authors mean “room temperature rate constants”. You should specify this.
Line 47. Assuming that the authors have by now become more familiar with the kinetic database, you will of course know that the range of reactivity of alkanes goes from 6.36E-15 (methane) to 2.16E-11 (n-hexadecane) at the time of writing. The range provided is therefore misleading.
Line 47. “mol” is absolutely not an abbreviation of “molecule”. “mol” is an abbreviation of “mole”, which would be highly misleading.
Line 48. Rate constants are not faster or slower than other rate constants. They are larger or smaller.
Line 66. In fact, precise measurements are highly desirable in the relative rate method. Low precision in your GC-FID measurements would lead to scatter in your relative rate plots. Therefore, this statement is misleading.
Methods:
General comment: several tests have been made with respect to dark losses, photolytic losses etc. However, as far as I can tell, no tests were performed regarding storage in the 1 litre sample bags. In your experiments, your samples are stored for some time before they are analysed by the GC-FID are they not? During this time, your samples are subjected to conditions of higher surface area to volume ratios, and it is here, where I would expect to see the most wall loss.
Line 115. Excess with respect to what?
Line 145. “self-developed”.
Line 155. It is not clear to me how you have improved or expanded the work of Shaw et al. Furthermore, it is also not clear to me how the results of this work are significantly different from any other relative rate study in which several reference compounds are considered.
Line 173. There is a certain irony to this statement, because I would strongly recommend that you should use the available expert-evaluated rate constants wherever possible.
Line 193. Was the H2O2 purified?
Lines 211-212. I don’t know what the authors mean by general error is 2 sigma… Do you mean that the uncertainties for SAR estimates are generally within a factor of two? This is possibly true in a global sense, but it is considerably lower for the alkane dataset (the subject of this paper).
Line 238. I don’t know what an “error strip” is. I think the authors mean “error bars”.
Line 238. What is fitting dispersion?
Results:
Figure 3. It would be useful to include literature recommendations for each of these rate constants where available, allowing us to see how well the experiments are performing.
Table 1. As noted above, the errors in this table are unacceptable at present. In addition to this, the formatting of this table is confusing and should be rethought to help the readers understand it better.
Structure-activity relationships section:
You only compare with one SAR (the Atkinson SAR). This is a missed opportunity, there are several others to choose from (some examples include: Neeb, 2000; Jenkin et al., 2018; McGillen et al., 2024). In the case of Neeb, this is of particular relevance because there is some critical discussion on the use of a ring-strain correction factor on page 6 (300) of that study, the authors should consider this in their discussion of SAR performance for cyclic compounds. Incidentally, the recent SAR of McGillen et al. (2024) is not currently configured for cyclic compounds, however, I have assessed its performance on the selection of compounds of this paper. This is very easily done by running the Python code of that paper, from which I find that it performs marginally better than Kwok and Atkinson (1995). This, at least for this limited selection of compounds, supports Neeb’s statements about ring strain corrections. However, it is most likely the case that more data on cyclic alkanes of differing ring size would be very useful in assessing this further.
References:
McGillen et al. (2020) DOI: 10.5194/essd-12-1203-2020
Sprengnether et al. (2009) DOI: 10.1021/jp810412m
Neeb (2000) DOI: 10.1023/A:1006278410328
Jenkin et al. (2018) DOI: 10.5194/acp-18-9297-2018
McGillen et al. (2024) DOI: 10.1039/D3EA00147D
Kwok and Atkinson (1995) DOI: 10.1016/1352-2310(95)00069-B
Citation: https://doi.org/10.5194/egusphere-2023-2802-RC1
- AC2: 'Reply on RC1', Chengtang Liu, 27 Feb 2024
  
  The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2023/egusphere-2023-2802/egusphere-2023-2802-AC2-supplement.pdf
  
  Citation: https://doi.org/10.5194/egusphere-2023-2802-AC2
RC2:
'Comment on egusphere-2023-2802', Anonymous Referee #2, 09 Jan 2024

see attached file

Citation: https://doi.org/10.5194/egusphere-2023-2802-RC2
- AC1: 'Reply on RC2', Chengtang Liu, 27 Feb 2024
  
  The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2023/egusphere-2023-2802/egusphere-2023-2802-AC1-supplement.pdf
  
  Citation: https://doi.org/10.5194/egusphere-2023-2802-AC1
RC3:
'Comment on egusphere-2023-2802', Anonymous Referee #3, 16 Jan 2024
General comments:
The article entitled “Rate coefficients for the reactions of OH radical with C3-C11 alkanes determined by the relative rate technique” by Xin et al., reports a series of rate coefficients measurements for the reactions of 25 alkanes with OH radicals using a relative rate technique. The research employed the GC-FID technique and a simulation chamber to evaluate the rate coefficients values at 25 C and Arrhenius expressions in the 273-323 K temperature range. The authors also explored the structure activity relationship approach to evaluate the OH radical rate coefficients of the alkane series. The main objective of the author’s research was to provide multiple kinetic data studying simultaneously a large number of compounds, but even achieved, however, the lack of higher accuracy, quality and novelty for released rate coefficients do not justify the publication of the article in the present form. An extensive revaluation of the data could help to approach this study from a different perspective and enhance the quality of the results.
Major comments:
The introduction provides a large number of literature data; however, a very chaotic presentation induces to readers the feeling of jumping from one study to another, all of them mostly with very general information regarding the kinetic of alkanes. The studies mentioned in the introduction are presented without an effective detail of the rate coefficient information. I would write the introduction assessing the importance of alkanes for air quality with their impact to atmosphere, then I would add information about their concentrations in troposphere and the impact on potential ozone formation, potential SOA formation and their sources and sinks. One important point of the study is to highlight the importance of accurate kinetic rate coefficients for database, global model atmospheric processes and degradation mechanisms. As one of the reviewers mentioned already, the McGillen et al., (2018) database is very important to be used as a start in the literature data assessment and comparison.

