Stars, brown dwarfs and planets
Stars, brown dwarfs and planets
S Oxley & M M Woolfson
Physics Department, University of York, Heslington, York YO10 5DD, UK
A paper with the above title was submitted to the Monthly
Notices of the Royal Astronomical Society on 20th November 2000.
It was seen by three referees, all of whom recommended against publication.
The purpose of this presentation is to place into the public domain a contribution
to cosmogony that otherwise would not be available. For completeness the objections
that have been raised are also recorded here together with associated responses
and comments by the authors. The presentation is in four parts:
The paper, as presented to the journal, but with minor typographic corrections
not affecting the scientific arguments.
Referees' reports (as written without correction of spelling and other
errors) accompanied by authors' responses.
Rejection statement by Editors of the journal.
General comments on the Editorial policy of the MNRAS and on the ethics
of scientific refereeing.
One of the authors, Stephen Oxley, on whose D.Phil thesis
much of this work is based, is no longer in the academic field and this presentation
is made solely by M M Woolfson.
1 The paper
Click here
to view the paper in pdf format. (553K)
2 The refereeing process
The paper above was a revised version produced in response
to referee's reports on an earlier version. The first report received on the
earlier version was:
Report of referee A
MA409 is about the formation of planets and brown dwarfs through
Woolfson's 'Capture Theory', in which massive interstellar clouds are tidally
disrupted and induced to fragment by encountering a compact star in a young
stellar cluster. The authors also present new SPH models of this process.
Every serious astronomer - except Woolfson and his collaborators
- uses the planetesimal theory of planet formation. In this model solid matter
in the circumstellar protoplanetary disc agglomerates into protoplanetary cores.
Those that accrete substantial quantities of gas from the disc become gas giants,
such as giant planets of the Solar system. Evidence for accretional processes
in the early Solar system is well known and overwhelming. Recent (well known)
observations of an extrasolar planetary transit also confirms standard planetary
structure models. No serious astronomer believes there is any need to ditch
the standard model in favour of Woolfson's 'Capture Theory', which has under
gone very little detailed development since conception and has not been able
to account for the details of any significant observation. I can only recommend
that MA409 is not accepted for publication in MNRAS.
I should also note the following:
Much is made in MA409 of the protoplanet 'discovery' announced for TMR-1C,
this claim has now been repudiated (HST press release April 6, 2000).
Of MA409's 36 references 16 are to Woolfson and his collaborators - this
is not a fair reflection of the work done in star and planet formation. In
short, the paper shows extraordinary bias.
This report fell short of being an objective
scientific critique of the paper itself and the editor approached another referee.
Report of referee B
I have read through the paper and the previous referee's comments.
First of all I cannot agree with the previous referee that we should not discuss
alternative theories for planet formation as there is a standard model believed
by most astronomers (the use of "serious" astronomers I find needlessly insulting
and probably incorrect). It is clear that our ideas of planet formation based
upon one object, the solar system, needs some revision in the light of the newly
discovered extrasolar planets and their unexpected locations close to their
parent stars.
Nevertheless I cannot recommend publication of the paper as
I find that there are several minor flaws and one misleading major flaw that
invalidates the results.
Firstly, the timescale derived for the interactions uses an
encounter radius of 1500 au in order to achieve realistic numbers. In contrast,
the encounters that are presented in the paper have encounter radii of order
100 au. Thus the encounter rate derived is wholly inappropriate and misleading
to the reader. The relevant rate is at least 225 times less than the 5 per cent
quoted. In fact, using actual number densities (such as the ONC) encounter rates
at 100 au occur on timescales of > 1e08 years which explains why so many
of the stars in the ONC (age 1e06 years) still have disks of this size. This
would imply that BDs have a probability of encounters of ~1e-5, and thus in
a cluster of 1000 stars is negligible.
Secondly the paper states that it has used an SPH code including
radiative transfer yet not details of the calculations, methods or test cases
to prove the code are presented. This would be necessary before the results
can be published (or a reference to a refereed journal where the methods etc
is published).
