How to respond to biased reviews

It has been almost 15 years since my first submission of a manuscript for journal publication. Some of my recent experience, grateful and furious, makes me decide to write such a post. After completing the rebuttal, I feel the rebuttals worth more than the paper itself, for young researchers, regardless of the result of publication (the manuscript was eventually accepted recently, available here link).

I must clarify that majority of the times, the reviews for your manuscripts are fair and constructive. Technical questions in the reviews are straightforward to respond, even though some questions might be tough and require more work to be conducted. But they are technical questions and it is your responsibility to respond. That is the purpose of peer review. I respect all technical questions because they push me to think more about my own work and there must be a scientific response accordingly. However, sometimes you might receive non-technical questions/comments in the review. Those are the really hard ones to respond. Occasionally, the reviews might be biased. Here I would like to share my recent story on how I responded to biased reviews.

Here is the background of the whole story. We submitted one manuscript to a top-notch journal in our scientific community, the Proceedings of the Combustion Institute. It is a biennial publication following the International Symposium on Combustion. The overall acceptance rate of manuscripts is about 35%. So it is competitive. One of our manuscripts is about the research of hydrogen/carbon monoxide ignitions at high pressures using a shock tube. We conducted detailed experimental measurements and thorough (I think) numerical analysis. I think it is good work and useful to our community. So we submitted this manuscript to the Proceedings of the Combustion Institute. On the other side, it is important to let you know that I am a newcomer in the shock tube community (a customized and classical research device) even though I have been working in the general combustion community for over 10 years. my first publication on shock tube was in 2019 (link).

There were three reviewers in the first round of review. One reviewer (Reviewer 2) gave a “very good” rating of our manuscript and acknowledged the importance, value, and novelty of the study.

Reviewer 3 said that this work had no value and little can be learned from this work because experiments agreed with simulation. One can get the answer by just doing simulation without experiments. Interesting logic. Without experiments, how could one know the performance of models? I consider this as a biased review because our work was conducted at a very challenging condition and no such study was conducted before. Without our study, how could we know the performance of existing models?

Reviewer 1 (rated the manuscript "rejection") came back with lots of questions, some of them were technical and some of them were not. Some technical questions/comments were misleading. But one thing is clear to me, Reviewer 1 and Reviewer 3 just wanted to kill this manuscript. Reviewer 1 insisted that the ideal gas equation of state should not be used. This is an odd comment. It has been proved by several previous publications that the ideal gas equation of state is applicable at similar conditions as those in our study. Reviewer 1 also insisted that we should not use existing models to conduct numerical analysis because they are not validated by any experiments. This is “chicken or the egg” logic. One purpose of our work is to evaluate the performance of existing models because nobody did it before. Technically, no one could validate a model but assessing its performance at given conditions. This is how our understanding progresses. Now, Reviewer 1 is prohibiting us to do it. I simply started to question the qualification of this reviewer or the motivation of this reviewer.

I told my hard-working graduate student that I must fight back regardless of results otherwise the same reviewers would do the same thing to our next manuscript. (I am saying so because our first publication in 2019 on shock tube experienced very similar reviews. At that time, only one reviewer opposed the acceptance of that paper but two others strongly supported the publication. In the end, our first paper was accepted in 2018 and published in 2019). I then started to put a bold and strong response as a rebuttal. I just wanted to pass the message clearly that I do not yield to bias. I also wrote to the colloquium co-chairs who handled our paper to express my concern. I sincerely thank them to listen to me and looked into this issue.

Below I expanded the first rebuttal as below from a one-page limited version.

----------------------------------- our first rebuttal-----------------------

Rebuttal for PROCI-D-19-01072

High Pressure Ignition Delay Times of H2/CO mixture in Carbon Dioxide and Argon Diluent

Reviewer #1 (Reject): “Comments summarized in italics before rebuttals” Authors present IDT data in shock tube mixtures of hydrogen and CO diluted with CO2. Overall the topic is of interest to the community and there have been recent efforts in this area. However, the paper in its present form is not suitable for publication. I broadcast my concerns and comments below:

A: Review and rating from Reviewer #1 are clearly biased as shown below. We request scrutiny from the colloquium chairs.

(1) Q: Authors cited references 3 &7 for the statement "inlet pressure range of 10-30 MPa inlet temperature of approximately 900-1500 K". But those references do not talk about 10MPa pressure at the combustor inlet and 1500 K temperature at the inlet. This statement is misleading the reader.

A1: Figure 3 in Ref [3] and Table 1 in Ref [7] clearly list the inlet conditions. 

(2) Q: Several of the reported ignition delay times less than 70us are typically prone to error from simple emission measurements. See Davidson, D. F., and Hanson, R. K., 2004, "Interpreting shock tube ignition data," Int. J. Chem. Kinet., 36(9), p. 510.

A2: We are fully aware of this. However, high pressure IDTs are short, and uncertainty is clearly indicated. IDT measured by Hanson and Vasu’s groups was as short as 36 μs (Figure 8 in Ref [14]).