The reason of selected those 25 alkanes is not presented in the study and their selection looks arbitrary. An organized evaluation based on their separation on straight-chain, branching and cyclic alkane structure would be more interesting and helpful to get valuable information. First class of alkanes including linear compounds could provide information regarding reactivity of each CH₂ group added to their structure and how the rate coefficient value would change over increasing alkane chain. Secondly, from the branching alkanes the authors could have more information related to CH groups added to the alkane structure. The third class in the evaluation would be cyclic alkanes where the authors could extract information regarding the reactivity increase with the cycle size from cyclobutane to cyclodecane. The authors should include in their evaluation the alkanes rate coefficients studied in present study and those existing in the literature, to release more complete discussion on their behaviour and reactivity (figure 3 and 4). As an example, there are a lot of data which could be included, mentioning here only a few (k_OH for cyclooctane, bicyclo octane, methyl octane, etc.).

Since the authors highlight their first study on 3-methylheptane why they do not cover other not studied yet branched alkanes (2,2,3-trimethylpentane, etc.)

The data reported in the Table 2 should be reevaluated and presented in more concise and understandable form. There are multiple examples of inconsistency of the data with many average data not well calculated (i.e. isopentane in N2).

With the extensive interpretation of data including the existing literature rate coefficients, the authors would be able to evaluate the accurate reactivity trends for the class of alkane toward OH radicals and calculate new factors for the SAR method and then to improve the SAR method. A simple comparison with the Kwok and Atkinson SAR method is not worth to do. Evaluation of existing SAR approaches in the literature, with discussion about the influence on the substituent factors, is necessary. (McGillen et al., 2024 (doi.org/10.1039/D3EA00147D), Jenkin et al., 2018 (doi.org/10.5194/acp18-9297-2018)

The reaction channel of the OH radical initiated degradation of alkanes is strictly related to hydrogen abstraction in the presence of oxygen. There are clearly correlations on the alkane reactivity with OH radicals and Cl atoms for all saturated class of VOCs. Please evaluate a log-log correlation of k_CL and k_OH as presented by Calvert et al., 2011 (Calvert, J., Mellouki, A., Orlando, J., Pilling, M., and Wallington, T.: Mechanisms of Atmospheric Oxidation of the Oxygenates, Oxford University Press) for alkanes, saturated alcohols and ethers and also by Tovar et al. (2022) (doi.org/10.5194/acp-22-6989-2022) for saturated epoxides.

The importance of the bath-gas is over highlighted in this study and a single example for a selected alkane would be enough to prove that is no bath-gas effect on the rate coefficient value. A revaluation of the paper consistency should be performed.

Please add more information regarding the conditions needed for relative rate techniques. Also include more advantages and disadvantages of the absolute and relative techniques.

The authors should highlight the atmospheric implication and the impact of their research as requested by a scientific journal as “Atmospheric Chemistry and Physics“. Please add information about the alkane lifetime in the atmosphere toward the OH radicals. A more extensive conclusion and atmospheric implication should be performed.

Minor comments:
Both reports of the previous reviewers have included a detailed list of minor comments and only additional comments I would add here:
Line 84: Finlayson-Pitts
Line 127: “at253”
Line 130: please avoid given values in the form of 0.00013 or 0.00048. Change the units to pptv/h.
Line 283 and 285: please add units
Line 460: please revise the rate coefficient
Line 104: The figure of the simulation chamber shows a ratio of 200:50 of N2:O2 mixture. The study used synthetic air or this mixture shown in the figure?
Citation: https://doi.org/10.5194/egusphere-2023-2802-RC3
- AC3: 'Reply on RC3', Chengtang Liu, 27 Feb 2024
  
  The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2023/egusphere-2023-2802/egusphere-2023-2802-AC3-supplement.pdf
  
  Citation: https://doi.org/10.5194/egusphere-2023-2802-AC3

Interactive discussion

Status: closed

RC1:
'Comment on egusphere-2023-2802', Anonymous Referee #1, 22 Dec 2023
Xin and co-workers present a new set of kinetic measurements of the oxidation of a variety of aliphatic hydrocarbons by the OH radical. This work was performed using a temperature controlled reaction chamber in which the kinetics were determined using the relative rate method and the relative decays of hydrocarbon reactants were tracked using a GC-FID instrument. As the authors point out, the oxidation of hydrocarbons is a subject that is relevant to atmospheric chemistry and the publication of new kinetic measurements is of fundamental importance if we are to assess the effects of these reactions upon atmospheric chemistry. Therefore (in principle) I am in favor of the publication of papers such as this in Atmospheric Chemistry and Physics. However, I do have some serious comments to make, and I would insist that the authors address each one of them to the fullest extent, only then would I support publication.
Major comments:
The authors assessment of the kinetics literature is currently incomplete. This is made clear by the fact that they take credit for making the first temperature-dependent measurements in cases where measurements are clearly available, as well as the incomplete literature data presented in Table 2. I would suggest that the authors make use of the database paper of McGillen et al. (2020), and download the accompanying database. This will achieve two things: 1. It will give the authors a more comprehensive knowledge of the kinetics literature for OH + hydrocarbon reactions. 2. It will provide these authors with critically evaluated rate coefficients for many of the species that are contained within their paper. Regarding the latter, I would strongly encourage the authors to use these recommendations as their reference rate constants where applicable and reanalyze their data accordingly, and if not, I would expect the authors to justify why they do not accept these recommendations.

