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Anthony Readhead

I strongly favor Option #2.
_______________________________________________________________

Lyman Page

I'm for 2 with the exception of the second paragraph.  I'd say the
only trigger it needs is a competitive funding opportunity with other
science missions in the mix. If it competes well then good, if not
then it won't get funded. I think the only precondition is that it
needs to work technically and must have a high probability of
success. This means we need a robust program of ground and balloon
experiments now. I'd follow the Weiss report on this one.
_______________________________________________________________

Hiranya Peiris

I believe that the middle plan, proposing a space mission within five
years, is the best. From working on the Fisher and Foreground working
groups I formed the impression that our modelling of foregrounds are
educated guesses at best. Foreground removal is the most important
consideration is the detectability of the signal (assuming the
sensitivities can be technologically achieved). The capabilities of
the strawman missions in the white paper depend dramatically on the
foreground model and foreground removal. It would be much easier to
optimize the experiment for their removal when there is data in hand
from high frequencies over the full sky from Planck.

A careful outlining of the triggers for the proposal should be
emphasized, as you suggest. Possible options are: announcement of
opportunity by NASA, a hint of a signal in ground-based experiments or
Planck, and theoretical advances, given the rapid progress e.g. in
string theory. But in the absence of explicit triggers, it should be
proposed as soon as the technology is sufficiently mature and the
requisite improvement in understanding the foregrounds from
ground-based experiments or Planck is in hand to allow the optimal
design for a mission.

I was a bit concerned that this document seems to focus on a B-mode
mission. There are some other novel ideas out there, for example to go
after non-Gaussianity. I think it pays to mention that there are other
interesting signatures which will benefit from a space mission of a
very different design which would have a complementary set of
auxiliary science.  _______________ SM responds

Thanks for the comments. In particular I'm interested in what you say
about other signatures. There is Gary Melnik's approach with H-alpha
to go after the spectrum at k above that which CMB can get to. I
believe he is also after a high-z baryon acoustic oscillations. I
believe you are talking about still using the CMB no? For a good run
at non-Gaussianity, my understanding is that we need a small beam
(never mind a good understanding of the experimental noise) and good
sensitivity. That is not necessarily in conflict with the B-modes, I
think. The sensitivity of the tests of non-Gaussianity are most likely
to be compromised by the angular resolution if we go with the
intermediate or low cost options. Do I have this right?

Beyond that do you have other signatures that we could go after with
other designs in mind?  

_________________ 

Peiris responds

There are two separate things: what are potentially exciting tests of
inflation, and what subset of those are best suited for CMB
missions. I think B-modes are the most definitive test of inflation,
but complementary tests of early universe physics (non-Gaussianity and
shape of scalar spectrum in particular) are very important. When I
mentioned non-Gaussianity I was mainly thinking of CIP (the H-alpha
mission), but of course (with the requirement of the small beam and
noise/systematics control) this can also of course be done with the
CMB. Tests of the inflationary consistency condition need a CMB tensor
detection combined with a gravitational wave interferometer, which
will presumably be sold on non-inflationary physics too.

In my email I conflated "tests of inflationary/early universe physics"
with "CMB research", and while the inflation (theory) white paper
makes the broader case for observational tests of early universe
physics very well, these alternative tests should of course not be
discussed in the CMB research mission statement. I had my "early
universe" hat on, not my "CMB" hat.
_______________________________________________________________

Shamit Kachru

Of the three strategies presented in your note, I favor approach 2. I
think going directly against a previous recommendation, and doing so
when near term data seems likely to shed considerable light on related
scientific questions, seems a bit too radical for me (hence my
favoring option 2 over option 1). On the other hand, it seems quite
plausible that if $r$ is in the interesting range (say $> .01$),
ground or balloon based experiments will give hints of its detection
in the next few years. I believe this (your option b) under approach
2) would make the case for a space-based mission compelling.

So I favor option 2, while believing it is important to stress that
support for related research should begin to ramp up now (if nothing
else, this will help promote the ground and balloon based experiments
that will really make option b) under approach 2) a realistic thing).

Of course I am a rather formal theorist by the standards of the CMB
community (or probably any community at all!), so my reactions may be
atypical; but I sent this in case they are of any use to you.
_______________ 

SM responds

Thanks very much for your reaction. In fact, your thinking is very
parallel to mine and seems to also be similar to that of others.

