Dear Editor,
I feel that neither referee has fairly reviewed this manuscript, both
having made errors in judgement that convey an unfamiliarity with the
field. I would therefore petition that a third referee be assigned to
this paper. Since the crux of this paper, as both referees acknowlege,
lies in the viability of a parallel electric field, I would recommend
that a known expert in the field be assigned as the third referee.
Barry Mauk, Elden Whipple, Carl McIlwain all come to mind as pioneers
in this field. I would caution against Michael Schulz, however, since
we are locked in a cross-refereeing battle presently.
We have made some changes to the paper, though perhaps not as
extensively as the referees would have liked to see. The paper suffers
from too much content rather than too little, and we do not see a
clear way to convey this new storm model in fewer words. Neither the
data nor the theory can stand on their own, but are inextricably
linked. That is, the data by themselves reveal a disturbed time period
with very puzzling peaks in the spectrum but otherwise would be
ignored by both the energetic (MeV) radiation belt community or the
plasma (<1keV) community. Only a ring current specialist would notice
something odd. Likewise, the theorists pursuing parallel electric
fields have developed theories for the auroral zones and have had no
cause for finding 30 keV potentials. Without experimental evidence to
the contrary, there may exist the temptation to say such fields cannot
exist. Thus we see this paper as a Gestalt, a whole that cannot be
divided up into lesser parts, and the whole will stand or fall
together. Therefore we take very seriously the criticism of our
referees who imply that we have been shoddy in our experimental
technique. On the contrary, we have tried to explain this data many
other different ways and concluded that indeed we were observing a
previously undiscovered phenomenon. One could write a paper describing
all the theories that fail to explain this data set, but not in the
space of 4 pages. Thus we beg our referees and our editor to put aside
all experimental or theoretical prejudices and examine this paper with
new eyes. We know we are being controversial, we would like to be
proven wrong. It is by such efforts that the field advances. But
science has always opposed pedagogy, and we hope that the referees
will avoid appeals to intuition or experience as conclusive
proof.
Reply to Referee A:
1) The first clear (not implied) criticism is that we did not include
Dst in our paper, and that when Dst is examined, no storm could be
ascertained. We begin by noting that definitive Dst is available only
through 1994 (from NGDC, perhaps 1995 from Kyoto), and by the numbers
quoted by the referee, we can only assume he is confusing the
provisional Dst with definitive Dst. Now the provisional Dst is
generated automatically as the result of a spherical harmonic fit to 4
low latitude stations, and, as far as I can tell, has not had the
ionospheric contribution subtracted. In the past, this subtraction was
done manually by Sugiura himself which caused the 3 year delay in the
Dst. Noting that the provisional Dst for April, has a continuous
period of 32 hour duration (beginning on the 7th) where the Dst never
drops below +9 and increases up to +28 with an average of about +18,
we would say that the ionospheric Sq variation has not been properly
removed from the provisional Dst. Making the assumption that there
were no compressive events in the solar wind that were increasing the
Chapman-Ferraro magnetopause component for such a long time (SSC's are
known to cause a short, positive excursion, but normally such SW
compressive events trigger "unloading" events that prevent such a 32
hour positive Dst) then we would assume that the Sq variation had at
least 28 nT of effect on Dst during this period. If one then subtracts
(at same UT), day 7/8 from day 15 as the MINIMUM correction necessary
to Dst (e.g. using the quietest day of the month technique), one finds
a quite respectable storm of -63nT occuring the very first hour of
April 15, consistent with the entire analysis presented in this
paper. Now is a -63nT storm sufficient to call this a magnetic storm?
Actually, yes, because we present a mechanism by which individual
storms can have widely varying Dst response to the same SW
input. Predictive models based on the SW alone can explain up to 70%
of the Dst response, we can predict a good chunk of the remaining 30%.
Why did we not include this paragraph in our paper? It was an
executive decision not to get involved in the Dst controversy (see the
recent EOS article by Wally Campbell). We have included a sentence in
the revised paper however.