The presentation of the data/ quality of the data is unsatisfactory. When I inspect the contents of Table 1, taking the reference rate constants as provided on page 7 of the manuscript, I am able to reproduce kOH for the first 3 entries (i.e. propane in N2 with n-hexane, cyclohexane and n-octane as references). Following this, the next 3 entries (propane in air) are inconsistent. I noticed that throughout this table there are many problems of this type. In my judgement, this is not acceptable for a paper whose principle subject is kinetic data and it undermines your experimental work. What is the purpose of this data, if your readers cannot trust it? For this reason, I insist that the authors return to their spreadsheets, remake this table correctly and triple check its contents.

The authors insistence on Arrhenius parameters for this selection of reactions in Section 3.3. is unjustified. With all the high-temperature data available for this collection of compounds, it is plainly obvious that the Arrhenius equation is insufficient to describe the temperature dependencies of any of these reactions. The only reason for using such an equation would be for datasets spanning a small temperature range (or where data precision is insufficient). I strongly encourage the authors to consider fitting their data within the context of the available measurements, because I don’t think these new Arrhenius parameters add any value to your paper.

Problems with general consistency. This is an example (but there are several others), Figure 6(a) shows temperature-dependent literature measurements for OH + methylcyclopentane. In the abstract, it states that “… Arrhenius expressions (in units of cm3·molecule-1·s-1) for the reactions of various cyclo- and branched alkanes with OH were determined for the first time: methylcyclopentane…”. I can interpret this in one of two ways: 1. The authors don’t appear to be aware that there is temperature-dependent data, even though they have presented it in their figures. 2. The authors are discounting the work of Sprengnether et al. because it is not presented in Arrhenius form. If the former, then the authors should organize their manuscript more carefully. If the latter, then I find this to be a strange idea (after all, if you don’t like their equation, just re-fit their data with an Arrhenius equation!)…

It is not clear to me why the authors chose to consider the bath-gas as an important aspect of these measurements. The literature has many examples of measurements that were conducted in a wide variety of bath gases (helium, argon, nitrogen, air etc.). As far as I am aware, no dependence on bath gas has been noted. In fact, a small amount of oxygen would be necessary in relative rate experiments such as yours, otherwise alkyl radicals formed from the hydrogen abstraction reaction would themselves abstract hydrogen from other alkanes in the system, re-forming the original alkane, consuming some of the other hydrocarbons and confusing your results. In practice, it is difficult to remove oxygen to such an extent, and I would therefore assume that your experiments are not affected by this anoxic chemistry. Either way, I suggest that bath gas is an irrelevance in this paper and can be ignored.

There are some advantages to studying so many compounds simultaneously, the main one being that it can save you some time. However, there are also some possible problems. The main one would be the formation of products which could interfere with some of your analyte peaks. I see no discussion of any sort regarding products of the reaction. Do you see any product peaks in the GC-FID? If not, why not?

Minor comments:
General: the symbol for rate constant in the kinetics literature is an italicized lower-case k. It is not to be confused with an upper-case K (which is reserved for units of kelvin), or an italicized upper-case K (which is normally reserved for equilibrium constants).
Abstract: revise according to suggestions above.
Introduction:
Line 44. why are you making comparisons with NO3? It is well known that the abstraction reactions are unimportant for the alkanes. Chlorine on the other hand may become important in some environments.
Line 44. “Dehydrogenation” of alkanes leads to alkenes. You mean to say “hydrogen abstraction”.
Line 46. I assume by “rate constants”, the authors mean “room temperature rate constants”. You should specify this.
Line 47. Assuming that the authors have by now become more familiar with the kinetic database, you will of course know that the range of reactivity of alkanes goes from 6.36E-15 (methane) to 2.16E-11 (n-hexadecane) at the time of writing. The range provided is therefore misleading.
Line 47. “mol” is absolutely not an abbreviation of “molecule”. “mol” is an abbreviation of “mole”, which would be highly misleading.
Line 48. Rate constants are not faster or slower than other rate constants. They are larger or smaller.
Line 66. In fact, precise measurements are highly desirable in the relative rate method. Low precision in your GC-FID measurements would lead to scatter in your relative rate plots. Therefore, this statement is misleading.
Methods:
General comment: several tests have been made with respect to dark losses, photolytic losses etc. However, as far as I can tell, no tests were performed regarding storage in the 1 litre sample bags. In your experiments, your samples are stored for some time before they are analysed by the GC-FID are they not? During this time, your samples are subjected to conditions of higher surface area to volume ratios, and it is here, where I would expect to see the most wall loss.
Line 115. Excess with respect to what?
Line 145. “self-developed”.
Line 155. It is not clear to me how you have improved or expanded the work of Shaw et al. Furthermore, it is also not clear to me how the results of this work are significantly different from any other relative rate study in which several reference compounds are considered.
Line 173. There is a certain irony to this statement, because I would strongly recommend that you should use the available expert-evaluated rate constants wherever possible.
Line 193. Was the H2O2 purified?
Lines 211-212. I don’t know what the authors mean by general error is 2 sigma… Do you mean that the uncertainties for SAR estimates are generally within a factor of two? This is possibly true in a global sense, but it is considerably lower for the alkane dataset (the subject of this paper).
Line 238. I don’t know what an “error strip” is. I think the authors mean “error bars”.
Line 238. What is fitting dispersion?
Results:
Figure 3. It would be useful to include literature recommendations for each of these rate constants where available, allowing us to see how well the experiments are performing.
Table 1. As noted above, the errors in this table are unacceptable at present. In addition to this, the formatting of this table is confusing and should be rethought to help the readers understand it better.
Structure-activity relationships section:
You only compare with one SAR (the Atkinson SAR). This is a missed opportunity, there are several others to choose from (some examples include: Neeb, 2000; Jenkin et al., 2018; McGillen et al., 2024). In the case of Neeb, this is of particular relevance because there is some critical discussion on the use of a ring-strain correction factor on page 6 (300) of that study, the authors should consider this in their discussion of SAR performance for cyclic compounds. Incidentally, the recent SAR of McGillen et al. (2024) is not currently configured for cyclic compounds, however, I have assessed its performance on the selection of compounds of this paper. This is very easily done by running the Python code of that paper, from which I find that it performs marginally better than Kwok and Atkinson (1995). This, at least for this limited selection of compounds, supports Neeb’s statements about ring strain corrections. However, it is most likely the case that more data on cyclic alkanes of differing ring size would be very useful in assessing this further.
References:
McGillen et al. (2020) DOI: 10.5194/essd-12-1203-2020
Sprengnether et al. (2009) DOI: 10.1021/jp810412m
Neeb (2000) DOI: 10.1023/A:1006278410328
Jenkin et al. (2018) DOI: 10.5194/acp-18-9297-2018
McGillen et al. (2024) DOI: 10.1039/D3EA00147D
Kwok and Atkinson (1995) DOI: 10.1016/1352-2310(95)00069-B
Citation: https://doi.org/10.5194/egusphere-2023-2802-RC1
- AC2: 'Reply on RC1', Chengtang Liu, 27 Feb 2024
  