(3) Q: "Moreover, to the authors' best knowledge, no experimental data on IDT of syngas have been reported under large dilution levels of CO2 above 1 MPa." This statement is incorrect!. Researchers have published syngas IDTs with high levels of CO2 dilution in multiple publications up to 10MPa. They have also used 6 different syngas fuel compositions (H2/CO ratio) ranging from low CO to high CO values (H2/CO ratios 1/9) and multiple equivalence ratios. See for example,

[a] Barak, et al. "Ignition Delay Times of Syngas and Methane in sCO2 Diluted Mixtures for Direct-Fired Cycles," Proc. ASME Turbo Expo 2019: Turbomachinery Technical Conference and Exposition, https://doi.org/10.1115/GT2019-90178.

[b] Barak, et al. "High-Pressure Oxy-Syngas Ignition Delay Times With CO2 Dilution: Shock Tube Measurements and Comparison of the Performance of Kinetic Mechanisms," Journal of Engineering for Gas Turbines and Power, 141(2), pp. 021011-021011-021017.

A3: This comment is purposely misleading. We are aware of these papers. In all those studies, the experimental pressures are well below critical pressures of the mixtures.

(4) Q: It is misleading to use the term syngas in this study. Typical syngas compositions are far away from the composition used in this study. See for example, Wang et al., Front. Energy Power Eng. China 2009, 3(3): 369-372 DOI 10.1007/s11708-009-0044-7 The composition used in this study is H2/CO=95:5 mixture, which is effectively a hydrogen mixture. I understand that the authors are not able to add more CO in their test mixtures due to safety reasons?

A4: We did not use the term “Syngas” in the title and only refer to this mixture as a “syngas surrogate” (in the abstract). CO level is regulated by our institute.

(5) Q: Authors mentioned "real-gas EoS (Peng-Robinson) is used in normal shock relations [33] and the overall uncertainty in T5 calculations". As a reviewer, I do not agree to this approach as this approach is not plausible or scientific. Please find my following reasons:

i)         For real gases, two isentropic exponents appear in normal shock relations instead of constant ideal gas exponent. Accuracy of these exponents are equally important as the equation-of-state. This paper does not talk about how authors have accounted these isentropic exponents.

ii)       Peng-Robinson is empirical type equation-of-state. Various constants involved in this equation-of-state are fitting coefficients for certain data. Authors did not justify why this particular equation-of-state is used. Referring previous works does not help as previous experiments are for different mixtures and conditions.

A5: This comment is erroneous. The applicability of ideal gas EoS in normal shock relations at high P5 and T5 conditions has been extensively studied. See work by Davidson & Hanson Ref [33], Hanson & Vasu Ref [14], Brenzinsky [IJCK, (38)2006 , 75-97], and our work (Ref [13]). 

(6) Q: Authors discussed about comparison between idea-gas and real-gas in page seven and the conclusions of this discussion are not scientific due to following reasons.

i.         Unlike Peng-Robinson and Soave-Redlich-Kwong, Redlich-Kwong equation-of-state does not account acentric factor which is important under supercritical pressures. Under many conditions, Redlich-Kwong fails to predict state of a pure substance. Hence, we cannot trust that Redlich-Kwong model is giving true result due to its preliminary formulations. Then, how an untrustable equation-of-state can be compared to an ideal-gas assumption to conclude real-gas effects are negligible?

ii.        Authors have used REPROP to justify that mixture compressibility factors are between 1.0224-1.0491. But, as more products are formed (H2O concentration increases), the mixture critical point would increase significantly (H2O critical point is higher) and bring the products close critical point of that mixture. Under such conditions, compressibility factor may vary drastically. All these possibilities are not considered and discussed. So, the conclusions beyond the level of justification.

iii.       16-18% experimental uncertainty in IDT cannot justify avoiding ~4% difference in compressibility factor in a simulation. Here, IDTs are from the traces of OH* only. The trend of OH* can be different from heat release rate. But compressibility factor influences the heat release rate. Hence, the logic of not using real-gas equation-of-state is not convincing.

A6: Refer to Q(5). The effect of various EoS on kinetics modeling and thermodynamics relevant to shock tube experiments are extensively discussed in Ref [39]. One of the main conclusions from this reference is that the choice of EoS is not crucial for shock tube kinetics studies done at temperatures above 1,000 K. We have previously shown this for similar experimental conditions (Ref [13]). Along the same line, the justification of using REFPROP is also shown in Ref [13] with the same 2σ uncertainty analysis performed for the experimental conditions in this paper.

(7) Q: Author have used Aramco 2.0 for sensitivity analysis and illustrated sCO2 combustion kinetics. sCO2 combustion kinetics can be understood from a mechanism which is physically correct. Comparing a mechanism for few OH* profiles does not guarantee that it is physically correct for that application. The main purpose of kinetics in a combustion simulation is to predicts heat release rate correctly. Hence, it is most important to validate a mechanism on experiments which are representing heat release rate and then learn chemical kinetic behavior. It is understandable that there are no such sCO2 experiments exists. But that is not the supporting criteria to accept Aramco 2.0 is correct for sCO2 combustion simulations.

