A solvable model for graph state decoherence dynamics

- The manuscript provide an analytical solution to a non-trivial open many-body problem
- Interesting insights for the behavior of the OSEE

- The authors consider only the H=0 case

The authors of the manuscript "A solvable model for graph state decoherence dynamics" an exact analytical solution of the dissipative-only dynamics of permutation-invariant graph states of N qubits. They provide the exact equation of motions for observables as well as predictions on the OSEE. Analytical predictions are benchmarked against tensor-network simulations and shown to be exact. The paper is very pedagogical and allows the reader to follow all the calculations that has been done. The theoretical framework is robust and scientifically sound. I support the publication of the manuscript provided that the authors answer to my criticisms.

- On the reduced density matrices. In Sec.3.4 the authors provide the structure of the reduced 2- and 3-site density matrix. They comment on the fact \rho_2 is separable at all times while \rho_3 and \rho_4 show zero negativity. Given that the construction of the N-qubit density matrix can be obtained by iteratively I was wondering if the global density matrix of the N qubits can be constructed as well. If this is the case would be possible to obtain some results for the time evolution of the system negativity at least for small N?

- Again on entanglement. I understand that the OSEE does not distinguish between classical and quantum correlations. As a matter of fact the negativity is entanglement witness. For small N it would be nice to compare the behavior of the entanglement negativity compared to the OSEE and see how classical and quantum correlation are progressively killed by the dissipative evolution.

1) Analytic solution to open quantum system.
2) Benchmark against numerical method.
3) Additional example exploiting operator space entanglement entropy.

1) Some of the general acceptance criteria are on the weak side, and considering them all together, they should improve in my opinion to make the paper stronger. I am referring here to the citations, some ambiguities in the language, and a detailed introduction. Some of the suggested points below address the primary concerns.
2) For reproducibility, the authors may think about attaching their setup for iTensor either as a data repository or as git repository, especially if they might consider the step in the future. Estimating the work behind it, I understand if they do not want to provide it, but it would fit well into SciPosts idea aiming at reproducibility.
3) Purely dissipative model without Hamiltonian, i.e., H=0.

The article "A solvable model for graph state decoherence dynamics" (arXiv:2305.17231v1) describes the exactly solvable dynamics of a Lindblad master equation for graph states. The Lindblad master equation herein is purely dissipative and the results are scalable to the many-body regime. Therefore, the simulations are a useful fixpoint to compare with numerical simulations like tensor network methods. The exactly solvable model and the comparison to tensor network methods are the strong points of the article. I would suggest some revisions concerning the presentation before being accepted for publication in Scipost Physics Core; then, I would be looking forward to seeing it published in SciPost Physics Core. Larger revisions including cases with a Hamiltonian would move the submission probably into the top 50% in Scipost Physics Core.

Suggested revisions before acceptance:

The following points 1 - 12 are the suggested revisions; if they cannot be resolved, a comment why the point does not apply in the response to the referee report would be appreciated.

1) The case with a Hamiltonian unequal to zero would unlock a lot of potential use cases. It is understandable if the Hamiltonian cannot be added in the revision, although it would be highly beneficial to the paper, e.g., as a simple Ising model or XXZ model. If H is not added, I am missing a detailed comment if the authors consider it unfeasible or which complications they anticipate or already encountered when trying to integrate H into the model.
1a) page 6, "thermal steady state population": the thermal state goes a bit against the H=0 choice, so I would maybe clarify that this temperature requires choosing a diagonal local Hamiltonian and choosing the coupling of the Lindblad operators according to the temperature and energy gap.
1b) The conclusion is talking about a "vanishing Hamiltonian", while the main part does only take into account H = 0. I would therefore replace "a vanishing" with "no".

