Dear Dr. Hildebrandt,
We would like to thank the referees for their helpful comments,
suggestions, and criticisms. Enclosed is a revised manuscript which
addresses their various points.
Below, we have reproduced the comments from the three referees
verbatim. After each, we detail the changes to the manuscript that
have been made in response to those comments. In almost all cases, we
have made the changes that were suggested or recommended or implied.
There are however a couple of places where we do not entirely
agree. In those cases, we have explained and justified our reasoning
and choices in more detail.
We also enclose a plot and short calculation intended for the first
referee, showing three different values of the chirp mass obtained
directly from the time/frequency data. These are described but not
detailed in the manuscript (where they have been left as an exercise
for the reader) but we thought it would be helpful and save time for
the referee.
Referee #1 is clearly an expert in the field, and we are extremely
grateful for the mistakes and errors that they spotted. However we
would like to point out that the target audience for this paper is not
the specialist or expert, but precisely the opposite. It is for this
reason that we have not always detailed every imaginable caveat and
caution. Doing this would make the paper less accessible, and
complicate what are essentially simple paper-and-pencil arguments. We
believe that the revised manuscript reflects a reasonable compromise
between these two opposing tensions.
Sincerely,
Bruce Allen, Ofek Birnholz, Alex Nielsen, on behalf of the LIGO
and VIRGO Collaborations.
----------------------------------------------------------------
Reviewer #1:
* Finding zero crossings
Footnote 3 says "we averaged the positions of the (odd number of)
adjacent zero crossings." This is not clear, as the sentence without
the parenthetical statement implies something different from what is
implied by the parenthetical statement. Does it mean that to find the
position of zero crossing i, the average was taken of the positions of
zero crossings i-1, i, and i+1? If so, I would suggest saying
something like "we averaged the positions of the zero crossing in
question and its two neighboring zero crossings." For which zero
crossings was this averaging necessary?
We clarified this in footnote 3 and the first paragraph of section
2: we averaged 5 zero-crossing positions for the data point at
t~0.35s. Averaging was not required for any other data points.
* Nonlinear effects
"The merger of two black holes could have included highly nonlinear
effects, making any Newtonian analysis wholly unreliable for the late
evolution. However, solutions of Einstein's equations using numerical
relativity (NR) [10–12] have shown that this does not occur." This
is sloppy. The cited papers show that PN disagrees to some
significant extent with the numerical results (even when using higher
orders than 0PN), and it is clear that the merger does include
"highly" nonlinear effects. From a PN perspective, the "late
evolution" is actually singular, leading to infinite metric
perturbations. Numerical simulations show that nonlinearities take
over before the singularity is reached, meaning that PN cannot model
the end very well. The authors have overextended here. I suggest
rephrasing this very carefully, to allow that nonlinear effects are
important, but to explain that PN still gives a good qualitative
representation of the data until quite late in the inspiral.
We rephrased as suggested, and rearranged paragraphs 4 & 5 of the
Introduction for clarity.
* Reason for frequency doubling
The authors say that "the quadrupole moment [of gravitational
radiation] is invariant under reflection about the center of mass,"
which they say "implies that the gravitational wave must be radiated
at a frequency that is twice the orbital frequency." There are a few
problems with this.
1) I cannot find a similar statement in the cited reference. Perhaps
the authors only meant that reference to support the claim that the
radiation is quadrupolar at leading order. If so, the citation should
be moved closer to that statement. It is also possible that Landau
and Lifshitz do actually make a similar statement, but I cannot find
it because the citation is just to the book as a whole. Generally one
should provide page numbers when citing a book for a particular fact.
2) Reasonable interpretations of the statement are false. It is not
clear precisely what is meant by "the quadrupole moment", but if one
takes the 2,2 mode, one may note that while it is maximum along the
orbital axis, it is actually zero in the opposite direction.
