Hi Justin,
      I have a couple of comments on this.  First, I think it misunderstands the role of the European Strategy Process.  The strategy doesn't assign 10's of millions to anyone - that would bypass the elaborate and well-tested CERN process for approving projects.  You might want to look at the old one at: http://council-strategygroup.web.cern.ch/council-strategygroup/Strategy_Statement.pdf ,which will give you a feel for the level of the statements made. The Strategy Process will set the direction for CERN over the next five years (which, of course, will also strongly influence what options will be available for the longer term).  So possible statements about neutrino physics might, if we are extraordinarily convincing, be something like "Given the importance and timeliness of physics discoveries in the neutrino sector, CERN should prepare to host a long-baseline neutrino oscillation experiment", or, if we are less convincing, perhaps "CERN should play an active role in the international neutrino programme including contributing to long-baseline experiments as part of a global programme", or some such.  We could get an additional statement like "CERN should assign appropriate resources to R&D in support of building new neutrino detectors".  It would be useful for people to think about what kind of statements along those lines would be most helpful - telling CERN to spend $10M on a particular experiment will go nowhere as part of the strategy.  
    My other comment is about the 60 reactor experiment and PINGU.  As part of an SPC presentation I have reviewed all the experiments that have claimed to have sensitivity to MH, and it would appear to me that none of the experiments has >3 sigma sensitivity for all delta.  The two you mentioned do not seem to me to be amongst the more promising.  The reactor experiment assumes 3% energy resolution for a 20 kT liquid scintillator detector.  Does anybody have any idea how that could actually be done?  Have you ever heard of an organic scintillator with 3% energy resolution, even at the kilogram scale?  At 20 kT? I have spoken to the most senior people in the collaboration and the story is that they will need at least 6 years R&D before they would even be ready to submit a proposal.  As for PINGU, the analysis presented so far is a joke.  I would be happy to discuss the analysis in detail, but perhaps not in an email because of length, but my guess is that the bottom end of the claimed sensitivity scale (3 sigma) is extremely optimistic.  The collaboration is pursuing a full analysis and hopefully we will get a result on the time scale of a year, in the meantime, I simply do not take this seriously (and neither do some of the senior people in Icecube, who have a better appreciation of the systematics).  To me the only serious contender for determining the MH on a short time scale would be T2K/NOvA getting lucky.  In the longer term an atmospheric neutrino measurement in a real detector (HyperKamiokande, probably, maybe INO) if the value of theta23 turns out to be favourable (although basically this is the same as the PINGU measurement, and thus open to the same concerns, but with a better detector and some hope of quantifying the systematics).

Cheers,
 Dave


Hi,


The aim here is to develop a European strategy for the next five to ten years. Having a long baseline project such as the Pyhasalmi proposal as an end goal is a great idea, but Europe also has to be involved in projects that will do physics on an intermediate timescale.


It seems that either PINGU or the Daya Bay 60 km project are likely to be the next new projects producing results, and one of those is likely to achieve the discovery of the mass hierarchy. Europe should aim to be a part of that discovery, so should get heavily involved in one (if not both) of those projects. I don't think it's true that Europe has no way of influencing these projects. As an example, PINGU will need to find £20 million or so for the new holes; if Europe went in and provided a significant chunk of that money, it could be the catalyst that makes that project happen, and European physicists could take credit as being leaders of the project. Similarly, the Daya Bay 60 km project would be given huge momentum if Europe went in with a chunk of money and a commitment to some of the R&D towards a 10-20 kt liquid scintillator detector. 


Likewise, as we aim towards a massive liquid argon detector, the need for a staged programme needs to be highlighted with significant effort put into projects such as a liquid argon test beam project and intermediate physics projects such as GLADE.


So I would personally structure the document to make three concrete requests:


1) Europe should commit ten million pounds or so to joining PINGU and/or Daya Bay 60 km, with the aim of discovering the mass hierarchy in the next five or so years.
2) Europe should commit ten million pounds or so to a staged programme aiming towards a massive liquid argon detector. This could include projects such as a liquid argon test beam project, GLADE, and hadroproduction or cross section measurements.
3) Europe commits a significant chunk of money towards the next major long baseline project such as CERN to Pyhasalmi.


I'm not wedded to any particular combination of specific projects, and there may be good projects I've not mentioned. I'm just advocating that our strategy for the next five to ten years needs to be broader than just aiming for the CERN to Pyhasalmi project, and needs to have physics returns within the next 10 years.


Justin.