  The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2023/egusphere-2023-2802/egusphere-2023-2802-AC2-supplement.pdf
  
  Citation: https://doi.org/10.5194/egusphere-2023-2802-AC2
RC2:
'Comment on egusphere-2023-2802', Anonymous Referee #2, 09 Jan 2024

see attached file

Citation: https://doi.org/10.5194/egusphere-2023-2802-RC2
- AC1: 'Reply on RC2', Chengtang Liu, 27 Feb 2024
  
  The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2023/egusphere-2023-2802/egusphere-2023-2802-AC1-supplement.pdf
  
  Citation: https://doi.org/10.5194/egusphere-2023-2802-AC1
RC3:
'Comment on egusphere-2023-2802', Anonymous Referee #3, 16 Jan 2024
General comments:
The article entitled “Rate coefficients for the reactions of OH radical with C3-C11 alkanes determined by the relative rate technique” by Xin et al., reports a series of rate coefficients measurements for the reactions of 25 alkanes with OH radicals using a relative rate technique. The research employed the GC-FID technique and a simulation chamber to evaluate the rate coefficients values at 25 C and Arrhenius expressions in the 273-323 K temperature range. The authors also explored the structure activity relationship approach to evaluate the OH radical rate coefficients of the alkane series. The main objective of the author’s research was to provide multiple kinetic data studying simultaneously a large number of compounds, but even achieved, however, the lack of higher accuracy, quality and novelty for released rate coefficients do not justify the publication of the article in the present form. An extensive revaluation of the data could help to approach this study from a different perspective and enhance the quality of the results.
Major comments:
The introduction provides a large number of literature data; however, a very chaotic presentation induces to readers the feeling of jumping from one study to another, all of them mostly with very general information regarding the kinetic of alkanes. The studies mentioned in the introduction are presented without an effective detail of the rate coefficient information. I would write the introduction assessing the importance of alkanes for air quality with their impact to atmosphere, then I would add information about their concentrations in troposphere and the impact on potential ozone formation, potential SOA formation and their sources and sinks. One important point of the study is to highlight the importance of accurate kinetic rate coefficients for database, global model atmospheric processes and degradation mechanisms. As one of the reviewers mentioned already, the McGillen et al., (2018) database is very important to be used as a start in the literature data assessment and comparison.

The reason of selected those 25 alkanes is not presented in the study and their selection looks arbitrary. An organized evaluation based on their separation on straight-chain, branching and cyclic alkane structure would be more interesting and helpful to get valuable information. First class of alkanes including linear compounds could provide information regarding reactivity of each CH₂ group added to their structure and how the rate coefficient value would change over increasing alkane chain. Secondly, from the branching alkanes the authors could have more information related to CH groups added to the alkane structure. The third class in the evaluation would be cyclic alkanes where the authors could extract information regarding the reactivity increase with the cycle size from cyclobutane to cyclodecane. The authors should include in their evaluation the alkanes rate coefficients studied in present study and those existing in the literature, to release more complete discussion on their behaviour and reactivity (figure 3 and 4). As an example, there are a lot of data which could be included, mentioning here only a few (k_OH for cyclooctane, bicyclo octane, methyl octane, etc.).

Since the authors highlight their first study on 3-methylheptane why they do not cover other not studied yet branched alkanes (2,2,3-trimethylpentane, etc.)

The data reported in the Table 2 should be reevaluated and presented in more concise and understandable form. There are multiple examples of inconsistency of the data with many average data not well calculated (i.e. isopentane in N2).

