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
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March 14, 1997
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 revision)
Dear Dr. Sheldon,
Enclosed are three reviews of your revised paper. Two are by Referees A
and B, who also evalueated the earlier version of the paper. The third
review is by a new referee (C), to whom I made available, in addition
to the revised paper, the comments of Referees A and B on the first version
of the paper and your responses.
As you can see, Referees A and B are not persuaded by your responses to their
earlier criticisms and remain skeptical of the model that you propose.
Referee C raises a number of apparently substantive questions but finds
"that the model has merit and that it appears that it could well be a
reasonable explanation of the observations." However, he also feels that a
convincing case for your model requires a far more detailed discussion of
both the data and the model than can be accommodated in a GRL article. On
this point all three referees are in complete agreement.
Despite their skepticism about your model, Referees A and B both
acknowledge that the observations you present in your paper are
significant and interesting. Both suggest that a report of these data alone would constitute a good GRL paper. (Referee C made the same suggestion in
the covering letter to me that accompanied his/her report.)
It is clear from the reactions of all three referees to the paper that
the presentation of your model belongs not in GRL, but in JGR, where
it can be developed in the detail required to convice--perhaps--those
members of the community who, like Referees A and B, will react
initially with skepticism. For this reason, I am afraid I must decline
the present version of your paper. I urge you to consider carefully
the comments and criticisms of all three referees and address them in
an expanded, more detailed paper for submission to JGR.
At the same time, it is clear that the data you present and the event they
describe are interesting and unique. I would therefore encourage you to
submit for our consideration a paper that simply presents these data
without trying to make a case for a controversial model. Although the
focus of such a paper would be on the data, it would, as Referee A points
out, be appropriate to conclude the paper with some speculative comments
about the interpretation of the data.
Thank you for considering GRL. I am sorry that the outcome of the reviewing
process ws not the one that you and your co-author had hoped for.
Sincerely,
J.H. Waite, Jr.
Referee A
Referee's Remarks on "A New Magnetic Storm Model", by R. B. Sheldon and
H. R. Spence
General Comment
I have carefully read over the author's responses to my previous
review and find that the paper still makes a number of claims, central
to the proposed storm model, without sufficient observational or
theoretical support. I find this criticism to be quite explicit and
not "implied" as the author suggests in his reply. Details to
substantiate this criticism will be given below in evaluating the
author's responses.
The presentation of the magnetic storm model as a viable mechanism
seems to be a bit premature requiring significantly more theoretical
development and observational support for its component parts. I
strongly urge the author to present the GRL paper as a report of the
observations, which are quite interesting, and include a paragraph at
the end in the discussion section speculating on their interpretation,
to be followed by a more complete treatment of the model, proposed
here, in a JGR article. Having made this recommendation, I will
nonetheless return to the present paper and respond to the author's
comments on my previous review.
Responses to the author:
(1) The author's response is sufficient ot convince me that a storm
may have occurred at this time though it was a very short-lived event
and highly asymetric. The fact that the "provisional" Dst disturbance
was atypical in that it lasted only about 1 day ans was extremely
asymmetric may be an important piece of information in understanding
and interpreting the observations, though it is up to the author whether
or not he chooses to include some discussion of this.
(2) The signature in the IPS energy time spectrogram (on the CEPPAD
web site) appears to be a nose event as the author suggests. However,
turning to observations for the moment, the nose event (peaking at 30
keV) in the Kozyra et al. [1993] paper occurred during a storm with
minimum Dst ~-60nT, maximum Kp = 6+, and the estimated peak
cross-polar cap potential difference was 161 kV. the April 15 event
had very similar minimum Dst (-63 nT?), maximum Kp (7) and estimated
cross-polar cap potential difference (>150 kV) values though it was
much shorter in duration. Why should the peak energy of the nose event
ions be ~90 keV? It cannot be simply a matter of cranking up the
electric field if the storm conditions are similar. This is an
interesting piece of the puzzle. Modeling of the ion trajectories to
establish that this is definitely a nose event would make a much more
convincing case. But if this is not possible for this initial report,
at least some discussion of the characteristics of this event compared
to other nose events in the literature would be helpful.
