In this manuscript, the authors report on the ESI-CID-MS/MS data of a series of pentacyclic triterpenes displaying different skeletons. The importance of this class of compounds is undeniable due to the wide diversity of biological activities, and data about their fragmentation patterns are always important and useful.
Although the authors followed the standard methodology adopted to investigate gas-phase fragmentation reactions, I have found serious issues in this manuscript, as I have listed below.
The authors did not mention in the manuscript any stereochemical aspect of the fragmentation steps, so showing the configuration of the stereocenters in the product ion structures is completely unuseful. Please, remove the stereochemistry of all the Chemical structures.
Also, there are a huge number of mistakes in bond angles in all the schemes (e.g., m/z 191 in scheme 1 – please, check and remove the stereochemistry of the vinylic methyl and correct the bond angle).
Many aspects of the mechanisms are highly speculative. For example, in Scheme 1, the carbonyl oxygen is expected to be the most basic site, but the authors rather display the protonation at the hydroxyl oxygen of the carboxyl group. Why? In the same scheme, elimination of 18 Da occurs from the precursor ion (m/z 457) to produce m/z 439 (by the way, please, show “-H2O” above the reaction arrow). Which argument do the authors have to support that the first elimination of water does not occur from the hydroxyl group at C3 through a charge-remote fragmentation, which is energetically more favored as compared to fragmentation processes that require charge separation? Although I understand the point of view of the authors, there is no way of confirming this without theoretical calculations. Without theoretical calculations obtained by computational quantum chemistry, all of these beautiful and elegant ion structures the authors proposed become speculative.
In Scheme 2, the authors used the term “1,5-methyl shift” to refer to a called a “1,5-hydride shift”.
I strongly disagree with the occurrence of RDA reactions to produce unstable vinylic carbocations (e.g., m/z 217 and m/z 203 in Scheme 2), which display a high hydride affinity. If the authors would run theoretical calculations, these ions likely will be converter into other much more stable ion structures during the geometry optimization. Moreover, there are many others more elegant options that could lead to more stable ion structures. However, without theoretical calculations, they would be speculative as well!
In Scheme 3, compound 10 display a carboxyl and a hydroxyl groups like for compound 1 (Scheme 1). However, in this case, the authors proposed that the protonation occcurs at the hydroxyl group of the alcohol function instead of the OH group of the carboxyl group. Why?
Also in Scheme 3, it is not clear that the formation of m/z 187 from m/z 205 – some intermediate ion structure is missing. Again: without the theoretical calculations, the readers can think the authors proposed these ions structures because they are “elegant”.
In Scheme 4, the authors have chosen to represent the proton attached to the hydroxyl group instead of the carboxyl oxygen, then a RDA followed by a formic acid elimination occurs and nothing happened with the OH2+ attached to a tertiary carbon! This is at least highly unlikely, not to say impossible...
In Scheme 5, the coumaroyl moiety was drawn as a linear molecule – please, correct.
In summary, all the points I have listed here could be easily elucidated with the use of computational chemistry. I would like to see this manuscript published, but unfortunately, without the theoretical calculations and for the reasons I have discussed, this manuscript cannot be accepted for publication in RCM.

This is a revised version of the manuscript RCM-21-0163. The authors replied to the reviewers’ comments and stated that all the corrections suggested by the reviewers were incorporated in the manuscript. However, unfortunately, the authors did not highlight these corrections, so it is easier to review the whole manuscript than seeking for these corrections. Below, I have listed my comments, suggestions, and criticisms about this manuscript.
First, congratulations to the authors for the good experimental job. They have very nice data on their hands, but the discussion about these data needs improvements. I agree with the other reviewers about the importance of computational data, but the authors could write a very nice manuscript making some modifications in the way they deal with their data. For example, plots of collision energy versus relative intensity of the product ions should be used to identify “optimum” collision energy, in which the product ion spectra could be compared and the differences among them will be associated with their specific structural features. Honestly, I did not understand why the authors selected the collision energy of 20 eV, in which fragmentation of compounds 4 and 5 does not occur. Why did the authors not select the energy of 35 eV as optimum energy? Differences in the fragmentation routes are expected from one compound to each other, but this could be only mentioned in the manuscript in each case. I mean that it is more acceptable to show a product ion spectrum at 20 eV without product ions and mentioned that specific ions are formed only in higher collision energies than comparing the product ion spectrum in different collision energies. However, I think the analysis should be done at a collision energy value of 35 eV.
Second, the structure-fragmentation relationships the authors mentioned in the manuscript are not clear. The authors could think of the readers and prepare a map combining specific fragmentation processes (e.g., elimination of C2H4O2) and specific m/z values, which are divided into diagnostic and product ions (for example, m/z 203). This map could be easily obtained from a careful and detailed analysis of tables. For example, compounds that display a carboxyl group eliminate CO2. However, in principle, every compound displaying a carboxyl group in its structure will display the same CO2 elimination. On the other hand, the RDA eliminations produce ions with some m/z that could differ from 2 (presence of an additional double bond), 14 (a homolog or a compound with an extra oxygen plus a double bond) mass units. These ions and their m/z must be used to identify the nature of the substituents. This structure-fragmentation map could be useful for other authors to identify these compounds and their analogs based on ESI-CID-MS/MS (for example, DOI 10.1002/jms.4284).
Third, I totally understand the authors’ decision of using the brackets at the right top of the ion structure showing the structure as neutral and assuming that the charge can be everywhere. I agree that proposing a vinylic ion is not a good idea. However, I still think the authors could be more ambitious and show the positive charge at the tertiary allylic positions of the product ions, where they will be most stabilized. This will make the proposed fragmentation much more elegant. However, this is a personal comment and other reviewers could eventually disagree with me.
Other minor comments:
- The term “structural fragmentation relationship” sounds weird to me. I suggest the use of the term “structure-fragmentation relationship” throughout the manuscript.
- In the abstract: The sentence “... the presence of protonated molecules [M+H]+ of all analyzed compounds” is not true, as compound 1 underwent water elimination in the ionization source (see lines 120 and 121).
- Please, replace “Retro Diels Alder” with “Retro-Diels-Alder”
- “Structure-fragmentation relationships” are not developed; they are obtained or presented.
- In Keywords, I suggest including terms that are not in the title (e.g., retro-Diels-Alder) to increase the visibility of their work.
- On page 3: I suggest starting a new paragraph with “Over the past few decades...” (line 55)
- On page 4, please, move the sentence “The rapid 86 characterization and elucidation of the gas phase fragmentation pathways of pentacyclic 87 triterpenoids will be helpful for the identification of its congeners in other plant species” (lines 85-87) to the conclusions.
- On page 6, line 121, change “loss of water peak” to “peak due to water loss” or something similar.
In my opinion, this manuscript could be accepted for publication in RCM after major revisions.