Renormalization approach to bound states

1 - Paper addresses in an innovative way an important problem of ABS states in the superconducting version of the Kondo model.
2 - Solution of this difficult many-body problem is done in a semi-analytical way, which is a remarkable achievement.
3 - The approximative solution found seems to correspond quite well to the numerical solution via NRG, i.e. the solution is meaningful and reliable.

1- The presentation is in my view not fully optimal, there is too much space and stress given to the semi-trivial preliminaries (impurity scattering and classical spin cases, which can be far more easily solved by other methods such as, e.g., Green's functions, which was correctly pointed out by the first referee), while the really new and important part is relatively succinctly explained. Reverse would be highly welcome.
2 - Connection with numerically exact solution is reduced to a single figure and is not even there done explicitly. Importance of the obtained semi-analytical results would certainly deserve a much better and thorough comparison with the existing numerics.

I consider this paper as a potential breakthrough in the solution of the superconducting version of the Kondo (or Anderson) model. The remarkable achievement of this work is a semianalytical approximate solution of this very complicated many-body problem, which appears to agree quite well with the known numerically exact solution obtained via the numerical renormalization group approach. This strongly suggests that the chosen approximation, although that is by no means clear a priori, captures the most important aspects of the physics of the model. As such I can heartfully recommend this work for publication in SciPost.

However, before that and fully in line with the criticism of the first referee, I strongly recommend the authors to restructure the presentation. The problem with the current version of the manuscript is that it doesn't sufficiently focus on and stress the main achievement which is the solution of the quantum spin problem. Even the title suggests something more general, but that is quite problematic. For single particle problems (the first two parts of the manuscript, i.e., Sec. 2 on nonmagnetic impurity and Sec. 3.1 on classical spin), the presented method is probably one of the most complicated, yet equivalent, approaches to the problem of finding bound states. Here, I must fully agree with probably all the reservations of the first referee. The real achievement though is in the quantum spin part, which to the best of my knowledge gives the first semi-analytical nonperturbative solution to the superconducting Kondo problem. I also understand that the first two parts are preliminaries to this crucial part, but that is likely not too obvious to non-expert (in SC Kondo/Anderson model) readers. I had this impression when reading the paper and the reaction of the first referee fully confirms that.

I would suggest the following:
1. Focus the paper on the quantum spin problem, including the title.
2. Diminish the non-interacting parts; I understand they are necessary technical introductions into the whole formalism, but they are subsidiary, so perhaps move them into appendices or so.
3. Expand the presentation of the quantum spin calculation. It's too short and cannot be easily reproduced. Perhaps also expand explicitly on the concepts taken from references [31] and [37].
4. Make a better and more thorough comparison of your findings with existing numerically exact results obtained by NRG.

Apart from these general comments I have a couple of specific questions and comments to the text:
- Definition of the mean value of an operator between Eqs. (20) and (21) misses the statistical sum/trace over the canonical state in the denominator.
- I am wondering why is the k-resolved omega-integrated weight of the bound states in Figs. 2b and 3b exactly 1/2 at the Fermi momentum. You don't show the analogous quantity for the quantum spin, would it be the same? Is it a general/universal property or something specific say for k-independent couplings V?
- In Sec. 3.1.1 on pp. 10 and 11 you mention at least twice that the signs in front of the quasiparticle scattering terms should be equal. I understand that it is somehow important for your procedure but I didn't get why it is important.
- 2nd line on p. 15: yield (not yieldS); the end of that paragraph - you write about a TRANSITION between two singlets (BCS and Kondo), that's perhaps a bit dangerous word in that context, since there is no true phase transition unlike between the singlet and doublet but just a smooth crossover.
- I am very confused about the statements just below Eq. (71). First of all, in the decoupling you substitute quartic product of quasiparticle operators by a mean value of two of them times the remaining two operators. With respect to which Hamiltonian (or state) is actually the mean value taken? It's not fully clear to me since you make the unitary rotations and things of course correspondingly change... You write that the mean value of number operator alpha_q depends on omega_0. I honestly can't see that but that shouldn't be the sole reason for the necessity of self-consistent solution of Eq. (70) in omega_0 and its ensuing temperature dependence, right? Obviously J_k0 of (71) does depend on omega_0 as it enters the sum in the denominator and the temperature dependence comes in through the mean value even without its explicit omega_0 dependence. So this part is very unclear (and way too short) to me.
- 2nd line on p. 20: you definitely should elaborate on the statement about the correspondence with the former numerical studies [6,20]; the last three lines of that paragraph - I have absolutely NO idea what you mean by the singularity of the J_k coupling, please explain and elaborate
- line below Eq. (76): builT (not builD)
- Fig. 5, YSR states: why are their weights for various values of J the same (despite their position is moving as it should)?
- p. 23, last paragraph of Sec. 3: it might be useful to actually show the behavior of the spectral weight as a function of J

1 - Restructure the manuscript text, suppressing the noninteracting parts and elaborating on the quantum spin problem.
2 - Make a far more thorough comparison of your results for the quantum spin with the existing NRG data.

Before proceeding to the report, I'd like to state that my background is single particle theory, including numerical methods. I am therefore knowledgeable in the subject of the manuscript.