As a side point, Wodnicka [Planet. Space Sci. 37, 525, 1989] claims to
have reproduced Ejiri's [JGR, 83, 4798, 1978] trajectories.
(3) The composition of the 30 keV population is important, in the
sense that you would like to explain the temporal history of the O+
component of the ring current with this unifying storm model. After
thinking over the authors remarks, I can accept the arguments that the
author presents for assuming the 30 keV ions have a major O+
component. However, the 100 keV ions also have a significant O+
component which implies the plasma sheet source population was
enriched in O+ prior to the nose event. What are the relative
strengths of the two sources of O+ and how does this fit into the
proposed storm model?
Regarding the O+ charge exchange lifetimes, the lifetime for
equatorially-mirroring 100 keV O+ at L=5 should only be about 2 days,
at L=3-4 less than 1 day. The CAMMICE measurements were made 3-4 days
later. At what L value were these measurements made?
Lastly, CEPPAD was not designed to detect O+ ions. If the lower energy
ions are indeed oxygen, it is my understanding that there is an energy
threshold below which these ions cannot penetrate into the CEPPAD
instrument. What is this energy threshold and could this produce a
seemingly monoenergetic distribution because ions below this threshold
though present were unable to access the detector.
(4) The author is not simply reporting on the observations and
speculating that a field-aligned potential could produce this
signature, he is asserting that the potential exists and using it as
the basis for a storm model which explains a host of subauroral
signatures. The existence of a 30 keV field-aligned potential at such
low L values is essential for the claims that the author makes
throughout the paper to be valid. The author claims that such a
solution exists (though counterintuitive) under certain very
restrictive conditions but can offer no observational proof that these
conditions have occurred. At the very least, semi-empirical models of
the thermal plasma density might be used to establish that the
required conditions are possible on the field lines in
question.
The main focus of the paper is on the storm model and at this point it
is a "house of cards". the assertions of the paper go too far without
a better theoretical and observational foundation for the existence of
a field-aligned potential of this magnitude on plasmaspheric field
lines, and for the proposed association with SAIDs, accelerated
electron distributions in the subauroral region and upflowing
subauroral oxygen beams.
(5) After reading the authors remarks, I looked back at sevveral SAID
papers and found that they indeed have been observationally linked to
substorms. The reason that I assumed that they were linked to storms
is that the current theory explains them on the basis of the closure
of region 2 currents through conductivity gradients at the edge of the
diffuse aurora in the ionosphere [Anderson et al. JGR, 96, 5785, 1991;
Anderson et al., JGR, 98, 6069, 1993]. A component of region 2
currents has been associated with the partial ring current.
The link between nose events, 30 keV field-aligned potentials and
SAIDs is an unsubstantiated portion of this paper. The signature of
accelerated electrons (< 32 keV), that would indicate the existence of
a potential drop on SAID field lines, has been looked for on several
occasions, and not found, using DMSP and DE-2 observations. This was
presented in Phil Anderson's thesis. However, it is certainly worth
looking for signatures in the ionosphere associated with the April 15
event and others like it. Riometer signatures to my knowledge have
also not been associated with SAIDs. Please give a reference for this
association before using it as evidence for the presence of
SAIDs. There are characteristic zones of ion precipitation (many 10's
of keV to MeV) that move to low L values and intensify during
storms. These zones have not been associated with SAIDs but appear to
result from violation of the first adiabatic invariant on stretched
magnetic field lines [c.f., Sergeev et al., JGR, 98, 7609,
1993]. These would certainly produce a signature in the riometer even
if no SAID was present. For the April 15 event, the presence or
absence of SAID signatures should be established and the details of
the precipitating electron distribution established using readily
available DMSP and NOAA observations which extend to 30 keV before
parallel potential drops are proposed as their cause. Also it would be
very interesting to know the location of the discrete auroral oval in
relation to the accelerated ion beams that apparently exist in the
data.