Minor flaws include the lack of any recent references for the
parameters chosen. Indeed, densities of >10.4 stars/pc.3 are high for the
majority of stellar clusters (except the core of the ONC). Furthermore, there
is no convincing evidence for the low-mass stars having formed later than other
stars in the cluster. Pre-main sequence ages are extremely difficult to determine
and any reliance on PMS tracks is untrustworthy (see for example Tout et al
1999, MN, 310, 360). Along these lines the claim for free-floating planets in
the ONC is unreliable as there is as yet no way to confirm the PMS evolutionary
tracks used.
In general the idea seems interesting but the timescales involve
argue strongly against a significant number of planets forming in this way.
Details of the calculations would have to be made clear in order to determine
if they were reliable. It does seem that more realistic approach is that of
protostellar disks providing the mass for the planet formation (the work of
Whitworth and collaborators published in MN). The advatages are clear in that
the disks are sufficiently long-lived in order to have a reasonable chance to
undergo a close interaction (~1e7 years), and that the mass is already orbiting
the star.
This report was received on 26th
July 2000. While some of the points made could be challenged the major point
was accepted. The calculation of probabilities was made corresponding to a different
linear scale to that used for the SPH calculations. The calculations were repeated
at an appropriate scale and, at the same time, other pieces of analysis were
finished off that were included in the revised version of the paper presented
here. This was sent to MNRAS on 29th November 2000. On 4th
March 2001 I wrote to the editor asking if there was any response from the referee.
On 6th March the following report arrived by email.
Report of referee B on the revised version
This paper purports a new mechanism to explain the formation
of planetary system via the disruption of proto-Brown Dwarfs in stellar clusters.
The idea is interesting and there is certainly some validity in investigating
alternative mechanisms for planet formation. Unfortunately I cannot recommend
that this paper be published in MNRAS. I will list below my reservations about
this paper in decreasing importance.
The authors make much of a new algorithm for treating radiative transfer
in SPH, and that this inclusion is crucial for the results. In order to trust
the results, this algorithm and the results of tests and comparisons need
to be detailed. For example, the authors could compare results with other
numerical simulations of star formation that include radiative transfer. For
example, there is no mention of the actual evolution of the gas temperature
during the simulations. A failure to include any such information will bias
any reader against trusting the results of the paper.
A quick analysis of the initial conditions used and the condition that the
interaction occur on timescales less than the free-fall time imply that the
proto-brown dwarf must already be filling its Roche lobe. It is extremely
difficult to see how such a situation would arise as, presumably, the proto-Brown
Dwarf would form from less dense material and thus would be disrupted well
before attaining the desired ICs. This appears to be the case for any collapsing
cloud that contains less than 1/8 of the stars mass.
The section on the orbital evolution is completely unclear. A simple physical
explanation of the orbital migration on the necessary timescales would be
required. In any case, the authors have neglected further stellar encounters
that would disrupt many of the systems.
Significant amounts of the paper are actually irrelevant to the problem
and detract from the scientific content. This includes a large part of the
introduction, section 3, section 4, section 8 and most surprisingly, the majority
of the conclusions. It appears that far too much of the paper deals more with
defending previous work by the authors and possibly overturning the community's
opinion of that work. This is highly distracting from the paper's subject
matter and will surely bias the reader against the subject matter. It is also
clearly a waste of journal space. It does not belong in the paper.
I also have difficulties with several individual statements starting from
the first sentence of the introduction. This statement, that the first stars
that form in a clusterhave masses of 1.35 solar masses is not supported by
current research on star formation, nor could it be due to the large inaacuracies
in our present understanding of pre-main sequence evolution. The use of a
reference from 1969 when there is significant recent research in the subject
area does not give the reader confidence in the arguments advanced in the
paper.
on pg 13 the authors state that a protostar is formed when
a body of higher density than the surrounding medium is stable and able to being
the slow process of contraction. This is misleading as it implies a non-dynamical
nature of star formation.
In fact, a protostar is formed at the end of a gravitational
collapse event (from unstable Ics), once the density has increased sufficiently
such that infrared radiation can no longer escape freely from the object. This
occurs on the object's free-fall time and is not slow, but in fact is generally
faster than the interaction timescale for realistic Ics.
In conclusion I cannot recommend publication of this paper.
