• Update on decadal panel
• Preparations for a future possible midex (Al Kogut)
• Strategy for Decadal Panel

Chuck Bennet explains the steps leading to the decadal panel:

• The Space Studies Board (SSB) and the Board on Physics and Astronomy (BPA) guided the process that produced the internal proposal to initiate a decadal survey. (I was involved with this.) This effort included recommending the timing, size and scope of the survey.
• The end result was the NRC proposal to NSF, NASA, and DOE.
• The agencies then weigh in on whether the scope and broad outlines of the Decadal Survey is acceptable to them. There is a lot of back and forth at this stage. Questions and answers, proposed modifications, etc. In the end, everyone (NASA, NSF, DOE, and the NRC) needs to agree on the broad outline, scope, and process before any funds flow. That has not happened yet.
• The National Research Council (NRC) will internally nominate people to serve on the Decadal Panel. The nominations need to be approved internally at the highest levels of the National Academy. (The decadal panel is not selected by any of its boards) There are strict requirements on a number of balance and conflict-of-interest issues. Balance means a lot of things (geographic, small-vs-big institutions, male/female, scientific sub-field, etc.). No one closely associated with a project to be reviewed is likely to be selected.
• Once the NRC convinces itself that it has a reasonably conflict-free panel that “looks like America” people will be invited to serve. Some people will decline.

Two approaches that bracket the range of possibilities.

(a) While B-mode science is compelling, no case can be made for a satellite any time soon.

(b) A strong case for a satellite can and should be made to the decadal panel even as of today because the science return, even with a null detection, is compelling. Not only a satellite is justified, it is critical to the health of our field.

B-mode science is compelling, and must be pursued by a program of technology development, suborbital experiments, and a space mission (whose ultimate need and configuration will depend critically on the outcome of the suborbital experiments).

As to your question if we should bring to the decadal panel a) a satellite to detect B-modes or b) a plan for a satellite once B-modes are detected from the ground, I have an alternative. What if we instead bring forth the comprehensive science satellite to study all aspects of the CMB in temperature and polarization, and then say if the B-modes are detected from the ground at a high level we can come back with a cheaper small satellite option. This strategy gets all of our science on the table, puts the issue of B-mode amplitude in the most favorable light, and keeps CMB in a favorable position programmatically at NASA.

• A satellite is justified when the science can not be done from sub-orbital platforms.
• CMB Polarization has been measured by sub-orbital experiments. There is no reason to assume that B-modes can not be measured by such experiments as well.
• At the moment there is no compelling argument to go to space.
• A compelling case for space may present itself when we know more about sub-orbital measurements, but this is not the case now.

I expect it will take at least one telecon to come to some consensus on the issue of whether a CMBPOL satellite is justified. I also expect that this will turn on issues of politics and semantics, not technical capabilities. I don't think anyone argues against the notion that anything a ground-based or suborbital experiment can do, a satellite can do better, so the question of whether a satellite is necessary or not will depend on what the defined mission for that satellite is. If the primary mission is a statistical detection of non-zero B-mode power, consistent with inflation and inconsistent with lensing or foregrounds (in analogy to the initial COBE-DMR detection of CMB anisotropy) then a satellite is hard to justify. If the mission is something beyond a statistical detection (e.g. measuring the primordial B-mode power spectrum in some detail, in analogy to WMAP or Planck and the unpolarized anisotropy) then the requirements of very long integration times and substantially lower systematic error limits make a satellite much more attractive.

There are two sticking points. The first is that a primary mission to map the B-mode power spectrum may not be a high priority once the initial statistical detection has been verified (at least that's one take from the series of theory telecons). The second is that “more attractive” is not the same as “absolutely required”. A telecon might help sharpen our arguments to go beyond the simple “satellites are better” reasoning to give specific examples of what we expect the limiting factors to be from ground-based or suborbital missions and why a satellite would avoid these limits.

Playing Devil's advocate, we might look at the progress measuring the unpolarized CMB anisotropy to see what limits we would have today if we ignore all COBE and WMAP data points. If the goal had simply been detection, then clearly COBE was not necessary: we simply could have waited ten years for the ground-based and suborbital missions to improve. Extrapolating to B-mode polarization, what limits might we expect to obtain given 15 years of successively more capable ground-based and sub-orbital experiments? Of course, this ignores the positive feedback that major mission like COBE, WMAP, and Planck have on the field, and this may well be the best reason to push for a satellite.

I believe that “waiting to see what we find from Planck, the ground, and balloon missions” before moving ahead is the wrong approach to the future of our field. Here is why:

1)I think the science from a CMBPOL mission is as least as interesting as that from any other satellite mission with the exception of LISA.

2)If we do not plan for it it will not happen. A CMB satellite is a long way off no matter what we do. Unless we make real plans for it now, we'll all be retired (if not worse), before we see the results.

3)You need a satellite for a full sky census with a comprehensive set of null tests. Though there were many great experiments before WMAP, there are at least a couple of orders of magnitude difference in the control of systematic error with WMAP, not to mention the large improvement in statistical error, full sky coverage, etc.

4)There is a lot of ancillary science. We should take seriously measuring the neutrino mass with a satellite mission. Looking for isocurature modes, cosmic strings, topological defects, and other non-Gaussianities, are all important. We have no a priori reason for excluding these possibilities. Finding any one of them is as likely as finding w ne -1 (though of course we support a comprehensive science plan!). I think Planck will be at least as exciting for what it will tell us about these new things as for what it will tell us about the current suite of parameters. This is all great physics from the highest energy accelerator we'll ever have a chance to access, the early universe.

5)Though we should look to theory for guidance, we should not plan a mission around it. What's in vogue in theory changes every couple of years. We need a longer time scale perspective. For me the view is that the CMB sky is our best hope for finding new “fundamental” physics. It hasn't let us down yet. Let's look at it with all we've got.

6) By seriously planning we will keep NASA, NSF, NIST, and with luck the DOE, engaged. The quest to understand the CMB has led to fantastic technological development especially on the detector front. It will take years for these developments to percolate but they will.

7)There are a lot of misconceptions about the feasibility of the mission. We can change that.