The manuscript by Wiame, et al. presents a first analysis of long‑lived ¹⁹F spin order in fluoroalkyl chains, building on the group’s previous works investigating long-lived ¹H spin order in aliphatic chains such as Sonnefeld et al. 2022, https://doi.org/10.1103/PhysRevLett.129.183203 ibid 2022, https://doi.org/10.1126/sciadv.ade2113, and Sheberstov et al, 2024 https://doi.org/10.1063/5.0196808.  Unfortunately, I feel that compared to those impressive works, the presentation of the current manuscript is uneven and, in many places vague, clumsy and confusing, and requires substantial improvement.  

It is very strange to me that the abstract claims the interesting results

“The lifetimes TLLS(19F) can be strongly affected by binding to macromolecules, a feature that can be exploited for screening of fluorinated drugs”.

And

“TLLS(19F) and T1(19F) should be longer at low fields where relaxation due to the chemical shift anisotropy (CSA) of 19F is less effective, as will be shown elsewhere”

but presents zero results about either of these in the current manuscripts.  I would strongly discourage this sort of “splitting results” across two papers.  It seems to me like the authors want to publish two or even more papers where they should really only be publishing one.

I would like to emphasize this using the most positive aspect of the paper - that the authors measured collective-¹⁹F singlet lifetimes that are longer than the ¹⁹F T₁ by around a factor of 3, which might indeed be useful in some applications. But the conclusions section begs the question what the relaxation times are at other magnetic fields.  Even if you went to a 300 or 400 MHz spectrometer, the lifetimes would be significantly different if there were a major contribution from chemical shift anisotropy (where the rate contribution is proportional to field squared)

If the authors already have these results in hand, as stated in the abstract, it would be poor conduct not to discuss these – at the very least, in some preliminary form – in the present paper directly.

Below is some more detailed criticism that I hope allows the authors to improve their manuscript.

1. The text lacks detail in many places. In many places, as detailed below, the authors’ claims are vague and to make any sense to readers these deserve explanation or extra qualification/quantitation.

Line 24, “The absence of background signals offers decisive advantages (Buchholz and Pomerantz)”.  Please help the reader by spelling out what these “decisive” advantages are.

Line 26, “Good contrast can be achieved in 19F NMR”.  What is “good contrast”?  Good is not an objective word.

Line 46, “These remarks apply to many molecules”. Please say what these are, give a few examples.

Line 88, “different symmetries of the spin permutation group”. Can you elaborate a bit further on this?  I think it is only a specific type of symmetry of the transition dipole operator that leads to long lived spin order, rather than “different” symmetries, so you can comment more explicitly about that.

Line 97, “their chemical shifts cover a sufficient spread”.  There is no indication of what “sufficient” refers to.  Needs clarification, preferably use alternative wording.

Line 120, “These OSTs are much harder to detect… because the scalar couplings are more favorable” is a sentence that I can appreciate the meaning of. However, it is again not objective, and will be nearly impossible to understand for most readers.

There are also a few very long and cumbersome sentences that need to be rewritten. Ideally as several sentences, to get the point across clearly. For example

Line 29, “The latter two effects can be distinguished by comparison of, on the one hand, conventional Carr-Purcell-Meiboom-Gill (CPMG) echo trains with high repetition rates required to suppress echo modulations due to homonuclear scalar couplings nJ(19F, 19F), which also inhibit echo decays due to intermediate exchange, and, on the other hand, slow CPMG echo trains using the so-called “perfect echoes” to eliminate the effects of nJ(19F, 19F) couplings while retaining the effects of intermediate exchange (Takegoshi et al., 1989; Aguilar et al., 2012; Lorz et al., 2025).”

Yes, that is one sentence.

Plus

Line 59, “The degeneracy of vicinal scalar couplings is lifted provided the potential wells of the different rotamers that result from rotations about the C-C bonds are not equally populated.”

This is shorter, but still more convoluted than it needs to be.

1. I have many comments on scientific rather than grammatical issues:

Line 16 (Introduction), the published literature also contains examples of long-lived spin order between ¹⁵N₂, ³¹P and 103Rh spin pairs, which I think deserve a mention along with ¹H and ¹³C.  A mention of dihydrogen (or specifically ortho or para-enriched H₂) is also notably absent.

Line 16 (Introduction), another application of long-lived spin order that should be mentioned is spectral editing, which has been used by many research groups in fact in NMR of proteins and large biomolecules.

Line 22, Fluorinated drugs can in some cases be synthesized with a 18F radiolabel and their biodistribution studied using PET scanners. An important application that the authors could mention.

Line 46, “mono-exponential decays” should be “an effective mono-exponential decay”.

Line 64, “PFAS molecules…, which have been widely studied for the detrimental effect on the environment”. It seems backwards to perform a study on a molecule that has negative environmental effects.  I don’t think this (as the sentence currently reads) can be claimed as a motivation or justification for the molecules studied.

Line 83, “T00 filter” is missing a reference.  A general one is the chapter “Filters for long-lived spin order” https://doi.org/10.1039/9781788019972-00188

Line 91, “J(19F-19F) couplings obey different rules compared to J(1H-1H) couplings”.  I don’t agree with this sentence. Physically speaking, a J coupling is a J coupling and there are no “rules” that depend on the nuclear spin species involved.  I think the authors instead mean “J(19F-19F) and J(1H-1H) couplings differ in the dependence of their magnitude on the number of chemical bonds between atoms”.

Line 119, “(henceforth called Outer singlet-triplet transitions or OSTs)” introduces this terminology late in the paper, where it is already used two pages earlier in the caption of Figure 1. For cleanliness please introduce this terminology earlier, before referring to Figure 1.

Line 125, “Once the amplitude νSLIC has been optimized, the duration τSLIC can readily be optimized by searching empirically for the highest signal amplitude.”  Similar optimization procedures are used for pulse sequences such as M2S or PulsePol-type sequences that excite OST states. The authors might want to refer to those too.

Line 131, “forbidden combination lines” should read “weakly allowed combination lines”.

Line 143 (caption of Figure 4) is sloppy, reading “actually admixtures of two-, four-, and minor amounts of six-spin order LLS terms”.  Alternative, more formal wording is needed here. However, I am generally not convinced about including the Figure in the paper because all of the important information can be found instead in Table 1.  If the authors do want to keep the figure, then perhaps plotting on a semi-log graph (with error bars) would be a better way to show that the decay curves are close to monoexponential.

In this work, authors excite and measure the lifetimes of long-lived states (LLS) of 19F spins in three fluorinated aliphatic molecules and show that the LLS time constants are 2.1 to 3.6 times longer than the T1 time constants. They claim that LLS time constants are sensitive to binding partners, in which case this study will be interesting. While this claim is supported by previous literature (Buratto et al., 2016, J. Med. Chem.), this manuscript does not contain any studies with binding molecules. This work may be interesting for those who want to take it further for actual applications. The authors should address the following questions and make appropriate revisions before proceeding further.

Questions

1. What challenges are faced for excitation of LLS in the case of 19F instead of 1H?

2. In the final state, what are the relative proportions of different spin order terms (2, 4, and 6)?

3. From the optimal SLIC parameters, how to estimate the F-F J-couplings?

4. Why was the first F-F pair not considered in all three cases?

5. Will this method extend to low fields and strong coupling cases?