For example, in Fig. 7, authors discussed about CO mole fractions. These trends can be believed, when the reaction CO+OH=CO2+H behavior is represented in Aramco 2.0 at high pressures. Authors can refer Joshi, A. V., & Wang, H. (2005) to understand the nature of this reaction at high-pressures. Aramco 2.0 only has low-pressure rate of this reaction.

A7: Aramco 2.0 has been used for sCO2-relavent simulations previously in work by Hanson & Vasu Ref [14] and our work Ref [13]. There is no published kinetic model showing improved results.

(8) Q: Detailed information is not given on the type of sensitivity analysis shown in this work. Example, what species sensitivity? At what time instant the sensitivity is plotted? One reaction can be sensitive of OH and another CO etc.

Conclusion: The technical merit of this paper is poor.

A8: The type of the sensitivity analysis (Brute-force) is added to the manuscript along with the time for the analyses (ignition time).

(9) Q:… Page 6, are you saying a +/- 12K uncertainty is yields a 12-14% change in IDT? If so, would adding one more gate for attentuation of the shock (another PCB+timer counter) reduce some uncertainty? What about measurement equipment uncertainty such as sampling rate, detector, etc?

A9: The major contributing factor in IDT uncertainty is the uncertainty in T5 calculation, which has many contributing factors (including the number of PCBs and resolution of frequency counters, etc.). The 2σ approach takes all these factors into account.

(10) Q: page 8, Why is constant pressure used instead of constant volume? Was the same assumption used for Argon where a clear pressure rise is observed?

A10: This is well-known in shock tube community. Using the endwall pressure traces, the reflected shock pressure (P5) is constant up to the point of ignition as shown in Figure 1.

(11) Q: How are you determining IDT from the models?...

A11: The IDT in the model is defined by the time where the maximum rate of change of OH is achieved. This is added and clarified in the manuscript. 

(12) Q: Fig. 2, Perhaps graphically or textually include the model IDT uncertainty of 3% due to EOS?

A12: On log scale, graphically adding 3% uncertainty is not clearly observable. Therefore, we only mention this value in the main body of the manuscript.

(13) Q: Fig. 1, Can you comment on why OH* signal from the side-wall is rising faster than the end-wall?

A13: This is explained in detail along with supporting references under section 2.2 of the manuscript. A detailed analysis of this phenomenon could be found in our previous publication (Ref [13]). The discussion on exact definition for time zero is also listed in section 2.2.

(14) Q: fig. 4, Is a positive coefficient reducing reactivity? Please make that clear.

A14: yes, this is clarified in the revised version.

(15) Q: page 10, "Further calculations show that varying the H2:CO ratio in fuel does not significantly alter the IDT difference between CO2 and Ar mixtures because ignition is primarily controlled by H2 kinetics" do not believe this statement is correct. I would encourage either: experimental proof of this or at the very least some modeling. Perhaps a figure on showing IDT with a large variety of mixtures?

A15: The variation refers to ~50% and is clarified in the revision.

(16) Q: "reactions in controlling ignition...." slowing or speeding it up?

A16: in hindering ignition. This is revised in the manuscript.

(17) Q: Fig 7, Aren't we seeing deviation on IDT here if using OH as a tracer in models?

A17: IDTs for cases using different diluents are close, however not identical to each other. These deviations are within the experimental uncertainty as shown in Figure 5.

Reviewer #2 (Very Good): The authors present a shock tube study of the ignition delay times of syngas (H2 and CO) mixtures dilute in CO2. The state conditions studied are predominantly above the critical point for CO2. The paper is well written and includes uncertainty analysis, considerations of the validity of the equation of state for an ideal gas at supercritical conditions, potential concerns regarding shock wave bifurcation, etc. and is overall a high quality work. The discussion includes a description of the shift in elementary reaction kinetics based on one of the widely used reaction mechanisms for syngas. The modeling work is straightforward, but presented well and thoughtfully. The experimental data are new and valuable for understanding the effects of CO2 dilution as might be found in direct-fired combustion systems operating at supercritical conditions. It would have been useful to compare the experimental results with other syngas studies, particularly since the authors conclude that Ar and CO2 yield similar ignition delay times albeit through different kinetics pathways (based on the reaction mechanism). The study has been thoughtfully planned and executed and is well suited for combustion community.

A: The authors appreciate the understanding of the reviewer on the importance, value and novelty of the study.

Reviewer #3 (Marginal): “Comments summarized in italics before rebuttals” This paper provides new data on reflected shock ignition delay times for syngas highly diluted in CO2, at elevated pressure of 100-200 atm, along with comparison data for Ar dilution.  However, the data themselves allow little that is new to be learned in that the multiple available detailed mechanisms used for comparison with data all yield essentially the same results. That is, values of IDT are not strongly sensitive to the likely large differences in the details of these various mechanisms. That is because the IDT is mostly sensitive to just a few key reactions, for which there is relatively good confidence in the rate coefficients and hence relatively little variation in the mechanisms tested. The paper does include extensive evaluations of reaction sensitivity, and some useful discussion of the sensitivity plots obtained, but again, there is no surprise here. The same observations and conclusions could have been drawn from work based entirely on

kinetic simulations and without any experimental data. As a result, the value of the paper is somewhat limited. The key point that that while the paper does provide IDT data not previously published, such data are not really useful in advancing the capability to simulate IDT in syngas mixtures dilute in CO2. Clearly the best path forward, to improving simulation capability would be to design and execute experiments (or perform accurate theoretical calculations) of the few key reactions, notably the recombination reaction H + O2 + M --> HO2 and related HO2 reactions. Enhanced accuracy for the rate constants of these key reactions would have broad utility and potential impact on the various detailed mechanisms under development across the world. In light of the limited new knowledge gained/presented here, and the likely low fraction of papers that can be accepted, I cannot give the paper a strong recommendation for presentation at the symposium.

