GEOPHYSICAL RESEARCH LETTERS
J.H.WAITE, JR. EDITOR
SOUTHWEST RESEARCH INSTITUTE
P.O.DRAWER 28510
SAN ANTONIO, TX 78228-0510 U.S.A
TELEPHONE (210) 522-5261 / 5262
grl@swri.space.swri.edu
FAX (210) 647-4325
November 22, 1996
Dr. Robert B. Sheldon
Center for Space Physics
Boston University
725 Commonwealth Ave
Boston, MA 02215
Re: "A new magnetic storm model" (GRL ms. #6841)
Dear Dr. Sheldon,
Enclosed are the reviewers comments on your paper. As you can see, the
reviewers have concerns about the validity of this work. Therefore, I
must conclude that this paper is not converging toward publication
and that further handling of it in its present form is not warranted.
As significant additional work appears to be required to render the
paper acceptable, we would treat any revised version of it that you
may wish to submit as a new submission, with a new received date and
manuscript number.
I am sorry that the outcome of the reviewing process was not the one
you had hoped for. Thank you for considering GRL.
Sincerely,
C. Farmer
for J.H. Waite, Jr.
Referee A
Comments on "A New Magnetic Storm Model", by R. B. Sheldon and
H. R. Spence
General Comments
The authors present a scenario for magnetic storm development on the
basis of observed monoenergetic ion signatures in the CEPPAD
instrument. The central element in this model is the production of
field-aligned potential drops in association with nose events in the
ring current. These potential drops then accelerate heavy ions out of
the ionosphere to populate the ring current and produce a whole suite
of subauroral signatures. Though this is an interesting model, the
authors offer very little evidence that any of these processes are
actually occurring and the evidence that is presented is largely weak
and circumstantial. In addition, the Dst did not vary in the typical
manner that one would associate with a magnetic storm during the time
interval of the CEPPAD observations but is more consistent with plasma
injection penetrating in only to relatively high L values, never
becoming part of the ring current, but drifting to the magnetopause
boundary and being lost. (The Dst, which was not shown in the paper,
decreased to -48 nT over a period of a few hours then recovered
rapidly within a few hours. The asymmetric component of the Dst
decreased to nearly -200 nT during this same interval and rapidly
recovered.) How does one construct a magnetic storm model on the basis
of data taken during this very weak perturbation in Dst which does not
really appear to be a magnetic storm? Without more concrete
substantiation of the various claims made in this paper, including
some verification that a magnetic storm actually occurred during this
interval, I cannot recommend publication.
Specific Comments
Page 3, paragraph 3
The authors identify the 90 keV ion peak as a nose event on the basis
of its trapped pitch angle distribution and monoenergetic
nature. However, a study of the penetration of newly injected ring
current particles by Ejiri et al., (JGR, 85, 652, 1980) demonstrated
that 10-30 keV ions penetrated the deepest into the magnetosphere. The
sharpness of the energy peak in the ions was a function of local time
being very broad in the 24 MLT sector and much narrower in the dusk
sector. A nose event observed by AMPTE/CCE during a storm in late
September 1984 showed a very pronounced peak at 30 keV in agreement
with these results (Kozyra et al., 1993). The nose event identified in
this paper was in the 0 MLT sector and thus should have been difficult
to pick out because of its broad spread in energy. In addition, the
authors must demonstrate that the deepest penetration should have
occurred for 90 keV ions (as opposed to much lower energies) under the
existing magnetospheric conditions.
Page 4, paragraph 3
This is very weak circumstantial evidence for O+ beams during the
CEPPAD observations [sic] period.
Page 4 paragraph 4
As I recall from the published literature on nose events, they always
penetrate into the plasmasphere. What exactly is the thermal electron
density? It seems to me that at L values near 4 on the nightside
during very weak magnetic activity, the electron densities could be
substantial. This is a critical point, since you require very low cold
electron densities or the field-aligned potential will be rapidly
shorted out.
