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"Constellation" Missions and Future Research

by David P. Stern




    Unlike the rest of this web collection, this is a somewhat personal account, concerning the current state and future plans of magnetospheric research.

    Magnetospheric physics was the first major scientific area opened up by artificial Earth satellites. The discovery of the radiation belt in 1958, the mapping of regions and boundaries of the Earth's distant magnetic field, the probing of the upper ionosphere, the confirmation of solar wind theory, the discovery of auroral currents and of parallel electric fields--these and other discoveries were major triumphs of early space research.

    Today the field is almost dormant, with no major discoveries in the last 20 years. (A "major" discovery here is one expected to have a significant place in textbooks of 50 years hence.) Missions are few, and not enough bright young minds are joining this research effort. How did that happen, and can the old excitement be recaptured?

    I became aware of this drastic change around 1985, when Marsha Torr--then a notable researcher--conducted a survey inside the community. For every year since 1958, she asked, could you please name what in your mind seemed to be the most important achievement in the field. (Results were to be published, but they never were.)

    For the early years of space research the choice was not easy. In 1958 the radiation belt was discovered--but that also was the year of Parker's theory of the solar wind. In 1961 Dungey proposed the open magnetosphere--but that same year Axford and Hines independently introduced the notion of global magnetospheric convection. In 1962 the front boundary of the magnetosphere was found, but that same year Mariner II also observed the solar wind and its streams.

    With later years the choice became easier, and after a while, more and more dates stayed blank (see chronology of magnetospheric research). In 1983 ISEE-3 in the far tail observed the streaming of plasma away Earth, and in 1985 the CCE spacecraft of the AMPTE mission finally closed the gap in our information about the energy and composition of the ring current. But hardly anything comparable has happened since. Had all significant questions been resolved, leaving little more to be discovered?

Developing a Strategy

    Around 1995 I looked into this very question and concluded that magnetospheric physics had not run out of unsolved puzzles, many still remained. A list of some 25 non-trivial unsolved questions was presented in an Eos article, titled "Developing a Strategy for Magnetospheric Research."

    Two kinds of reasons for the slow-down turned out to exist: some were rooted in the science, some in the research community and the way it operated. The 1996 article (reproduced below; it is in the public domain) focused on the first kind alone. The second, no matter how significant, could not be discussed without involving details, individuals and institutions, which would have completely distracted attention from any constructive attempt to re-establish productive progress. Let others discuss such matters--or else, let future historians puzzle them out.

    The 1996 article noted three reasons for the slow-down. One related to the nature of scientific discovery. It certainly counts as a discovery when a phenomenon is first observed, perhaps by visiting a new region in space for the first time. But it takes a completely different kind of discovery to come up with the physics explaining what was observed. This second kind of discovery is often much harder, requiring theory and focused observations, usually of a much more detailed sort. Most discoveries of the early heady period of magnetospheric research were of the first kind; the explanations still lagged.

    Secondly, practically all space missions in the past have used isolated satellites, or at most, closely spaced ones (e.g. ISEE 1/2, or more recently, the Cluster mission). After all regions of the magnetosphere were visited and studied in this fashion, a logical next step seemed to be observing three-dimensional patterns by coordinated networks of satellites. Indeed, the 1996 article proposed one such mission, tentatively named "Profile," a string of 6-10 identical small spacecraft, strung out along a highly elliptical orbit and thus providing a simultaneous cross-section (profile) of the magnetosphere. It was meant to be a shared facility, involving the entire community in a wide diversity of research tasks.

    And third, an effort was overdue to consolidate existing knowledge, creating texts and review articles--especially the latter, an essential step in bringing together diverse observations and theory. A coherent view of the magnetosphere would result, helping give future researchers a broad base of knowledge rather than one narrowly defined through apprenticeship. Until that happened, our community was like an army which had outrun its supply train.

    Publishing "Developing a Strategy for Magnetospheric Research" was an interesting experience. Because of Eos limitation, the original text had to be shortened, and the chronology was omitted. The editor, sensing a controversy, appointed no fewer than eight referees--plus himself and a referee from AGU headquarters. Too many, it turned out: they contradicted each other (one even felt that no problem existed) and in the end the editor just advised me "satisfy them to the best of your ability."

