If we simplify a little bit, Sean says that science should be about new things that are not yet seen while Julianne argues that science should be about things that are likely to be true.
If we exaggerate a little bit, Julianne doesn't care whether things are new while Sean doesn't care whether they are true. ;-)
Who is right?
Well, I agree with Sean that new insights are more desirable than equally valid insights that are not new, and I agree with Julianne that true or likely scenarios are more valuable than equally exciting scenarios that are unlikely.
As Michael Turner has said, physics critically depends on the balance between hot philosophical ideas and speculations on one side and cold data from experiments on the other side. If this balance is broken, physics deteriorates either into philosophy or into zoology.
This is a wise comment that emphasizes that physics can't work without non-trivial hot ideas just like it can't work without tests of its statements. The right quantitative appraisal of some work is probably given by the expectation value of the excitement: you must essentially multiply the amount of excitement that the work creates by the probability that it will actually occur i.e. by the probability that the theory is true.
People working in different scientific fields have different strategies: they differently decide whether the excitement or the likelihood of validity is more important. Nevertheless, we still need some general criterion that can be used to compare results in different fields; the product is a very useful choice.
Astrology vs cosmophysics :-)
Julianne defends astrophysics while Sean defends cosmology. That shouldn't be too shocking. OK, which one is more valuable? Surely, this is a silly question. Astrophysics is closer to zoology in Turner's classification and it studies many particular dirty phenomena involving celestial bodies that are not overly mysterious and that can be compared with observations quite directly, via relatively cheap experiments and observations. Cosmology is closer to philosophy in Turner's classification and it studies aspects of clean, fundamental laws of the Universe whose validity is more universal but whose testability is often difficult and typically requires big scale experiments.
See also: Simon White and fundamentalist physicsAs far as these strategies go, theoretical high-energy physicists are clearly closer to the cosmologists. But I think that this focus on universal and hot results should always be constrained by reality. People should never forget about the factor of probability that the theory is correct.
Many physicists study the Standard Model or some well-known astrophysical processes whose essence is almost certainly well understood. Using our metaphors, they are the extreme zoologists.
Other physicists propose new models for physics at the TeV scale. There are so many possibilities that a randomly chosen model is nothing else than a guess. If you construct 100 very different models that you believe to be comparably likely, the average probability that one particular model among them is correct cannot exceed 1%. Is that enough? How much work, time, and money should be spent on models that are motivated purely by physics but that have a 99% probability to be wrong i.e. a 99% probability to be fully recycled or discarded in a few years?
Well, I would say that not too much. If these models don't bring any truly fascinating new theoretical ideas - something that would impress mathematically inclined observers - it might be better to simply wait for the experiments that will settle the question.
String theory as a framework has a very high expectation value of excitement because theoretical reasons imply that it is very likely to be correct while the amount of excitement and conceptual breakthroughs in it is extremely high. This good score applies to the general framework only, of course. Any particular work that looks into something more concrete than "all of string theory" is guaranteed to have a lower probability to be relevant for this Universe as well as a lower index of mathematical excitement.
I think that the value of ideas should still be judged wisely. Is it really so important to construct 50 more specific models of inflation? Are these models much more likely to be true than the simplest models of inflation that we can write down? Do we have any chance that the experiments will tell us? Or are these newer models much more mathematically solid or exciting? I think that in most cases, both answers are No.
As a conservative, I prefer the best and most natural or accurate model that has been found so far over the newest fad.
From this viewpoint, I find it obvious that the task for experimenters is to construct their experiments, especially those that may say something interesting to the theorists, while the "pure" theorists' task is to solve the remaining conceptual puzzles such as the Planckian cosmology regime in string theory that prevent them from trivilizing the rest of the doable experiments. Most other things can look like random, unlikely guesswork - that could be replaced by a year of waiting for experiments - or as a moderate variation of true things that have been done many times in the past.
When the dust settles and all kinds of hypes fade away, it becomes very clear what puzzles are important and what puzzles are not. The really difficult question is what are the right answers. ;-)
And that's the memo.