2a) Again, despite Ejiri's flawed paper (his trajectories are not
reproducible by any technique that we are aware of, so that we assume
he must have used a forward Euler integration technique in which the
error grew faster than the solution. This raises the question of how
one can ever test the computer results of a JGR paper without having
access to the computer code that generated them) in which he showed
the "energy notch filter" response of the magnetosphere, it is obvious
both in his paper and many other ones that the particular value of the
energy transmitted in the magnetospheric "notch filter" depends on
electric field, magnetic field, magnetic latitude, LT and L-shell. One
need only ramp up the electric field to go from 30keV to
90keV.
2b) The energy "width" of the peak reproduced by Ejiri or observed by
AMPTE/CCE/CHEM (I supplied the data to Janet) is a product of magnetic
latitude as well as LT. (See my 1993 AGU abstract.) Even the
off-equatorial passes of ISEE1/2 showed exactly this same peak (see
the 92 STEP paper, Sheldon 94), but with a very curious pitchangle
dependence, which was not, to my knowlege, simulated by any previous
modeller, yet which fall naturally out of the UBK analysis used in
that paper. You are quite right in saying that the spectral peak
should be wider at 2400LT than at 1800LT, though you perhaps do not
realize that these ions I am describing cross the 2400LT boundary
twice. Look carefully at the figure in the Sheldon 94 paper, because
it shows that the ions can cross a particular LT sector twice, once at
high-L, and once at low-L. The "notch filter" effect is more important
the lower the L-shell, so that it is important to differentiate not
just what LT, but what L-shell the observation was made. Thus a low-L
2400LT measurement may still be "sharper" than a high-L 1800LT
measurement. In a very similar way, the magnetic latitude plays a
part, with the energy width correlated to pitchangle, so that the
smaller the pitchangle (higher the latitude of the measurement) the
wider the energy width. After saying all that, I will now admit that
the energy resolution of the IPS data is too poor to really resolve
the energy width of these peaks. Often we get a single energy channel
response so that we can only put an upper limit on the energy width of
the peak. This is also why I refer to the peak as "mono-energetic",
since I cannot determine the width.
2c) The claim that we should have modelled this day to show that 90keV
ions were "nose" ions is a valid point. I seriously considered adding
this to the already too full paper. If this were the primary or only
objection of the referees I would do it now. But it seemed to me that
even if I proved this point by dint of great effort (resurrecting code
from backup tapes of 1990), objection would still be made
elsewhere. Nonetheless, I will simulate this storm and quote the
result, though the simulations will have to be presented in another
publication.
3) This paper is not about O+ beams. They can be H+ beams for all the
difference it makes to the model. The identification of these beams as
O+ enables the model to explain a multitude of observations that
otherwise are somewhat mysterious. It is the explanatory power of this
hypothesis that makes it so attractive. But let us address the
evidence, which the referee impunes.
a) It is well known that O+ is lacking in the ring current during
quiet times, but present during storms. POLAR/CAMMICE sees a complete
absence of O+ in this region for months at a time. Now unfortunately
the instrument was off (for fear of discharges during the hydrazine
release required to flip the axis of the spacecraft) for a few days
around the 15th of April. But it was remarkable how much O+ was
present when the instrument switched on 4 days later. Because of the
rather rapid decay of O+ in the ring current (on the order of days at
this L-shell), one can conservatively postulate that the O+ came
during the only magnetic storm of this period, namely, April
15.
b) A very similar beam signature was seen March 21 on IPS, and in that
case CAMMICE was operating nearly normally and saw the temporal
concurrence of O+ and beams, though the geometric factors of CAMMICE
preclude determining the pitchangle distribution of its O+
measurements. Other factors led us to favor the April 15 event over
March 21, and again, space limitations cause us to cut the discussion
of March 21.
c) TIMAS showed enhanced O+ beams on April 15 in preliminary plots
shown me by Bill Peterson.
d) I have not looked at TIDE data, though I would be greatly surprised
if they observed a 30keV O+ beam, and that wraps up the composition
experiments on POLAR.