With the extensive interpretation of data including the existing literature rate coefficients, the authors would be able to evaluate the accurate reactivity trends for the class of alkane toward OH radicals and calculate new factors for the SAR method and then to improve the SAR method. A simple comparison with the Kwok and Atkinson SAR method is not worth to do. Evaluation of existing SAR approaches in the literature, with discussion about the influence on the substituent factors, is necessary. (McGillen et al., 2024 (doi.org/10.1039/D3EA00147D), Jenkin et al., 2018 (doi.org/10.5194/acp18-9297-2018)

The reaction channel of the OH radical initiated degradation of alkanes is strictly related to hydrogen abstraction in the presence of oxygen. There are clearly correlations on the alkane reactivity with OH radicals and Cl atoms for all saturated class of VOCs. Please evaluate a log-log correlation of k_CL and k_OH as presented by Calvert et al., 2011 (Calvert, J., Mellouki, A., Orlando, J., Pilling, M., and Wallington, T.: Mechanisms of Atmospheric Oxidation of the Oxygenates, Oxford University Press) for alkanes, saturated alcohols and ethers and also by Tovar et al. (2022) (doi.org/10.5194/acp-22-6989-2022) for saturated epoxides.

The importance of the bath-gas is over highlighted in this study and a single example for a selected alkane would be enough to prove that is no bath-gas effect on the rate coefficient value. A revaluation of the paper consistency should be performed.

Please add more information regarding the conditions needed for relative rate techniques. Also include more advantages and disadvantages of the absolute and relative techniques.

The authors should highlight the atmospheric implication and the impact of their research as requested by a scientific journal as “Atmospheric Chemistry and Physics“. Please add information about the alkane lifetime in the atmosphere toward the OH radicals. A more extensive conclusion and atmospheric implication should be performed.

Minor comments:
Both reports of the previous reviewers have included a detailed list of minor comments and only additional comments I would add here:
Line 84: Finlayson-Pitts
Line 127: “at253”
Line 130: please avoid given values in the form of 0.00013 or 0.00048. Change the units to pptv/h.
Line 283 and 285: please add units
Line 460: please revise the rate coefficient
Line 104: The figure of the simulation chamber shows a ratio of 200:50 of N2:O2 mixture. The study used synthetic air or this mixture shown in the figure?
Citation: https://doi.org/10.5194/egusphere-2023-2802-RC3
- AC3: 'Reply on RC3', Chengtang Liu, 27 Feb 2024
  
  The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2023/egusphere-2023-2802/egusphere-2023-2802-AC3-supplement.pdf
  
  Citation: https://doi.org/10.5194/egusphere-2023-2802-AC3

Peer review completion

AR: Author's response | RR: Referee report | ED: Editor decision | EF: Editorial file upload

AR by Chengtang Liu on behalf of the Authors (29 Feb 2024) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (14 Mar 2024) by John Orlando

RR by Anonymous Referee #3 (27 Mar 2024)

RR by Anonymous Referee #1 (30 Mar 2024)

Suggestions for revision or reasons for rejection

Following the reviews of their manuscript entitled “Rate coefficients for the reactions of OH radical with C3-C11 1 alkanes determined by the relative rate technique”, Yanyan Xin and co-workers have attempted to revise their manuscript. Some clear improvements to their earlier manuscript are noted, however, some problems remain. As a result, I would only recommend this manuscript for publication in Atmospheric Chemistry and Physics after these problems have been properly addressed.
Major points:
Figure 5: There are many problems with this graph.
I am assuming that the black lines are Arrhenius fits. As discussed in your review, Arrhenius fits aren't very useful for this set of compounds over a large temperature range (for example, panel D shows just how poorly this approach describes the data), and I would recommend other fits such as k(T) = Aexp(B/T)(T/300)^n or k(T) = AT^n*exp(B/T), where A = A-factor, B = E/R and n = an additional term to provide curvature.
The units on the y-axes are wrong (cm^3 molecule^-1 s^-1).
There are missing data from the plots:
Panel A:
Anderson et al., 2004 (DOI: https://doi.org/10.1021/jp0472008);
Behnke et al., 1988 (DOI: https://doi.org/10.1016/0004-6981(88)90341-1);
Nolting et al., 1988 (DOI: https://doi.org/10.1007/BF00048331);
Han et al., 2018 (DOI: https://doi.org/10.3390/atmos9080320);
Ferrari et al., 1996 (DOI: https://doi.org/10.1002/(SICI)1097-4601(1996)28:8%3C609::AID-KIN6%3E3.0.CO;2-Z)
Panel B:
Sivaramakrishnan et al., 2009 (DOI: https://doi.org/10.1021/jp810987u);
Pang et al., 2011 (DOI: https://doi.org/10.1524/zpch.2011.0156); Han et al., 2018 (DOI: https://doi.org/10.3390/atmos9080320)
Panel C:
Atkinson et al., 1984 (DOI: https://doi.org/10.1002/kin.550160413);
Cox et al., 1980 (DOI: https://doi.org/10.1021/es60161a007);
Darnall et al., 1978 (DOI: https://doi.org/10.1021/j100503a001);
Lloyd et al., 1976 (DOI: https://doi.org/10.1021/j100549a003)
Panel D:
Harris and Kerr, 1988 (DOI: https://doi.org/10.1002/kin.550201203);
Wilson et al., 2006 (DOI: https://doi.org/10.1021/jp055841c)
Also, the work of Sivaramakrishnan et al., 2009 is conducted at high temperature and the other points don't seem to match up with the figure legend.

Conclusions:
The conclusions have not changed since the review. They should be updated to reflect the contents of the revised article (for example, it was already pointed out that your study does not present the first temperature-dependent data for methylcyclopentane, and yet, this is what you claim in your conclusions. This is unacceptable, this error has already been pointed out in your earlier review. Also, you have now applied several SAR methods for rate constant estimation, it would be useful to summarize the findings of these different methods.