One of the main things I keep hearing is that we will learn SO much
about the dust foregrounds from Planck and what your model for these
contaminations is changes what you need to have in terms of the
frequency bands and sensitivity that it makes a great deal of sense to
wait a couple of years.

One trigger for the initiation of the space mission that could be a
new theoretical understanding that changes the current thinking about
a non-detection at the r=0.01 level. If we were to discuss that in our
report, we would like to have some example lines of thinking that
could lead to such a development. How would you frame such a thing?

I am also interested in your thought about the issue of a sub-orbital
detection as a trigger. Some believe that such a detection would
short-circuit the need for a satellite. Quite the contrary, as you
say, I think a low signal to noise detection would be the strongest
reason to pursue the question with all possible energy.
_______________ 

Kachru responds

I completely agree that a sub-orbital detection would make a
compelling case to do the final, and very clean and decisive,
measurement from space. It would therefore seem to me to serve as a
trigger for the CMBPol mission, and not as a competitor. I understand
there is a reasonable history in CMB experiments of e.g. balloon-based
experiments getting a first hint of interesting data, but also of
having (presumably systematic) errors that cause hints of new physics
where none is present. So I would view the much cleaner space-based
experiment as the one that would be really decisive.

Regarding theoretical progress on the issue of how likely $r \sim .01$
is, or how fundamental a detection at that level would be:

One can already say with confidence that a detection at that level
would indicate that the inflaton was very sensitive to Planck-scale
physics, and was probably a Nambu-Goldstone boson or axion. This is
because the Lyth bound quite simply shows that it had to traverse a
super-Planckian distance in its field space, to generate such large
$r$.

However, I am personally also of the belief that a slightly smaller
value (say $r \sim 10^{-3}$) is not implausible; I do not believe that
there is really a gap in theory space between models with $r > .01$
and models with much much smaller values (well below the realm of any
near future detection).

A theoretical argument about the fine-tuning of initial conditions
required for large field vs small field inflation might allow one to
conclude that large field models are favored. However, such arguments
to date have been far from convincing. So I would not hold out much
hope of theorists giving a very good and convincing reason that
inflation implies measurable $r$; but I would say that theorists have
given good reasons that measurable $r$ is not implausible, and would
give a direct hint about physics at very high energy scales.
_______________________________________________________________

Bruce Winstein

I like the 2nd statement/plan the best.

I would think it should be strengthened by emphasizing that a space
mission is definitely required, following what is on the platter now.

We could say that while on the ground one might be able to get near
r=0.02 or so, this is only for the last-scattering signal; and that it
is crucial, for something as important as verifying/studying
inflationary scenarios at the highest energy scales, to also see the
effect for the reionized signal, and that this is only possible from
space.

This is just wording but I would start the statement with strong words
about the crucial importance of a space mission. Then follow with what
will inform the mission; what is going on now.

As far as triggering a proposal, I might suggest saying that we need
further information about galactic foregrounds and that once we know
how well we can deal with these in Planck/ground based experiments, we
could very well have an initial detection and we will be able to
better forecast how deep we can go in a space mission.  Only that
knowledge is what is needed to trigger a proposal.
_______________________________________________________________

Clem Pryke

I vote for option 2 and strongly against option 1.

I think we should make the case that the science is extremely
important and exciting and that the current round of ground and
balloon experiments should be strongly supported, together with the
technology development efforts.

The case for a space mission should be re-visited within five
years. However we should make it clear that if there are hints of
B-mode detection sooner than that the case for a full blown space
mission would immediately become very strong.
_______________________________________________________________

Licia Verde

I think I would be more inclined for plan # 2.

is there any "trigger" on the detector/instrumentation side that could be used?

another possible trigger is that since foregrounds are the main issue,
we need to see Planck data and digest them to know better what we are
to be dealing with, and adjust the instrumental set up.

Also, it may well be my ignorance, but I think "we" might want to try
a bit harder from the ground before going straight for space. Even if
ground ends up only putting upper limits... It would be great if in
the next 5 years it could be shown that ground has done as well as it
could, and that the next improvement must come from space. (but again
this is a "theorist" view...)
_______________________________________________________________

Richard Easther

I am very much in favor of option 2. As is well known, the next few
years will either see a detection of primordial tensors, or the upper
limit on r will be substantially reduced. Moreover, Planck and
forthcoming balloon /ground based experiments will yield a much better
understanding of polarized foregrounds along with better estimates of
our ability to subtract them. I think it makes sense to have this
information in hand before committing to a particular design (which is
implied by my understanding of (1)) for a large CMB mission.

