Peer review of: On quantum gravity tests with composite particles (2020)

Reviewers' Comments: 
 
Reviewer #1: 
Remarks to the Author: 
The paper by Kumar and Plenio discusses the possibility to test a class of quantum gravity theories 
in which a minimal length scale, possibly of the order of the Planck length, is obtained by means of 
deformed commutators. 
 
In particular the paper focuses on the possibility to test these theories and obtain an upper bound 
in the deformation parameter \beta using composite macroscopic system made of many 
constituents. 
 
I see three main results of the paper: 
 
i) a new phenomenological proposal for comparing this kind of tests introducing a 
phenomenological dependence upon the number of particles N, in order to take into account the 
so-called "soccer-ball" problem. In this proposal \beta is replaced by \beta/N^\alpha, and one has 
to compare results in a 2d plane for \beta and \alpha. 
ii) the use of an accurate old experiment testing the amplitude dependence of the period of a 
pendulum for deriving a new more powerful bound for the deformation parameter and \alpha, 
improving recent bounds derived from experiments with various microscopic and macroscopic 
resonators. 
iii) The analytical study of the deformed algebra and the demonstration of the equivalence of the 
classical treatment with deformed Poisson parentheses and a quantum treatment with deformed 
commutator and appropriately defined deformed coherent state. 
 
The paper is clearly written, and the results are novel and interesting, implying that the paper 
certainly deserves publication. However I think that, even though the topic is interesting and up-
to-date, the above results are of quite technical nature and therefore not suitable for the broad 
and general audience of Nature Communications. I think it would be more suitable for a more 
technical physics journal. 
 
To be more specific I add some comments on the three above results. 
 
1) Proposing to include an additional scaling of the deformation parameter upon the number of 
constituents adds a second phenomenological parameter (\alpha). 
In principle such a scaling should be deduced from theory and there are even arguments (see eg 
ref. 19) for 1/N^2 or 1/N scalings. Moreover the results of Ref 5, at three different masses suggest 
a scaling close to this. Nonetheless the difficulty of dealing with composite systems is here 
bypassed by adding this second exponent parameter \alpha. This is certainly legitimate in these 
phenomenological approaches, but the meaning of this approach and of \alpha remains quite 
unclear and a better justification would be appreciated. 
 
2) The pendulum experiment used by the authors is able to provide a much better bound because 
in this case the nonlinearity is well known and measurable. In this respect, the limiting factor of 
Ref 5 and 8 is that the measured nonlinearities cannot be compared with known analytical models 
and therefore in those cases they cannot take into account the intrinsic nonlinearities of the 
systems adopted. 
 
Moreover I am quite skeptical about the improved estimation for the magnetically levitated 
nanosphere. It is quite unrealistic and even not too much correct to assume the limit on the 
trapping frequency only given by the extremely low value of the nanoparticle damping. In fact, in 
this cases, the drifts and phase/frequency noise of the resonance frequency cannot be neglected 
and it usually becomes the main source of error in the estimation of the resonance frequency. 
Therefore I would take a much more conservative value for the frequency error. THis frequency 
noise is the analogous for qubit systems of T_2 dephasing processes, while mechanical damping 
refers to energy relaxation processes, T_1, which may be typically longer. 
 
3) I have found the comparison with the classical approach with Poisson parentheses and the 
quantum one with the commutator very interesting. As correctly pointed out in the paper, this 
works with a given (well justified) choice of coherent state, and I wonder if this approach con be 
further generalized and make it independent of the coherent state definition. 
 

 
Reviewer #2: 
Remarks to the Author: 
Rather than offering a recommendation I prefer to provide to the editors my assessment of the 
main strengths and the main weaknesses of this study, hoping to be of assistance for determining 
whether the manuscript is suitable for NatComm 
 
Overall I believe that this is valuable exploratory research. It proposes a way to face the challenge 
exposed in Ref.[19] 
(and partly in Ref.[3]) concerning the use of macroscopic systems in quantum-gravity 
phenomenology. The authors propose to handle this by modeling the dependence of the effects on 
the macroscopicity of the system, which in principle is a solid approach. 
 
The main limitation of the analysis resides in the assumption 
that the magnitude of the effects should scale simply like 
the inverse of some (fractional) power of the number of 
constituents of a macroscopic system. This might be a good (though still rough) starting point for 
phenomenology based on weakly interacting constituents, but in a typical macroscopic body the 
constituents interact strongly. 
When interactions are important one may expect that two different bodies, even when composed 
by the same number of constituents, would be affected by effects of different magnitude. 
 
