Absence of a dissipative quantum phase transition in Josephson junctions: Theory

I have read very carefully the responses by the authors to my report and to the other referees. The authors have tried to rebut every single point of criticism. However, I disagree with the rebuttal by the authors.

Apart from some non-trivial technical aspects about the numerical procedure and the low-temperature limit, the authors have not investigated the correct physical quantities. In particular, I also agree with Prof. Snyman that <cos(phi)> is not the relevant quantity to reveal the localization-delocalization transition because it does not show if the phase is localized in a single potential minimum.

Moreover, I disagree with the qualitative argument by the authors about the counter-term, which is simply a diamagnetic-like term that can disappear with another representation of the circuit Hamiltonian. The authors should focus on the whole Hamiltonian and not just one part of it.

Last but not least, the authors' review of the previous literature is more than questionable. The authors are mischaracterizing the paper by Houzet, Yamamoto, and Glazman by boldly claiming that Houzet et al. overinterpret their response functions. I believe that it is the present manuscript that overinterprets the numerical findings.

Furthermore, the revised version of the manuscript represents a very minor update and does not address the fundamental issues raised.

In light of this, I must unfortunately reject the paper. The paper is already accessible via arXiv. To be published in a peer-reviewed Journal, as a referee, I cannot endorse a manuscript that is inconclusive and overinterprets results with bold claims that are not substantiated.

Reject

I thank the authors for their detailed response, and for submitting a revised manuscript.

Considering the various referee reports and reactions from the authors, I am afraid that this reviewing process has reached somewhat of a deadlock state, with many conversation threads branching off in various direction. In this final response, I try to give an overall pragmatic recommendation, and then provide more detailed feedback on a few select points, either raised by me or by the other referees.

Overall, I maintain that the authors seem to have formulated the model correctly, and are applying what appears to be sound methods to make concrete quantitative predictions. I however also maintain, that according to my understanding, this model hosts a dissipative quantum phase transition, visible in certain well-defined limits, and I while I would very much expect that adding an explicit UV cutoff to the bath renders the transition blurry or even invisible in some cases, I still fail to see how taking the UV cutoff to infinity should play such a huge role in this model (more on that later).

That being said, the proper treatment of the Caldeira-Leggett model (either in this work or in the existing literature) is far from trivial, and in order for me to definitively say where the problem lies (e.g., did the authors make a mistake in their calculation or the interpretation or their results, or are they actually uncovering a deep issue in the existing literature) I would have to redo the entire calculation myself. This can hardly be the purpose of the peer review process.

I therefore recommend the editor to consider the work for publication on the following grounds:

1) the issue of the Schmid transition in Josephson junctions is of very high fundamental importance and interest, and remains at the very least on the experimental side as an unresolved problem — hence all possibilities on the theoretical side (revision of the models, as well as revisions of the treatment of existing models) need to be explored, and even seemingly well-established literature results should be open for questioning.

2) Theory works are in general very easily falsifiable. This is particularly so in the present case: the authors clearly describe their theoretical treatment and provide all necessary parameter regimes and assumptions, making their work perfectly reproducible. Given the appropriate amount of time, I believe their work can (and likely will) be subject to full scrutiny by the community. I therefore consider publishing this work as a high risk/high gain situation. It is my expectation that over time, the treatment by the authors will either be found to be consistent with existing literature results (only that the parameter regimes or observables are poorly chosen to see the transition) or flaws in the treatment will come to light. But, on the (in my eyes) lower chance that this work genuinely brings about some new understanding on quantum phase transitions (and given their fundamental importance), it should deserve a highly visible platform.

After these general remarks and my recommendation, I now choose to comment on two issues that were part of the reviewing process so far, concerning both UV and IR cutoffs. I kindly ask the authors to add clarifications regarding these two aspects in their manuscript.