(1) Q: However, the data themselves allow little that is new to be learned…

A1: We respectfully disagree: The new and important information in this manuscript is experimental validation (whether agree or not with modeling). Furthermore, there is an urgent need in sCO2 combustion community to obtain the IDTs at the relevant and applicable conditions. Hence one of the main objectives of the current study is to report the first-of-its kind data at these severe conditions in a meticulous way.

(2) Q: …The same observations and conclusions could have been drawn from work based entirely on kinetic simulations …

A2: We respectfully disagree: Without experimental validation, such effort is meaningless. Current work makes an effort in 1) validating kinetic models at challenging experimental conditions, 2) studying the chemical effect of CO2 in IDT, globally and at elementary reaction level. Ultimately, this work tries to pave the path by providing key information for future chemical kinetic modeling applications.

(3) Q: Clearly the best path forward, to improving simulation capability would be to design and execute experiments (or perform accurate theoretical calculations) of the few key reactions, notably the recombination reaction H+O2+M --> HO2 and related HO2 reactions…

A3: It is well-known that measuring the rate coefficients or radicals including HO2 at the severe conditions of 10 MPa and 20 MPa, while valuable, is impossible due to absorption ratio signal saturation. The authors agree with the reviewer to have more in-depth experimental techniques to be employed, such as speciation of stable species by sampling method. However, such effort induces huge challenges and is well beyond the scope of this work.    

----------------------------end of the rebuttal------------------------------

In the second round of review, a fourth reviewer was added and reviewer 4 also highly regarded our work. Reviewer 2 and Reviewer 4 also commented on some reviews made by Reviewer 1 and Reviewer 3. We sincerely appreciate the help, fairness and time devoted to the review of our manuscript from reviewer 2 and reviewer 4. Below is the full rebuttal for the second round review. There is no page limitation for the second rebuttal. I suggest you read through the non-technical parts in the rebuttal below for more details.

----------------------------------- our second rebuttal-----------------------

Rebuttal for Request Revision of PROCI-D-19-01072R1

High Pressure Ignition Delay Times of H2/CO mixture in Carbon Dioxide and Argon Diluent

We respectfully request the editor to scrutinize the reviews and potential conflict of interest from Reviewer 1 and Reviewer 3. Reviewer 1 and Reviewer 3 are clearly biased and not professional in our opinion. We appreciate the positive reviews and recognition of the value of this work from Reviewer 2 and Reviewer 4. Especially, comments from Reviewer 2 and 4 on Reviewer 1 and 3’s reviews are greatly appreciated.

Reviewer #1: “Comments summarized in italics before rebuttals”

Q1: This paper can be summarized as ignition delay time measurements in essentially a hydrogen mixture (with just 5% of the fuel containing CO) in CO2. Majority of the work is done at or below around 100 bar while, ONLY 3 data points are provided near 200 bar. The experiments were performed with just ONE composition (no change in equivalence ratio or fuel composition or relative hydrogen to CO ratio). There exists already ignition delay time measurements in the literature for hydrogen and hydrogen/CO mixtures in the literature by both Hanson and Vasu groups. Hanson and Vasu groups have provided measurements in multiple mixtures and span pressure higher that what is presented in this paper. In terms of the modeling, because the mixture is hydrogen dominated, it is not a surprise that CO does not have any effect. Therefore, the impact of the work is very marginal and does not represent the standards expected for the symposium.

R1: As pointed out by both Reviewer 2 (in first round review): “The experimental data are new and valuable…” and Reviewer 4 (in second round review): “Within the constraints of the mixtures they could prepare I think they have chosen a reasonable set a reasonable set of mixtures. They have varied the stoichiometry, changed the bath gas from CO2 to Ar, and doubled. There are only three data points at 20 MPa but these are well spaced in T5 and at other conditions there are plenty of data points. Given the length of a symposium paper, I think the authors have provided an adequate amount of data when considering the complete set presented.”

Please be reminded that the experiments were performed under different conditions with variation of both compositions and equivalence ratios. Obviously, statement in Q1 from Reviewer 1 is not true. There is no existing H2/CO mixture data and no comparison of its ignition delays in CO2 and Ar bath gases. This is the major contribution of this work. The previous work done by Vasu and Hanson (Ref [15] in the revised version) reports IDT data of H2 ONLY in CO2 bath gas. These two works are fundamentally different.