The policy of MNRAS is to base rejection
on two referee's reports but, in view of the brief nature of report A the Editors
gave us the opportunity of having the paper sent to a third referee if we chose.
However they stated that they would send the report of Referee B to the third
referee. We requested that if they did so then they should also send our response
to the report. This follows.
Response to comments of Referee B on revised version
The referee's comments are dealt with, by and large, in the
order presented that is in his order of decreasing importance.
In his preamble to making specific points the referee refers
to the paper as describing the disruption of brown dwarfs in a cluster. Actually
the interactions considered are not restricted to those involving a brown dwarf
and he should have noticed that the three computational examples most relevant
to later parts of the paper involve protostars that have main-sequence masses.
During the more-than three months the referee kept the paper we have concluded
that in the embedded stage of cluster development proto-bodies at the lower
end of the brown dwarf mass range may not play a role. This makes no significant
difference to calculated probabilities - at most a factor of two. Probabilities
depend much more, and linearly, on stellar number densities in the embedded
state that can vary by three orders of magnitude.
We are fully aware of the need to validate new code (see An Introduction
to Computer Simulation by Woolfson & Pert, OUP, 1998, pp.30-31). In
correspondence with the Editors it was agreed that the Web reference giving
access to the entire doctorate thesis of one of us (S.O.), that describes
the radiation transfer algorithm in some detail, would negate the need for
description within this paper. Pages 180-198 of the thesis are devoted to
validation in four situations relevant to the model we are exploring.
In the top paragraph of page 10 (towards
the bottom of p.6 in the present paper format), that must have escaped
the notice of the referee in his scan of the paper, we refer to this testing
quite specifically. I cannot believe that the referee wishes us to reproduce
in detail what has occupied 19 pages of a previously-published piece of work.
This comment needs to be taken together with comment 5. The referee is correct
in that the protostars in simulations A and C fill their Roche lobes but that
is not true for simulation B. The starting point for the calculations is quite
arbitrary so that starting, say, 500 AU further away would give an outcome
different in detail but similar in general characteristics - i.e the formation
of some bound and some free protoplanets. In practice, moving the initial
position of the protostars slightly further away helps protoplanet formation.
The protostar is still diffuse when it comes within the distance for significant
distortion but the slow collapse it is then experiencing helps to give a more
compact filament. Having said that we do not believe that a protostar cannot
form at a distance that places it within the Roche lobe.
We seem to differ in our definitions of a protostar. The
referee's definition puts the start of the protostar stage somewhere close
to the beginning of Kelvin-Helmholtz contraction whereas we take it to begin
when there is a discrete identifiable mass of material that will evolve to
form a star. Our definition seems more in accord with usual nomenclature -
for example, Hayashi's original description of the evolutionary track of a
protostar on an H-R diagram starts with a very diffuse body of radius
about 4,500 AU that then begins a free-fall collapse. Anyway, we make it quite
clear what we mean by a protostar; at the top of page 14 (middle
of p.10 in present paper format) we say explicitly that we refer to
a body at the beginning of its free-fall stage. The referee failed to notice
this, assumed that we are referring to a protostar according to his definition
and then points out the problems that this would introduce.
In our paper we did not raise the question of how, and in
what state, protostars form but since this is an issue raised by the referee
we must respond to it although I do not think that this material needs to
be added to the paper. We refer to the paper, Woolfson (1979), given in the
references. This describes star formation as due to the collisions of streams
of matter within a turbulent collapsing cloud. Stars formed in this way have
comparatively little angular momentum and, indeed, peripheral material in
the colliding streams, which is not compressed, can be captured to give a
surrounding disk within which almost all of the angular momentum resides.
This is the kind of starting point from which planet formation can begin in
the solar nebula approach. As the referee has stated, star formation is a
dynamic process. Streams of matter with high Mach number can collide and form
condensations anywhere. Clearly, in the vicinity of another star the initial
shape would not be spherical but, in any case, our spherical starting model
very quickly adopts the shape required by the prevailing equipotential surfaces.