Regarding UV cutoffs, I may have expressed myself in a misleading way, when calling the addition of an explicit UV cutoff to the otherwise Ohmic bath “spurious”. I am fully aware, and fully agree with the authors, that such cutoffs are in most cases real and physical. The point that I was trying to make was another one. To reiterate: when analysing the action in frequency space, we see that the circuit capacitance provides a term \omega^2/E_C, whereas the Ohmic bath provides a term \eta*\omega. We thus see that there is always a finite frequency window where the Ohmic bath term is dominant — but at the same time, above a certain frequency, the charging energy term dominates. In this sense, the charging energy provides a natural UV cutoff to the theory. The authors are by all means free to add an additional explicit cutoff to the Ohmic bath. But I kindly (yet firmly) ask the authors to consider the argument that if the cutoff in the Ohmic bath is chosen at a frequency where the \omega^2/E_C term dominates, conventional mathematical arguments indicate that the Ohmic cutoff can no longer be of importance. Hence, if the authors observe a strong impact of the additional Ohmic cutoff, they either consider parameter regimes where the Ohmic cutoff is always below the charging energy cutoff, or they uncover some features in their theory that go beyond our basic mathematical understanding of convergence of integrals. Either way, I find the discussion of this aspect in the manuscript is still unclear. Note in addition, that I fail to see the connection with the zero temperature limit that the authors mention in their response to my report. In my understanding of regular RG methods, the temperature impacts the low-frequency (IR) cutoff, and not the UV sector.

Concerning IR cutoffs, I fully share the concerns raised by one of my co-referees, in that the Caldeira-Leggett model, at least in its “vanilla” formulation, is perfectly 2\pi-periodic in the phase, such that the treatment of the counter term (i.e., whether it should appear within the qubit Hamiltonian or the kernel) should be immaterial. While I know that the authors are aware of this issue (given their response to that report, and the various discussions I had with the authors by different communication channels), I cannot help but insist that the authors provide very little clarity on this issue, even in the revised version of the manuscript. This is by the way also the reason why I immediately jumped to the conclusion that the authors include an actual, physical inductive term (such that the bare qubit is indeed the fluxonium and not the charge qubit). Also, as I likewise already communicated with the authors via other channels, I believe that a physical inductive shunt might indeed be a reality for various circuits, providing a natural IR cutoff. Note in particular, that the limit of L->\infty is not straightforward to take (even more so than R->\infty), as a finite inductance breaks 2\pi-periodicity even for the closed (uncoupled) qubit, and has an impact on various thermodynamic quantities, such as the heat capacity, and others. And while I currently don’t have any more concrete arguments, I feel that a proper inclusion of such an IR cutoff might provide a nontrivial ingredient with respect to orders of limits, or might at the very least clarify the localised versus extended phase issue related to the counter term. As a final thought on that matter: if I understood the authors correctly, they observe that it is the combined order of limits of R, temperature, and Ohmic cutoff which is important in their calculation. As pointed out in the previous paragraph, the temperature has an impact on where to stop the RG flow in the low-frequency, and not the high-frequency sector. Could it be, that a physical inductive shunt could therefore regularise the behaviour with respect to temperature?

Ask for minor revision

I have carefully read the authors' response to the referee reports. The response is in the form of an attempted rebuttal. The authors believe the referees were mistaken in their reports. The whole rebuttal hinges on the following claim:

"[I]n the equations we use, the counter-term forbids delocalized states. This is most clearly visible after the Hubbard-Stratonovich transformation is performed, in new Eq 12 (former Eq 10): at large $\varphi$, the position-independent random noise linearly coupled to the phase is always small compared to the parabolic inductive term (otherwise our truncation of the fluxonium basis would not be justified). With the equations we use, all states of this system are localized in phase. A fully delocalized phase state would have an infinite energy and cannot by any means be the ground state of a system with that action (except for $R=\infty$, the bare CPB, where the counter-term vanishes). Hence, the localization/delocalization transition predicted by Schmid cannot exist. We do not even need to perform numerical calculations to prove our point. We added this qualitative discussion early in the revised manuscript; our stochastic Liouville results can be seen as just illustrating quantitatively the above qualitative argument, for different parameters."