(6) (a) I disagree that the temporal correlation between Dst and the
O+ content cannot be explained by sources of O+ other than the 30 keV
parallel potential drops discussed here. As the convection picks up,
Cladis showed that the cleft ion fountain deposits oxygen ions over a
smaller L value range and closer to the Earth than during times of
slower convection. This results in a very pronounced Earthward
gradient in the O+ content which is then convected inward to form the
ring current with an associated temporal history. Timing problems
associated with the rapid appearance of O+ in the inner plasmasheet
prior to storm main phase are alleviated somewhat by the fact that Kp
is usually elevated to some low level for a time prior to storm main
phase. In the case of the April 15 event, Kp was 3-4 for some time
prior to the rise of Kp to 7 in the interval 21-24 UT on April 14. In
addition, oxygen ion beams moving up auroral field lines rapidly bring
oxygen directly into the near-Earth plasma sheet. This is the
mechanism that Iannis Daglis proposes for the fast time-scale increase
in the oxygen component of the inner plasma sheet (7-9 Re) seen in
AMPTE/CCE observations [Daglis et al., JGR, 99, 5691, 1994].
(6) (b) I was not suggesting that the author perform such a
statistical study but that he might get an idea of the morphology of
upflowing O+ with L value by looking at past work in the
literature. Andy Yau working with Bill Peterson and Ed Shelley did
several statistical surveys of upflowing O+ beams using the DE-1 EICS
instrument which measured ions over the energy range 0.1 - 17
keV/e. Granted this is at slightly lower energies than the beams
presented here. As I recall, the occurrence frequency of upflowing O+
at low L values was small. Variations with magnetic activity were also
examined. If direct injection of upflowing O+ beams are a major source
of ring current ions, one should find evidence for such a source in
these statistical studies. After all nose events with peak energies of
30 keV definitely occur and would produce field-aligned potentials
with values within the DE-1 EICS energy range.
(7) It is not necessary to debate the details of theories and
observatioins of ion cyclotron waves in the dusk sector for the
purposes of this paper, and I apologize to the author for beginning
such a discussion in my previous comments. If, as you say, ion
cyclotron waves are produced by these upflowing ion beams, then there
should be clear evidence for this in the POLAR wave measurements. Such
observations would lend important support to the storm scenario the
author proposes.
Referee B
Referee (#B) report on the revised GRL ms. #6841:
"A new magnetic storm model," by Sheldon and Spence
To repeat from my first review: the data presented in the paper are
significant, and a presentation and general discussion of these data,
including even speculations on field-aligned electric fields, is
certainly suitable for a special GRL issue on ISTP. Unfortunately, my
principal original objections to the present paper still stand, and
thus I cannot recommend the paper in it[s] present form.
In the first paragraph of their response to my original comments, the
authors indicate that they have somehow convinced themselves that for
a trapped or isotropic pitch angle distribution (assuming initially no
field aligne[d] electric fields) the density will peak off the
magnetic equator. It is a straightforward exercise to demonstrate
otherwise. What the authors are saying is that if one begins with a
quasi-neutral plasma, and then injects positively charged ions with a
density distribution that strongly peaks at the magnetic equator, the
system will respond with an electric field that tries to force even
more ions towards the equator. I am open-minded enough, I think, to
believe that occasionally 2 + 2 = 5 in science. However, the person
making the claim of such an astounding conclusion must accept the
burden of proof. These authors have refused that burden. They have in
effect stated: "go prove it yourself." The fact that it may not be
practical for the authors to accept this burden within the confines of
a short GRL letter is all the more reason that this paper is not
appropriate for GRL in its present form. I would suggest that the
authors expand their presentation to whatever length it takes to prove
their point and then submit it to JGR. I stated in my original review
what kind of presentation it would take for me [to] recommend
acceptance of the authors' paper.
Referee C
Comments on GRL MS 6841: A New Magnetic Storm
Model, by Sheldon and Spence
The magnetic storm model that the authors propose in this paper I find
to be interesting and attractive. It puts together a chain of
processes that are triggered by a large cross-tail electric field
caused by a large increase in the solar wind pressure together with
southward turning of the IMF Bz for some significant period of
time. They propose that magnetospheric ions are convected toward the
earth from the tail with a selected group at the appropriate energy
penetrating deeply into the inner magnetosphere. These ions then
generate a parallel electric field in a narrow L-shell band (because
of the excess psitive charge) which accelerates electrons to and
extracts ionospheric oxygen from the ionosphere. They are led to this
model for a storm by their data which shows a penetrating band of ions
near 90 keV ("nose protons") and a band of field-aligned ions near 40
keV which appear to be correlated in energy and intensity with the 90
keV band.
