Wigner localization at extremely low densities: a numerically exact \emph{ab initio} study

This is actually a pretty simple work, following up on a previous investigation [17] by the same group.

The authors study the behavior of two electrons that are implicitly confined to a ring of varying diameter by the choice of computational basis. The main differences with respect to the previous work Ref. [17] from the same group are:
* Ring geometry instead of open line segment.
* No positive background charge.
* Refined spatial resolution thanks to a customized code.
* 2 instead of up to 8 electrons.
The authors claim that this study allows them to detect signatures of a Wigner crystallization. However, for a true Wigner crystal, one would need a many-electron system while the present work considers only the relatively simple two-particle problem. Given that this is a follow-up study to Ref. [17] and that the problem investigated is a simple two-particle problem, I am not sure if this manuscript contains sufficient substance for publication in SciPost Physics. In any case, the authors should choose a title that makes the two-particle problem explicit. The terminology "Wigner molecule" (see end of the second paragraph of the Introduction) might be an option.

Apart from this, chapter III is a bit short, in particular for a work whose main merit is supposed to be a specially written dedicated code. Specifically, I would find the following information useful:
* Was the rotational symmetry of the ring exploited? In other words: conservation of angular momentum should allow to reduce the two-electron problem to an effective one-body problem.
* What is the structure of the matrix representation of the Hamiltonian Eq. (2) represented in the basis Eq. (1)? Specifically: is it a sparse matrix or can it be approximated by a sparse matrix to numerical accuracy?
* What algorithm was used to find the ground state? A library routine or an iterative algorithm?

Further questions/comments:
* The references [17,38-46] on applications of the "localization tensor" are all from the group around Stefano Evangelisti. If this tool was also used by other groups, appropriate references should be added.
* I did not find a definition of "natural spinorbitals" such that the particle-hole entropy Eq. (11) is ill defined. A related comment concerns the particle part of the entropy in Fig. 3. It seems to me that the asymptotic value (2ln(128) ?) measures just the number of basis functions and thus is not intrinsic to the problem. If so, the asymptotic value shown in Fig. 3 is actually a bit misleading.
* The units of the full-width at half maximum in Fig. 1 are not clear (I suspect that it is normalized by the length L).
* It is good to have a perspective on two dimensions in the Conclusions. Among others, this justifies some of the more general discussions throughout the manuscript. However, it would also be good to have the authors' opinion on the possibility to go beyond two particles to the true many-body Wigner crystal.

1) Adapt title to two-particle problem studied (e.g., using "Wigner molecule").
2) Expand section III "Computational details".
3) Add references on applications of the "localization tensor" by other authors (?).
4) Define "natural spinorbitals".
5) Specify units of the full-width at half maximum in Fig. 1.
6) Clarify impact of number of basis functions used on the asymptotic value of the particle entropy in Fig. 3.
7) Add comments on the possibility to go beyond two particles to the true many-body Wigner crystal to the Conclusion.

Comments to the Author

The authors study by means of exact diagonalization method the Wigner localization at very low density of a quasi one dimensional ring. Three observables, two-body reduced density matrix, localisation tensor, and particle-hole entropy are used to capture the Wigner localisation transition. The authors conclude with introducing the localisation tensor as more accurate and versatile, mainly for higher dimension, observable than the others.

The methods used in this study are well established and the results
physically sound. Although the present work does not extend much the previous work’s of authors (ref. 17 in the manuscript), but I believe the present article has a broad appeal for the community of researchers working in this field due to its pedagogical character and clarity. Thus I think that the paper can be accepted for publication once the authors address the following few points:

1) I would suggest to add a section or appendix about the details of numerical, for the pedagogical purpose.

2) I think that the authors should discuss more about transition point!!!, whether it can be found with the introduced observables or not?

The paper presents a study of the electron localization as a function of the electron density, focusing in particular on the Wigner crystallization (WC), for a quasi-1D system composed of two electrons Gaussian-confined on a ring of perimeter L. Full understanding and characterization of the Wigner crystallization is an open problem because of the difficulty in the description of correlations in the framework of the most general unsolved quantum many-body problem. The present work is along this research line, and therefore interesting per se.

The work is scientifically sound and the methodology valid. It is, to the best of my knowledge, original. To the extent I could check, I did not find any issue, mistake, or error that can, bona aut mala fide, affect the findings. I anyway warn the authors that I do not assume any responsibility for possible errors which therefore fall under their full liability.
I solicit the editor to publish the paper.