The referee seems, by implication, to be disparaging the
1969 paper we quote on the analysis of young stellar clusters. This depended
on locating stars on an H-R diagram and hence determining their ages and masses
from theoretical evolution tracks on to the main sequence. It indicated one
stream of development, starting at about class F5 or so and progressing with
time to smaller mass stars and a separate stream in which progressively larger
mass stars are produced. The 1979 paper interpreted the first stream as due
to the primary formation process and, as indicated above, these stars spin
comparatively slowly. The second stream was analysed in terms of mass increasing
by accretion. The derived relationship of angular momentum to mass was in
excellent agreement with that deduced from observations. Recent work on pre-main-sequence
evolution uses up-to-date computer codes and considers factors such as mass
loss or mass gain during the evolution. While, for stars neither gaining or
losing mass, the new evolutionary tracks are better than the older ones I
do not think that it would change the general character of the mass v time
pattern as deduced in 1969. Even if it did it would not be greatly important
to the model presented here; as long as compact stars are present while new
stars are being formed in the embedded stage of the cluster, then the mechanism
would apply whatever their respective masses.
As an example of how later work may not necessarily be better
than older work I refer to a paper on star formation by Bhattal et al.,
1998, MNRAS, 297, 435. This produces protostars by collisions of massive
clouds. The protostars are in the form of disks and in a typical case, detailed
in the paper, a stellar condensation has a mass of 40Msun and angular
momentum 1011 times that of the Sun and more than 108
times as much angular momentum than that of a fast-spinning O or B star. How
this is supposed to evolve into a main-sequence star is not explained.
The orbital evolution section is described as unclear. On re-reading this
section I cannot see what the problem is - it is certainly less complicated
than a paper on planet migration that I have recently refereed and accepted.
But then, of course, I took the time to read it. The evolution is in a resisting
medium, the density of which decays with time. The effect of the solar wind,
also decaying with time, is to cause the resisting medium to orbit at less
than Keplerian speed. Orbital decays are then calculated using the resistance
law, as given by Dodd and McCrea (1952) and as used by Dormand and Woolfson
(1974, 1977). The section gives details of this model; had the details not
been given then I am sure that this would have been quoted as yet another
reason for rejection.
The referee takes exception to anything that relates the present work to
other work done by the York group or to any comparison of the conclusions
derived from this work compared with the outcomes from other models of planetary
formation. The York group is perhaps unique in that over the last more than
thirty years work has been done that traces the development of the solar system
from initial collapse of the ISM (Golanski & Woolfson, 2001, MNRAS, 320(1),
1-11) through to details of the system as listed at the bottom of p.28
(bottom of p.22 in present paper format). The events leading to this
evolutionary sequence are causally related and explaining that these linkages
exist seems to us to be relevant. Again, to compare the outcomes of different
theories seems to us to be a legitimate thing to do, as long as it is in context.
There is a tendency in this field for workers to take a blinkered view of
the subject. Thus in the solar nebula theory one worker will assume a quiet
nebula so that planets can actually form while another will have a turbulent
nebula so that they can form quickly enough. To be able to present a self-consistent
picture for many features of the solar system is not a trivial achievement
- although it may irritate those antagonistic to what we do.
More than three months passed before
we received the following report on 19th June 2001. On the basis
of this report the editor finally rejected the paper. Any opportunity to respond
to the report was denied us by the editor (see §3) but the report is given here
with responses added.
Report of Referee C with Responses
Omitting the brief re-statement of the manuscript's contents
customarily given in referee reports (as this must now be well known to the
editor) I will cut to the chase. I do not believe the crucial details
of the proposed processes are described correctly.
As the first referee correctly pointed out (cf. his/her last comment), the
process of star formation is more dynamic in nature than the picture presented
by the authors. Certainly at some point (interval) in time the to-be-stars
(to avoid specific names like protostars or protocondensations) must have
the many-thousand AU sizes assumed in the calculations. But that interval
is of order the dynamical time and not the stellar cluster lifetime. If that
is taken into account, either the sizes of things that have a chance to collide
with main-sequence stars are overestimated (the PMS sizes essentially similar
to MS sizes would need to be taken, and the interactions allowed to proceed
for 1-10 Myr) or alternatively the very large and very temporary sizes can
be assumed but the proability of encountering a MS star at that stage becomes
very small or zero (if indeed collapse to a typical PMS star is dynamical).