2) The citations are a bit sparse and could improve, especially after the introduction. It would benefit the reader to repeat relevant citations in the main part and give a broader view of the literature in each chapter. More citations would align as well with the suggested citation policy on SciPost.
2a) One example would be the section on tensor network methods, where the complete simulation side is covered with few citations. In my opinion, it should be extended in the introduction and the chapter about numerical methods.
2b) The operator space entanglement entropy is covered basically with one citation, where the field is probably much bigger. The work of P. Zanardi would be something to mention, likely amongst others. The OSEE is not mentioned in the introduction at all, although it covers a complete subchapter later.
2c) It is good practice to cite software and I am glad to see the authors do so, see Ref [21, 22]. Can the authors add the developers in Ref [21] and ideally the version or commit with which they were running the simulations? This information would add valuable information for reproducibility.
2d) Names are frequently not capitalized in the citations, e.g., it should be Greenberger-Horne-Zeilinger; please correct.

3) Page 6, "It is interesting, ... inversely proportional to the system size": as the analogy to the GHZ is frequently mentioned, this feature looks less surprising in my opinion. Also, the coherence in the GHZ state depends on the number of qubits as decay or dephasing on any qubit will affect the GHZ state. Therefore it would benefit the article to investigate if it is linked to the number of neighbors in the initial graph by running additional numerical simulations or if it comes from the similarity to the GHZ state. The language is a bit vague here ("may be related"; "interesting", but interesting because surprising, contradicting or confirming previous knowledge) and could improve.

4) Page 7, "presumably": the language is vague here, does it hold or not? Up to which system size do the authors have numerical evidence? Can it be constructed as well from a sum of outer products, which could help to prove separability? Defining Mz = [[z+, 0], [0, z-]] and My = [[0, -i y], [i y, 0]] and x as outer / Kronecker product, rho_2 = 0.25 * Mz x Mz + 0.25 * My x My which makes the argument about being a separable state easier. Is there maybe a similar construction for larger reduced density matrices or is by "product" already meant outer product.

5) Page 7,8: The authors point out the perfect agreement between numerical simulations and theory, but on the plots, one can probably only say that the errors are less than five to ten percent. Can the authors please add an error plot of the absolute difference between the theory results and the numerical results on a log-scale? Log-error plots are an essential step of a numerical analysis in my opinion. These plots would also fit well into an extended appendix.

6) Page 8, caption of Table 1: Captions should aim to be self-consistent and this caption neither explains g0, g1, g2 nor alpha, beta, gamma.

7) Page 8, Fig 1.: A comment on the left frame about why all cases yield the same expectation value would be useful. Is it expected? At this stage of the article, it raises the question of why all the cases were defined, which only becomes clear later on.

8) Page 10, caption Fig. 4: "by a factor N" sounds like a new variable, unknown to the reader. Since N is the system and assuming the factor is actually the system size, it should read "by the system size N". In contrast, if it is a factor different from the system size, a new variable should be used instead of N.

9) Page 11: "suppose" and "seems" could be more clear (first paragraph on page 11). What are the indications that it holds or does not hold?

10) Page 12: Discussion about MPO representation beyond 1d, where the claim is that the simulation indicates that MPOs work in "a high space dimension", which seems to be beyond 1d. This statement is a bit misleading as the GHZ-like states can be prepared in 1d systems and are not limited to 2d or higher dimensional systems. Furthermore, I would characterize the dimensionality of the system by the interactions present in the system, where we have only local Lindblad operators and therefore no obvious geometry. The dimensionality might affect the efficiency of how the initial state can be prepared, but does not affect the time evolution discussed in the article in my opinion. As pointed out in one of the next comments, the initial bond dimension should be sufficient for local problems and therefore I would remove the whole statement about suitability for higher dimensions unless it is reflected in the propagator when changing the dimensionality.

11) Page 12, "possibly classical": vague language, as a reader I would like to know if they are classical or not, e.g., for readers interested in using quantum correlations as a resource. Even if the correlator to be considered is not known, tools like quantum mutual information should help to distinguish classical from quantum correlations and make a clear statement here.