I'm not sure how much more evidence I can muster, I can only say that
I found this evidence compelling, and not "very weak" and
"circumstantial".
4a) We don't know of any particle measurement that gives us the
thermal electron density. It is not an easy measurement to make. One
could look at the lower hybrid noise line and infer a total electron
density, if the wide band data were available, and if the PI were
willing to go out on a limb in his interpretation. POLAR does not have
the resolution of the WIND instrument, so that cold plasma densities
are not routinely derived from this data. At any rate, the
interpretation of the wideband data would be as long as the entire GRL
paper itself, so that we have not pursued this line of inquiry. One
must also recognize that the POLAR/CEPPAD data set is precociously
mature compared to other POLAR data sets. Perhaps such a comparison
could be made more carefully in the future.
4b) We do require a balance between the nose ions and the cold
electrons, so that the referee is correct in saying that the mechanism
we propose can be shorted out by these cold electrons. However the
densities alone are not the most crucial factor, it is the
currents. What we require is that the current of convecting cold
electrons be less than the current of convecting hot ions. If this be
the case, then local (Debye sphere) charge neutrality is lost and
space charge effects set up the 30 keV potentials. This moves the
distribution from the first to the second of Whipple's
solutions. Unfortunately Elden himself didn't recognize that a second
solution existed, this was pointed out to me by Barry Mauk at the 96
Huntsville conference, so that the characteristics of this second
solution are not well known. My analysis indicates that the space
charge set up by trapped, bouncing ions will peak at some point away
from the equator. This then becomes the point of maximum
potential. Equatorward of this point the potential is entirely
determined by the phase space density of the ion population. For most
"reasonable" distributions of nose ions, this electric field points
equatorward. Thus any cold electron that convects into this fluxtube
"from the side" will experience a force propelling it into the
ionosphere, while removing that amount of energy from the space
charge. Earthward of the maximum potential point, determined in part
by the pitchangle of the hot ions and in part by the cold electron
densities, the space charge is neutralized and the potential rapidly
approaches the ~kTe value predicted by Whipple's first solution. Note
that this point is a DYNAMIC equilibrium, and therefore very sensitive
to time-dependent processes. This rapid change in potential produces a
double layer that really can't be described, as Whipple admits, by the
theory in his 77 paper. Now others have asked the question where the
potential field lines close, how can one create a space charge on a
flux tube or a double layer without affecting the potential on
neighboring flux tubes. The answer is that there does exist a
secondary, perpendicular electric field in which neighboring flux
tubes respond to "shield" the space charge. This is evidenced in the
polarization electric field seen in the SAID plasma motion.
Now I know I have raised more questions than I have answered in the
above paragraph. That's why I didn't attempt to include it in this GRL
paper. It is clearly the subject of a second paper. As I said before,
this paper is a Gestalt, a whole that must stand together. Rather than
develop the above theory to the level of believability (which might
take decades) I have attempted to circumvent it by establishing
empirically the existence of a 30 kV potential. So to make a very
long-winded answer to the referee, who obviously heard my Huntsville
talk since I carefully didn't mention any of the above theory in this
paper, yes, the cold plasma density is important, but without further
theoretical work, the actual cut-off density is unknown and therefore
arelevent to this particular paper.
4c) I don't really require monoenergetic (empirically that is) ions,
it just so happens that the "notch filter" of the magnetosphere
produces monoenergetic ions. One can solve for Whipple's second
solution with any distribution. At my current level of understanding,
there's no a priori reason why a monoenergetic distribution is
required to get large parallel potentials.