That makes the computed frequency of the encounters unreliable.
The whole basis of the calculation
in §6 is that the protostar is in a diffuse state and that the time available
for a planet-producing interaction is at most the dynamical timescale
(the free-fall time). This will be of the order of a few thousand years. Because
of other rather conservative constraints introduced into the analysis regarding
minimum distances etc. the actual time for a fruitful interaction is less.
As far as we can judge from the comment the referee is suggesting that we
used the initial radius of the protostar for several million years (we are
not sure what he means by the lifetime of the cluster in this context). Our
analysis shows that with an initial radius of ~1 000 AU, justified by the
argument involving equations (5) to (7) (and not 'many-thousand AU'), together
with a dynamic timescale gives the probabilities shown in Figure 10. If our
analysis had been shown to be flawed then we could accept the referee's conclusion.
However, we cannot accept a conclusion based on fantasy rather than the model
we have presented. A generous interpretation is that the referee has not understood
what we have presented. Less generous interpretations are possible.
I am affraid that SPH is not a good scheme for radiation transfer. This
is admittedly my private and biased opinion (resulting from my experience
with SPH going back to the mid-1980s) A 10000-particle simulation corresponds
to something like a (cubic!) star of 20×20×20 particles; in fact fewer of
them will be in close interaction with a compact MS star. Smoothing length
being of order 2 mean interparticle distances, typically, one always faces
a huge problem with non physical speed with which shocks spread numerically
((>> physical speed which is of order soundspeed). This affects the
energy release in the interaction and possibly its final outcome. This is
one reason why the calculations would need to be verified in SPH runs with
much smaller smoothing length (which is impossible in practice) or by other
schemes.
There are two separate components in
this comment. One is related to SPH as a general scheme, as used and developed
since 1977. It is a free Lagrangian code with artificial viscosity introduced
to handle shocks and it is widely used for astrophysical problems. No computational
procedure can precisely simulate physical reality but SPH has been shown to
reproduce the expected form of behaviour in collisions and tidal interactions
without necessarily giving precise quantitative results. In fact collisions,
particularly supersonic collisions are the most challenging applications and
special procedures have been developed to handle these situations. Fortunately,
collisions do not play a role in what we do and the normal SPH part of our
application here follows standard procedures. Actually very similar results
for the break-up of the protostar are found with 1 000 points or fewer but
more points are needed to be able to follow the progress of the protoplanetary
condensations. Again, wide variations of parameters (over several orders of
magnitude in dimension) give similar behaviour patterns, suggesting that the
simulation is a robust one and reproduces something that could occur in the
physical world.
The other component relates to radiation
transfer where the referee states that, for this, SPH is not a good scheme.
We can concur with that. We have used the expression 'a novel and realistic
model of radiation transfer, incorporated within our general SPH package.'.
This is briefly described in the third paragraph of §5 and in some detail
in the Oxley reference. It is not part of the SPH procedure as such but is
interwoven into it. It should not be lightly dismissed without proper, or
in this case any, examination. Its development and validation took nearly
two years and it contains a great deal of physics. Just as an example, for
opaque situations the algorithm leads to a diffusion form for radiation transfer
with proper speed of propagation. It is also not a cheap procedure. Attaching
it to the SPH package increases computation time by up to two orders of magnitude.
On p.16 the authors state that in their simulations all the captured bodies
have masses ~ 10 Jupiter. Then they state that these are the maximum final
masses because e.g. some mass will remain in a small disk around a "planet".
Such disks indeed will form, and accrete even more mass from the surrounding
medium before the day is over (see for instance papers in MNRAS by Bate and
Bonnell). Their short viscous timescales will cause most of this matter to
be added to that of the protoplanets. Thus 10 m_j is a low, not high estimate,
and calling these putative objects "planets" is questionable.
