Some people have this annoying habit of starting a blog post with an embarassing statement about how they haven’t posted for a while, thus drawing unecessary attention to their failings. Well, I have absolutely no intention of mentioning… oh hang on. Bugger. Already done it. Oh. Well. Anyway. LUCKILY, old chum and intellectual sparring partner Martin Elvis has supplied me with a lovely guest post. It follows on from my previous post, and is a plea for asking answerable questions. I think its spot on – how about you ?
Martin Elvis, Harvard-Smithsonian CfA
Scientists are sometimes criticized for their hubris, trying to explain the whole Universe, searching for the beginning of Time, or for the God Particle that gives mass to all things. But excuse us, that was never our intent. A feature of science, why it has been successful, is that it asks humble questions.
The alchemists famously wanted to find the Universal Solvent, or to turn Base metals into Gold. It’s good to have ambitious goals, surely. “Make no small plans”, they say. Well, no. Not if you have no idea how to achieve them. Your plans should be just as big as they need to be to answer a well-posed question. It’s too easy to ask a big question. Science began when some folks decided to ask small questions: How does a ball roll down an inclined plane? What if I pump the air out of a closed container? Being happy to get answers to these questions, led on to more questions, and those to more still. And after 400 years of one tractable question after another, we have the extraordinary questions we can ask today.
Linking these questions up with mathematics was often a good way to make the questions sharper, though not always. Some technologies – gunpowder, transparent glass, printing – made progress more rapid. And publishing our answers to these questions publicly made a huge difference. But the main point was to ask tractable questions, ones that you had an idea how to answer.
For some time I’ve felt that present day philosophers are stuck with asking the same Big Questions, and have made only as much progress as the alchemists did. But now I’m worried that Big Science has run off in the same direction. We want a Theory of Everything, but 50 years of searching has produced only tantalizing clues in 6 dimensions. We want to understand Dark Energy, the ‘anti-gravity’ that accelerates the expansion of the Big Bang. But all we know how to do is to measure that acceleration more and more precisely. So far that has produced zero insight. There are an infinite number of theories that can fit the data, and there will still be an infinite number of theories if we measure the acceleration 10 times more accurately. We will want to image the Other Earths that we expect find soon, map their continents, study their vegetation. But that needs telescopes far, far, larger than we can currently build. These are not good questions. In his Op-Ed “The ‘Nightmare Scenario’ ” James Owen Weatherall (UC Irvine) says of high energy physics: “We are faced with a struggle between the questions we want to answer and the limitations of our abilities – and at some point, perhaps soon, our limitations will win the day”.
Is there really a point at which we should say “This is too hard a question. We don’t have a clue how to answer it, or the best plan we have costs so much we couldn’t do anything else. So let’s shelve it for now. Maybe in 50 years we’ll see how to get at it.” Superconductivity remained unsolved for 50 years. No-one knew how to attack it and/or they didn’t have the technology. It’s plausible that another clue to Dark Energy will come up thanks to research in some other area of astrophysics, or elsewhere. Perhaps in 50 years we’ll be able to afford much bigger telescopes in space to image new Earths. Perhaps In solving another problem, maybe in mathematics or computing rather than physics, we may see how a Unified Theory of quantum gravity can be built. Almost certainly it won’t be the tricks that worked before. Einstein and Feynman failed. New ways of thinking are needed. They may be Outsider now, but perhaps the approaches of Robert Laughlin (“A Different Universe“) or Stephen Wolfram (“A New Kind of Science“) are what we need. What now seems a weakness, may be re-imagined as a strength. 1/3 cannot be expressed as a decimal. Is that a problem, or does it point the way to irrational numbers?
This is not a cry of despair. Weatherall is too pessimistic. Building ever bigger colliders has probably hit its limit. But we will find other ways. We’ve always made these choices. Asking what the stars were made of, even though it’s an obvious question, was left alone because there was no way to address it. Then Kirchoff and Bunsen were taking their exercise along the Philosopher’s walk in Heidelberg talking about how their new spectrograph had analyzed the composition of a fire in the nearby city of Mannheim. Bunsen half joked “Why should we not do the same with regard to the Sun?”* Moment of silence. Bingo! Now we can ask what the Sun is made of, because we can see a way to find out. This was the birth of modern astrophysics. There’s still a huge amount of science we do know how to make progress on. Modest specialized telescopes found exoplanets and Dark Energy. New ones can test quantum chromodynamics, not to mention understanding galaxies and quasars. Ongoing laboratory searches could well identify the Dark Matter. Meanwhile, we leave unanswerable aside.
The trick in science has always been to ask the right questions – not too easy, not too hard. (Imre’ Lakatos, a philosopher of science, called it being able to imagine a research program.) We do best when we see how we can go forward easily; the means of doing so may not be all that cheap, though it can be. What we do have to do is to ask humble, but not too humble, questions.
* as recounted in an anonymous article in Nature in 1902 (vol.65, p.587).