In the interim we should push ahead with technology development, and
non-orbital CMB experiments.

For me, the key "decision point" is whether there are any hints of a
nontrivial value of r emerging in the next five years -- if this
happens, the case for a satellite that can provide a high quality
measurement of this signal (and in particular, a mission that was able
to put tight constraints on its spectral index) is enormously strong.

On the other hand, if we knew that r<0.01 (say) with good confidence,
the case for a CMB satellite (or at least the case that you would make
on the basis of inflationary physics) seems weaker, in the absence of
major theoretical developments.  Looking at the white paper numbers,
it would seem to be very hard to measure r significantly below 10-3
(at least without subtracting the E->B lensing signal). From, the
current theoretical perspective, the difference between r< 10-2 and
r<5 10-4 is less dramatic -- whereas it will have a big impact on
inflationary theory if we move from the current bound of r<0.2 to
r<0.01.

Likewise a detection of non-trivial primordial non-Gaussianity would
obviously have a huge impact on any future CMB mission design, and
constraints on f_NL are very likely to tighten in the next few years.

On a more general note, there is potentially a "sociological" fault
line that will become important at around r~10-2. (At least if we
don't feel confident about our ability remove the E->B lensing signal
-- although this would simply lower the critical number, not remove it
entirely.)

At this point, I think that much of the case for a CMB satellite would
need to be driven by what the CMB community would now describe as
"ancillary" science; whereas the inflation / very early universe
community might be more tempted to look at experiments which
(especially when taken together with Planck) will put tight bounds on
alpha (dn_s/dlnk), or provide sensitive probes of primordial
non-Gaussianity.

Up until now, there has been an obvious "coalition" between the early
universe / inflation community and CMB experiment, but there is a
point (and r~0.01 is as a good a guess as any, based on current
knowledge) where this would begin to unravel.

From a much longer term perspective, I think determining r<0.01 would
bring about a similar "reconceptualization" of BBO (ie a "LISA 2"),
which would see it change from being primarily about its ability to
measure primordial tensors to doing gravitational wave astronomy, with
any improvement on stochastic backgrounds (which, in the BBO range,
can come from phase transitions as well as the primordial inflationary
signal) being seen as a secondary objective.  However, this is
definitely academic, since BBO cannot be a concern for the coming
Decadal, even if LISA has to be squarely on their agenda -- whereas an
upper limit on r around 0.01 is imaginable within the next decade.
_________________ 

SM responds

I personally am in agreement with you on the best plan. A hint of detection of b-modes will make the case strong.

I had not thought about the potential divergence between inflation and
broader cosmology community at r<0.01. Somewhat to my surprise, the
ancillary science (and I mean everything except inflationary b-mode
polarization here) case continues to look pretty weak. If you were
after the scalar spectrum or non-gaussianity, CMB is probably not the
way to go. From an experimental perspective either of these would push
you to higher angular resolution and probably end up driving the
entire scale of the mission. The galactic polarization stuff I've seen
so far does not justify this kind of mission in my view.

The one exception may be the lensing b-modes. This is a signal we will
see. At the moment there is not much interest in CMB lensing maps in
the community but I wonder if that is not an oversight. As we get an
increasing number of large surveys at all kinds of wavelengths, I
cannot imagine that a good, all-sky CMB lensing tomography map would
not be the standard thing to cross-correlate with anything new. I
don't know the sensitivity of the CMB lensing as a function of
spacecraft capabilities off-hand but that is worked out.
_______________________________________________________________

John Ruhl

I'm in favor of the 2(a) route.

I can't imagine a compelling theoretical development that would drive
2(b). That is, I can imagine theoretical developments that would try
to say something, but it's a very long shot that anything new will be
compelling to a wide audience.  I worry that the "initial detection"
route of 2(b), if we are not already rolling on a satellite, will lead
to debates over whether ground based efforts can gain a couple factors
of 2 in sensitivity (or frequency coverage, or whatever) in a shorter
timeframe and thereby "nail" it sufficiently that the one number we
can get out of this is gotten well enough that a satellite doesn't
make sense.

eg, if r >= 0.1, I suspect we'll never fly a satellite. Do you think that's wrong?

I can imagine changing the "5 years" to "5 to 10 years", but definitely keeping it in this decade.