This comment is related to the following
one (§3 in the referee's disjointed numbering system). The referee is clearly
a supporter of the solar nebula concept and possibly someone working in that
area. He/she therefore has a strong fixation on the conditions that occur
when planets are produced by planetesimal accretion. Because planetesimals
come together with a small hyperbolic excess the protoplanets are initially
in more-or-less circular Keplerian orbits within a medium moving in similar
fashion. In this rather quiet environment medium material needs to lose very
little energy to be captured by the protoplanet. There may be various ways
of losing this energy - for example, material striking the surface of the
protoplanet may share its energy with surface material all of which is then
moving at less than the escape speed. This naturally leads to accretion. Incidentally,
Bate and Bonnell use SPH in their work!
A protoplanet produced by the capture
model as described here is large diffuse object, with an escape speed from
its surface of order 1 km s-1 or less, moving on a highly eccentric
orbit. For most of its orbit, especially near periastron, its speed relative
to the medium would be several times the escape speed from its surface (even
more so for the surrounding disk) and the net result would be abrasion rather
than accretion (see Woolfson, The Origin and Evolution of the Solar System,
p.88). Without detailed analysis it would be difficult to predict what
the net outcome of the exchange of matter with the medium would be - but intuitively
it seems much more likely to be a loss by the protoplanet.
Perhaps the most serious objection I have regards the issue of orbital evolution
which is so much oversimplified in the manuscript that not only the magnitudes
but the very signs of the predicted effects come out opposite to what really
happens.
First the strongly sub-Keplerian rotation of the disk which
I understand is an important part of the theory, is not demonstrated convincingly.
The stellar wind able to remove the nebula (reminiscent old and no longer
supported theories from 1970 for disk removal) is assumed. Then it is said
to act on dust grains in the nebula (well, so is it a nebula or a wind or
a radial wind permeating a nebula in circular motion or what?)
Then the miscalculated sizes of the secondary bodies ("planets")
together with an inapplicable formula (from Dodd and McCrea, 1952) containing
a huge gravitational focusing factor and not at all desribing the situation
in a rotating disk, give rise to incredible and unreal reduction of the initial
semi-major axis a~1000 AU to a fraction of AU (relevant to exoplanets). The
only feasible mechanism for migration that goes so far is the so-called type
II migration in disks (cf. Articles in Protostars and Planets III and IV volumes,
Arizona Press 1993 and 2000 respectively). Unfortunately, at large distances
like those cited as initial in the paper the type II migration may be outward
instead of inward (if most of the disk mass is inside), so that even this
mechanism is very uncertain.
Finally, eccentricity evolution is misunderstood as well,
since the large "protoplanet" masses of 10 m_j migh cause eccentricity pumping
of the orbits, not damping (cf. PP IV volume). The manuscript seems to neglect
a substantial body of work started by Goldreich and Tremaine in the late 1970s,
on disk resonances, torques and consequent secondary body evolution. They
work in sometimes non-intuitive, if well physically grounded, ways. Modern
theories show that gas drag is ineffective compared with gravitational torques
at object masses larger than planetesimals.
The discovery of extrasolar planets
close to their primaries and the longstanding problem of producing Uranus
and Neptune on a sufficiently short timescale has stimulated solar nebula
theorists to look at various mechanisms for planetary migration. A currently
well supported idea involves the way that a planet in a circular Keplerian
orbit interacts with a Keplerian disk. Spiral waves are generated, travelling
both inwards and outwards from the planet's orbit. Those moving outwards carry
angular momentum that is deposited when the energy in the spiral wave is dissipated.
The reaction on the planet producing the wave is to cause it to lose angular
momentum and so spiral inwards. Conversely those travelling inwards give a
reaction that causes the planet to move outwards, a 'reverse migration'. This
is the point of the referee's comment that if most material is interior to
the planet then it will move outward. Another aspect is that if a wave generated
by, say, Jupiter, moves outwards and interacts with another planet then angular
momentum can be added to that planet so causing it to move outwards. A brief
account of wave transport, with some mathematics will be found in Woolfson's
The Origin and Evolution of the Solar System, pp.168-169. Spiral waves
and other possible migration mechanisms are also briefly mentioned in the
sixth paragraph of §9 of the present paper.