The statement in Q1 “In terms of the modeling, because the mixture is hydrogen dominated, it is not a surprise that CO does not have any effect.” is not true. We request Reviewer 1 read this paper carefully. Our simulation clearly showed the effect of CO at elemental reaction level (see Figure 7 and 8 in the manuscript). We also explained why such effect is washed out in IDTs.

Q2: Reviewer already referred these references and understood that combustion chamber in the Allam cycle will be at ~300 bar. So, if the aim of authors is to address combustion kinetics of Allam cycle, why is current experimental conditions are at ~100 bar? Authors stated that "In the Allam cycle, the turbine pressure ratio is expected to be 8-12, which translates into a combustor inlet pressure of 10-30 MPa". May be, authors would have admitted that their approach is an intermediate step to understand kinetics at 300 bar. But, altered inlet conditions of Allam cycle as "10-30 Mpa" to justify their 100 bar experiments.

R2: The experimental data we report here is at 100 AND 200 bar, which are above the critical pressures of mixtures. Given the similarity of results and no effect on results with doubling the pressure from 100 to 200 bar, it is reasonable to expect that the change of pressures by a factor of 1.5 does not show dramatic difference. No sorcery is expected to happen suddenly at 300 bar, and as long as the pressures remain above the critical pressure of the mixtures, it is sufficient for this application background. In the reference recommended by Reviewer 1 (Ref [13] in the revised version), 70-100 bar data are claimed relevant for sCO2 power cycle.

Q3:  I already shared a reference which has IDTs of syngas at ~100 bar. Even, authors are also doing experiments at 100 bar for so called "Syngas surrogate", essentially a hydrogen mixture. If authors are already aware of such work, why they are not cited in the previous or current manuscript? It is not fair to avoid citing existing literature and claim the novelty.

R3: Please be aware that the work (Ref [13] in the revised version) provided by Reviewer 1 was published on Nov. 5th 2019 online as a conference proceeding and this manuscript was submitted on Nov. 4th 2019 (the deadline of symposium manuscript was Nov. 7th). However, as far as we are aware of the publication, it will be cited (if it is relevant). The first work is now cited in the revised version of the manuscript (Ref [13] in the revised version). The second work reports IDT only at a pressure range of 34.58–45.50 atm (below the critical pressures of mixtures), which is not relevant for the theme of this paper. Pleases also refer to the comment from Reviewer 4 on this matter. 

Moreover, it is very reasonable that researchers will not be aware of the publication immediately within days after it is published. Reviewer 1 also should notice that the work from Vasu’s group (Ref. [13] in the revised version) did not cite our previous work on high pressure CH4/O2/CO2 IDTs (Ref. [14]) which appeared online on March 2019. The comment/blame from Reviewer 1 “It is not fair to avoid citing existing literature and claim the novelty.” is unreasonable and biased.

Q4:  I request authors to read the work "Kouremenos, Dimitrios A. "The normal shock waves of real gases and the generalized isentropic exponents." Forschung im Ingenieurwesen A 52.1 (1986): 23-31". As per this work, when the normal shock wave of an ideal gas is considered, both flow conditions immediately in front of and behind the normal shock wave are isentropic relative to their corresponding stagnation points. For that reason, the relations of the isentropic flow are used to connect the state variables, on both sides of the normal shock, to the corresponding stagnation points. The same way can be followed for the case of the real gas as, but here, for the real gas, the two different isentropic exponents appear instead of the constant ideal gas exponent. Identifying appropriate real gas exponents in shock calculations is important before understanding the need of real gas equation-of-state. None of the citations mentioned by author talk about how these exponents are computed.

For ideal gases, isentropic pressure exponent is just γ. But, for real gases it is γ?〖Pβ〗_T where P is the pressure and β_T is the isothermal compressibility. So, before justifying the need of Peng-Robinson in shock relations, one must justify the coefficients used in their shock relations.

Next, as I mentioned in my previous comments, Peng-Robinson EOS is an empirical equation and historically developed for petroleum industries. We need to validate for our conditions before using. So, Peng-Robinson is not a benchmark prediction for all real gases. When it has no difference with ideal gas predictions, we can't say that the real gas effect is negligible. Citing previous works is not a justification, especially when people are historically presenting similar methodology.

R4: First, comprehensive analysis and discussion on the applicability is well beyond the scope of this work. Ideal gas equation is used in both references recommended by Reviewer 1 (Ref. [13] and Ref. [15] in the revision) at similar conditions in terms of pressures (100-300 bar), temperatures (1000-1600 K), and mixture compositions. As pointed out by Reviewer 4, why ideal gas assumption is justified and valid in those two references but not in this manuscript?

Second, the thermodynamic variables, such as γ of all gases in this study are calculated by REFPROP from NIST, which is a state-of-the-art tool for such calculations. The compressibilities of the mixtures are all between 1 to 1.1. This can also be justified by the work from Kouremenos. Figure below is from the paper from Kouremenos required by Reviewer 1. It can be clearly seen that the ratio of different isentropic pressure exponent γ (k in the figure) are between 1 and 1.1 at the conditions covered in this study (Pr~1-3, Tr~4-5). This is simply because of the conditions in the study are away from the critical point. 

