OK folks, here is Andy’s entry for the possibly overcrowded “end of science” market. I am not really making a case that Astronomy as a whole is finished – just that the Golden Age of Surveys is closing. This is not for any profound reason, but just because we have already ticked off the easy wins, and there is only so much money in the world.
This material is recycled from my long overdue article for “Astronomy and Geophysics” – its the written version of a review talk at last year’s National Astronomy 2006 meeting. (Sorry Sue). The astro-ph version is here. Off we go:
In 1950, the universe seemed to consist of stars, and a sprinkling of dust. Over the last fifty years, the actual diverse and bizarre contents of the universe have been successively revealed as we surveyed the sky at a series of new wavelengths. Radio astronomy has shown us radio galaxies and pulsars; microwave observations have given us molecular clouds and the Big Bang fossil background; IR astronomy has shown us ultraluminous starburst galaxies and brown dwarfs; X-ray astronomy has given us collapsed object binaries and the intra-cluster medium; and submm astronomy has shown us debris disks and the epoch of galaxy formation. As well as revealing strange new objects, these surveys revealed new states of matter (relativistic plasma, degenerate matter, black holes) and new physical processes (bipolar ejection, matter-antimatter annihilation). Having opened up gamma-rays and the submm with GRO and SCUBA, there are no new wavelength windows left. Has this amazing journey of discovery now finished ?
Well… wavelength is not the only possible axis of survey discovery space. Lets try some others.
Photon Flux. We could just go deeper. Historically, this has been as productive as opening new wavelength windows. The classic example is the discovery of the entire extragalactic universe, which did not become apparent until reaching ten thousand times fainter than naked eye observations, requiring both large telescopes and the ability to integrate. We can now see things ten billion times fainter than the naked eye stars. However, we have reached the era of diminishing returns. The flux reached by a telescope is inversely proportional to diameter D but its cost is proportional to D**3. Significant improvements can now only be achieved with world-scale facilities, and orders of magnitude improvements are unthinkable. The easy wins have been covered already – our detectors now achieve close to 100% quantum efficiency; we have gone into space and reduced sky background to a minimum; and multi-night integrations have been used many times. We will keep building bigger telescopes, but it no longer seems the fast track to discovery.
Spectral resolution. Detailed spectroscopy of individual objects is of course the key technique of modern astrophysics, but what about spectroscopic surveys ? This has been a big winner over the last few decades, because the spectrum of a galaxy gives you the redshift, and so the distance. This way we mapped out the Universe in 3D. We were not expecting the voids, bubbles and walls that were found in the galaxy distribution in the 1980s. This industry will continue, but there is no obvious new barrier to break. Narrow band imaging surveys centred on specific atomic or molecular features (21cm HI, CO, H-alpha) have been fruitful, but again its not obvious there is anywhere new to go. Some of my X-ray chums have suggested that deep X-ray surveys are the next-big-thing. I can see they will be v.good, but I can’t see it really cracks open a new part of parameter space.
Polarization. Polarisation measurements of individual objects are a very important physical diagnostic, but are polarisation surveys plausible ? Surveys of samples of known objects to the 0.1% level have been done, with interesting results but no big surprises. Perhaps blank field imaging surveys in four Stokes parameters would turn up unexpected highly polarised objects ? This has essentially been done in radio astronomy but not at other wavelengths.
Spatial resolution. If we can just resolve tiny tiny detail, perhaps we will see something really new ? This is the dominant big-project target of the next few decades, and of course is the real point of Extremely Large Telescopes. Put together with multi-conjugate Adaptive Optics, we hope to achieve both depth and milli-arcsec resolution at the same time. However, the royal road to high spatial resolution is through interferometry. Surveys with radio interferometers in the twentieth century showed the existence of masers in space, and bulk relativistic outflow. In the twenty first century we will be doing microwave interferometry on the ground (ALMA) and IR interferometry in space (DARWIN/TPF), hoping to directly detect Earth-like planets around nearby stars. So there is excitement for at least some time to come; however, as with photon flux, we are hitting an economic brick wall. Significantly bigger and better experiments will be a very long time coming.
Time. The observation of temporal changes has repeatedly brought about revolutionary changes in astronomy. Classic example number one is Tycho’s supernova, which cracked open the crystal spheres. Classic example number two is the measurement of stellar parallax, which showed how unspeakably vast the Universe is. The last two decades has seen a renaissance in this area, with an impressive number of important discoveries from relatively cheap monitoring experiments – the discovery of extrasolar planets from velocity wobbles and transits; the discovery of the accelerating universe and dark energy from supernova campaigns; the location of substellar objects from survey proper motions; the existence of Trans-Neptunian Objects, and Near Earth Objects (killer rocks in space !); the final pinning down of gamma-ray burst counterparts; and the limits on dark matter candidates from micro-lensing events. The next decade or two will see more ambitious photometric monitoring experiments, such as PanSTARRS and LSST, and a series of astrometric missions, culminating in GAIA, which will see external galaxies rotating. Overall, the “time window” is well and truly opened up. However, the temporal frequency axis is far from fully explored. My instinct is that this technique will continue to produce surprises for some time.
Non-light channels : particles. The origin of Cosmic Rays was one of the key puzzles of the twentieth century, and still can’t be considered solved. But you can’t really do surveys – indeed the central mystery has alway been where cosmic rays come from. Today, the underground experiments trying to directly detect Dark Matter particles are confronting what is arguably the most important problem in physics, let alone astrophysics. But again no survey is plausible. The big hope is neutrino astrophysics. Neutrinos should emerge from deep in the most fascinating places that we could otherwise never see – supernova cores, the centres of stars, the interior of quasar accretion discs. Measurement of solar neutrinos has solved a long standing problem, and set a challenge for particle physics – but what about the rest of the Universe ? New experiments such as ANTARES (under the sea) and AMANDA (under the ice) seem to be clearly detecting cosmic neutrinos, but no distinct sources have yet emerged. Possibly the next generation (ICECUBE and KM3NET) will get there. This looks like the best bet for genuinely unexpected discoveries in the twenty first century.
Non-light channels : gravitational waves. Like neutrinos, we know that gravitational waves have to be there somewhere, and their existence has been indirectly proved by the famous binary pulsar timing experiment. However after many years of exquisite technical development, we still have no direct detection of a gravitational wave. The space interferometer mission LISA should finally detect gravitational waves, unless current predictions are badly wrong. However even LISA will not produce a genuine survey. We will detect many events and understand more astrophysics, but will have essentially no idea where they came from, except that hopefully some will correlate with Gamma-ray bursts. If we see totally unexpected signals, it will be very hard to know what to do next.
Hyper-space planes : the Virtual Observatory. As we explore the various possible axes one by one, many if not most of them are running out of steam, or are too expensive to pursue. But we are a long way short of exploring the whole space – for example narrow line imaging in all Stokes parameters versus time. This exploration does not necessarily need complex new experiments. More survey-quality datasets come on line every year. As formats, access and query protocols, and analysis tool interaction protocols all get standardised, the virtual universe becomes easier for the e-astronomer to explore, and unexpected results will emerge. This, of course, is the agenda of the worldwide Virtual Observatory initiative.
So there we have it. The fify-something Prof’s recommendation for the eager young survey astronomer : time, neutrinos, and the internet.