A defining characteristic of type II
migration, mentioned by the referee as the only possible mechanism, is that
a massive planet in a medium with Keplerian motion opens up a gap within which
it moves in a circular orbit. The spiral waves that transmit angular momentum
inwards and outwards depend for their formation on this particular arrangement
of planet and medium. It is incredible that the referee could believe that
a planet in a highly eccentric orbit could establish a gap (what would it
look like?) or that the ever-changing relative motions of medium and planet
could generate spiral waves. In short, a resistance model based on spiral
waves cannot be applied to a body moving in a highly elliptical orbit through
the disk. However, the factors giving rise to the Dodd and McCrea resistance
will apply; the effects of the Keplerian pattern of motion of the medium will
be completely swamped by the resistance due to the high relative speed of
the planet relative to adjacent material. If there are additional forces
at play then this will simply reduce the time for evolution of the orbit.
The referee has a strong fixation on
what the solar nebula model involves and cannot seem to think outside it.
The migration mechanisms considered by the solar nebula community are complex
and, until recently, were barely understood. That such mechanisms must be
considered in relation to solar nebula ideas does not mean that simple mechanisms,
that are intuitively obvious, are invalid.
The referee may be right in saying
that strong solar winds may not be a necessary feature of young stars. We
simply do not know enough about the behaviour of YSOs. However, the idea of
a strong solar wind to remove the nebula is still mentioned in recent papers,
despite the referee's protestation. Actually the sub-Keplerian rotation of
the disk is not critically important to the round-off process. Down
to when the eccentricity is quite small the relative speed of body and medium
is comparatively little affected by departures of the medium from Keplerian
motion. Figure 11 shows that by the time the eccentricity has reduced to 0.1-0.2
the semi-major axis is down to a few AU or less. That is where the solar nebula
theorists begin. We could go along with Goldreich and Tremaine at this stage!
Although not mentioned in the paper
there is also a small but significant effect from stellar luminosity. For
present solar luminosity at a distance of 5 AU the effect on the medium is
equivalent to a 0.1% reduction in solar mass. If young stars are several times
as luminous as the sun (which is suggested by theoretical PMS evolutionary
tracks) then the effect on orbital evolution may not be negligible, but this
has not been tested.
As far as eccentricity pumping is concerned,
unless there has been some very recent new work that has changed the
situation in the last couple of years, I understand that it only operates
for bodies of brown-dwarf mass or above - probably well above according to
the theory. Is this why the referee has attempted to promote our captured
bodies to brown-dwarf status by stating that they are ~ 10 MJ
in mass (7 out of 11 in our modelling are well below this) and will subsequently
grow?
Another form of eccentricity pumping
involves two planets in commensurate orbits (e.g. Melita and Woolfson, 1996,
MNRAS 280, 854-862) but this is not applicable here.
The manuscript is far too long in places, it contains extraneous and unnecessary
information, mostly relating to the history of conflict between the author's
concepts and the mainstream, non-catastrophic, planet formation theory, but
also such things as a table of exoplanet orbital elements (incomplete by a
factor of 5!), references to BBC television show etc.
Here I believe is the real problem
- clearly raw nerves have been touched. The paper shows that various observations,
especially those of recent origin (e.g. close exoplanets, free-floating planets)
are explained by the present model and the model developed in Cardiff but
not (yet) by the solar nebula model. The reference to "the history of conflict"
suggests that a vigorous debate has been taking place over some period of
time. On the contrary, the capture-theory model has been largely ignored,
is comparatively unknown and is never included or even mentioned in conferences
on planet formation. In addition it receives very harsh treatment at the hands
of referees, which explains why papers on this subject have to be written
in sufficient detail to try to anticipate unjustified criticism. The present
referee has repeatedly suggested that we are ignorant about various matters
or do not understand various theoretical approaches. Had we anticipated this
and included material to show that we were not, then this too would have been
slated as unnecessary and making the paper too long!
The table of orbital elements was to
illustrate the types of orbit that existed. It was stated as "a sample" and
that was all that was required for the purpose. Why was this made an issue?
In general, "extraordinary claim require extraordinary evidence". The manuscript
is short the latter. Instead, it has severe problems which I can summarize
this way: either the lifetime or the sizes of the proposed bodies are miscalculated,
as are their final mass and subsequent orbital evolution. I cannot recommend
the paper for publication in MNRAS, and I doubt that it can be substantially
improved while retaining both the main methods and conclusions.