To clarify this issue, additional explanation is added in the revision: “…. Moreover, ideal gas assumption was employed at similar pressure and temperature conditions in Ref. [13-15]. Therefore, without further detailed justification, which is beyond the scope of this study, the ideal-gas EoS is used in the remaining analyses. ” on page 8 of the revision.

Q5: Here is a statement from the reference that authors have cited:

Incorporating non-idealities decreases the predicted ignition times by approximately 20% between the R-K and ideal gas EoS simulations at a pressure of 40 atm. Although the non-ideal effects are moderate at 40 atm, they increase in significance at elevated operating pressures. At p = 80 atm, the relative difference between ideal and real gas EoS predicted ignition delay times is roughly 50% in the NTC region.

I request authors to refer, "Manikantachari, K. R. V., Vesely, L., Martin, S., Bobren-Diaz, J. O., and Vasu, S. (April 26, 2018). "Reduced Chemical Kinetic Mechanisms for Oxy/Methane Supercritical CO2 Combustor Simulations." ASME. J. Energy Resour. Technol. September 2018; 140(9): 092202. https://doi.org/10.1115/1.4039746". This paper states that, effect of EOS on IDTs is dependent the mixture and operating conditions. So, we can not generalize it for every mixture and avoid using real gases. Also, even the choice of kinetic mechanism can influence the difference between various EOS.

We understand that ignition delay is an important aspect but not enough to describe combustion phenomenon in a shock tube. For example, as per the definition of authors, IDT is the point in the time history of OH* where the profile has maximum slope. Now, this IDT can't describe what is the peak OH* concentration and where it is and how heat release rate is happening in the reactor. Now, if real gas EOS has no affect on this IDT, it does not necessarily mean that it has no effect on heat release rate as well. Authors can't extrapolate this to do a sensitivity analysis with ideal gas assumption and avoid real gas effect to conclude on chemical pathways. Sensitivity has much to do with heat release rate than OH* maximum slope.

So, using ideal gas assumption for sensitivity analysis is not correct for the operating conditions that authors targeted.

R5: Please refer to R4 regarding the ideal gas assumption.

Review 1 is asking self-contradicting questions. The work requested to be cited (Manikantachari, K. R. V., Vesely, L., Martin, S., Bobren-Diaz, J. O., and Vasu, S. (April 26, 2018). "Reduced Chemical Kinetic Mechanisms for Oxy/Methane Supercritical CO2 Combustor Simulations." ASME. J. Energy Resour. Technol. September 2018; 140(9): 092202) used PFA to generate reduced kinetics. PFA means (chemical) path flux analysis and it is developed by one of the authors of this manuscript. It uses ideal gas assumption and conduct chemical reaction pathway analysis. The work by Manikantachari et al. justifies the validity of ideal gas assumption, reaction pathway analysis and sensitivity analysis using Aramco 2.0 under the conditions of this study as they employed the same approach as this study.

In the work by Manikantachari et al., the authors showed that ideal gas assumption has the best prediction of H2 IDTs, therefore ideal gas assumption was used in majority of IDTs calculations. They also pointed out that IDT calculations from different EOSs are within the uncertainty limits except SRK EOS for H2 mixtures. They also found that different EOSs have larger effect for H2 mixture than CH4 mixture, however still within the uncertainty of experiments. The larger deviation for H2 mixture (comparing to the results for CH4 mixture) is mainly due to extremely short IDTs for H2 mixture (H2/O2/CO2=10/5/85) compared to CH4 mixture, in our opinion.

Aramco 2.0 is used in the paper by Manikantachari et al. and its title clearly indicated it is for the application of sCO2 combustion. This is contradicting with the initial review from reviewer 1 that Aramco 2.0 should not be used for sCO2 combustion.

Regarding heat release, the mixtures in this study are highly diluted to avoid significant heat release. After ignition, the temperature increase is less than 10 K. This can be justified from the nearly constant pressure trace before and after ignition at 200 atm condition (Figure 1 (a)). In the sensitivity analysis, 4 K temperature rise is used to define ignition point because of the large heat capacity and low fuel concentration. Therefore, heat release is not a concern in this study. To clarify, “…To avoid issues caused by significant heat release and different heat capacities, low fuel concentration is employed in this study. Therefore, temperature and pressure are almost constant before and after ignition events with CO2 as the diluent. In the sensitivity analysis, temperature rise of 4 K is used to define the ignition point and it is consistent with experimental observation. …” is added in the revision on page 9.

To clarify the effect of EOS on IDT calculation, below figures are added in the supplemental material. In the revision, “…The comparison is shown in Figure S1 in the supplementary document.….” is added on page 8 and the figure below is added to the supplemental material document. 

The work by Manikantachari et al. is focused on reduced kinetic models and the discussion on EOS is very vague and brief. It is less relevant to be referenced.

Q6: Previous studies as mentioned by authors do not talk about chemical pathways in sCO2 combustion. To understand chemical pathways, we must use a validated mechanism, not just a closest mechanism based on IDTs alone.