The model is attractive because it invokes a set of known physical
processes and ties them together sequentially so that there is a
causally linked chain of events that can be investigated theoretically
and compared with observations.
I believe that the model has merit and that it appears that it could
well be a reasonable explanation of the observations. However, both
the data and the model require detailed treatment in order to make a
convincing case, and I do not think that it is possible to do justice
to the model and to the comparison with the observations in a
four-page GRL paper. It appears that this is also the main reason why
the previous reviewers had problems in recommending the paper.
Thus my recommendation is that the authors do a detailed treatment of
the basic processes which are involved in the model, using their data
as the basis for the treatment, and put together the kind of
substantial paper that would be appropriate for a possible major
advance in the field, and submit it to JGR.
I will list below some of my comments and questions regarding each of
the basic processes they invoke:
(1) On the large induced cross-tail electric field
What is the threshold on the enhanced IMF Bz magnitude, direction, and
duration in order for saturation of the tail's ability to shield the
polar cap potential to occur? Is this well known (then it should be
documented) or can this be demonstrated?
(2) On the ion nose events:
It is difficult from the spectrograms to get a good idea of the actual
energy and pitch angle distributions, for both the 90 keV and the 40
keV bands. (This is a problem with a short paper--not enough room to
do justice to the data.) How near 90 degrees do the beam ions have to
be in order to form a nose event? The authors also need to document
their statement that nose events are highly correlated with
storms.
(3) On the 40 keV beam ions:
The monoenergetic 40 keV ions are really not very monoenergetic since
their FWHM is about 35 keV. What is the pitch angle distribution of
these ions--is this also quite broad? Nevertheless the constant ratio
of (nose/beam) energies is supportive of the idea that the beam is
related to the nose ions. But what about the time scales involved,
since this is a very dynamic event? If the beam ions come from the
ionosphere, one would think that the ratio would decrease over time as
more ions are pulled up from below, unless this all happened quite
quickly at the beginning of the storm. What stabilizes the ratio?
This needs to be addressed.
(4) On the parallel electric field:
The authors appear to be mixed up between the potential gradient and
the electric field. If the nose ions generate an excess of positive
charge away from the equator, then there will be a positive potential
at a point away from the equator which means that the potential
gradient is positive away from the equator but the electric field is
negative (pointing towards the equator). This has the required effect
of pulling electrons away from the equator and pulling ions out of the
ionosphere if indeed the electric field extends far enough along the
magnetic field line to reach the oxygen ion populations. This is an
important question since the authors are proposing that the parallel
electric field may involve a double layer. If the double layer is
located well above the ionosphere with little electric field below,
then it is hard to see how a significant ion population can be
extracted.
The question of how the parallel electric field is generated needs to
be addressed in some detail. The pitch angle distributions of the nose
ions and of the beam ions is of particular importance, since the ion
density dominates the generation of the electric field according to
the mechanism which they invoke, and the density of mirroring
particles along a field-line is determined by the pitch-angle
dependence. It seems unlikely that there could be a significant
contribution to the ion density from such a high energy (i.e. 90 keV)
ion population. Thus it seems doubtful that any parallel potential
drop would be at a significant fraction of the full nose ion
energy.
The statements at the end of the 2nd paragraph on page 5 (complete
expelling of electrons from equator and then neutralization at some
point where a double layer occurs) need to be put on a firm basis. The
introduction of a "Chapman Layer" is puzzling since this is the only
equation in the paper, but the terms are not defined nor is the
expression used for anything. If the extraction potential is extended
over distance, as stated, this would seem to contradict the idea of a
double layer. Also, the process of "shielding" by neighboring flux
tubes is again something that needs to be either worked out or
juustified somehow if it is important to the chain of events.
(5) On the riometer absorption:
The relation of the observed riometer absorption (page 6) in a "narrow
strip in latitude" to the latitude of the parallel electric field
should account for the fact that both the nose ions and the beam ions
are seen over a reasonably large range of L-values (L = 5.2 to 3.3),
which translates into a magnetic latitude range on the earth from
about 63 to 57 degrees. Does this latitude range agree with the
riometer data? It would be helpful to see what the riometer data looks
like.