Evaluation of the Gas Content in Archived Shale Samples: A Carbon Isotope Study

Round 1

Reviewer 1 Report

In this paper, Frantisek and coworkers investigate the effects of diffusion on the composition (relative content and d13C) of the gas contained in shales, both kept as rock chips for decades or freshly collected. They recalculate the initial gas content and give estimates for the apparent diffusive fractionation factors during gas loss.

In its current state, the paper is not ready for publication. The analytical methods are sound and the data set is potentially of interest to advance our understanding of diffusion/desorption of gases from shales. However, the analysis of the data is lacking and the discussion stays at the comparative level with other studies. The presentation is also inadequate. There are many mistakes in the syntax or usage of words (I sympathise as I am also not a native speaker). The organisation of the manuscript should be re-evaluated: categories are redefined with the same letters in 2 places, the assumptions for calculations are not made explicit, and necessary pieces of information are not well organised within the manuscript.

Specific remarks and comments:
The syntax is generally understandable but clumsy or not correct in places, but some portions of the text are worse than others in that respect. The manuscript could be much improved on that front. One very common mistake is the omission of 'the' or 'a'.

Vitrinite reflectance given for B and C but not A.

What is the provenance and d13C of the acetanilide used as a standard for the carbon isotopic analysis?

ll 106-108: I do not understand what the authors mean by "as a standard, about three [...] to be injected inside".

ll 114: "measured on another line": the phrasing is a bit awkward. Is there a second, separate crushing experiment for d13C? For consistency, the same details about the GC procedure should be reported for both (He flow, temperatures and rates).

The description of the sampling loop and its use are unclear. On figure 2 it looks like the mill is connected to the sampling valve, but in the text we read that the gas is injected in the system manually. From the volumes of the loop and the injections, several shots are necessary to fill the loop.

ll 146: the equation does not appear correctly in the manuscript. I can only see Deff = DAM* R, with no τ visible.

ll 148-150: it is not explained clearly why higher hydrocarbons diffuse more slowly relatively to methane compared to what can be expected from the relative masses. This should be rephrased to explain how surface interactions cause those differences, that are enhanced by high tortuosity.

l 151: it's not the measured, it's the actual isotopic ratio that changes with the given model.

l 161: loses not looses. The sentence is a bit strange too. "The residue is progressively enriched in heavy isotopes". The next two paragraphs in section 2 are also difficult to understand. "acceptable agreement" should be described in a quantitative way here.

There is an unstated assumption in the model chosen by the authors: they describe the hydrocarbons as a reservoir of gas surrounded by air. Gas loss by the samples is by diffusion of individual alkane molecules through air. It may be that this is an adequate model to understand gas loss from the shales, but there are two potential issues with it:
1) it does not deal with adsorption of hydrocarbons on surfaces, and progressive desorption (possibly with fractionation factors different from diffusive fractionation)
2) it assumes that the hydrocarbon molecules diffuse in the porous media through air (rather than diffusion through methane).

Figure 3B is too busy and difficult to read and interpret. Another vertical scale (log) may be helpful to separate those overlapping curves.

In the description of the results, this sentence "Higher thermal maturity is also reflected in increased S1 (up to 0.09 mg HC/g rock) and S2 (up to 1.1 mg HC/g rock) values" seems inconsistent with the ranges obtained on the samples described as less mature.

l200: "Studied samples were distributed into three groups (A, B, and C) by thermal maturity and kerogen type": previously in the manuscript A B and C were attached to the geographical origin of the samples. Looking at the tables it seems there is 100% agreement between the two classifications but this may cause confusion for the reader.

There is no clear explanation of how C0 are calculated to yield the plots in figure 5, just a mention of "extrapolation of gas chromatography data". The reader is referred to Table 3 for the initial δ13C. This should be described more precisely or in a more organised fashion. Was it by projecting back to a gas composition like the starting one in figure 3A? Is that appropriate for B where there are up to 3 times as much ethane and propane as modelled at low % of methane loss? Some of the assumptions for the calculations are found explicitly only in the conclusion ("To find a common solution for the entire set, we assume that we analysed one sample in a different stage of the gas loss").