Why do you require monoenergetic ions to produce the field-aligned
potentials? Ring current ions in general have very trapped
distributions and therefore the mechanism you propose should generate
field aligned potentials everywhere in the ring current region where
thermal electron densities are low and the ring current electrons have
a substantially different pitch angle distribution than the ring
current ions.
Page 5. Paragraph 3.
I believe that SAIDs have always been associated in the literature
with storms and in fact most generation mechanisms center around
processes associated with ring current shielding of the inner
magnetosphere. The signatures associated with SAID events were well
documented by the Dynamics Explorer spacecraft. In the observational
literature regarding SAIDs, that resulted, is there any evidence for
signatures associated with field aligned potentials? I do not recall
any reports of O+ ion beams occurring on SAID field lines but only
upwelling O+ ions associated with low altitude heating by the SAID
electric fields. Is there evidence of a SAID event coincident with the
monoenergetic ion peaks in the CEPPAD data? If not, why is this
relevant?
Page 6, paragraph 2
The dependence of the O+ content on Dst can easily be explained by the
observed substantial O+ outflows from the cleft ion fountain. Why are
subauroral O+ beams required to explain this dependence on the
directly driven component of magnetic activity? How frequently were
subauroral O+ beams observed by Dynamics Explorer and how substantial
were the O+ fluxes associated with those beams? My recollection is
that they were only occasionally observed but were not a major
component of the total O+ outflows. Since a large body of observations
exist on O+ outflows, it should be easy to verify observationally the
magnitude and frequency of O+ beams at subauroral latitudes. However,
verifying their association with ring current nose events is another
issue entirely.
Page 6. paragraph 4
The reason that ion cyclotron waves are seen primarily in the dusk
local time sector is that the ring current ions penetrate into the
dusk bulge region of the plasmasphere. The higher thermal plasma
densities lower the resonant energies and allow ring current ions to
amplify EMIC waves in this region. If the ring current is high in
oxygen content as is usually the case with very large storms then
significant amplification of waves below the O+ gyrofrequency will
occur. The presence of upflowing O+ beams at subauroral latitudes in
the dusk sector are not required to explain these
observations.
Page 6. paragraph 5.
The applicability of these cited results to the present model is
unclear. Over what L values were the GEOTAIL observations made? Is it
possible that they were on field lines that map to the auroral
ionosphere? What were the peak energies of the O+ and H+ distributions
(50 keV O+ and H+ have very similar charge exchange lifetimes)? It is
not clear how asymmetry in the ENA observations of a storm by CEPPAD
lend support to the storm picture that has been constructed. Please
explain this statement further.
Referee B
Referee report on GRL ms. 6841: "A new magnetic storm model," by
Sheldon and Spence
This letter displays some very interesting energetic particle data
sampled by the POLAR spacecraft, concerning the storm-time ring
current particle distributions and dynamics. A presentation and
discussion of this data is certainly suitable for a special GRL issue
on results of WIND/GEOTAIL + POLAR. However, as discussed below, I
believe that the authors run into considerable trouble in their model
interpretations. I therefore cannot recommend publication of this
letter in its present form.
Unfortunately, the most basic premise of the proposed interpretations
does not make sense. The authors state (e.g. see the abstract) that
the injection of a fresh population of ions with a "trapped" pitch
angle distribution (the nose ions at ~90 keV) without accompanying
fresh electrons (they cannot penetrate to these L values) generates an
electric field that further confines the ions to the magnetic equator
and accelerates electrons into the ionosphere. Perhaps I am being
dense but it is quite obvious to me that the injection of these fresh
ions will have exactly the opposite effect. To the extent that any
appreciable parallel electric field is generated at all, the electrons
will be accelerated towards the equator. Thus, the authors entire
premise seems to fall immediately apart.