Minor points:

Title:
The numbers 3 and 11 should be in subscript. This change should be applied throughout your manuscript (not just the title).

Abstract:
Line 16: the edit is worse than the original. I suggest to change it back to how it was.
Line 18: kOH. k should be italicized. OH shouldn’t be italicized. The authors should carefully go through their manuscript and correct each instance of this problem.
Lines 20 – 26: The authors have employed several SAR methods now, and the results of these calculations should be included in your abstract.
Line 35: Remove the word “very”.

Introduction:
Line 68: I am not familiar with the term “some secondary oxides”. I recommend “oxygenated molecules”.
Lines 71 – 73: This is purely tautological. Essentially, you are stating that you need to measure how fast something reacts in order to evaluate how fast it reacts… Just delete these lines.
Line 90: relies, not relied.
Line 98: “method” not “mehod”.

Methods:
Line 144: “H2O2 with respect to …”.
Line 159: lower-case k for kd.

Estimation of the rate constant at 298 K (SAR):
Mostly, this section has been improved, and I think the inclusion of the different methods is interesting. However, it was recommended by my review (referee 1) and that of referee 3 that you should try to compare with the recent SAR method of McGillen et al., 2024 (DOI: https://doi.org/10.1039/D3EA00147D). The reasons for this are that it is a distinctly different methodology to that of Atkinson, Wilson, Neeb, etc. The authors appear not to have been able to include these predictions. They are easy to do, and I list the results here:
name k SAR
propane 1.20E-12
isobutane 2.17E-12
n-butane 2.38E-12
isopentane 3.37E-12
n-pentane 3.67E-12
cyclopentane 7.30E-12
2,2-dimethylbutane 1.94E-12
2,3-dimethylbutane 4.27E-12
2-methylpentane 4.65E-12
3-methylpentane 4.67E-12
methylcyclopentane 8.34E-12
2,4-dimethylpentane 5.56E-12
cyclohexane 8.76E-12
2-methylhexane 5.97E-12
3-methylhexane 6.00E-12
2,2,4-trimethylpentane 4.10E-12
n-heptane 6.40E-12
methylcyclohexane 9.76E-12
2,3,4-trimethylpentane 6.39E-12
2-methylheptane 7.34E-12
3-methylheptane 7.36E-12
n-octane 7.80E-12
n-nonane 9.21E-12
n-decane 1.06E-11
n-undecane 1.21E-11

I recommend that you include these new predictions in this section so that you can make a more complete comparison of the available SAR methods, and to discuss whether or not accounting for the cycle size is a useful parameter in these SARs.
Also, why don’t you compare the SAR estimates at different temperatures?
Line 269 (and everywhere else): k SHOULD NOT BE UPPER-CASE!
Line 271: “update” not “updated”. “modify” not “modified”.
Line 272: It is not clear what is meant by fundamental rate constant. Maybe chose “base rate constant” or something like this.

Results and discussion:
Line 307: There is no such thing as a second-order C-H bond. You mean “secondary” perhaps.
Line 311: “reactivity increases” not “reactivity increase”.
Table 1: This table is mostly OK, but I find it confusing that you have a column entitled “reference” (which should not be confused with your reference rate constant). I suggest to rename this column to “Literature measurements”.

Comparisons to structure-activity relationships:
Lines 453 – 455: Under the circumstances of this study, I find it strange that you would evaluate the reliability of experimental data by comparing with SAR estimates. If conducted well, an experimental measurement will be considerably more reliable than an estimation technique. Therefore, rather than assessing how reliable the experiment is, more realistically, this comparison assesses how accurate the estimation technique is.
Line 462: “branched” not “branch”.
Line 464: what is “shadow range”? The meaning is unclear, rephrase.
Line 497: “n-nonane”.

Temperature dependence (273-323 K):
Table 2: similar to Table 1, I suggest to rename this column “Reference” to “Literature measurements”.
Figure 6: Similar to Figure 5, there are several errors here. Figure caption contains misspellings of 3-methylheptane and 2-methylheptane.

Panel A: The work of Anderson was conducted at 296 K. The high temperature measurements were conducted by Sivaramakrishnan and Michael, 2008 (so your legend is incorrect).

Correlation between the rate coefficients of the reaction of alkanes with OH 672 radicals and chlorine atoms:
Line 677: replace “discrete” with “weak”?

Atmospheric lifetime and implications:
Lines 693 – 694: The reference Li et al., 2018 did not assess the atmospheric abundance of OH radicals. Choose a relevant reference for this point.
Line 696: “in” not “on the”. “lifetimes” not “lifetime”.
Line 698: “lifetimes are reduced” not “lifetime seems to reduce”.
Lines 701 – 702: RO2 will serve to convert NO to NO2 directly. The role of HO2 is also important, but is not directly related to the peroxy radicals mention here.
Line 703: 11 days is not a “long time”.
Lines 703 – 705: This is tautological in its present form, and should be removed.
Line 710: previous temperature dependent data exists for methylcyclopentane. You must change this accordingly.
Lines 716 – 717: is this true of all SAR techniques or just one of them?
Line 720: More than one method has been employed. The use of the singular “method” is inappropriate and should be updated.

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RR by Anonymous Referee #2 (07 Apr 2024)

Suggestions for revision or reasons for rejection

The authors have made a substantial effort to improve manuscript's quality based on the three reviewers suggestions.

However, there are still a few minor and major issues that the authors need to take into account before the current version of the draft to be in a publishable form.

1. Minor: It is highly recommended the authors to preferably use rate coefficient instead of rate constant. k is not a constant - although the term is used in the literature - and they have clearly described that depends on T! This comment was also present in the first review.