R6: Please refer to the comments from Reviewer 3 and Reviewer 4. There are no validated mechanisms. However, it does not prohibit performing simulations using existing kinetic models to improve our understandings. Calculation of IDTs is just a reflection of cumulative effects of chemical pathways. Following Reviewer 1’s logic, no one should calculate IDTs before a kinetic model is validated. Reviewer 1 needs to be educated that kinetic model developers conduct chemical pathway analysis to develop their models.

Moreover, the work by Manikantachari et al. (required by Reviewer 1) used Aramco 2.0 and conducted chemical pathway analysis and sensitivity analysis. It justifies the validity of numerical approaches used in this study.

Once again, this comment is self-contradicting and uses double standards.

To address the comments/questions from Reviewer 1 in initial reviews, the details on sensitivity analysis is clarified in the revision on page 9 as “…brute-force sensitivity analysis on IDT is conducted… In sensitivity analysis, temperature rise of 4 K is used to define the ignition point and it is consistent with experimental observations….” 

Reviewer #2: “Comments summarized in italics before rebuttals”

It is interesting that the 3rd reviewer rejected the paper because the experimental data were in good agreement with the model predictions and hence concluded the experiments weren't necessary! That statement sets a terrible precedence.

The authors have responded adequately to the other comments. 

A: The authors greatly appreciate the understanding and the support of the reviewer.

Reviewer #3: “Comments summarized in italics before rebuttals”

Q: I am disappointed in the authors' rebuttal. They propose no corrective refinements of substance but rather mostly argue that the reviewer's comment are not correct. My continued opinion is that this paper fails to add substantially to current knowledge. Equally or more important is my concern that the authors hold strong to their view that the IDT data presented serves to validate the detailed kinetic models utilized. While agreement of detailed kinetic simulations with IDT data is necessary, it is certainly not sufficient to "validate" a many-reaction kinetic mechanism or model. The very fact that all the models tests match their data, while the models differ in detail, serves to make the point that model validation isn't feasible with single measurements such as IDT. Perhaps this is a question of terminology, but the tone of the authors' comments suggest that their definition of validation is a confirmation of the detailed mechanism or model. I also take issue with the authors rebuttal point that measurements of the key reaction H + O2 + M is impossible by experiment. It isn't necessary to match the conditions of the current experiments precisely in order to provide an improved value/determination of this rate coefficient that hold at the conditions of the current experiments.  

In summary, I find no need to modify my rating of this paper after reading the authors' rebuttal. 

R: The authors replaced the term “validation” by “evaluation” or “assessment” in the revised manuscript. Indeed, validation of a kinetic model requires extremely substantial efforts with huge amount of data. Strictly speaking, kinetic model evaluation or assessment is more accurate. We believe this is a terminology issue similar to “kinetic model” or “kinetic mechanism”.

Measurement of H+O2+M reaction is a classical challenge and a complete different scope from this work. Its measurement has been done mostly at relatively low-pressure conditions. See recent work from Shao et al. (Shao, Jiankun, et al. "Shock tube study of the rate constants for H+ O2+ M→ HO2+ M (M= Ar, H2O, CO2, N2) at elevated pressures." Proceedings of the Combustion Institute 37.1 (2019): 145-152.) showing measurement up to 33 atm. The authors of this paper clearly pointed out that the rate constants found are consistent with earlier studies. Therefore, there is no need to repeat these measurements at low pressure conditions. The results from Shao et al. agreed with both previous results and modeling, so it should have not been published using Reviewer 3’s standard. 

Moreover, the reaction rate of H + O2 + M is a strong function of pressure and temperature. Therefore, measuring the reaction rate at conditions well below the critical point of the mixture (e.g. at its low pressure limit) does not provide much intuitions about the kinetics at supercritical conditions. Please also refer to comments from Reviewer 4 regarding this matter.

The authors feel sorry that Reviewer 3 is disappointed because of no corrective refinements of substance in the rebuttal. However, we are also confused by Reviewer 3 because no technical questions/comments were raised by Reviewer 3, but simply considering the data provided by this work is not valuable. Once again, we respectfully disagree. As pointed out by Reviewer 2, “the 3rd reviewer rejected the paper because the experimental data were in good agreement with the model predictions and hence concluded the experiments weren't necessary! That statement sets a terrible precedence.”

There are no other technical questions/comments from Reviewer 3 in initial review.

Reviewer #4: “Comments summarized in italics before rebuttals”

Q1: I have reviewed the revised manuscript, the authors rebuttal to the Reviewers comments and the responses of the Reviewers to the rebuttal. In addition, I have obtained copies of the papers that Reviewer 1 cited in point 3a and 3b of their original review - these seemed pertinent to much of the discussion. I note that in the original manuscript, it would have been hard for the authors to refer to the paper cited in 3a, it was published on the Web only on the 5th Nov 2019. It is relevant and could be cited in the revised manuscript. The citation in 3b is less relevant, covers experiments much closer to 50 bar than 90-200 bar of the current work and maybe below supercritical conditions.

R1: The authors agree with the reviewer and we have paper 3a cited (Ref [13]) in the revised manuscript.

Q2: The experimental work in the submitted manuscript appears to have been performed well and due consideration given to the challenges of interpreting data from high pressure experiments in sCO2. Comments are made about the challenges of ignition in the boundary layer and why the authors subsequently chose to make emission measurements through the endwall, rather just at the sidewall. The experimental results are reasonable and will be of use to the modeling community.

