(This post was delayed due to a profound lack of togetherness on my part)
On Wednesday evening, in a crowded and uncomfortably warm meeting room, a sampling of European planetary scientists with an interest in Mars, including a number of Mars Express people, gathered to discuss plans for the surface. So far, European attempts to reach the Martian surface have not been happy ones. The joint Russian/ESA Mars 96 mission, which carried some surface landers and penetrators, never made it to orbit. Netlander, which would have set up a system of seismometers and other instruments, never made it to the launch pad. And then there was Beagle 2.
This string of failures means that the surface of Mars is effectively an American preserve, and European scientists don't particularly like that. So for a couple of hours they kicked around ideas about what might be done. There were no decisions, and no consensus. But the debate did throw up a number of key factors and some fundamental choices.
Key factor the first: it is going to be very hard for Europe to do anything that comes even remotely close to the ambition, scope and achievement of the current American program, let alone the vigorously expanded American program that might be in place by the time any of the European missions actually flies. Europe is talking about Pathfinder scale missions like that which America mounted in the mid-1990s for flight opportunities when America will be flying the Mars Science Laboratory, an all-singing, all-dancing, long-duration "MER on steroids". (There's an interesting piece in the New York Times today arguing that America's scientific and technological lead is slipping. This may be true on earth, in some respects, but it surely isn't true on the surface of Mars)
This is the context for a first crucial choice: "keep it simple, stupid" versus scientific ambition. There's a strong argument for a KISS mission with a lot of safety margin built into its engineering specifications, one that would be counted a success if it simply got something on to the surface. It might not have much of a scientific payload, but it would get the job done. Later missions could then build on the first success. It's hard not to feel sympathy for this view: getting to Mars is hard, it's best to walk before you run, and so on. The argument is given extra weight by previous failure. Like the MER rovers this year, the next European attempt to reach the surface really has to work.
There's a technical problem here, but not an insurmountable one. Proponents of such a mission argue that once you have a landing system you can modify it for future missions. In practice this has not proved to be possible. Landing systems don't scale very well. Turning the airbag system designed for Pathfinder into teh airbag system that served for the much larger MERs was incredibly hard work -- various people on the mission ended up wishing they had designed something new from scratch. The rocket system designed for the Polar Lander will be used, in modified form, on the Phoenix lander; but teh system for the Mars Science Laboratory landers will be different again. If you design a nice little lander for a KISS mission, its entry descent and landing (EDL) system might not be much good for follow on missions if they were more ambitious.
However, that's really jsut a warning against overselling such a mission, rather than trying it. EDL systems don't scale -- but EDL expertise does, as Albert Haldemann of JPL pointed out. JPL's advantage is not that it has existing off-the-shelf EDL systems, but that it has a cadre of engineers capable of designing new ones because of the experience they've amassed. Even a primitive KISS mission would provide the beginnings of a similar body of expertise within ESA.
Perhaps a bigger problem is that a safety-first bare-bones lots-of-margin mission, sensible though it might well be, might end up satisfying no one. The scientists will want science. The politicians will want something that makes Europe look at least vaguely competitive -- spending hundreds of millions on an extraordinary technical achievement that is completely overshadowed by someone else is not terribly attractive. A KISS mission would fall into the ancient trap of making sense as part of an ongoing programme, but not on its own.
Hence the argument for ambition; let's plan a mission that does something really ballsy on the science front, thus trying for an end run of some sort. The problem here is that this was the Beagle strategy. And right now it doesn't look very good.
The thing the people in the room seem most clearly agreed on is that a straightforward reflight of Beagle is not an option. No one knows what happened to Beagle -- according to people who seemed to be in the know, no single fatal engineering flaw has been discovered by the ESA inquiry into the loss. Instead a range of things that might have gone wrong has been identified. The inquiry apparently briefed Pillinger and UK science minister David Sainsbury on its findings last week -- including, I imagine, its criticisms of management and oversight -- but it is not going to release them in a final form until mid-May or so. (An interesting detail here is that the Mars Express results that had seemed to support the idea that the atmosphere's density profile was very different form what had been expected -- effectively pinning some or all of the blame on Mars itself, or at least on those who model its atmosphere -- seem to have gone away, at least as far as the Mars Expressionists in Nice were concerned.)
With no certainty as to the nature of the Beagle loss, it's a fair bet that the next European mission to the Martian surface will have an EDL system designed afresh, almost certainly by ESA's own technical staff. Among other things, that means there would be no chance of flying anything before the 2009 launch opportunity.
This scheduling points up the more general problem with an end-run high-ambition approach: American scientists are just as bright as European scientists, they and their engineers are much more experienced in this area, and they are far better funded. While Beagle had the putative advantage of doing science that the MER rovers couldn't in terms of analysing carbon compounds, by 2009 that will be gone. MSL may well end up with instruments capable of doing a lot of the things that Beagle was meant to do -- and doing them to a series of samples carefully chosen from any part of a large well-mapped field location, rather than to whatever came to hand (or paw) within a metre or so of the landing site.
A more plausible way of distinguishing the European program would be to go for science that America is not currently pursuing. This is the allure of "network science" -- stations scattered across the planet that would do seismology and also monitor the weather and climate. A surface science program built along those lines would produce science that nothing currently planned in America is looking for. The problem is that this is exactly the science that the cancelled Netlander project was going to do. And, not to belabour the point, it was cancelled.
Some Netlander advocates at the meeting seemed to think that they might get a successor project up and running by co-opting the Beagle community. Develop a spacecraft that could carry a modified Beagle package or a Netlander package. Fly a few of each. Everyone's happy. Except the people who pay for what looks a lot like two missions, not one -- with a series of further netlanders now in the pipeline. And the engineers who get asked to design a single spacecraft bus that can do two very different things -- something that never works out as well as people contrive to convince themselves it might.
And then there's the problem of ExoMars. ExoMars is meant to be the first stage of the European "Aurora" programme, a lander and orbiter combination dedicated to Mars's biological potential that ESA talks of launching in 2009. The fact that there was a hot-and-sweaty-meeting-room-full of people discussing completely different approaches to the martian surface when they could have been off having convivial dinners can be taken as an indicator of how likely the European planetary science community thinks that 2009 mission is. If people really believed there was going to be a sophisticated European rover mission launched just five years from now they wouldn't have needed to discuss anything else.
But the people committed to ExoMars -- who are probably pretty reconciled to the idea that their mission will slip to 2011 or 2013 -- know that if some other mission sneaks in in front of them then they'll be delayed even further, especially if it's an ambitious mission.
So my reading of the micropolitics ended up like this. Netlander people are unlikely to get to Mars unless they can expand their remit and their interest-group-constituency with some set of astrobiological objectives. ExoMars people are likely to resist a major pre-ExoMars astrobiology mission. Beagle people will be in the middle of that conflict.
And if I was in charge? Of the possibilities on offer, I'd tend to back a simple Netlander-plus, with the crucial proviso that all its landers be nuclear powered and long lived. If you can develop a robust EDL system for dropping a series of seismic stations to the surface, and if those stations are long lived (which means nuclear batteries) then you can build up your network of seismometers (and surface weather stations) over time. It's a very different sort of virtual presence from that offered by rovers, but you could argue its a crucial and complementary one. It's not something America is likely to do soon, because it's probably too ambitious an undertaking for a single Scout mission (network-science scouts didn't make it to the final shortlist last time) and most of the other missions are pretty well defined. And if the Mars Express Mars-is-still-active theme pans out, seismology could look newly attractive. (As one scientist put it, "we need to be sure there are seisms before we try seismology")
And the Beagle instruments? I'd put them forward for inclusion on MSL.