2. Major: In absolute and relative rate methods comparison the authors should be very careful! They use the term known, although they should use the term recommended. The fact that a reaction rate cofficient has been measured doesn't mean that is known! It deppends on them whst k-values they would use for their reference reaction used, but they need to justify why they used those. It is strongly recommended to use the evalusted rate coefficients values from NASA/JPL and IUPAC panels, where exist and if not they need to do their own evaluation and justify their selection. Please keep in mind that absolute rate coefficients determinations although sometimes might be more demanding and challenging do not rely on other measurements and thus are not subzected on systematic errors of previous measurements, that are larger at temperatures away from room temperature. Particularly when so many reaction rate coefficients are measured at once it is very likely that reaction products etc might interfere in their subtraction analysis and the error bars that should be quoted cannot be less than 15 %. Like mentioned in the previous review, the error analysis of the kinetic data presented in this work is actually missing! What are the estimated systematic uncertainties of authors measurements? How they have been estimated?

3. Major: Figure 5: (a) First please use the same symbols in all 4 plots when you refer to the same literature study, for consistency purposes. For instance, for Atkinson et al. (2003) you have used three different symbols and colors, which makes the comparison confusing for the reader. (b) Include temperature as mirror to bottom axis, so as the reader to have a direct access to the temperature that the kinetic data refer to just lookin the plot. (c) do the 2σ error bars include systematic uncertainties? How the error bars shown in figure 5c, for instance, were determined? Why the error bar at 273 K is that smaller compared to 296 K and then becomesd that smaller again at 313 K? Systematic uncertainties normally become larger away from room temperature, where most of the test measurements are carried out. This plot doesn't seem to include the systematic uncertainties from the reference reactions or they have mistakenly included. If this is tonly the 2σ precision of the fits, why the present measurements have so large error limits? (d) What are the fits shown in all 4 plots. First they do not fit the data! Why the authors didn't try to fit the actual data with a modified Arrhrnius expression? To present fits that are not representing this work or combined with literature measured data seems odd. The easiest way around it is to fit their data and discuss the agrrement with other literature data in the same temperature data. The k(T)-trends observed in these plots might contain important mechanistic information that the authors have disregarded!

So, based on these comments, the present reviewer suggests that this work might be publishable, but the present form needs some additional improvements.

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ED: Reconsider after major revisions (18 Apr 2024) by John Orlando

AR by Chengtang Liu on behalf of the Authors (18 May 2024) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (04 Jun 2024) by John Orlando

RR by Anonymous Referee #1 (06 Jun 2024)

Suggestions for revision or reasons for rejection

Yanyan Xin and co-workers have submitted a revised manuscript on the temperature dependent kinetics of the reactions of OH with a suite of alkanes using the relative rate technique. This manuscript has been through several review phases, and these authors have improved several important aspects of the paper, notably, the presentation of their data and their discussion of SAR methods. In recognition of this, I would recommend this article for publication. There are some minor points that remain where simple improvements could be made, which I will detail below.
Minor considerations:
Lines 20-21: in general, our understanding of alkane oxidation is good (relative to other types of compounds). I would suggest to rephrase this to something like: “… highlighting that there may be additional factors that govern the reactivity of highly branched alkanes that are not captured by current SAR techniques.”
General: some of the new edits contain typographical and grammatical errors. An example of this would be lines 41-43, which is considerably worse than the sentence that it replaces. I won’t concern myself any further with these small details, since I assume they will be fixed during the finalization of your manuscript. However, I would suggest to the authors that hasty edits such as this can degrade the quality of your presentation and distract your readers.
Section 3.2, Figure 4: Firstly, why don’t you include the predictions of McGillen et al. (2024) in this plot? It seems strange to put it in the SI. Secondly, it appears that there are fewer predictions of Wilson et al. (2006) (18 compared with 25 for the other methods). Is this a limitation of the method, or is this a mistake?
Line 468: finger activation energy?! What is this?
Figure 7: To be consistent with the other figures, it would be useful to number the points in this graph according to the compound (e.g. (1) = propane, (2) = isobutane, etc.).

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RR by Anonymous Referee #3 (16 Jun 2024)

RR by Anonymous Referee #2 (24 Jun 2024)

