2010 July 12
(First deadline: blown. I ended up taking on a few more topics in this post than I originally envisioned.)
For my thesis, I’m observing the dynamic radio sky. The centerpiece project is a search for radio transients towards the Galactic Center, the ATA Galatic Center Transient Survey (AGCTS). A second major component is monitoring of Cygnus X-3. As we find interesting things in the both of these datasets, we’ll pursue them in focused, smaller-bore scientific projects.
This post is about whether these are interesting projects to pursue. To be honest, the two pieces are pretty independent of each other, so I’ll treat them independently.
Is a search for galactic radio transients scientifically compelling? The abstract argument is that systematic surveys of the variability of the radio sky (as opposed to its constant component) are very new, and every time a new way of probing the sky has been developed, significant discoveries have been made.
It’s important to pinpoint what’s new: surveys of the radio sky for variability, rather than monitoring of particular radio sources for variability. Due to the technological limitations of radio astronomy, the former are just becoming feasible, but the latter has been around for a while, often in much more sophisticated form than it has for other wavebands. (E.g., pulsars.) As best I can see, we should think about this distinction being about a vastly increased ability to discover, rather than monitor, radio-variable sources. So, would it be exciting to find more of these sources? Here are some of the kinds of objects that we might find, with the galactic ones italicized:
- RRATs (if worth distinguishing from pulsars)
- Flare stars
- Brown dwarfs
- Non-variable sources subject to interstellar scintillation (could be either galactic or XG, but likelier to be XG since depends on chance alignments and there are more XG radio sources by areal density — I think this line of argument is valid)
- ESEs (distinct from above?)
- Masers (also XG; not relevant here since we’re working in the continuum)
- Objects of unknown nature that have been discovered in radio transient/variable surveys or serendipitously (there are suggestions that at least some of these are galactic: Becker+ 2010, though they don’t consider scintillation; the Burper; Galactic Center transients; etc.)
I think that list speaks for itself. Now, even if there are many interesting radio-variable sources, it’s not necessarily worthwhile to hunt for them by surveys of radio variability, especially if we consider source classes in isolation. Assessing this worthwhileness blocks on my looking into feasibility — though, of course, a radio variability survey is the only path to discovering radio variables of an unknown nature.
Another aspect “interestingness” is whether the AGCTS is novel and competitive with other ongoing efforts. We certainly hope that the answer is yes: the ATA is supposed to be a unique instrument for performing surveys of this kind. The more detailed answer depends upon consideration of the competition:
- Hyman+ VLA/GMRT GC 330 MHz: 2002, 2003, 2005 (Burper), 2009
- Becker+ GP VLA archival: 2010
- Langston+ NRAO Galactic Plane A survey: 2000, website
- Bower+ VLA archival: 2007
- Carilli, Ivison, Frail Lockman Hole search: 2003
- Levison+ FIRST/NVSS comparison: 2002, 2006
- Frail+ GRBA search: 2003
- Kida+ drift scans: 2008, among others
- Gregory & Taylor drift scans: 1981, 1986
- McLaughlin+ Parkes multibeam piggyback: 2006, 2010a, 2010b
- Cordes Arecibo pulsar survey: 2006
The last two are concerned with fast transients, which is a pretty different region of parameter space than what I’m interested in. All of the others except for the first three are concerned with extragalactic sources, whereas I’m interested in the galactic population. The NRAO GPA survey never published any transient results. That leaves the Hyman and Becker works. I’m working on comparing the expected AGCTS results with these two projects — this gets a little hairy, and ties in with feasibility questions, so I’m OK with this aspect needing a bit more investigation.
Are microquasars interesting? Definitely — they should be able to teach us a lot about full- size quasars. (See eg Mirabel & Rodriguez 1998 for a short version of the case and Mirabel & Rodriguez 1999 for a review article that also goes into justifications.) Fundamentally, while many of the physics seem to be analogous, the timescales are much, much shorter and the spatial resolution is much, much better. And there’s definitely a lot that we still don’t understand about accretion disks and relativistic jets.
Is it interesting to monitor the radio variability of a microquasar? Well, empirically, yes, because people are doing it.
- Cyg X-3 is being monitored with the OVRO 40m by Fermi LAT Collaboration members (mentioned in FLC 2009, no direct ref I can find)
- Ditto for with AMI (e.g. Pooley 2006)
- And the RATAN-600 (mentioned in Tavani+ 2009, no direct ref)
How is our project different than these? The OVRO monitoring seems to generate one flux measurement every few days. The AMI monitoring has bursts where they get fluxes every ~hour but generally is at the same cadence. RATAN seems to have a 2-day cadence. We, on the other hand, are aiming to get fluxes on a 5-to-10-minute cadence. At least some of these measurements are simultaneous with X-ray and observations.
Will this different approach yield novel results? This also starts getting a bit tricky to address, and starts getting into the “feasibility” domain. Szostek and Zdziarski 2007 argue that there won’t be orbital modulation of Cyg X-3’s emission, but not because of scattering effects, so shorter-timescale variability would still be possible due to e.g. jet variability. Hjalmarsdotter+ 2004 says that periods between 0.01 and 1000 days were searched for in a Ryle telescope run around 2002 Dec 22-23 and that none were found, with no word on what the variability may have looked like. (Given the lower limit to their period search, they were probably sampling every 0.005 d ~= 8 min.) This is a little worrisome, but given the skimpiness of that reference and the others above, it looks like no one has really sat down and looked at the radio variability of Cyg X-3 on timescales of less than a day — for instance, there’s no word as to what the Cyg X-3 radio variability looked like just as a simple time series. We’ll also have simultaneous and near-simultaneous X-ray data, so I think there’s ample opportunity for us to find something interesting that others haven’t. Unfortunately, before the reduced data are in hand, it’s hard to predict what, if anything, we might find.
Another point in favor of the projects I’m proposing is that they have good potential for spinoffs. Firstly and most obviously, if we find anything interesting, we can follow it up and try to do some science with the particular results. Secondly, we’ll generate static sky maps as byproducts, and those should be interesting in their own right. We expect to have 200 MHz of bandwidth centered on 3.09 GHz, so there should be some leverage on spectral indices. We should also land in a nice medium-resolution point, with larger area covered than high-resolution surveys but much better resolution previous radio surveys covering a similar area. With the Cyg X-3 project, while the main goal is to get good Cyg X-3 lightcurves, we should be able to search for transients using the AGCTS pipeline pretty easily. The Cygnus region is very crowded so it’s a good place to look for galactic transients too.
Earlier: Public Talk, July 14
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