In the following minor remarks/comments/suggestions which might be correct or wrong and that the authors may optionally take into account, or discard at all if they will find them fully irrelevant:

I personally found the work really interesting (per se, as I said above) and stimulating further developments along the same line. For this reason, I don't understand the authors' need to add an introduction bringing on a "technological interest" of the present study, making a link with "quantum dots" and their "tuning" to make them "promising candidates for qubits", up to even evoking the legendary and mythological "quantum computer". These introductions are in the style required by editors of those high-IF journals with divulging character. But on high-level journals, like SciPost, whose readership is composed by highly competent scientists who can perfectly understand the importance of the present work, such introductions are an offense to their intelligence. I think that they are unworthy and reduce the scientificity of the article.
It is not immediately clear from the title, the abstract and even the introduction which is the system studied precisely. Indeed, until section II.A the reader is uncertain if the system is a really 1D ring with 1D kinetic and interaction terms. Or for quasi-1D the authors mean a 3D system but rigidly confined on a ring (in analogy with spherium with electrons rigidly confined on a 2D manifold but with a 3D interaction). I think that a more immediately comprehensible definition for the present system is "a quasi-1D system composed of two electrons Gaussian-confined on a ring of perimeter L". I think that this is an important information to be quickly delivered for a reader to promptly classify this work with respect to his interests.
I don't know if the use of the term "ab initio" in the title is appropriated in this case: ab initio normally refers to treatment of all (or a maximum relevant) of the degrees of freedom in a real system by referring to the microscopical (and not a model) Hamiltonian. The present is rather a model. Even Wigner, Nozieres et al., when studying the 3D electron-liquid jellium model, did not define it an ab initio study. And jellium has much more close realizations in nature (e.g. bulk sodium or lithium) than the present model. On the other hands, I agree that the present study "is important to be able to describe Wigner localization within ab initio theory".
The present work casts some interesting doubts on the ab initio quantum chemistry (full-CI) Gaussian methodology, that is whether it possesses a real full 3D ab initio valence or it should be rather considered a reduced quasi-1D study. As it emerges here, a Gaussian basis-set, with Gaussians appropriately placed along a ring, in practice makes the system quasi-1D. Then also what in quantum chemistry are defined as ab initio full-CI studies of molecules, for examples in dimers with Gaussians placed at the two atomic positions or at best placing a further midbond set, might be rather receiving a strong bias toward a quasi-1D situation. And so, for the use of the Gaussian basis-set itself, they deviate from a genuine description of the real 3D system. It would be interesting if the authors could provide the comparison of their numerical study as a function of Gaussian width $\alpha$, with the available analytical study on the rigid 1D ring: the case of one electron is already sufficient to show how much, depending on $\alpha$, a Gaussian study is closer to the quasi-1D or rather evolves towards the full 3D.
It is to me evident that the diagonal of the 1-RDM (the density) is constant, and only the diagonal of the 2-RDM can be used to characterize a WC, but it is not clear why raising the dimensionality of the system (from the 1-torus/ring to the 2 and 3-torus) one needs higher order RDMs (3-RDM and 4-RDM). I would have said that the 2-RDM is sufficient always. Is this valid also for the full 2D and 3D electron liquids not confined on the torus? Can the authors provide an intuitive explanation, or at least a reference where this can be understood?
Since the beginning I had the impression that the particle-hole entropy is a quantity that strongly depends on the number M of natural orbitals taken into account, and so strongly depends on the basis-set size. At least much more than the two other considered indicators. If the authors confirm this impression of mine, than since the beginning it is evident the difficulty in using this quantity as a robust indicator of WC.
Finally, from this work it does not emerge a net criterion to exactly pinpoint the density at which the phase transition to the Wigner crystal really occurs. If one looks to the 2-RDM, for small L the FWHM is not well defined, so that the normalized FWHM is manually set to 1: therefore, we cannot take the WC phase transition to occur when the normalized FWHM departs from 1. The trace of the localization tensor does not achieve a well defined plateau for high densities, and so what to take for phase-transition boundary? I have the impression that the system is a Wigner crystal even at high densities and since the beginning, so that there is no real phase transition to another phase. Isn't this really the case?