Review History


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Summary

  • The initial submission of this article was received on August 13th, 2015 and was peer-reviewed by 3 reviewers and the Academic Editor.
  • The Academic Editor made their initial decision on August 26th, 2015.
  • The first revision was submitted on September 25th, 2015 and was reviewed by 3 reviewers and the Academic Editor.
  • The article was Accepted by the Academic Editor on October 15th, 2015.

Version 0.2 (accepted)

· · Academic Editor

Accept

The authors have addressed all concerns raised by the reviewers. Reviewers #1 and #2 are pleased with the revised manuscript. Reviewer #3 has some additional suggestions that are in the form of either comments for the authors to consider, or very minor proofreading edits.
Although I encourage the authors to take these comments on board at production stage, I do not believe a further round of revision is required at this stage, and thus consider that the revised manuscript is now acceptable for publication.

Reviewer 1 ·

Basic reporting

The major suggestions has been implemented in the revised verison of the manuscript.

Experimental design

no additional comments

Validity of the findings

no additional comments

Reviewer 2 ·

Basic reporting

The authors have adequately addressed my comments.

Experimental design

The authors have adequately addressed my comments

Validity of the findings

The authors have adequately addressed my comments

·

Basic reporting

Only a little mistake: in the caption relative to Figure 9, NaBH4 is said to be a catalyst, whereas it is a stoichiometric reagent.

Experimental design

The experimental description is now almost OK, just a couple of remarks:
When the authors describe the sample preparation before injection in GC or HPLC, they say the sample was dried and then dissolved in the appropriate solvent. How were they dried? Rotary evaporator (what T?), lyophilizer...?
Probably a portion of the mixture (buffer salts, protein) couldn't dissolve in the organic phase: were the samples maybe filtered or centrifuged?

Validity of the findings

I have only a little, still important, concern. When reducing the diacetyl, the enzyme appears to be quite selective, affording mostly (S) stereocenters. The authors state that, if some (R) acetoin is produced as an intermediate, then the enzyme creates a new (S) sterocenter, thus providing the meso compound (line 374). On the other side, the authors have not been able to detect any activity during the oxidation of the meso compound, which is actually the same reaction run from the other side. In other words, if the enzyme was (S) selective on both the two stereocenters, it couldn't catalyse the reduction of (R) acetoin. If, conversely, was (S) selective on just one stereocenter (the one involved in the reaction), the meso compound, which possesses a (S) stereocenter, would have been oxidised to (R)-acetoin, at least partially. See for example: Giovannini et al., Bioorg. Med. Chem., 4(8), p 1197, 1996.
What do the authors think?
Is it maybe possible that some racemization at the acetoin level occurs in the chosen reaction conditions?
Wouldn't be worthwile to run the reaction on racemic acetoin (I see it was done) and investigate the stereochemical outcome (been done, yet?)?

Comments for the author

In my opinion it would be worthwile to solve the little contraddiction I have outlined, also in order to be more accurate on the description of the enzyme stereospecificity.
Nevertheless, I reckon the quality of the manuscript has greatly improved, and I believe it is ready for publication after amending some little particulars.

Version 0.1 (original submission)

· · Academic Editor

Minor Revisions

The submitted manuscript will be of interest for the biotechnology and biocatalysis scientific communities, but I find myself in agreement with the reviewers regarding the need to make the experimental section more robust, and to reconsider how potential applications are presented.

I encourage the authors to implement as much as possible of the technical comments from reviewer 1, although I do not believe that additional experimental work is needed for the manuscript to be publishable. Concerning the implications for biocatalysis section, both reviewer 2 and reviewer 3 express concerns about a discrepancy between the depth of the experimental analysis and the statements made regarding the enzyme's potential applications. This discontinuity is perceived as a weak point in the paper. As both reviewers suggest, integrating existing data from the available literature and trimming out any conclusion that cannot be supported by the experiments here presented will significantly improve the message of the manuscript.

Considering the nature of the reviewers' comments, I am expecting to assessing an amended version of the manuscript soon.

Reviewer 1 ·

Basic reporting

please see attached review file

Experimental design

please see attached review file

Validity of the findings

please see attached review file

Comments for the author

please see attached review file

Reviewer 2 ·

Basic reporting

The manuscript submitted by Stankevičiūtė et al describes the biochemical characterization of the ketoreductase TpdE from Rhodococcus jostii TMP1. The text is generally well written and the experimental work is solid. From a practical perspective, this enzyme might find application in the enantioselective reduction of (di)ketones for the production of optically pure (di)ols. However, this aspect is not discussed very thoroughly (see further).