Obviously, we would need to also use the 2,-2 mode, but even then it
is not clear how to evaluate the field at the reflected point when the
field depends on the orientation of the detector. If one instead uses
a quadrupolar tensor, how are the components found? How does one
compare tensors at two different points on a manifold? One could
speak of the *amplitude* of the field, but this is not what is
measured by a detector. The point is moot, of course, for the
following reason.
3) Most importantly, the conclusion would not actually follow
logically from any knowledge of the field's behavior under reflection
about the center of mass. An observer at a fixed sky location
relative to the binary does not soon measure the field at a point
reflected about the center of mass unless the observer is on the
equatorial axis, which is presumably not relevant to the case of
GW150914.
Instead, the authors presumably intend to point out that the
quadrupolar components are invariant under rotation by \pi about the
orbital axis, since the waveform modes vary as e^{-i m \phi} and the
quadrupolar components are m=+/-2. (The authors will need to find a
suitable and specific reference for this fact.) An observer at a
fixed sky location will measure the field at one instant, the binary
will have rotated by \pi a moment later, and the observer will measure
(roughly) the same field at that instant. This is why the dominant GW
frequency is roughly twice the orbital frequency.
Of course, it should also be noted that this is only roughly true,
because the frequencies (and amplitudes) are time dependent, and the
"amplitude" itself is actually a complex quantity. The authors should
simply say that the dominant time dependence is due to rotation about
the orbital axis.
We rephrased the entire paragraph (now paragraph four of page 3)
to explain the origin of the quadrupolar nature of the radiation,
relating to rotation by \pi about the orbital axis as the relevant
symmetry. Note that for a fixed observer, the rotation by \pi
symmetry implies an identical h_{ij} by Eq. (4). We also added a
reference to Appendix A (which demonstrates where "2\omega" comes
from) and to the exact pages in Landau & Lifshitz. We did not
take up the spin-two form of the argument as suggested by the
referee because this paper assumes minimal (undergraduate)
knowledge.
* Determining the mass scale
In Sec. 2, the authors say that "a value for the chirp mass can be
determined directly from the observational data, by plotting the
frequency and frequency derivative of the gravitational waves as a
function of time," and say that "the implied chirp mass value
... remains constant to within 25%." This is an important claim
because, as the authors write, "The fact that the chirp mass remains
approximately constant ... is strong support for the orbital
interpretation." Unfortunately, I see no evidence for this claim.
The authors do plot the frequency (^-8/3) in Fig. 2, but these values
are very noisy. How do the authors estimate the frequency derivative,
df/dt? Is it estimated directly from the data? If so, how do they do
it, and how reliable are the results? If not, are they using Eq. (7)
in some sort of circular reasoning? Are they using the slopes of the
lines shown in Fig. 2 somehow? If so, they are using a constant value
for df/dt, which is obviously wrong, and would seem to argue that the
orbital interpretation is wrong.
It seems like the most convincing evidence for this important claim
would be to find the values of f and df/dt at various times (and
explain how those values are found), and then plot the right-hand side
of Eq. (7). This would be an interesting plot. However, I suspect
that the data is simply too noisy, meaning that this paragraph would
have to be removed. Of course, the following argument is sufficient,
and uses the analytical formula to avoid calculating df/dt from the
data. The conclusion to be drawn, however, is slightly weaker: the
data are consistent with Eq. (7).
The manuscript describes two methods for estimating the chirp mass:
the first uses point-wise values for f and fdot (Eq. 7), the second
uses an integral form over several cycles (Eq. 8). The second
method uses only t and f=1/(2\Delta t) (estimated for zero
crossings, as described in the manuscript). The first method
additionally needs fdot values for the fitting. In the paragraph
following Eq. (7) we have added a clarification text describing how
fdot was obtained for the first method: we estimated tangents to
the time-frequency curve (Fig. 2) to obtain the slopes (d ln(f)/dt
= fdot/f). While we don't give further details in the manuscript,
we have provided a plot for the referee to show how this works. In
this plot we used 3 points (f = 45, 64, 128). The chirp mass Mc
estimates came to within ~35% (32, 41, 30) (rather than the
previouslu quoted %25). We have not added this explicit plot with
the tangents to the manuscript, so this is left as an exercise to
the reader.