There is no mention of what 'Ex' refers to in the last line of the tables before figure 6. In all tables there are formatting issues with the special characters, and in table 1 the third column has the minus sign and the number for all but two of the entries on 2 lines.

The discussion does not contain new insights and stays mostly descriptive, putting the measured value in context of other studies rather than expanding.

Figure 6 looks like a Chung diagram, but with the number of carbon atoms rather than the inverse of it on the x-axis. It is interesting to see that methane is closer to the source rock than ethane for B and C, and that the pattern is very different from the one obtained from the model of fractionation suggested by Chung et al (with the methane being most fractionated compared to the kerogen from which it originates). The authors do not comment on this.

About half of their samples also have higher propane than ethane concentrations. They also do not comment on this or on the effect this has in reconstructing the initial gas contents.

In the conclusion the fractionation values for ethane are misreported. There is no explanation of the range given in for the fractionation factors in the rest of the paper. The "very near" statement is not substantiated, or quantified.

Author Response

Please see attachment

Author Response File: Author Response.docx

Reviewer 2 Report

Line 18-19: Quantification or some comparison required, instead of “consistent”.

Line 39-48: The introduction need to be expanded by describing the similar kind of work done by other researchers, may be some hint of other unconventional resources, like, coal bed methane etc.

Line 58-61: Figure of lithostratigrapic, EPOCH, period required, and another figure showing the location map from where sample taken. Sample depths ? formation pressure and stress regime ?

Lilne 90: is centrifuge used during the water washing ?

Line 146: The equation 3 is not completely visible in the pdf file.

Line 131: include this method explicitly in the abstract clearly.

Table 1, 2 and 3: graphical comparison with the literature is required for results presented in these tables.

Table 2: change the gas volume unit from L/g to m3/tonne

Table 1: Classify source rock based on TOC using the table 3 of

Bacon, C., C. Calver, C. Boreham, D. Leaman, K. Morrison, A. Revill and J. Volkman (2000). "The petroleum potential of onshore Tasmania: a review." Geol Surv Bull 71: 1-93.

Line 238: any canister type desorption test from the similar location can be address from the literature to get an idea about q1 q2 q3 gas contents.

Author Response

Please see the attachmnet

Author Response File: Author Response.docx

Round 2

Reviewer 1 Report

The manuscript has been modified to answer many of my comments. The
core criticism I had was that the paper stayed too descriptive and was
just putting their data in context, the authors acknowledge this in their answer, so it is up to the editor in that regard. My Overall Recommendation below assumes that the editor agrees with the authors that the scope of the paper is adequate.

Nevertheless, there are still many specific points that have to be
addressed or corrected in the manuscript.

There is an inconsistency between line 99 and 128 about the reproducibility of the δ13C measurement (0.1 vs 0.5 permil).

l171 the first sentence is not grammatically correct and I am not sure
of the intended meaning of the next sentences until equation 5. I do
not understand what the authors mean by expression the chemical
composition in relative volume percentage.

There is a contradiction between the text ll188-189 that says a
different initial composition is chosen for C and the caption of
figure 3 that says the same initial composition is used for A, B and
C.

ll228 to 234 the authors have added some discussion about how their
model results for the group B do not fit well with the natural
data (high C2+ concentrations and C3>C2), and calculate for figure 5
how much ethane was lost, which is between 20 and 60% (using the
values of the x-coordinate in fig 5B). 1) if the same calculation is used on A or C do they obtain low percentage of ethane loss consistent with their assumptions? 2) They say ll237-238 that they used the volume reduction from the methane model, but it is not clear to me how that value was used.

In figure 6B (the added Chiung diagram), we can see that the isotopic
pattern for B and C are reversed compared to the classical case:
propane is more depleted in 13C than ethane. The statement about
upward convex (l 270) is incorrect here and the reference (Chung 1988)
does not state that the shape will change, but that the slopes will get
shallower with larger extent of cracking. The interpretation for
ethane heavier than propane given by Chung is mixture of different
sources (in section 4.2 of the Chung paper - although isotopic reversal have been observed in shale gases and interpreted differently since, i.e. Zumberge et al 2012).