R2: The Authors would like to thank the reviewer for understanding and acknowledging the value of the data presented in this paper.

Q3: These were challenging experiments to do and provide much needed data to test mechanisms against The data are in a regime where there is little experimental data. I would point out that these experiments, by themselves, do not validate a mechanism. The work simply demonstrates that the mechanisms used can provide reasonable simulations of the data. I think some confusion has arisen in the rebuttal and responses regarding 'validation'. I also think it important that the authors avoid the use of the terms 'syngas' and 'syngas surrogate'. The term 'syngas fuel mixture' is used on page 4 of the manuscript, contrary to the authors rebuttal to point 4 of Reviewer 1. If the authors want to call their mix a syngas surrogate then they should define why it is a surrogate. Simply, calling it a H2/CO mix that is relevant to syngas chemistry would be adequate.

R3: Indeed, we agree with Reviewers on the use of “validation”. We replaced the term “validation” by “evaluation” or “assessment” in the revised manuscript. We also replace the terms “Syngas” and “Syngas surrogate” by “H2/CO mixture” in the revised manuscript. Thank you for pointing this out.

Q4: On the whole, I am in agreement with the comments of Reviewer 2.

R4: The authors greatly appreciate the support from the reviewer.

Q5: I do not agree with comments from Reviewer 3 that the data could have been obtained simply by running kinetic simulations and that they have no value. Furthermore, Reviewer 3 demands experiments that are probably not feasible with current techniques.

R5: The authors strongly agree with this comment. Thank you.

Q6: Reviewer 1 raised a large number of points focusing on ideal gas and real gas. The authors have made some arguments in the manuscript about why the sCO2 mixtures they studied can be treated as ideal from the perspective of calculating post-shock conditions. i note, that in the articles cited by Reviewer 1 in points 3a and 3b that shock tube experiments were performed in similar mixtures to those in the current work and that there is no discussion of real gas effects in those articles. The standard shock equations, based on ideal gas, are used and assumed to be valid. If ideal gas holds in these articles, particular the one in 3a where conditions are very similar to the lower P of the submitted work, why does ideal gas not hold in the current work? The authors could, perhaps, focus their discussion of real-gas effects somewhat better. They could also refer to other works at not dissimilar conditions, as they do in their rebuttal, to support the contention that ideal gas is fine for calculating T5 and P5 near the endwall of the shock tube.

R6: The discussion of the choice of equation of state is revised correspondingly in the revised manuscript and further work (Ref [35] in the revised version) are cited as recommended by the reviewer.

On page 8, “…Moreover, ideal gas assumption was employed at similar pressure and temperature conditions in Ref. [13-15]. Therefore, without further detailed justification, which is beyond the scope of this study, the ideal-gas EoS is used in the remaining analyses.   …” is added to further explain the choice of EoS.

One figure (Figure S1) is added in the supplemental material document to compare the IDTs calculation using ideal-gas EoS and Redlich-Kwong (RK) EoS.

Q7: There also seems to be some contention about the use by the authors of Aramco 2.0 to simulate their results. I note, that both of the papers referred to by Reviewer 1 in point 3 use Aramco 2.0 to simulate OH* profiles in near supercritcal and supercritical syngas combustion. Again, why is one use acceptable and the other not? I come back to the point I made above, that simulating the ignition delay times and OH* profiles does not validate a mechanism. It simply means the mechanism can reproduce those data, to some degree. I do no think the authors are trying to validate any of the mechanisms they used. They are mainly showing how well they reproduce their results and where some problems might be in the mechanisms.

R7: The authors completely agree with the reviewer. As mentioned earlier, the use of the term “validation” is modified in the revised manuscript. Please see the response to Reviewer 3. 

Q8: There is discussion about the range of experiments presented by the authors. Within the constraints of the mixtures they could prepare I think they have chosen a reasonable set. They have varied the stoichiometry, changed the bath gas from CO2 to Ar, and doubled P5. There are only three data points at 20MPa but these are well spaced in T5 and at other conditions there are plenty of data points. Given the length of a symposium paper, I think the authors have provided an adequate amount of data when considering the complete set presented.

R8: The authors would like to thank the reviewer for the support and detailed attention to the methodology used in this work.

Q9: A minor comment: The authors should consider revising Fig.1 At the least an expanded portion of FIg.1a should be provided to show the detail in the pressure profiles in the first 100 us or so. I also suggest the authors consider using different line styles as well as color if the figures are to be printed in B/W.

A9: These changes to Figure 1 are made in the revised version of the manuscript. The line styles are correspondingly adjusted in Figure 1 to fit B/W print. Thank you for pointing this out.

----------------------------end of the rebuttal------------------------------

After the second round review, our manuscript was accepted. The rebuttals are as long as the paper itself. So I think they deserve a publication somewhere. Of course, I hope this will never happen to you. Please do not speculate who were the reviewers because that’s not helpful. What you need to do is to respond with solid technical evidence. Let’s simply be professional and honest. That is the bottom line of a researcher.