Rather than addressing every point of disagreement between myself and the authors, I will show that this claim, which is the foundation for their rebuttal, is mistaken. The authors' error is of the same variety as saying $P(x,y)=N \exp[-(x-y)^2]$ is a joint probability distribution for $x$ and $y$ in which $x$ is always localized because we can write $P(x,y)=W(y)\exp(-x^2+2xy)$, and see that at large $x$, the "counter term" $-x^2$ always dominates the "position independent noise" $y$ linearly coupled to $x$.

If the authors' claim is corrected it simply reads "When the phase $\varphi$ makes a large excursion, the environment must adjust itself accordingly, to avoid a large energy cost," and does not imply localization by an energy barrier. This is obvious from the outset: the environment is a bunch of particles attached to the CPB "particle" with springs.
If one does not want to stretch the springs when displacing $\varphi\to\varphi+\Delta \varphi$, one must displace each environmental particle $\varphi_n\to\varphi_n+\Delta\varphi$ as well. It is also contained in Eq. 11 and Eq. 12, the equations that the authors believe to support the opposite conclusion. To see this, note the following. In Eq. 11, $W[\xi]=\exp(-S_\text{env}[\xi]/\hbar)$ where $S_\text{env}[\xi]=\sum_\alpha \phi_0^2(1+|\omega_\alpha|/\omega_c)\xi_\alpha\xi_{-\alpha}/4E_L$ in Matsubara frequency representation. (I denote the flux quantum as $\phi_0$ to avoid confusion with fields $\varphi_n$, and use greek Matsubara indices, to distinguish them from environmental mode indices.)
The "fictitious action" naturally splits into three parts $S^E_\text{Fict}[\xi,\varphi]=S^E_\text{CPB}[\varphi]+S^E_\text{CT}[\varphi]+S^E_\text{Coup}[\xi,\varphi]$. In Matsubara representation $S^E_\text{CT}[\varphi]+S^E_\text{Coup}[\xi,\varphi]=\sum_\alpha \left(E_L\varphi_\alpha \varphi_{-\alpha}+\phi_0\varphi_\alpha\xi_{-\alpha}\right)$.
The authors claim that the counter-term part $S^E_\text{CT}[\varphi]$ guarantees localization of $\varphi$. However,
because $\omega_{\alpha=0}=0$, the zero Matsubara frequency component of
$S_\text{env}[\xi]+S^E_\text{CT}[\varphi]+S^E_\text{Coup}[\xi,\varphi]$ equals $\phi_0^2\xi_{\alpha=0}^2/4E_L+\phi_0\varphi_{\alpha=0}\xi_{\alpha=0}+ E_L\varphi_{\alpha=0}^2=
E_L(\phi_0\xi_{\alpha=0}/2E_L+\varphi_{\alpha=0})^2$. Thus, Eq. 11 and 12 is invariant under the translation $\phi\to\phi+2\pi n$ accompanied with $\xi\to \xi- 4 \pi n E_L/\phi_0$.
Localization occurs if this symmetry is spontaneously broken, something that cannot simply be read off from these equations.

Perhaps it is helpful to point out how Eq.11 and Eq. 12 inherit this symmetry from the original Hamiltonian: the authors obtain Eqs. 11 and 12 in two steps, by first integrating out the environment, and then performing a Hubbard-Stratonivich transformation. One could however also obtain them in one step,
by integrating out all environmental modes, except for the collective field $I_Y=\sum_n \phi_0\varphi_n/L_n$ that couples to $\varphi$. Indeed, the field $\xi$ in Eqs. 11 and 12 is nothing but $-I_Y$. So displacing $\psi_n\to\psi_n+2\pi$ induces $\xi\to\xi-\phi_0\sum_n 2\pi/L_n=\xi-4\pi E_L/\phi_0$.