* "Proving" compactness
The title of Sec. 3 begins with "proving compactness". Proof is a
delicate topic, and this section surely does not meet the criteria. I
suggest using "evidence for" in place of "proving".
We changed "proving" to "evidence" in the title of Sec 3.
Similarly, "the possibility of non-compactness is thus refuted" is too
strong, because "to refute" means to disprove. This should be
replaced by something like "non-compactness is inconsistent with our
model of the data."
We changed "refuted" to "inconsistent" in footnote 4.
* Defining compactness
The rest of the paper uses the compactness parameter frequently, but
Sec. 3 never establishes the scale of interesting compactness. What
would the compactness be for some types of star, white dwarfs, and
neutron stars just as they touch or overflow their Roche lobes? What
if one component is a black hole, but the other is not? At what
compactness can we conclude that we have two black holes? This is one
of the most interesting questions about GW150914, but the reader is
left with no better idea about the evidence for two black holes after
reading this paper.
We've added several examples illustrating the compactness of binary
systems to the last two paragraphs of Sec 3 (Mercury, HM Cancri,
Sig A*, Cyg X-1). All are orders of magnitude less compact than
GW150914. A discussion of why such highly compact objects should
be black holes appears in Appendices B and C.
* Orbital eccentricity
The authors say in Sec. 4.1 that the correction due to orbital
eccentricity can be neglected because orbits circularize faster than
they merge. That's not a very strong argument, because the orbit may
have started out very highly eccentric or may have been disturbed in
the recent past (an event which might have initiated the merger, for
example). It would be better to say that we *don't expect* the orbit
to have such high eccentricity, and so we neglect the correction.
There is no positive evidence presented in this paper we *can* neglect
the correction; it's just what we do, and we find that we can tell a
consistent story.
If the authors have actual evidence that the system is not eccentric,
it would be great if they could include it in this paper. Otherwise,
they need to make clear that the assumption of low eccentricity is
just that, however well motivated it may be.
We've expanded this subsection (4.1). In the second paragraph of
4.2 we describe the modulation that would appear in a signal from a
highly eccentric system. There is no such modulation observed in
the data. In the third paragraph we also explain that this is to
be expected because the GW emission quickly circularizes the orbit.
* Effect of spin
In Sec. 4.3, the authors discuss the effect of spin solely in terms of
the change in the horizon radius, while still assuming Keplerian
dependence of separation on frequency. But surely extremal Kerr black
holes would alter that relationship. How does spin affect Kepler's
equation?
Sec 4.3 (the sentence after Eq. 12) specifically says it defers the
effects spins have on the orbital dynamics to Sec 4.4. Sec 4.4 then
explains that the spin effects on the dynamics are suppressed by
the post-Newtonian parameter, and so only significant in the
already-compactly-close regime.
* PN order
The authors say that "Strictly speaking, x = 0 corresponds to the 0PN
approximation." That's not precise enough to be true. Similar
statements may be true. For example: the 0PN approximation is only
precisely correct at x=0. Or: if x=0 then all PN approximations
agree. Alternatively: x^0 corresponds to 0PN. The authors should
reword this statement to be clear and true.
We reworded the first paragraph of Sec 4.4 as suggested.
* Validity of PN
"As Newtonian dynamics holds when x is small, the Newtonian
approximation is valid down to compactness R of order of a few."
How does this follow? If x~2/small. Why should
2/small be a few? The physicist's standard value of "small" is 0.1 or
less, in which case the approximation would only be "valid" for R>~20.
Surely this is not "a few". Even if I plug in the frequency from
Eq. (3), I get x=0.28, which implies R~7. Does 7 count as "a few"?
Perhaps the discrepancy suggests that the approximation is no longer
"valid".
And what does "valid" mean, anyway?
Thank you for spotting this!! There was indeed a typo in the second
paragraph of Sec 4.4 in the x to R relation, which we have
corrected to x~1/(2R). For x~0.28 this gives the ~1.8 (we used
x~0.3, thus quoted R~1.7), which certainly qualifies as "a few";
taking 0.1 as the definition of "small" gives R~5, which we think
also justifies the language for "down to a few".
