Reviewer #1: This paper describes the first gravitational-wave detection, GW150914.
It analyses the data using very simple techniques, and aims to rely on
a minimum of complicated physics to model the source. While full,
detailed analyses have been published elsewhere, this paper should be
approachable by anyone with a basic understanding of physics---even to
undergraduate physics students. It therefore fills an important niche
in the literature on this historic detection. The concept of this
paper is very exciting, and certainly should be pursued. It is also
fitting that Annalen der Physik should be the journal to publish this
paper, given its history in this field.
This paper should be published by Annalen der Physik, but it will need
substantial revisions first. While it is entirely appropriate for the
authors to use simplified analyses, they have oversimplified in many
cases, leaving out details that easily could (and should) be included.
Also, while it is appropriate for the authors to try to be as
convincing as possible, they have overextended in many places by
making far stronger claims than are supported by the evidence. There
is a persuasive case to be made that the GW150914 signal originated in
the merger of a pair of black holes; there is no need to overstep the
bounds of science and reason.
One of the most critical problems is that the authors frequently state
or imply that they are presenting proof of a statement, when they have
only supporting evidence that supports, suggests, indicates, or is
consistent with the claim. Proof is exceedingly hard to come by in
science. A key conclusion of the paper is laid out as if it were a
formal logical proof of that conclusion, which it is not (especially
because the logic is faulty). This is perhaps even more important in
this paper than usual---given the historic nature of the discovery,
the stature of the authoring collaboration, and the fact that the
target audience includes our impressionable youth, who need us to set
a good example regarding the place of reason and logic in
observational science. This is astronomy, not mathematics. We use
mathematics as a tool, but we can never hope to achieve the levels of
rigorous proof found in mathematics, because our observed universe is
more complicated than the simple and well-delineated universes
constructed in mathematics.
Fortunately, I believe all of these problems will be reasonably easy
to fix. Below is a list of the problems I have identified that will
need to be corrected before the paper can be published. If this comes
across as strident, argumentative, or simply long-winded, I hope the
authors understand that it is out of my great respect for the work
that they have accomplished, and my concern that their results should
be presented as well as possible.
* 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.
* 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?
* 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.
* 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).
* 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".
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."
* 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.
* 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.
* 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?
* 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.
* 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?
* 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.
[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.]
* Plunge trajectory
What is a plunge, when might it begin, and what drives the changes in
frequency when it does?
* 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.
* 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?
* 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.
* 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.
* Minor points
There seem to be some latex issues (missing backslashes?) in the units
for G and c on page 1.
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.
"Unto" -> "into" at the bottom of page 8.
"It's" -> "its" in the paragraph before Sec. 6.
Reviewer #2: This paper aims to describe how the essential conclusions from the first observed gravitational-wave signal inevitably lead to the conclusions drawn. Applying Einstein's quadrupole formula and Kepler's third law to the measured frequency and frequency change, the authors derive the chirp mass of the source and its orbital radius and conclude that only black holes can have created the observed signal. They then discuss the influence of their simplifying assumptions on the conclusions and show that they are qualitatively irrelevant. Finally, they estimate the distance from the observed gravitational-wave luminosity, conclude that the source must have been cosmologically close, and calculate the loss of energy by gravitational waves.
Even though the results have already been published elsewhere, I find this paper most illuminating and an intellectual pleasure to read. It is carefully written, clearly delineates its limitations, yet explains in a very accessible way how simple but robust conclusions from gravitational-wave observations can be drawn. I recommend the paper for publication in the Annalen der Physik once the authors have addressed the following comments and suggestions:
Major points:
– 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.
– 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. 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.
– 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.
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.
– 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.
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 fixed.
– 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".
– "During it's ten-billion-year lifetime" (p. 9, left column) should read "During its ten-billion-year lifetime".
– "does the end" (p. 11, left column) should read "Does the end".
Reviewer #3: Two clear events for the emission of gravitational waves
have so far been recorded by the Ligo (and Virgo) collaborations.
The purpose of the present paper is to give a detailed and
quantitative discussion of the first event GW150914 and its
basic physics. The paper is of great interest, well written,
and technically correct. It makes a strong case for the merging
of binary black holes to be the physical origin of the observed
gravitational waves. I can definitely recommend the paper
for publication in Annalen der Physik.