 
 
Reviewer #3: 
Remarks to the Author: 
The paper is very well written and treats a topic that is timely and definitely of interest to the 
scientific community: how can we use low-energy physics (not a particle accelerator) in a lab to 
potentially devise bounds on possible modifications to quantum physics due to influences from 
quantum gravitational effects. In particular, the authors consider changes to the commutation 
relation between the position and momentum operators. They argue that the commutation relation 
should depend on two yet unknown parameters, which one can put bounds on by doing the proper 
experiments. The authors demonstrate this by analyzing existing experimental data to determine 
what bounds these experiments put on the parameters of their model. They also suggest how to 
possibly improve on existing experiments in order to achieve more stringent bounds. I found the 
paper a very interesting read, and given that I am also working on test of the foundations of 
quantum physics, I can confirm that the authors' research definitely is of interest for the field and 
should have a notable impact. I therefore recommend the paper to be accepted for publication in 
Nature Communications, possibly with a few minor modifications given some small comments I will 
list below: 
 
.) for equation 10, the authors assume that $\beta$ is much smaller than 1. If my estimations are 
correct based on the parameters the authors provide, then this should definitely be true for 
$\alpha$ larger than 0.01, but for smaller values of $\alpha$, $\beta$ tends towards larger values. 
Nevertheless, I get the impression that it never rises above a few percent, so it is probably true 
that $\beta \ll 1$ can be seen as valid for all values of $\alpha$. It might still be worth a short 
comment in the manuscript, because it was not immediately clear to me that this assumption 
would hold true. 
 
.) the authors specify $\gamma=1.2\times 10^{-7}\,$Hz and say that 
$\Delta\omega\simle\gamma/\sqrt{M}$, but $\gamma$ is in Hz while I expect $\omega$ is in 
rad/s -> is there a factor of $2\pi$ missing? Since this corresponds to nearly an order of 
magnitude, it might be relevant for the bound the authors set. 
 
.) if I take the values the authors state beneath equation (16) in combination with their equations 
(16) and (15), and if I assume (as the authors state) $\omega=\gamma/\sqrt{M}$, I arrive at an 
angular frequency of $\omega=36.8148\,$rad/s, a mass of $80.8437$kg and a lower bound on 
$\alpha$ that is 0.428224 - compared to the lower bound of 0.35 the authors state. Did I make a 
mistake or did they? If one assumes that the bound on $\Delta\omega$ still needs to be multiplied 
by $2\pi$, then I get a lower bound of 0.398512 for $\alpha$ - which still differs from the value 
the authors give. I wanted to point this out in case my calculations were correct. 
 
.) equation (18): it is not so obvious to me that an increase of mass helps. In the exponent, one 
has a negative term proportional to mass AND proportional to $N^2_p$ and a positive term 
proportional to $N_p$ and to the average momentum. An increase in mass will lead to a VERY 
strong change in the negative term that does not depend on the average momentum, and it will 
also lead to an increase in the term that does depend on the average momentum squared. The 
latter term depends on the mass to the third power, the former term depends on the mass to the 
fourth power. In addition, there is a $\lambda$ dependence, which may also depend on the test 
mass. The authors actually mention that large masses may reduce the coupling. Nevertheless, the 
precise parameter dependence would be interesting to look into in more detail. 
 
.) APPENDIX, subsection 3 - the authors introduce Gazeau-Klauder coherent states $\vert 
J,\gamma\rangle$ - I think it would be useful for a more intuitive understanding to describe what 
meanings $J$ and $\gamma$ have in this respect. 
 


 
 
Reviewer #4: 
Remarks to the Author: 
This is an excellent theoretical/experimental article which merits publication in this journal. 
However, I have a couple of issues with it, which I hope the authors can address before a final 
version is published. 
 
Above all I think that the article mixes very different matters, which indeed may be related, but 
this should be spelled out. Usually the issues of the "soccer ball problem" and of the dependency 
of deformations on the number of particles, N, appear firstly in momentum space. It is found that 
dispersion relations should depend on N if they are to avoid producing obvious contradictions (such 
as a maximal mass/energy for macroscopic systems). Here, instead, the dependence appears in 
the commutation relations between position and momentum space. 
However, it is well known that in order to render deformed dispersion relations observer invariant 
one should impose non-linear "Lorentz" transformations to energy and momentum. 
In turn this creates problems in defining their dual space of positions. It has been suggested that 
the factorization of duals cannot even be achieved in an invariant way, in the face of this situation 
(a nice split of duals requires linearity of transformations). For example it may be necessary that 
the position transformation rules of a particle (or system of particles) depend on its energy and 
momentum. 
 
Hence I am puzzled at this mixture of x and p in a scenario where clearly p is already modified in a 
form that depends on N, and this affects the 'x'. The authors should explain how their work relates 
in detail to previous definitions of the "soccer ball problem", typically hailing from momentum 
space alone, with consequences to position space which are highly non-trivial. Is there a "rainbow 
metric", which would also be N dependent, besides energy dependent? In what way is the Poisson 
bracket 
postulated here consistent with the relativity of inertial frames 
(assuming it is)? The fact that the system considered is non-relativistic is no excuse for skirting 
these problems. 
 
In addition, I note that the appearance of N in the dispersion relations is usually related to the 
issue of how to add energies and momenta. Often solving the soccer ball problem implies non-
associative addition laws (since the grand-total must know how many "terms" there are in the 
"sum", thereby precluding "associating" them). I doubt a detailed analysis of the inner workings of 
the experiments reported in this paper could be altogether insensitive to this issue. 
 
Having said this, I hope that the authors can address these matters so that I can recommend this 
paper for publication.