* Proof by contradiction
"Reductio ad absurdum then shows that the orbit must be compact: if
one assumes that the orbit is non-compact, then the Newtonian
approximation is fully valid and leads to the conclusion that the
orbit is compact."
If one bandies about Latin terms for logical arguments, one must be
prepared to play by the meticulous rules of logic. In particular, one
must state the premises and apply the transformation rules of
propositional calculus correctly. Unfortunately, the authors failed
to state their premise completely, then failed to correctly negate
that premise, and thus fell victim to the fallacy of false dichotomy.
Here is a non-exhaustive list of premises required to conclude via the
Newtonian approximation that the system is compact:
1) The features identified in the data by the authors are real, and not
caused or substantially altered by noise.
2) Those features *prove* that the source is a binary system, as
opposed to a single or triple or some exotic source.
3) Those features *prove* that the binary is not highly eccentric.
4) Those features *prove* that the spin is not important.
5) The binary is non-compact during the observation interval.
6) General relativity (and by implication, the Newtonian model for
non-compact systems) is a good model for physics.
A proof by contradiction simply proves the negation of the conjunction
of the premises, or equivalently proves the disjunction of the
negation of each premise. For example, this might show that the
features identified in the data are not real, or are caused by noise;
or that the source is not a binary system; or that the binary is
highly eccentric; or that spin is important; or that the binary is
compact; or that we really don't understand how such a binary should
evolve. No one of these statements can be selected as the single item
that is proven by the contradiction without *proof* of all the other
premises.
Now, the authors might reply, for example, that in Sec. 4.3 they
argued that spin is not important, and thus the stipulation of small
spin can be removed. First of all, there's some circularity to this
argument: assuming the Newtonian approximation is valid (which is true
only if the system is non-compact), we "prove" that the spin is not
important, which allows us to "prove" that the system is compact.
Second, the model space is multi-dimensional, and the authors have
only investigated a single dimension at a time; perhaps a combination
of factors would lead to different conclusions. In any case, they
have not *proven* any of this, and physics is a messy affair of
multiple lines of (sometimes contradictory) evidence. If they wish to
approach the level of rigor in which a proof by contradiction is
possible, they must not be so quick to dismiss possibilities.
The cure for these problems is fairly simple: the authors should avoid
pretensions to proof. They should simply say that the contradiction
implies that either the system is indeed compact, or some other
element of their model is substantially wrong---or both. But if one
is persuaded that the model is reliable, one should believe that the
system is compact.
The contentious paragraph (2nd paragraph of 4.4) is important to
the logic of the paper and we do not want to water it down too
much. However we have softened the language a bit and reworded to
make it clear that the validity of Newtonian mechanics and the
validity our data analysis are assumptions. We do not use the term
"prove" but rather "leads to the conclusion", and removed the
Latin.
We do maintain that in any argument, assumptions must be made; for
example a student learning Newtonian mechanics "proves" that the
external gravitational field of a spherically symmetric object is
unchanged if all the mass is concentrated at the center. This
result is not stated in the form, "If Newton's laws of gravity are
correct, then...". Similarly here, we are discussing experimental
observational data, and are obviously assuming that our data set is
valid, that Einstein's theory of general relativity is correct, and
so on. So it's clear from context that our "proof" is contingent;
a complete list of assumptions is not required or appropriate here.
* [I should note that the end of Sec. 4.4 contains one use of the word
"refute" to which I will not object. The authors say that an argument
does not refute their conclusions, which is true because there is no
refutation in science.]
Thank you. There are now no other "refute"'s in the text, nor
"proof"/"prove".
* Plunge trajectory
What is a plunge, when might it begin, and what drives the changes in
frequency when it does?
In paragraph 1 of Sec 4.5 we have added a short discussion of the
innermost stable circular orbit, of the enery-loss-driven inspiral
for orbits outside that versus the plunge trajectories inside it.