4d) Perceptive question: If the presence of hot ions generates
parallel electric field, why don't ring current ions generate these
parallel fields? As I have attempted to answer in the above
paragraphs, it is not the presence, per se, but the time derivatives,
the dynamics that create these parallel fields. While the ring current
is being filled (or emptied?) these fields form. It requires an energy
input, a non-equilibrium in the hot ion and cold electron currents, to
produce such fields. Ultimately wave scattering and heating will erase
these pitchangle gradients (and free energy!) to produce the kTe type
potentials seen in the first solution to Whipple's equations. The real
marvel is that such waves grow sufficiently slowly that the parallel
fields can grow to this magnitude.
5a) My conversation with Phil Anderson (at Aerospace Corp) who did his
PhD thesis on SAID events, gave me the impression that SAIDs were
linked to substorm injections on the basis of AE or geosynchronous
signatures. Since I carefully distinguish between substorm and storm
injections, I try to refine the criteria, in my model, to be only
storm injections. i.e. substorms should not produce SAIDs.
5b) How would one look for a signature of field aligned potentials? If
they were in the kV range, one could look for optical signatures,
which to my knowlege, were only weakly correlated with SAIDs. But if,
as my model predicts, the potentials are 10's of kV, the precipitation
would be too low in the ionosphere to produce an optical signature. On
the other hand, they should produce a whopping big electron
signature. Both Bill Peterson and Phil Anderson suggested that I do an
analysis of the electron spectrometer on DMSP during identified SAID
events. I would love to, if there were more of me. So I can only
suppose that no one has looked yet.
5c) Have O+ beams been observed during SAID's? None that I know of,
though Bill Peterson would be the one to talk to. The problem is that
the O+ beam appears only at the double layer, which can occur, as I
describe above, some 1000's of km above the ionosphere. All that DMSP
would observe would be an enhanced heating and possibly 30 keV
electron precipitation. Bill Peterson confirms that getting O+ beams
out of the ionosphere is awfully difficult, and it has to happen
really fast. Furthermore a two satellite conjunction study showed that
this O+ beam had to form above 1000 km. All of which is "very weak
circumstantial evidence" for the support of my theory and therefore
not mentioned in the paper. I have Bill Peterson looking for holes in
my argument right now, if you find one, he would like to know about
it.
5d) Is there evidence for a SAID occuring the 15 of April? Again, I
don't know quite who to ask that question to. I suppose I could
request the DMSP data, and after some delay look for a signature. But
I find the riometer data from CANOPUS compelling. I am not an SAID
expert, but I would associate the deep riometer absorption feature
seen around L=4.4 with a SAID. The problem is that one would really
like an imaging riometer, and only parts of one have been deployed at
sub-auroral latitudes, according to Ted Rosenberg. That is a station
near L=4 in Alaska, from which he has a central meridian plane
functioning. He found exactly this signature in his riometer data
though to my knowlege has not been correlated with DMSP SAID
signatures.
5e) From the CANOPUS riometer data, and some extrapolation, I have
linked SAIDs to this mechanism. Perhaps it is not compelling on the
15th, but again, this paper is a Gestalt, of which the 15th is only a
part. To put it another way, Yuri Galperin, who has published a little
on SAIDs, finds this to be the first viable mechanism for producing
the 3 hour duration of a typical SAID. With that kind of predictive
power, I did not think the SAID connection to be too peripheral for
this paper.
6a) There have been many theories about the dependence of O+ and Dst,
and perhaps even entire careers launched on these theories. I did not
"require" O+ beams in my model to explain O+ in the ring current, it
came as a natural product of the model. I agree wholeheartedly that
the cleft ion fountain is responsible for most of the O+ in the tail
and current sheet, and through injection, the ring current. My thesis,
after all, was about the composition of the quiet time ring current
and we measured this O+ contribution. What is fundamentally new here
is the temporal correlation between O+ and Dst, which cannot be
explained by the cleft ion fountain. Look at some of Iannis Daglis'
recent publications. The O+ at keV energies shows up within an hour or
less of the storm decrease in Dst. One would have to strain to show
how the cleft ion fountain could produce such an immediate response of
such energetic O+.