It is the solar nebula theorists that
make extraordinary claims and the evidence that they offer is hardly extraordinary
since it has not solved major, indeed critical, problems after thirty years
of sustained work by a large community. All that is claimed for the present
work is that it offers a plausible alternative model - no more, no less. The
referee rehearses here the objections he/she has previously raised and we
can only refer to our refutation of those objections - in particular the first
that is completely unrelated to what we have written.
3 Rejection statement by Editors of the Journal
The following is an extract from the final rejection letter:
"The decision as to whether a paper is published is not made
by the referee but by the editor based on the advice of the referees as you
suggest. I am sorry to send you disappointing news on this occasion but we are
unable to give your submission any further consideration."
4 General comments on the Editorial policy of MNRAS
and on the ethics of scientific refereeing
The Editors of journals published by learned societies perform
an important service to the scientific community and they should be fully supported
by the communities they serve. I acted for many years as co-editor of an international
journal (not in astronomy), and handled well over 600 papers. The great majority
of papers were straightforward - sometimes accepted, sometimes requiring either
minor or major revision and occasionally rejected. The reason for rejection
was, as for MNRAS, that two referees had recommended rejection. However, no
paper was rejected absolutely before the author(s) had an opportunity
to see the referees' reports and comment on them. The final letter of rejection
was in the form that the paper was rejected unless it could be shown that the
referees' reports contained demonstrable factual errors. This was rarely so,
authors would accept the rejection and there was no further correspondence.
I cannot remember the exact number of comebacks there were to this approach
but it could probably be counted on one hand. This was, of course, extra work
for me as Editor, but it happened so rarely that the overall increase in effort
was negligible and I had the satisfaction of knowing that I had carried out
the editorial task in a fair and even-handed way. I can recall at least one
case where I used my editorial judgement in favour of the authors since they
had made a good scientific case for what they were doing and the referees' reports
were either biased or mistaken - I forget which at this distance in time.
The form of the rejection letter from the editor in the present
case gave no opportunity for response. The unusual report from referee A might
have rung an alarm bell that judgements made in this subject area might not
be entirely objective, but clearly it did not do so. Again, when referees delay
for more than three months before responding (perhaps only responding when reminded),
as did both referees B and C, then this might betoken some problem with the
refereeing process. The report from referee C, that led to the final rejection,
contained glaring factual errors in what was probably his major criticism -
his point 1. The referee boldly stated a conclusion based on the very opposite
of what is in the paper and this was accepted without question! In virtually
every other comment he was criticising the work based on conclusions drawn from
one model, the one he/she favours, carried over to another model based on an
entirely different scenario. There was no opportunity to point this out to the
editor who merely accepted what he/she was given at face value and therefore
presumably subscribed to it.
I was also very disappointed in the general approach of the
referees. As a referee myself I am occasionally asked to look at papers with
a solar nebula theory background. I never take that into account but merely
judge the paper on the basis of the science as presented. When there are points
about which I am doubtful I say clearly what they are and, where possible make
suggestions about how they can be put right. My general approach is to be supportive
of the author(s) although I do recommend the rejection of papers if they do
not meet an acceptable scientific standard. There is no sense in which the reports
of referees A, B and C could be described as constructive or helpful.
In the cosmogony field there is no way of knowing what is right
- only what is wrong. One characteristic of a good theory is that it must be
vulnerable, that is to say that it is detailed and specific enough to be subjected
to tests that may prove it to be wrong. Those presenting any theory in this
field must be prepared to face criticism. The way to meet criticism is either
to show that it is wrong or to develop new theoretical approaches that counter
it. However, it is not legitimate, and contrary to all proper scientific values,
to protect a theory by suppressing alternative ideas.
In view of the present experience with the referees of this
paper and the editorial process of MNRAS it seems unlikely that this work would
ever be published in a refereed journal in its present form. Presenting it on
the Web, seems to be the only, if a rather inefficient, way of making known
what I think is an interesting contribution in this area.
Stephen Oxley's D.Phil thesis can be found here
Please email any comments to mmw1@york.ac.uk
Last updated 24 August 2001
Prof M M Woolfson
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