Section 4.2 of the current paper starts with the assumptions of the
calculations made in the earlier sections. This should have been
earlier in the manuscript (in the current section 2.3).

I commented on the first version that "in the conclusion the
fractionation values for ethane are misreported. There is no
explanation of the range given in for the fractionation factors in the
rest of the paper. The "very near" statement is not substantiated."
Although in their answer to the reviewers the authors put "added",
there is no difference in the conclusion from the first version.

Author Response

Open Review 2

(x) I would not like to sign my review report
( ) I would like to sign my review report

English language and style

(x) Extensive editing of English language and style required
( ) Moderate English changes required
( ) English language and style are fine/minor spell check required
( ) I don't feel qualified to judge about the English language and style

 

	Yes	Can be improved	Must be improved	Not applicable
Does the introduction provide sufficient background and include all relevant references?	(x)	( )	( )	( )
Is the research design appropriate?	( )	(x)	( )	( )
Are the methods adequately described?	( )	( )	(x)	( )
Are the results clearly presented?	( )	(x)	( )	( )
Are the conclusions supported by the results?	( )	(x)	( )	( )

Comments and Suggestions for Authors

The manuscript has been modified to answer many of my comments. The
core criticism I had was that the paper stayed too descriptive and was
just putting their data in context, the authors acknowledge this in their answer, so it is up to the editor in that regard. My Overall Recommendation below assumes that the editor agrees with the authors that the scope of the paper is adequate.

Nevertheless, there are still many specific points that have to be
addressed or corrected in the manuscript.

 

There is an inconsistency between line 99 and 128 about the reproducibility of the δ13C measurement (0.1 vs 0.5 permil).

99 – 0.1 it is reproducibility of ¹³C measurement via elemental analyzer

l.128 – 0.5 in this case we consider external reproducibility of ¹³C measurement of C1,C2 for newly crushed sample. Added to the text

 

l.171 the first sentence is not grammatically correct and I am not sure
of the intended meaning of the next sentences until equation 5. I do
not understand what the authors mean by expression the chemical
composition in relative volume percentage.

l.171 – rewritted

Following paragraph would explain changes in chemical composition of the gas mixture after loss of one component. Using of C in Eq. 5, leads to misinterpreation - we decided to remove all the paragraph and continue without Eq. 5.

 

There is a contradiction between the text ll188-189 that says a
different initial composition is chosen for C and the caption of
figure 3 that says the same initial composition is used for A, B and
C.

I agree – a new Figure 3 was prepared – 3A which corresponds to the model calculation of changes in composition of the gas mixture No.1 together with the composition of samples from A and B formations; and 3B which represents changes of composition of the gas mixture No.2 and samples from C formation.

 

ll228 to 234 the authors have added some discussion about how their
model results for the group B do not fit well with the natural
data (high C2+ concentrations and C3>C2), and calculate for figure 5
how much ethane was lost, which is between 20 and 60% (using the
values of the x-coordinate in fig 5B).

I agree – there is discordance with measured C2+ data – but these are not natural data, just residuum after significant gas loss – we try to explain it better in the following text

 

1) if the same calculation is used on A or C do they obtain low percentage of ethane loss consistent with their assumptions?

-No, it is not consistent with a simplified assumption of methane loss only. We really lost up to 60% of C2 on some samples, but we do not have any data on the initial gas composition, and get back some estimates we have to do significant and limiting assumptions. First – we assume that samples are losing mainly methane. To estimate it, we simplified the calculation and removed just methane only. It helps to explain the unusual chemical composition of residual s gases. Second – isotopic composition of ethane is changing with changes in chemical composition, so there proceeds true loss of ethane and process similar to methane loss. But it can be evaluated only within validity of the first assumption. So we supposed that ethane loss proceeds after methane loss. We used calculated model composition of residual gases (C2, C3 etc) for methane loss as the estimates of initial C2₀ concentration before ethane loss. Measured concentrations of C2 were nearly always lower (with two or three exceptions, which are visible on Fig.3 – out of calculated changes in composition). Ethane loss was evaluated as a difference between model calculation after methane loss C2₀ and true measured concentrations. In this way we could evaluate ethane loss i.e (C20-C) and calculate the fractionation. Text was added to explain it in details.