6b) Asking why others have not done a statistical study of sub-auroral
O+ beams and storms is outside my purview. The implication that such a
study would have negative results seems a bit unfair. I question
whether the DE instrument would be sensitive to these energies, it
might be that the study has not been done because it couldn't be
measured.
7) Your explanation of the occurence of oxygen ICW at 1800 appears to
beg the question. Why should a storm have more O+? Look carefully at
Daglis' plots. Refuting a theoretical prediction by saying "we don't
need a theory, we have an observation" seems a little biased. And why
would the plasmasphere bulge not move when the ring current did?
Wouldn't the same electric field that brought in the ring current ions
to such low L-shells also strip off the outer layers of the
plasmasphere? And why should the ring current ions produce ICW at this
time only when they overlap the plasmasphere all the time? In fact,
Brian Anderson's ICW survey using AMPTE/CCE data show an appalling
lack of ICW at the plasmapause. When your theory is carefully
examined, I believe you will find that this alternative explanation
may actually be the more predictive.
8) I admit the ENA observations are peripheral and circumstantially
weak. It just so happened that at the COSPAR 96 inner magnetosphere
session, all these papers were presented together and I got a little
excited at how one theory could explain them all. In fact, ENAs are a
tracer of the ring current, so that a composition experiment, such as
ICS on GEOTAIL, should in principle be able to see global evolution of
the O+ population and verify our predictions, but in practice will
have to wait for the IMAGE mission. That is, the ENA observations
require a model for the cold electron donors (H, O+, He+) in order to
determine the original ring current densities. With so many unknowns,
the evidence is rather weak to support an O+ source that turns on
during the main phase of storms, though I still find the data very
intriguing.
Referee B
1) I admit that trying to do magnetospheric physics by the seat of
pants is counterintuitive. Who predicted that the magnetic bottle of
the earth should be full of plasma before the advent of space flight?
Likewise, applying a static, space-charge intuition to the electric
potential developed by a trapped population is counter intuitive. I
strongly recommend to the referee that he read the 1977 Whipple paper
we cite, and try to convince himself that the figure reproduced there
is correct, that the electric field does indeed point away from the
equator. I would also recommend that he solve the equilibrium
equations (eq 12) to convince himself that this solution is not a
freak BC dependent phenomenon. Finally, I would give the referee this
heuristic explanation of this counterintuitive result. Let us replace
the field line with a bowl, and the charged particle with a
marble. The marble rolls back and forth in the 1-D bowl, spending most
of its time away from the bottom. If one then asked, "in a
time-averaged sense, what is the density of marble in the bowl" one
would find a density maximum somewhere up on the sides, a minimum in
the center and density function dropping rapidly to zero above the
maximum--lets call this 1-D density curve a "crater" in the spirit of
FTE's. Now replace the density function by a charge, and one should
immediately recognize that the slope gives the electric field. Now
rather than make a sign error in derivatives, we argue from Lenz's law
by adding a second particle. We should see immediately that if we
placed a second particle of like charge in the crater function, it
would roll to the center, whereas a second particle of opposite charge
would roll away from the center. Thus my contention that the electric
field will accelerate electrons away from the equator in contrast to
the referee's intuition.
2) The referee would like to identify our field-aligned ions with
"butterfly" distributions described previously. It may well be that
the "butterfly" distributions previously observed were field-aligned
but rather than reanalyze that data set, we will attempt to show that
the 1987 theory of "butterfly" distributions does not apply to this
data set.
a) The 1987 paper argues that a "loss cone" can appear at 90 degrees
so that the maximum flux is found at, say, 45 degree pitchangles. The
process that produces this 90 degree loss cone is the dependence of
particle trajectories on pitch angle, the so called "pitchangle shell
splitting". Thus near the magnetopause, 90 degree particles can be
preferentially lost to the boundary layer. Since we are as low as
L=3.5, clearly magnetopause shadowing is out of the question.
b) A second more subtle effect occurs if there is a radial gradient in
the particle population. Such a radial gradient, can be transformed
into a pitchangle gradient on the opposite side of the earth due to
pitchangle shell splitting. Can such a radial gradient occur from L=7
down to L=3? The answer is no, simply because the densities of the
measured flux remain too high. That is, if we integrate such a radial
gradient from L=7 to L=3, we would run out of particles very
rapidly. Then why does the referee appeal to this interpretation?