    Considering the fuss, the article generated rather little debate. Some readers sent messages--one even told me "ten referees--that's a toxic dose!" But no wider discussion followed, about steps to be taken, or lessons to be heeded. Perhaps the time was already too late. The community was already divided, each group promoting specific missions (ones which would, presumably, ensure its own future) and few if any were willing to speak for the community as a whole, trying to pull together what had already become a fragmented effort. That was in 1996; since then fragmentation had only increased.

Multi-Satellite Missions

    In the existing line-up of proposed future missions, only one will be examined here--a "constellation" consisting of a large number of small satellites. More is needed, of course--missions to perform essential monitoring of the polar cap, the aurora, the Sun and the solar wind. In the more distant regions, however, "constellation" type missions are the ones most likely to add significantly to the understanding of our global magnetosphere.

    The need for coordinated simultaneous data from widely separated locations was appreciated a long time ago. The "OPEN" mission of 1978 (later morphed into ISTP) envisioned 4 spacecraft, each covering a region in the magnetosphere. It was later realized, though, that such coverage was much too sparse. Around that time, too, the National Space Science Data Center (NSSDC) organized "CDAWs," coordinated data analysis workshops, where data were assembled from all available spacecraft (also from the ground), for selected periods of special interest. Experience showed that such random collections generally gave inadequate coverage: even though considerable effort was expended, CDAWs produced few useful results.

    A proposal made around 1995 by George Siscoe went to the opposite extreme: observe the magnetosphere as a 3-dimensional "image" from 600 satellites (later halved to 300), each satellite contributing a "pixel." In one version the satellites would save power and cost by carrying no transmitter, only special corner reflectors, encoding the data into the reflection of a laser beam sent from the ground. This ingenious plan (possibly due to Arthur Petschek) was unfortunately undone by the Doppler shift of the returned beam. The related question of analyzing such an enormous data stream would also have been a serious problem.

    In response to a NASA solicitation, a more conventional approach calling for 56 satellites (and rather extreme miniaturization) was advanced in 1996 by Angelopoulos and colleagues of the University of California at Berkeley. The same solicitation also brought a study proposal for a "Profile" mission (following the above Eos article), calling for a string of 12 satellites (or rather, two close strings of 6 each--see below for more). Prepared by a team of physicists (includings this author) the proposal was submitted in May 1996 but the committee formed to handle those proposals rejected it, claiming it mainly focused on magnetic reconnection and was not innovative enough. That reasons for that decision were protested, but NASA refused to discuss them. The main result of the protest may have been the rejection of a request to participate in the mission study which followed and on the follow-up mission definition team.

    Believing in the merits of the proposal, it was pursued independently, without funding. Described below are the final versions-- the official plan of the mission definition team, named "Draco," and the "Profile" plan. Readers can then make their individual decisions.


    The report of the science definition team (NASA document TM 2001 209985) appeared in May 2001 and can be accessed in PDF format (2.1 Mb) here. DRACO is an acronym of "Dynamic Response and Coupling Observatory," also the name of a large constellation (somewhat vaguely defined) winding halfway around the northern celestial pole. "Draco" was meant to be a "constellation" of 50-100 small spacecraft in a series of nested elliptical orbits, with perigees of 3 RE and apogees ranging from 7 to 40 RE.

    The satellite design and many details of the mission resemble those used for "Profile"; major differences include on-board propulsion and the way satellites were to be "dispensed." The main goal in designing the mission was to ensure a spacing 1-2 R between spacecraft. The design also planned to use lessons learned from the ST-5 mission, an approved technology mission of 3 small satellites meant to serve as testbeds for the design of small satellites.

    An updated short version of the mission plan was released 1 January 2005 (or by one source, October 2004), where the number of satellites was dropped to about 30, using three "dispenser ships". The mission was now named MagCON (for "magnetospheric constellation"). The new release in PDF format (3.4 Mb) can be downloaded here, and both documents can also be downloaded from the NASA site
In what follows, the mission will continue to be referred to as DRACO, the name used in the PROFILE articles linked below, where the two mission plans are compared.