In summary, the manuscript proposes a diagonalization procedure for finding bound states in impurity models and applies it to a single impurity in a tight-binding chain, a Shiba state, and a quantum spin impurity in a superconductor.

# Novelty of the findings

Finding a bound state spectrum numerically, especially in a noninteracting model, is straightforward to formulate: one chooses a trial energy, computes the bulk Green's function, computes the self-energy of the impurity due to the coupling to the bulk, finds the bound states of the resulting finite Hamiltonian, and iterates this scheme until the trial energy starts coinciding with the bound state energy. A similar approach, together with including mean field corrections would likely also work for the quantum spin example. There are also works, e.g.
https://scipost.org/10.21468/SciPostPhys.4.5.026 that consider the numerical aspects like stability or efficiency of the bound state algorithm.
Therefore there exist alternative methods to solve this problem. The renormalization approach applied by the authors is reminiscent of a generic construction of the perturbation theory. Upon a closer inspection, however, I realized that the authors formulate an iterative approach to computing a matrix that diagonalizes the Hamiltonian—in other words they seem to just perform iterative numerical diagonalization.

This formulation of the impurity problem is to the best of my knowledge is new, however, given both the familiar nature of the problem, and the relatively standard perturbation expansion approach, the overall idea should be reasonably natural to the experts in the field.

# Validity of the reporting

While the overall structure of the manuscript is clear and appears correct, I find that in many aspects the provided information insufficient.

- The authors refer to a numerical computation that they use to find the bound states, however they do not provide the source code of this computation, and not even an overall description of what they do.
- The authors use finite sized systems, without addressing the question of how the complexity of the proposed approach depends on the system size. This is especially important because the Green's function-based approach applies directly to infinite systems.
- The authors' claim of proposing "a (semi)-analytical approach" is misleading: this approach is only analytic as much as is the underlying problem. A generic tight-binding model has no closed form solutions for the bound state problems, and being able to phrase the problem via a system of equations equation doesn't make the approach analytical.

# Relevance of the work

Unfortunately, I remain unconvinced about the relevance of the published work: researchers were solving the bound state problem for decades, and in a variety of physical contexts. The authors put forward several claims of usefulness or innovativeness of the manuscript. Below I quote the relevant parts and comment why I find these unconvincing.

> we propose a method that merely applies a single unitary transformation.

That is the definition of the eigenvalue decomposition.

> This power of our approach is rooted in the fact that bound states manifest themselves as singularities, and that it is therefore sufficient to extract this singular behavior from the full picture to investigate bound state physics.

Existing methods yield the bound state wave function as a linear superposition of exponentially decaying waves. There's no need to read anything out.

> our approach directly yields access to momentum-resolved observables

Fourier transform of the bound state wave function yields the same information.

# Clarity

Unfortunately, despite the familiar nature of the subject, I found it hard to work my way through the manuscript.

One reason for that is the sequence in which the authors introduce subjects. The authors refer to the material in the following text (for example promising "As we explain below, a convenient Ansatz for $X_V$ is..."), which makes the manuscript logic nonlinear. In this specific example I didn't actually find the promised explanation why this Ansatz is convenient.

Additionally, I can't avoid an impression that the authors introduce complex language to describe something standard. A "single unitary transformation that brings the Hamiltonian to a diagonal form" is the eigenvector decomposition. "Coefficients becoming singular" means that they form a vector in an eigensubspace (by definition). Since these are the key concepts used throughout the manuscript, I am actually not completely certain that the manuscript does anything beyond an iterative finite size diagonalization procedure. In this light, I am especially confused by the statement:

> Note that such a treatmant is not a usual diagonalization where the fermion operators in the Hamiltonian are rotated in the operator subspace. In our approach, the one-particle operators are kept in their original basis while the Hamiltonian is renormalized.

A unitary transformation that brings the Hamiltonian to a diagonal form is diagonalization. That the authors choose to call it differently does not change the equations that are solved. A consequence of this description is the introduction of the "bound state momentum" $k_0$, which, as far as I can tell, bears no physical meaning.

A separate point that I did not touch in my discussion above is the quantum spin problem. There, unlike in the other examples, the authors make an approximation (unlabeled equation above Eq. 61), but I am not sure what is its physical meaning. Since the authors eventually obtain an effective single-particle bound state operator, this appears to be some flavor of self-consistent mean field theory, but I cannot tell what it is and when it is valid.

# Summary

In view of the above evaluation, I heavily lean towards considering the manuscript unsuitable for publication. In order for me to revisit this evaluation, I would need the authors to implement the changes requested below.

1. Share the full numerical code used in the manuscript.
2. Reorganize the manuscript so that it follows a linear logic and does not contain "cliffhangers".
3. Avoid introducing new concepts where not necessary, in particular in making the seemingly artificial distinction between a diagonalized Hamiltonian and a renormalized Hamiltonian.
4. Remove the misleading claim of a "semi-analytical" approach.
5. Explain how the proposed approach is different from an iterative eigenvalue decomposition.
6. Demonstrate how the results and the computational complexity depend on the number of lattice sites in the chain.