We also reference the pages in the Misner, Thorne & Wheeler
textbook (MTW).
* Strain at 100km
"the strain can be at most h ~ 1, at a radius of the order of the
Schwarzschild radius of the system R ~ 100 km."
Why should that be the case and/or relevant? How well-defined is
strain at such a dynamic place?
"the amplitude decreases as h ~ R/d_L"
Why should this be the case? Surely the 1/d_L behavior can only
reliably be said to start in the wave zone, R ~ c/f ~ 2000 km, which
would lead to a distance bound of d_L <~ 65 Gpc, which is not very
interesting given the size of the universe.
I don't believe this entire paragraph; I suggest leaving it out.
This argument (given in the first paragraph containing equation 18)
is correct, and entirely in the spirit of the order-of-magnitude
arguments given in this paper. Yes, we could of course formulate
the argument in the wave zone of small linearized perturbations,
say starting at a distance R~2000km, with h a small perturabation
h~0.1 (the suggested acceptable "small"). Or at a distance of
2,000,000km, with h~0.0001. But the conclusion is the same,
because the amplitude decreases proportional to the inverse of the
luminosity distance 1/d_L (which certainly holds in the wave zone)!
The resulting upper bound would not change. So we are giving the
argument in its simplest and most direct form.
In the following paragraphs, we obtain a much more accurate
distance estimate. This more accurate estimate shows that the
luminosity distance d_L is about an order of magnitude larger than
given by the first cruder estimate. This demonstrates that h is
only about ~0.1 in the system zone. So bounding h<~1 in the system
zone is conservative and justified in this case.
To summarize, we do not give wave-zone calculation, because (a) it
does not lead to a different conclusion, and (b) we immediately
give a more accurate estimate.
* Universal peak luminosity
The peak luminosity scales roughly with the square of the mass ratio,
but the mass ratio varies from 1/4 to 0. Yet the authors say that the
given luminosity is universal. Would it be better to say that the
luminosity does not change in order of magnitude over some relevant
range of mass ratios?
Yes. We reworded this to make it clear that we are discussing cases
where the masses are equal or near-equal (3rd paragraph of Sec. 5).
* Emitted energy and power
"During the peak of its emission, GW150914 emitted about 23 orders of
magnitude more power than this, in the form of gravitational waves."
Is this meant to be calculable from the previous paragraph and a half?
If so, there's been some sleight of hand, involving translation from
energy to power. The conclusion of Eq. (21) estimates the total
energy output by the GW150914 system during its lifetime. How is this
converted to power? By multiplying the ~300x greater energy from
GW150914 by the 3e17 sec in ten billion years, and dividing by ~0.001
sec? Where could that last number come from? The authors might argue
that most of the energy is emitted in the final instants of the merger
due to the dot and square on h appearing in Eq. (19), but I would only
believe this comprises ~0.01 sec, judging by Fig. 1. The numbers need
to be checked. And in any case, this should be explained more
clearly, because it would be an interesting fact.
The text in the final paragraph of Sec. 5 was ammended to clearly
distinguish between total energy (x300 than the solar output) and
power. The power was corrected to 22 orders of magnitude greater
than the sun, calculated from the peak luminosity 0.2*10^-3
L_Planck, which corresponds to one cycle at peak amplitude (about
6ms).
* Generating gravitational waves
Appendix A starts into some detail about the relationship between
emitted waves and their source. It surprises me that the authors
don't bother going into any detail about where these equations come
from. It's relatively simple (see MTW, for example) to point out that
Einstein's equations can be linearized, and a simplifying gauge choice
can be made, so that you just get a wave equation for h_{ab}, for
which the equations are basically Q_{ij}, up to time-derivatives and
constant factors.
The point of this paper is to discuss the source system (and its
observational properties) rather than Einstein's equation or
linearizations thereof. But we added a footnote (number 5,
immediately after equation 5 in Section 2) on this derivation and
the exact MTW location, for the interested reader. This is in line
with keeping the Appendix as a "worked out exercise" that is
accessible even to first year students.