To be doubly certain about the authors' claim, on which they base their rebuttal, I quote another section of their response:
They say "The Hamiltonian we use in the manuscript is invariant when shifting the junction phase and all environment phases by the same multiple of $2\pi$. All forms of the action in the manuscript derive from this Hamiltonian, using only exact transformations. Under all equivalent writings of this action with this kernel (encompassing the action used by WT and Schmid), all states are localized because of the parabolic confinement made by the counter-term, as discussed earlier in this response. The ground state has a maximum probability (low temperature value of $|\text{tr}\rho(\varphi)|^2$ in $\varphi$ representation) at zero phase,
and possibly some presence in the neighboring wells, depending on the parameters.
Our results hence show that a rigorous tracing over the bath oscillators does not necessarily yield a ground state that is invariant under $\varphi\to\varphi+2\pi$."

This is similar to the first claim I quoted. We can show that it is wrong without referring to the analysis I performed above:
Look at Eq. 4, Eq. 5 and Eq. 6 in the resubmitted manuscript. It is easy to verify that
$S_\text{Fl}^E[\varphi+2\pi]=S_\text{Fl}^E[\varphi]+\int_0^{\hbar\beta}d\tau 4\pi E_L\varphi+4\pi^2 E_L \hbar\beta$.
Exploiting the fact that $\int_0^{\hbar\beta}d\tau K(\tau)=2E_L$ it is similarly easy to check that $\Phi[\varphi+2\pi]=\Phi[\varphi]-\int_0^{\hbar\beta}d\tau 4\pi E_L\varphi-4\pi^2 E_L \hbar\beta$. Thus $\rho_\beta[\phi+2\pi,\phi'+2\pi]=\rho_\beta[\phi,\phi']$ and thus, in Eq. 4, the density matrix does not represent a situation where the phase is localized around $0$,
unless a small symmetry breaking term is added. The Hubbard-Stratonovich transformation is designed not to alter $\rho_\beta[\phi,\phi']$, and so
the authors result in Eq. 11 and Eq. 12 cannot describe a situation where $\varphi$ can only be localized around zero.

From what the authors write elsewhere, it seems that when they sample the distribution represented by Eq. 11 and Eq. 12, they numerically observe a localized $\varphi$ with a finite
$\left<\varphi^2\right>$, although they do not present this data. If this is the case, I believe it is due to a sampling problem.
It likely results from the fact that in Eq. 11 and Eq 12, the probability to find large
$\varphi$ is split into the product of a very small probability to obtain large negative $\xi$, the variable sampled first,
multiplied by a very large conditional probability to obtain $\varphi \simeq - 2 \xi E_L/\phi_0$.
(This is why I said in my previous report that the authors' methods are probably unsuitable to study the delocalized regime.)

How must symmetry breaking be inferred? Not by any equivalent rewriting of an action, which will always preserve symmetries.
If representative sampling is performed without introducing a symmetry breaking term, a distribution in which $\varphi$ is equally likely to be in any of the cosine minima that are included in the allowed range of $\varphi$, should result (bar edge effects). Symmetry breaking must be investigated in the usual way: introduce a small symmetry breaking term, like $\epsilon \varphi^2$, and calculate a suitable order parameter at successively smaller $\epsilon$.
($\left<\varphi^2\right>$ will do, but not $\left<\cos(\varphi)\right>$, because the latter cannot distinguish between $\varphi$ localized in a single cosine minimum, or equally shared between all minima.)
If the system is in the localized phase, $\left<\varphi^2\right>$ will saturate to a finite value before the numerics break down due to too small $\epsilon$. If the system is in the symmetric phase, $\left<\varphi^2\right>$
will keep increasing as $\epsilon$ is reduced.

To conclude, the authors' attempted rebuttal reveals a fundamental error in their reasoning: their Eqs. 11 and 12, which they view as the main result, do not prove localization, any more than writing down the Hamiltonian. The points I made in my first report stand. The manuscript must therefore unfortunately be rejected.

Reject