    For further details about DRACO and MagCON, see the two reports linked above. Launch was originally planned for 2010, but a web page dated August 2005 places it outside the 5-year budget planning window.


    The original idea of "Profile" called for the launch of a dozen small satellites (25 kg) with no propulsion, from a single "mother ship" in an elliptical orbit with apogee 20 or 25 RE. They would be released in pairs on consecutive perigee passes, with small additional velocities imparted by the spin of the "mother ship," enough to create a separation of about 1 hour orbit time between consecutive neighbors. Because perigee would be fairly low, some transparent radiation shielding of the solar cells would be needed, while all satellites would ultimately re-enter the atmosphere and avoid adding space debris.

    Each spacecraft would carry a detector for ions and electrons (0.1-30 KeV), as well as a fluxgate magnetometer. Each would spin slowly around an axis approximately perpendicular to the magnetic equator, at about 20 rpm, and the spin modulation of the ion rate would allow two components of the bulk flow of the ion plasma to be estimated.

    The mother ship would first enter a suitable elliptical orbit and would then be turned 90 degrees and spun up at 20 rpm around an axis perpendicular to the plasma sheet. At each perigee pass a pair of satellites would be released, one thrown ahead and one backwards, keeping the mother ship in balance. When all have been released, two groups of 6 satellites would each share an orbit, those orbits having apogees 1 RE higher or lower than the mother ship. The groups will thus overtake each other while keeping a constant spacing, allowing a number of interesting experiments, as well as intercalibration of all detectors.

    Originally all orbits were calculated for an inclination similar to that of Cape Canaveral, though it was realized that orbits of smaller inclination (e.g. launched from the European site at Kourou) were preferable, taking advantage of the warping of the plasma sheet caused by the tilt of the Earth's magnetic axis. Later it was pointed out by Steve Hughes of Goddard Space Flight Center that with a little extra mid-course thrust, such orbits could also be achieved with launches from Cape Canaveral. The "Profile" articles were already in publication by the J. of Astronautical Science, and the best one could do is insert a "note added in proof" describing this possibility and giving Steve Hughes proper credit. An explanatory note was produced and distributed with the reprints, and a copy of it is linked here as well, together with the articles themselves.

    A specially attractive variant of the mission was "Twin Profile" of 24 satellites, released from two "mother ships" launched into the same initial low-altitude parking orbit, but then boosted into ellipses 180° apart. It turns out that the evolution of both groups of orbits (due to sun, moon and equatorial bulge) was quite similar and that they would remain 180° apart throughout the mission. The cross-sectional scans of the magnetosphere would now run end to end--from noon to midnight through all the interesting equatorial regions, also from dawn to dusk, and each formation would occur twice each year, not once, as the two groups of spacecraft exchanged positions.

In Conclusion

    Since the articles described here appeared, progress in magnetospheric research has been very slow, and a real risk exists that continuity will be lost. The same challenging unsolved problems remain, and addressing them would still require additional plasma physics and more extensive data coverage.

    Meanwhile, priorities in the outside world have shifted--at NASA, on the national level and in the international community. Those shifts have hit magnetospheric research especially hard--timetables have slipped, mission plans were trimmed, and the scientific community is slowly shrinking. Plans made in the past may not be realistic any more, and momentum may not be easily regained. It would be hard to guess when and where significant progress will resume, for as Yogi Berra supposedly said, "predictions are difficult, especially about the future."

    The best one can do now is preserve information, as was done here. Whenever magnetospheric research recovers its vigor and support, the same questions and insights of the Eos article will still apply, and the "Profile" program may still offer the most logical and economical use of limited resources. When that time comes, I hope, "Profile" will be seriously examined and considered, something not done before.

    Meanwhile, let these web documents serve as a reminder of an unfinished job.

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Author and Curator:   Dr. David P. Stern
     Mail to Dr.Stern:   david("at" symbol)phy6.org .

Last updated 21 January 2006

Above is background material for archival reference only.

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