Route 3 sounds way too slow given how close I believe we are to being
able to do the measurement. I also think it's a recipe for only
continuing the suborbital program at the current level, which will
make detector fab a long-term hassle to support. Not to mention
ramping up any "mission development" stuff.
_______________________________________________________________

Mark Wyman

Option 2 most closely expresses my feeling on the matter -- the
progress from ground-based experiments is the big thing I will be
watching to decide if / when the satellite is justified.
_______________________________________________________________

Meir Shimon

I read the proposed plan summary and my personal inclination is to go
with option (1); the only comment/question I have it why is lensing
not mentioned while the lensing-induced B-mode signal is guaranteed
whereas the inflationary B-mode isn't. I'm not sure, is it because the
definition of the CMBPOL concept is inflationary science ? if not, I
think CMB lensing is de-weighted in the current wording. As to the
other two options (2) and (3), from my perhaps limited view, I don't
think waiting few years will change that much on the theory front (I'm
not sure about technology though, but even if it would, the
theoretical uncertainties as to inflationary signal remain).
_______________________________________________________________

Mark Jackson

Thanks for your notes - I have looked them over and I definitely think
plan (2) best describes the situation. It doesn't seem like there is a
definite-enough plan to propose anything immediately, especially with
Planck just around the corner, but I think within 5 years there should
be more consensus. There is absolutely no doubt that such a mission
would be useful in constraining particular models and/or classes of
inflationary theories. As for what will trigger this - I suspect that
Planck will either see B-modes, or at least hints of B-modes (the data
will take a while to analyze, and could be ambiguous especially at
first) and this will cause people to ask for an experiment
specifically designed for such a thing.
_______________________________________________________________

Dean Johnson

As far as the mechanical cryocoolers are concerned I feel they are
ready for an immediate space mission now (Plan 1), and certainly
within 5 years (Plan 2).  While there is no current 4K cooler
development ongoing for space missions, there is at least one of
instrument concept study and one instrument incubator development
program that will require 4K mechanical coolers.  The JWST MIRI
instrument 6K cooler development is ongoing, and it directly
translates into a 4K cooler if either He3 is used in the JT circuit,
or if a second stage of compression is used in the JT compressor to
produce liquid He4.  

_______________ 

SM responds

Thanks for your comments. The more I have looked into this the more I
have come to realize that the enabling technology for a CMBpol mission
is the cryocoolers. (I used to think it was the detectors and
readout). The coolers and their proven capabilities are likely to
become the technological 'trigger' for this mission and a hint of a
detection from sub-orbital (or Planck) will be the science trigger.
_______________________________________________________________

Raphael Flauger

While I am very excited about the prospect of a satellite mission like
CMBpol, to me the second option was the most honest and thought
through option as I think there will no doubt be valuable information
gained from ground and balloon based experiments as well as, of
course, from Planck.

The third option would be a huge disappointment to me and even without
understanding the inner workings it seems clear that it would rule out
a satellite mission in the near future, and even worse than that I
think it would have rather adverse for the CMB community as a whole.
_______________________________________________________________

Eugene Lim

I think choices (1) is premature and (3) looks overly
pessimistic. Choice 2 is the most realistic, so I fully support this
line of approach.
_______________________________________________________________

Matt Dobbs (for the Canadian Community)

Thanks for keeping us informed about plans for the message to the US Decadal Survey Committee.

In Canada, our CMB polarization working group has discussed
this. Option 2: "The CMBpol community will propose a space mission
within about five years", agrees best with our perspective in Canada.

A reasonable trigger would be a demonstration from the current cohort
of high altitude and suborbital missions of the feasibility of
measuring the cosmological B-mode signal from space. This includes
1. the understanding of foregrounds that will be afforded by Planck
and the high altitude and suborbital missions, informing observation
strategy and band-choice decisions, and 2. the technology
demonstrations that will come from the current missions.  or
3. initial detection of the B-mode polarization.

In the interim period, it is essential that NASA (and CSA in Canada)
support the technology development for CMBpol, push forward with the
suborbital and high altitude missions, and support the
analysis/science return from all of these projects.

Matt Dobbs, Dick Bond, Mark Halpern, Gil Holder, Barth Netterfield, Dmitri Pogosyan, Douglas Scott
(Members of the Canadian Space Agency's CMB-pol Discipline Working Group)
_______________________________________________________________

From Douglas Scott directly

As I see it there are 2 basic problems with spending a huge pile of
money on a CMB polarization satellite (and I'm sure I'm only pointing
out the obvious here): (1) there's no clear prediction for how
sensitive you need to be for the primordial B-modes (2) the collateral
science isn't obviously very exciting

You can partly address (1) by noting that right now there's a
straw-man model, which predicts you need a sensitivity of r~few
percent in order to be able to get to limits of r<0.1.  Beyond that
it's very unclear where to draw the line, except purely from the point
of view of going as low as is feasible.  Things may change of course,
particulaly if we get a much tighter measurement of n. So you could
add to the text something like "or a change to the theoretical
landscape which suggests a new target for sensitivity".