Suggestions for revision or reasons for rejection

As mentioned in previous reviews the experimental results and the validation of the experimental approach comprise a nice piece of work and are worth to be published. However, although the authors made once again a substantial effort to improve the quality of the manuscript and tried to address most of the reviewers suggestions the present draft needs significant improvements, in order to be in a publishable form. A key-point would be to add a physical interpretation of the presented results – totally missing -, particularly since they have systematically measured the OH reactivity of a wide series of alkanes that can be utilized in SAR methods and significantly improve their predictions.
Therefore, although the present results are worth to be published, the present draft is not yet in a publishable form.
The present review is mainly focused on the scientific content. However, the manuscript needs substantial editing, in order to pass the messages across to the reader in a clear way. Some examples that might be of assistance and the authors may want to consider are given below (NOTE: The lines refer to the track-changed manuscript):
1. In several places when they refer to other kinetic studies, e.g., Introduction, line 56 “…in the Ar system at 300 K using…” they should include the total pressure and not only the bath gas, e.g., “at 300 K and xxx Torr in Ar, using…”. Another example is in line 70, but it also appears in several places that it is suggested the authors to change it and get rid of Ar or Air system.
2. Correct typo in line 42 “ano” and change to “are no”, replace “the absolute rate constant method and the relative rate constant method” with “both absolute and relative rate methods” Change “et al.” in line 53 with etc., line 72 replace “solely” with “limited to”, in line 77 replace “multiplied by” with “increased by”, in line 79 change “in varying degrees at 300-390 K” with “varying the temperature in the range 300 – 390 K”, Reword the paragraph between lines 84 and 87, correct the use of “respectively” in several places (e.g., line 300 – 3 numbers for one compound) and these are only very few examples of editing needed and make difficult for the reader to follow the messages that the authors try to pass across.
3. Please replace the expert-evaluated data use with evaluated data throughout the manuscript.
4. Figure 1: a more comprehensive, but brief, setup description needed here, e.g., describe the acronyms
5. Lines 109-110: The way that the tests that the authors carried out are described is deceptive and confusing. N2 does not react with NMHCs, so I guess that the authors want maybe to imply that they tried to ensure that no wall-loss (e.g., hydrolysis) of NMHC occurs under dark conditions and that NMHCs are stable when exposed at 254 nm. They should not present the tests here in reaction forms. Simply state what they did.
6. Lines 135 – 139: The whole sentence needs to be rephrased. The "basic principle" of the RR method is that the monitoring of the relative loss of two reactants when they both only react with the under study radical and one of the two rate coefficients is well established can lead to the determination of the other reaction rate coefficient (reaction of interest).
7. Lines 141 – 142: The statement here is not true in most of the cases! The product of the rate coefficient and the OH concentration needs to be substantially larger (100 times or more) compared to all the rest of the competitive reactions of the reactant with the other radicals X (kx [X]).
8. Lines 172 – 175: Here significant editing is needed (rate constants was used instead of rate coefficient – also in 2.2 section title), and the next sentence is not needed at all! It is well known that k depends on temperature!
9. Line 224: More important than reporting the R-squares is to present and discuss the intercepts of the linear fits, that is totally missing. This can reveal potential systematic errors and possible curvatures in their data.
10. Figure 3: In this plot any systematic divergence from linear behavior cannot be assessed by the reader. The same applies in the range of the change in the Y-axis, so as the reader to evaluate the sensitivity of the measurements. Although it is difficult to display it in figures like those (displaced), the authors can add a comparison between dX and dY change in the text, to enable the reader to assess measurements sensitivity, pinpoint the cases that dX and dY differ significantly and refer to figure 3.
11. Line 274 – 279: Difficult to follow, please rephrase and change “within a certain range” in line 281 with “taking into account the experimental uncertainties”
12. Section 3.2: There is no physical interpretation for the observed discrepancies both between this work and other experimental ones (e.g., 355 - 356), as well as between this work and SAR. The extensive experimental study the authors carried out should have led them to some conclusions about the sources of the observed discrepancies in SAR approaches. This would be of a particular value and could lead to SAR improvements. However, a comprehensive explanation is totally missing which is the main weakness of the manuscript.
13. Line 403: This is not THE tropospheric temperature range. Please change to “temperatures relevant to the troposphere”.
14. In several cases, e.g. line 459, 466, 513, 516 etc. “*” was used in Arrhenius expressions instead of “x”.
15. Figure 5: Please describe what the fits represent and change the insets since the fit are NOT linear regression! Describe in figure captions what expressions were used.
16. Figure 6: See comment for figure 5 (15).
17. Figure 7. log-log plot instead of double log plot. However, it would have been more of value and would have made more sense to present the axes scale in log basis and not the actual values, so as the reader to directly compare Cl and OH rate coefficients as well. This way the values would represent the rate coefficients.
18. Line 569: Correct “The atmospheric lifetime of alkanes in the troposphere can be estimated” with “The atmospheric lifetime of alkanes in the troposphere, due to their reaction with OH radicals, can be estimated”.
19. Conclusions: It would be of value to include potent weaknesses of SAR methods so as to be able to evaluate them and incorporate them in the future.
20. Supporting Information: Include typical RR plots at different temperatures so as the reader to be able to evaluate the quality of the measured data.

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ED: Publish subject to minor revisions (review by editor) (03 Jul 2024) by John Orlando

AR by Chengtang Liu on behalf of the Authors (12 Jul 2024) Author's response Author's tracked changes Manuscript

ED: Publish subject to technical corrections (31 Jul 2024) by John Orlando

AR by Chengtang Liu on behalf of the Authors (04 Aug 2024) Author's response Manuscript

Journal article(s) based on this preprint

11 Oct 2024

Rate coefficients for the reactions of OH radicals with C₃–C₁₁ alkanes determined by the relative-rate technique

Yanyan Xin, Chengtang Liu, Xiaoxiu Lun, Shuyang Xie, Junfeng Liu, and Yujing Mu

Atmos. Chem. Phys., 24, 11409–11429, https://doi.org/10.5194/acp-24-11409-2024,https://doi.org/10.5194/acp-24-11409-2024, 2024

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Yanyan Xin, Xiaoxiu Lun, Shuyang Xie, Junfeng Liu, Chengtang Liu, and Yujing Mu

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https://doi.org/10.5194/egusphere-2023-2802-supplement

Yanyan Xin, Xiaoxiu Lun, Shuyang Xie, Junfeng Liu, Chengtang Liu, and Yujing Mu

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The relative rate constants of OH radicals with C3-C11 alkanes under different bath gases (N₂, Air, O₂) were obtained, and multiple comparisons were made with previous literature and estimated values, expanding the existing database. The measured relative rate constants of air gases were found to be highly consistent with values obtained in N₂, suggesting that the rate constants obtained in this experiment can reasonably represent the rate constants in the actual atmosphere.


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