 

2) They say ll237-238 that they used the volume reduction from the methane model, but it is not clear to me how that value was used. – see previous paragraph.

 

In figure 6B (the added Chiung diagram), we can see that the isotopic
pattern for B and C are reversed compared to the classical case:
propane is more depleted in 13C than ethane. The statement about
upward convex (l 270) is incorrect here and the reference (Chung 1988)
does not state that the shape will change, but that the slopes will get
shallower with larger extent of cracking. The interpretation for
ethane heavier than propane given by Chung is mixture of different
sources (in section 4.2 of the Chung paper - although isotopic reversal have been observed in shale gases and interpreted differently since, i.e. Zumberge et al 2012).

I agree – I know that explanation was weak and not correct but discussion of the origin of the isotope reversal seemed to be not very appropriate with so many simplification – we change it and added possible reversal effect origins within literature.We remind that d13C-C3 are only few so it is difficult to find possible solution. Samples from C formation have quite “heavy”d13C-C2 what supports formation of reversal effect.

 

Section 4.2 of the current paper starts with the assumptions of the
calculations made in the earlier sections. This should have been
earlier in the manuscript (in the current section 2.3).

We put it to the section 2.3. with details about C and C0 evaluation for methane. Details on the evaluation of ethane fractionation are in section 3.

 

I commented on the first version that "in the conclusion the
fractionation values for ethane are misreported. There is no
explanation of the range given in for the fractionation factors in the
rest of the paper. The "very near" statement is not substantiated."
Although in their answer to the reviewers the authors put "added",
there is no difference in the conclusion from the first version.

We try to do it better – more details about ethane fractionation, a part of discussion about assumption we did, fractionation during ethane loss is probably affected by desorption from organic in the rock but without experiments it is hard to prove it - we know that there are so many simplications about processes which are not well specified.

 

Submission Date

19 September 2019

Date of this review

31 Oct 2019 19:29:42

 

Author Response File: Author Response.docx

Round 3

Reviewer 1 Report

The authors have addressed the comments in my previous review point by point. In particular they reorganised the content of the manuscript and modified it to explain more clearly their calculations and the choices behind them (l180 and following). The new figure 3 is much easier to read and illustrates much better their work.

The language is still awkward and in a few places difficult to parse. The article would benefit from the help of the Editorial Office.

Specific comments:

l165: "Wher" instead of "Where".

l170: should be ""the light isotopes are preferentially released from the rock surface" instead.

ll180 to 186: 'mixture(s)' is a bit awkward here, 'model/assumed initial compositions' could be clearer

l189: missing 0 in C/C0 ratio

ll221-249: the results presentation is much improved.

l306: degassing instead of degasation

ll319-324 and 325-334: minor point, but this could be re-organised a bit: the authors explain how classical explanations for the reversal are unlikely here (321-322), but the explanation they can give for heavy ethane (resulting from gas loss) is only given l333.

l 334 The Conclusion header is not separated from the last paragraph of the discussion

Author Response

Dear reviewer,

We corrected all text errors we did (unfortunately). Last paragraph section 4 was rewritted to be better understable (I hope) – see below.

Propane isotopic reversal can arise from the formation of the “heavy” ethane also as we observed for the samples from Liten Formation (subset C). Samples have the highest TOC content (Table 1) what affects both the adsorption properties of shales and the carbon isotope fractionation during desorption. While isotope fractionation decreases during desorption with a decreasing content of TOC in the sample [8], conversely increasing adsorption capacity increases isotope fractionation during methane desorption [11]. Desorption affects the isotopic composition of the expelled gas because the light isotopologue is preferentially desorbed. Finally, the gas residuum (which is released after rock crushing) is isotopically enriched.

 

We have to thank you again for your help and kind understanding with our poor English. Your remarks and suggestions improved our MS very much and we appreciate it. It is a pity that we cannot thank you namely in acknowledgement.

English correction would be provided by Editor Office.

Yours sincerely

Frantisek Buzek

Author Response File: Author Response.docx