REFEREE REPORT(S):
Referee: 2

COMMENTS TO THE AUTHOR(S)
The authors have successfully addressed most of my concerns. In
particular, my suggestion that the apparent (2,2,2^n) nature of their
inequality requires a FSSO analysis paradigm is reasonably well refuted
by the author’s explanation that their approach “includes the
realization part already in its definition,” and in this sense
inequality (9) can be applicable to a (2,2,2) scenario. The rewrite of
Section 2 is an improvement over previous drafts, though not quite as
extensive as I had been hoping. I therefore have only two remaining
comments. While the first comment in particular represents a serious
remaining concern of mine, I expect both comments can be addressed with
a small amount of rewriting. If the authors are amenable to a minor
revision addressing these comments, it is likely that I would recommend
the revised paper for publication, as I believe that the paper is
correct (modulo the comments below) and the results are novel and
interesting.

C1). I still believe that Figure 1 and the model it suggests are
problematic. This is because the paradigm of Figure 1 admits reasonable
local models for which the uniform complexity assumption is false. Thus
if one sees data violating (6), one could cite these models as a reason
for rejecting uniform complexity (UC) instead of local realism (see the
last sentence of Section 2, where this choice is made explicit) without
having to concede that anything strange or noteworthy is going on in the
experiment.
Here is a concrete example of a Figure 1 type model not satisfying
uniform complexity. Alice’s machine contains a program \Lambda for which
1) if the first settings input is a0, the readout for the rest of the
experiment is 000000000... regardless of future settings 2) if the first
settings input is a1, the readout for the rest of the experiment is a
random (or pseudorandom) string with a 50-50 probability distribution
over 0 and 1, independently of future settings. Suppose that Bob’s
machine does exactly the same thing as Alice’s. Now consider what
happens with respect to the uniform complexity definition in the last
paragraph of Section 2. A) For experiments that start with an a0 for
both Alice and Bob (25% of all experiments), all complexities K are very
low (just enough information to say “print N zeros”). B) For experiments
that start with a1 for both Alice and Bob (25% of all experiments), all
complexities will be large, of order N with high probability. I don’t
claim that this model violates (9), but this is irrelevant to the larger
point, and in any case it’s possible that a more creative example might
actually violate (9) with high probability.
An important characteristic of the preceding example is that the UTMs
have trial-to trial memory. We can consider more basic local models,
i.i.d. ones where each output bit is governed locally by a (p,1-p)
distribution, where p can be different for the two different setting
choices for Alice, and again for Bob, but the four p’s stay the same
trial to trial. This encompasses the entire class of i.i.d. local hidden
variable models that are usually assumed in the standard analysis of a
basic CHSH experiment. Such models DO obey uniform complexity (with high
probability). So the author’s paradigm of (9) with the UC assumption
covers the “usual” case, and probably covers additional reasonable
paradigms (for instance a FSSO experiment, but I accept that the authors
do not want to pursue this idea). But uniform complexity does not cover
the full richness of what is suggested by Figure 1, as exemplified by
the example above.
The authors seem to want to keep Figure 1. I can accept that if they are
willing to add some sentences proximal to the last paragraph of Section
2 (where uniform complexity is introduced). These sentences must 1)
point out that not all models obeying the UTM paradigm appearing Figure
1 will obey UC, which could be well addressed by describing a
counterexample like the one above, and 2) nevertheless motivate UC by
explaining that it at least covers the local i.i.d case, so the class of
rejected models is at least as large as that already rejected by a
standard CHSH analysis. On a related but less crucial note, the authors
should probably mention the uniform complexity assumption again in
Section 7 (Discussion).

C2). I think I finally understand Section 3.1, which was giving me some
trouble previously. I just have a few additional minor questions about
this section. First, it is said that “Inequality (5) becomes an entropic
Bell inequality if local entropies are maximal, H(x)=H(y)=N.” Is it true
that the local entropies are maximal if and only if all binary random
variables have a 50-50 distribution? This would be a rather restricted
case, failing to encompass many i.i.d. local models. While this is not a
problem per se, it might ease possible confusion to acknowledge this. On
a related point, the current paper seems to restrict the measurement
configurations to coplanar measurements separated by angles of theta,
theta, theta, and 3 theta when trying to maximize (6), and cites [2] as
a justification for such a restriction. But since (6) does not reduce to
the inequality of [2] (except for the local-entropy-maximal case), this
doesn’t seem like sufficient justification for reducing the search space
for maximizing (6) in the current paper. So it would be good to add a
sentence or two fleshing out why we look at only measurement angles
satisfying this constraint when trying to maximize (6) – even if the
only reason was that such configurations have an appealing symmetric
character. (My concern is one of clarity and exposition, not that I
think the search space needed to be bigger.)

There are also a few typos and grammatical errors: page 2 line 22,
“using the conditional Shannon entropy”; page 2 eq. (1) check the
subscripts; page 3 line 24 perhaps remove the comma after “instead”;
page 3 line 33-35 one occurrence of the word “to” is redundant, p 5 line
35-45 it would be helpful to specify i,j \in {0,1} here, see also p 11
line 20-30; page 6 line 17 I think you mean eq (1) not eq (5).

COMMENTS FROM EDITORIAL BOARD:
Associate Editor
Comments to the Author:
Please revise your manuscript a final time to address the outstanding
points of Referee 2.