12) Page 13: Bond dimension and small numerical errors: the bond dimension of the MPO of the density matrix is known for the two limits, i.e., the initial state and the steady state. As we have a local model without any interaction terms, the bond dimension should not grow beyond the bond dimension of the initial state, i.e., 4. What kind of update do the authors use for their numerical simulation? A two-tensor update or a single-tensor update? Are there global Krylov steps acting on the whole state? Knowing that the evolution operator is local, a single-tensor update is sufficient in my opinion, and would probably eliminate the numerical errors.


Optional revisions (no need to respond if not taken into consideration)

13) The authors could add some structural elements, which are not strictly necessary, but might improve the presentation.
13a) The structure of the paper does not appear at the end of the introduction, but at the end of Sec. 2. I would move it to the introduction unless it contradicts a SciPost policy.
13b) To avoid empty sections between a section and a subsection, e.g., see Sec. 3 and Sec. 3.1. or 4 and 4.1, it would be beneficial to add one short paragraph to explain to the reader what follows in the complete section.

14) Usage of past tense
14a) In my opinion, inconsistent use of simple past and present perfect in the conclusion, i.e., "we introduced" (p. 11) vs. "have compared" (p. 12). It should be consistent and, in my opinion, present perfect in the conclusion.
14b) The main part switches between simple past and present, e.g., on page 8 with "we also checked" and "we then observe", but I assume that was intended by the authors.

15) For the appendix, there are several small comments:
15a) The appendix with one paragraph seems to fit into the main part as is or should be extended, e.g., with the convergence study suggested in a previous point.
15b) A small paragraph with two sentences to introduce what the appendix discusses would be helpful before starting with details.
15c) What criteria do the simulations use in terms of cutting singular values? The bond dimension encountered as 15 will depend on which singular values are cut, e.g., if one cuts everything below 1e-8 or 1e-12. Please mention this parameter as well.

16) Page 3, Eq. (6): maybe a mention of the possibility to map it to a vector, i.e., super-ket, is here already useful. It is used for many numerical methods and allows readers to connect. Furthermore, it is used later on.

17) Page 4: * in the subscript is not explained, e.g., with "where $* \in \{0, 1, 2 \}$".

18) Page 4: "nontrivial action" to "non-zero" action?

19) Page 4: replace "is the same" with "has the same expectation value"

20) page 5, Eq. (18): can the authors highlight somehow how many qubits are in the state $\ket{-}$, maybe as $\ket{- \ldots -}_{1 \ldots n} \ket{+ \ldots +}_{n+1 \ldots N}$?

21) page 5: The language could be stronger here, e.g., multiple "do" and "this" without explicit reference to what "this" refers. For example after Eq. (19), "To be real, the last expression of Eq. (19) must be 0 ..." would be more accessible to the reader.

22) Page 6: "gives the two terms" to "results in two terms"

23) Page 6, "recurrence": would "recursion" be even more fitting as a term here?

24) Page 7: consistency, it is "2-qubit density matrix", but "two-point" correlations. Usually, small numbers can be written out as words.

25) Page 7, "whatever": replace with "independent of the" (whatever sounds colloquial)

26) Page 8: replace "whatever" with "independent of" (whatever sounds colloquial)

27) Page 8: "as it should" to "as it should be"

28) Page 8, caption Fig. 1. To aim at a self-consistent caption, I suggest writing "cases with N=64 qubits" to explain the variable N.

29) Page 9: "interesting", but interesting because surprising, contradicting or confirming previous knowledge?

30) Page 10, caption Fig. 3. To aim at a self-consistent caption, I suggest specifying "at intermediate times $t$" to explain the x-axis label.

31) Page 11: add a comma to ease the flow of reading: "... larger than the correlation length, the OSEE becomes ..."

32) Page 12: multiple uses of conditional, i.e., "would". I suggest "of analytic solutions is valuable" and "In a future study, we consider it valuable to compute".