The "field-aligned" ion component has been reported previously in the
literature, and these data must be discussed in the context of
previous findings. Figure 1 makes it clear that in fact these are not
"field-aligned" but are the so-called "butterfly" distributions. The
authors should see Sibeck et al. (in the book MAGNETOTAIL PHYSICS,
edited by Lui, 1987) and Sibeck et al. (JGR, 1987, p. 13485), where an
explanation of these butterfly distributions has been proposed.
The conclusion that a 30 keV magnetic field-aligned potential is
generated in the plasmasphere is astounding and not believable. Since
the data are open to many interpretations, only a solid theoretical
development proving that such fields are allowable in the plasmasphere
would convince the reader that such parallel potentials can exist. To
do so, a complete potential profile extending from the equator to the
ionosphere must be derived for the reader from the Whipple or other
works. Alternatively, the authors may speculate about the POSSIBLE
existence of such fields, but they may not claim that their
speculations are grounded in theory.
As a minor point, the distributions have reasonably broad widths in
energy, and thus they are not "monoenergetic". A better word should be
found. Also, there are published work on PC1 waves associated with
the oxygen gyrofrequency. The authors do not need to rely on
unpublished work.
Our E-mail Response
Date: Tue, 3 Dec 96 17:00 EST
From: r*sheldon@bu.edu
To : grl@swri.edu
Subject: to Hunter Waite re: manuscript #6841
Dear J. H. Waite, Jr.,
We knew that the paper we submitted to GRL would be controversial,
we had a lively discussion at the Huntsville Workshop where we first
presented it. We were both challenged and encouraged by the response we
received. But what we did not expect from GRL was the complete lack of
interaction, the rejection without rebuttal, presumably because of
private (cover letter) communication with the editor, since we did
not detect complete rejection in the referee reports. To quote,
"Therefore I must conclude that this paper is not converging
toward publication and that further handling of it in its present
form is not warranted." In the usage of physics, "convergence" is an
iterative motion towards a solution. There has been no iteration allowed,
and therefore, a priori, no convergence.
Since we have been summarily judged and found wanting, please permit
us the opportunity of judging our referees. Referee A uses as his major
objection, the fact that:
"(The Dst, which was not shown in the paper, decreased to -48 nT over a
period of a few hours then recovered rapidly within a few hours. The
asymmetric component of the Dst decreased to nearly -200nT during this same
interval and rapidly recovered.) How does one construct a magnetic storm
model on the basis of data taken during this very weak perturbation in Dst
which does not really appear to be a magnetic storm?"
On the surface this is an impressive dilemma. But one should look a bit
closer. Dst takes about 3 years to appear. This was April 15, 1996, only 6
months ago. Where is this referee getting his Dst? The answer is that he is
NOT getting Dst, but a computerized substitute, DSY, generated automatically
by a program at Kyoto that came on line in August, 1996, which to our
knowledge has never been compared to Dst. Furthermore, the reason Dst takes 3
years to come out, is because Sugiura manually removes the ionospheric
component, Sq, from the magnetograms, a difficult task that he feels
precludes a computer algorithm. The month of April had a week with
DSY above 20nT POSITIVE, a quite hefty Sq contribution. Thus we do not
include DSY because it is clear to us that it is contaminated, untested
and unproven. But what does this referee's assertions about Dst show? It
shows that he is speaking about a subject that he has superficial knowledge
of, yet the editor feels his criticism to be so severe as to preclude any
reply from the authors.
Let us continue. Referee B gave a single page response. The crux of his
criticism is:
"Perhaps I am being dense but it it is quite obvious to me that the
injection of these fresh ions will have exactly the opposite effect. To
the extent that any appreciable parallel electric field is generated at
all, the electric field will try to push the ions away from the
equator, and the electrons will be accelerated towards the equator. Thus,
the authors entire premise seems to fall immediately apart."