Experimental design

Because enantioselectivity is the key issue here, it seems strange that E- and/or ee-values are not reported. In fact, these parameters are not even mentioned once in the manuscript while they are standard references in this field. I understand that it might be too much work to determine them at this point, but I would suggest to at least discuss these parameters in relation to the available literature.

Validity of the findings

No comments

Comments for the author

No comments

·

Basic reporting

Figure 6 lacks an appropriate description: what do curves 1,2 and 3 represent, respectively?

Experimental design

It is possible to divide the manuscript in two parts: the former is about the biochemical characterization of the enzyme, the latter concerns the application of the described reductase in biocatalysis. Whereas the first part is consistent, well conducted and scientifically sound, the second part appears to be rather poorly described and does not allow a sufficient support for drawing the proposed conclusions.
Concerning the first part, I have only some remarks about the study of the enzymatic activity at different pHs:
- The appropriate pH interval in which TRIS-HCl should be used is 7-9: the point taken at pH 5.7 lacks some significance;
- How the authors explain the huge difference in activity observed (especially at pH 6) when different buffers are used?
Coming to the second part:
- Line 92: “Butan-3-one-2-yl nicotinate enantiomers were synthesized from nicotinic acid and
enantiomerically pure 2,3-butanediol…”. I imagine the authors here want to talk about the reduction products, so probably the sentence has to rephrased beginning with “3-hydroxybutan-2-yl nicotinate enantiomers…”. If this is correct, please provide a detailed experimental procedure for the synthesis of such compounds, including the relative amounts of the reagents (since diols are bifunctional, the reaction conditions have to be carefully chosen), the isolated yields and the chemical and chiroptical characterization (NMR, alphaD);
- Line 94: “HPLC-MS”. In the chapter “HPLC analysis” the authors describe an apparatus including a diode array detector only, without any coupling with a MS device. Please either erase the “-MS” label or describe the MS device. The same for Line 318.
- Line 304: “Biotransformation products of diacetyl were analyzed by GC-MS…”. Did the author employ the whole cells or the isolated enzyme? In the first case, please correct the “Whole-cell bioconversion” paragraph where it is stated that only HPLC was used, and provide a description of the sampling procedure from the reaction mixture and the relative workup before injection. Moreover, did the authors run a parallel blank experiment using E.coli cells not expressing the enzyme? This would be really mandatory in order to exclude parasite reactions coming from “indigenous” reductases and to better explain the results.
- Line 311: “…the oxidation reaction using optically pure 2,3-butanediols as substrates was conducted.”. How? Please provide a description in the experimental part. How was the reaction outcome analyzed? Did the meso-compound react?
- Line 322: “…the mixture of the reduction products, obtained using NaBH4 as catalyst, migrated as three peaks:…”. First of all, NaBH4 is actually a reagent and it is not a catalyst; then, again, an experimental description is needed. Moreover, weren’t the reference compound synthesized one by one through chemical coupling, as stated in line 92? What’s the point of carrying out a chemical reduction on the racemate?
- Line 323: “…three peaks:…”. Did the authors try to achieve a better separation of the mixture, for instance decreasing the polarity of the mobile phase?
- Line 326: “The same peaks were detected after biotransformation of racemic butan-3-one-2-yl-nicotinate…”. Why did the authors employ the racemic substrate, thus complicating the system? The reaction would be more conveniently run separately on each enantiomer in order to better understand the substrate acceptance of the enzyme. Moreover, a description of the sampling procedure and the workup before injection is necessary.

Validity of the findings

As stated before, the experimental part is not accurate enough to provide a sound base for the conclusions drawn in the manuscript. In particular, it is not possible to state that “TpdE catalyzes the stereoselective reduction of diketones to the corresponding (2S,3S)-2,3-diols.” (Line 313) employing only a single substrate (diacetyl). The stereochemical analysis of the reaction outcome should be applied to a more significant range of substrates in order to draw a general conclusion.
Also, the sentence “…the described bioconversions open a novel way for synthesis of unique lipid analogs such as 2,3-butanediols esterified with different carboxyacids.” (Line 335) is really too ambitious at this stage, with no data supporting the statement.

Comments for the author

The biochemical characterization of the enzyme is OK, but, if the authors want to promote it use in biocatalysis (see the manuscript title), the description of the biocatalytic procedures has to be far more accurate, and the product characterization should be precisely designed and conducted.

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