* Minor points
There seem to be some latex issues (missing backslashes?) in the units
for G and c on page 1.
Thank you, we have fixed this!
The shaded region in Fig. 5 seems a little misleading, as it suggests
(without careful reading of the caption) that it actually bounds the
region of possible. It would be better to place another line at e=0.8
and remove the shading. Or maybe this could be turned into a contour
plot, with y axis being the eccentricity and the "z" axis being the
compactness ratio.
We changed Figure 5 to a colour-graded contour plot with the "z
axis" marking the compactness ratio, as suggested.
"Unto" -> "into" at the bottom of page 8.
Fixed.
"It's" -> "its" in the paragraph before Sec. 6.
Fixed.
Reviewer #2:
Major points:
* Not Cosmologically distant
If I am not mistaken, Eqs. (4) and (5) hold relative to an
asymptotically flat background metric. If this is correct, then these
equations already implicitly assume that the source is cosmologically
nearby, and this should be mentioned right there.
We added this statement in the paragraph after equations 4 & 5.
* Keplers law holds even in GR (for test masses)
Following Eq. (6), the authors state that Newton's laws of motion and
of gravity were used to derive Eq. (7). I am not quite sure about this
statement since Kepler's third law continues to hold for circular
orbits in Schwarzschild geometry. As long as the two black holes can
be considered sufficiently detached, not even Newton's laws need to be
assumed. One might go one step further and define a modification of
the reduced mass such that Kepler's third law continues to hold
further beyond the Newtonian regime. Perhaps this could be further
clarified.
It is true that Kepler's third law is also holds for a test
particle orbiting a non-spinning BH in general relativity. This
indeed in gives the same mass-separation-(orbital)frequency
relation for (adiabatically) stationary orbits. But unfortunately
we can not give up Newtonian mechanics for this elementary
presentation: concepts such as energy and its time derivative
(power) are needed to describe the change in those orbits due to
energy loss.
* Adiabatic orbital changes
Also, in Appendix A, it seems to me that the assumption needs to be
made that the loss of energy per orbit is small compared to the
orbital energy because Kepler's law is used for evaluating the energy
loss. This does not harm the argument made, but should also be added
for clarity.
We added a statement of this assumption at the end of the paragraph
containing equation (27).
* Can near-equal masses be concluded in this paper?
The only assumption for which no strong (empirical) motivation is
given is that of equal masses. It is estimated later that even the
lower mass must exceed approximately 11 Solar masses, but this still
allows a large range of mass ratios. It would be helpful for the
reader to learn what property of the data forces the masses to be
similar even if the argument could not be given quantitatively.
The mass ratio has a considerable effect on the waveform at the 1PN
order, but that is unfortunately beyond the scope of this paper,
which is 0PN. But we have added a comment and discussion with
references about this point to the second paragraph of the
conclusion.
* Minor points:
The statement "main-sequence stars have radii measured in millions of
kilometers" should be rephrased in view of the fact that the Solar
radius is about 695000 km.
We fixed this by making a more precise statement after Equation 9.
Given that an upper mass limit of 4.76 Solar masses is conservatively
adopted later, the statement that 5 Solar masses were "significantly
above the neutron star mass limit" (p. 7) seems exaggerated.
We reworded the second paragraph after Eq. 9 so it is now slightly
milder, with a reference to App. B (using a limit of ~3 solar
masses for neutron stars).
* Tiny points:
It seems that the reduced mass µ is used for the first time in Sect. 5
(p. 8) without definition. This should be defined.
We moved the definition of reduced mass to before equation 6.
Following Eq. (1), "rm m^3/kg s^2" and "; m/s" should be replaced by
"{\rm m^3/kg s^2}" and "\; m/s".
Thank you, this has been fixed!
"During it's ten-billion-year lifetime" (p. 9, left column) should
read "During its ten-billion-year lifetime".
Fixed.
"does the end" (p. 11, left column) should read "Does the end".
Fixed
Reviewer #3:
There were no specific comments to address.