Perhaps because he is unfamiliar with the data from a polar orbit,
which has markedly different characteristics from the equatorial
orbits used in the 1987 paper. That is, we remain at a single LT and
intersect the magnetosphere nearly radially unlike equatorial
spacecraft.
c) An even more subtle effect is L-shell splitting caused by the
assymmetry of the magnetosphere. Again, this could mutate radial
gradients which under severe circumstances might produce a trapped
population that does not peak at 90 degrees. But again, such an effect
could not produce the prolate distribution we observe over a large
range of L-shells.
d) But all of the above methods described in the 1987 paper would
leave the loss cones symmetric, and the fact of the matter is, the
loss cones are not symmetric. One loss cone is substantially more
filled up than the other, though the 22 deg angular resolution of IPS
cannot resolve a separate beam in the loss cone. Since the highest
fluxes are seen just outside of the ionospheric loss cone, they appear
to be particles that have scattered out of the source cone in one
hemisphere to avoid being precipitated into the loss cone of the other
hemisphere. Furthermore, none of the processes mentioned in the 1987
paper would produce the maximum flux so close to the ionospheric loss
cone. Thus we categorically deny that these particles can in any way
be described by the theory of the 1987 paper.
3a) I agree with the referee that a 30keV potential in the
plasmasphere is astounding. I do not fully appreciate why any
empirical measurement can be called "unbelievable" a priori. One can,
of course, choose what one believes, and thus prove Thomas Kuhn
correct. One can hope, however, that other criteria be employed in
judging a scientific piece of work.
3b) If the referee has another interpretation of our data, (somewhat
more compelling than the butterfly interpretation above) we would be
more than happy to abandon our astounding theory. Occam's razor argues
that the simpler explanation be taken, and I confess openly that our
explanation is not exactly simple. However the mere fact that other
people might have a different explanation does not invalidate a
theory. As many philosophers of science have argued, the theory with
the greatest predictive power should be preferred, which is really
another way of phrasing Occam's razor. If the referee would like to
flesh out his butterfly theory, explaining the zippers and the O+ and
the other aspects addressed by our model, I would be happy to debate
the merits with him. However if he merely posits the existence of an
alternate theory combined with his resistance to this one, I am at a
loss to respond.
3c) The potential profile explained above in the heristic argument can
be fleshed out by solving the Whipple equations. The double layer
cannot be described by Whipple, mostly because of its small scale
size. But I think, as the above reply to referee A shows, such a
discussion would never fit in this GRL. I can reference a future work,
if the referee would like, but I am afraid that adding another
discussion to this already overloaded paper would sink it for
sure. Can the referee suggest something to replace with this
discussion if he deem it necessary?
3d) Need an author rederive previous results to claim definitive
treatment? Why should the second solution to Whipple's equations NOT
be a theory? Is the referee implying that the above analysis is mere
speculation? Or that we are incapable of theoretical analysis? Or am I
over subtle in my reading of a crass remark which only means that the
referee doesn't agree with my conclusions.
4a) The word "monoenergetic" means primarily that our instrument
cannot resolve the energy width of the peak. Nonetheless, I have fit a
Gaussian to the 3 point peaks and can add error-bars to the second
figure where the width of the error bar is the sigma of the fit (or
the FWHM if so desired).
4b) I reference the Mursula paper because it was delivered at the
conference that provided the gestalt for this model. It need not be
the one in the GRL paper. I would be happy to replace it with a better
reference if the referee could point us in the right
direction.