Point (2) is sometimes mitigated by discussing the lensing B-modes,
and also what can be done with the foreground polarization.  But
neither of those things are worth more than a miniscule fraction of
the required budget.  
_______________ 

SM Response

Thanks for your comments. Your points are very close to my thoughts.

One thing I keep thinking is that lensing will become more interesting
than it perhaps seems now when we begin to cross correlate with a
growing number of surveys at all kinds of wavelengths. Do you agree
with this? I keep thinking that a good CMB lensing tomography map will
be something that any data set in the future would be checked against.

Speculation more about the unknowable future, do you imagine the
theoretical picture of inflation observables to change much in the
next 5 years? Suppose sub-orbital expts do (or don't) see a hint of
something at r=0.03. This will engage the theory machinery much like
the non-detection of anisotropy did in the early '80s (-> CDM) and the
COBE detection did in the late '80s (tension between LSS and CMB ->
HDM or Lambda). Is the current situation different enough that we
should not expect that kind of evolution?

In any event, it is hard to sell this project on the rather small
interest in lensing now and speculation about where theory might go. I
think a hint of detection will simply make it imperative to go
further.  

_______________ 

Scott Response

I agree that correlations with the lensing will be interesting (in
fact cross-correlations will generally become a big industry I think)
- but won't the lensing come from the temperature maps directly,
rather than from the B-modes?

As for the theoretical motivation for a target: right now we have a
clear straw-man, which is potentially in reach for Planck and maybe
some of the other experiments.  If there's a hint that m^2phi2 is
right, then things will change utterly (in fact I think people will be
excited for about 5 minutes and then realise that all we've shown is
that the expansion around the minimum of a potential is a quadratic
function!).  But if we can rule out this simple model, then it's very
unlcear what the target should be for T/S.  This depends on what
happens with a tighter measurement of n of course (and running maybe).
If n creeps closer to unity, for example, then I think there's less of
a clear target for T/S.  But it's also the case that the theoretical
view could change for any number of other reasons.  So I think we
really are in a "wait and see" mode for a few years - but of course we
should be ready to quickly react if/when it becomes clear that the
time for a new satellite has come.

____________________________________________________________

Mark Birkinshaw

Dear Stephan

I have taken a look at the statement about the three possible plans
for CMBpol.

I think that option 3 is not the way to go. The technology available
now is capable of a CMBpol project, and some slight improvement in
robustness (a major issue) will occur during mission development, so
the technology readiness is already good. It's always possible to
squeeze more improvements out of device physics, but that's not a good
argument for not doing what's possible when it becomes possible.

B-mode detection will, in my view, require more attention to foregrounds
than is possible with the information we have available today, but it is
surely possible to optimize the system given what we know from WMAP and to
tweak the design when we get information from Planck. Much of the mission
design at that stage will probably involve scanning strategy, provided
that the optical design hasn't revealed significant polarization issues
from sidelobes/reflections/... and scanning strategy can probably be set
quite late provided that spacecraft control is sufficiently flexible.

I believe that it cannot be wrong to advance the possibility of a rapid
start to the Decadal Committee at this stage. If they comment that it
could do with further development, then so be it. On the other hand, if
they say that it's based on sound technology and good science, then it
can at least be shown to be important and by having a well-founded plan
out there it may be possible to push the agenda a bit.

So I'd go with plan 1, even though it means some swift thinking and
writing.

   All best wishes

   Mark 

_______________________________

Charles Lawrence


Hi Steve,

I strongly favor option 2.  Regarding triggers, it is clear from the
other responses to your query that it is not clear what a valid or
useful trigger might be, with one exception, namely, tentative
detection of primordial B-modes from Planck or a suborbital
experiment.  Therefore, instead of discussing triggers, I would
emphasize the point that detection of primordial B-modes from Planck
or a suborbital experiment would be an important result but could be a
result of systematic errors.  However, measurement of a B-mode
spectrum over 2 <= l <= 200, which can be done only from space, would
provide unambiguous and incontestable evidence of primordial B-modes
and the gravitational waves that produced them.

Regards,

Charles