We beg to differ, perhaps the referee is being intentionally dense. We
cite in our paper, which is far too brief to rederive all the well-known
results of the field, one of the seminal papers in the field of parallel
electric fields, Elden Whipple's 1977 JGR classic. In that paper, Elden
plots exactly our electric field. Now Elden does plot the field for a beam
of electrons, which we replace with a beam of ions, but the shape is
invariate, pointing away from the equator. Clearly the referee's intuition
has never been contaminated by reading the literature in the field or our
careful citations.
This ignorance on the part of the referee is reparable, but the second
criticism reveals a more profound and possibly irreparable difference. He
says:
"The "field-aligned" ion component has been reported previously in the
literature, and these data must be discussed in the context of previous
findings. Figure 1 makes it clear that in fact these are not "field-aligned"
but are the so-called "butterfly" distributions. The authors
should see Sibeck et al. (in the book MAGNETOTAIL PHYSICS, edited by
Lui, 1987) and Sibeck et al. (JGR, 1987, p. 13485), where an explanation of
these butterfly distributions has been proposed."
It seems curious to us that such a positive identification could be drawn
from the color contour spin sector plots provided in our manuscript,
which contain little information as to pitchangle, whereas the Sibeck
paper referenced above defined "butterflies" in terms of pitchangles. More
revealing is the fact that one of us was a severe critic of that same
identical 1987 paper. Could it be that this referee, unknown
to the editor, has an axe to grind concerning "butterfly" distributions,
a bias that might impair his impartial reading of our manuscript? Without
allowing us the privilege of a response, the editor could be falsely led
to believe that the credentials of the authors are somewhat less
reputable than the referees.
Now we ask you, should a carefully reasoned and written paper be
summarily executed by anonymous referees who can so "obviously" dismiss
it with their inerrant intuition? Should there not be an opportunity for
us to defend ourselves against such condescending treatment? Isn't GRL the
right forum for innovative ideas and new results? If not GRL then where
can one publish creative thinking? Is it in the best interests of the editor
and the journal to avoid the normal refereeing give-and-take? What then
is the difference between anonymous refereeing and ambushed assassination?
Sincerely,
Robert Sheldon
Harlan Spence
E-mail from GRL
Date: Tue, 3 Dec 96 17:11:48 CST
From: grl@swri.edu
To: r*sheldon@bu.edu
Subject: re: to Hunter Waite re: manuscript #6841
Dear Dr. Sheldon,
Thank you for your e-mail message regarding your paper,
"A new magnetic storm model" (6841). Your point about
the inappropriate use in our letter of "convergence" is well-
taken. Indeed, the phrase you cite is normally used in rejection
letters sent to authors of papers that have gone several
rounds with reviewers. I suspect that it remained in our form
letter as residue from earlier correspondence. For the
record, the text of the letter that should have been sent to you
follows:
"Enclosed are two reviews of your paper. As you can see, there
are a number of serious concerns that preclude publication of the
paper in its present form. Because it appears that a substantial
reworking of the paper would be required to render it acceptable
for publication, we will consider any new treatment of this subject
that you may choose to submit as a new paper with a new received
date and manuscript number."
This is our standard rejection letter, sent when there appear to be
very serious problems with a paper. Please note, however, that
it is the paper "in its present form" that is being declined and that
the possibility of your submitting to GRL a "new treatment" of your
subject is not ruled out. Moreover, the decision to treat such a
new version as a new paper with a new received date etc. is not an
irreversible one. An editorial decision can always be appealed, and
we are open to such appeals (up to a certain point, that is). Thus, if
you feel that you can satisfactorily address the reviewers' concerns
through the appropriate revisions and/or rebuttal of their arguments
and wish to submit a revised version of the paper for our further
consideration, you may certainly do so.
We would, of course, send the revised paper to the two original
reviewers for further evaluation. However, we would also consider
soliciting the opinion of a third reviewer, if you believe that the original
reviewers have not evaluated your paper objectively.
Sincerely,
Bill Lewis (for Hunter Waite)