Carrot eater asked me to consider what I would do if I were in charge of climate research. I assume that he wasn't going for answers like 'find a different job promptly', which does make the question a little more theoretical. Although I do have the copy of Nature that prompted his question, I've not read that article. So these are my own thoughts.
My first thought is the least creative -- pretty much what is already being done in pretty much the proportions it is already being done. No doubt that I would like to make some adjustments, say more for ice-related work. But the main lines have gotten to be the main lines because they consistently show up as areas that deliver improvement to our understanding (satellites, paleoclimate) or they consistently show up as areas hampering our understanding (clouds). Some areas probably get more funding than ideal, or less than ideal, because humans are involved and a particularly good, or bad, field leader can have effects beyond just writing good papers and proposals.
The two that I like for creative work should start as minor niches. If my intuition is right, they'll grow markedly, at least for a time. Because if my intuition is right, there's a lot to be learned from here that would be useful. But it is pretty much just my intuition, so the starting investment shouldn't be huge.
The less exciting already has some work being done, at least in related fields. Namely, 'no approximations' modeling. We do know the equations that describe how fluids move, for instance. We can write programs that carry out those equations accurately. But once you're examining a volume of fluid larger than a moderately large fish tank (call it 50 gallons, 200 liters), you have to make approximations. Computers can't deal with the full dynamics for a larger volume than that. Nevertheless, in the 1950s and 1960s especially, quite a lot was learned about the general circulation of the atmosphere by doing 'dishpan' experiments. Dishpans can be set back up, and the computers given accurate representations of them. And then we can see how close the models come to the observations.
More about the dishpans in a later post; they were a very clever way of approaching the atmosphere. But here's a modern version's photo:
and see also the original press release about the memorial lab, from which I got that picture. I was among the last students Fultz fired up his working lab for.
The more exciting, to me, notion turns on an observation that I find very striking, and very few others in the field find at all interesting. Makes it a high risk idea -- those other people are awfully smart, good chance they're seeing a flaw that I'm not. I'll have a little explaining to do, but the short form of the observation is: for something like the global climate surface temperature field, you only need something like 12 numbers.
If you look at our climate models, they have quite a lot more than 12 numbers to them. They've got at least 6 for every grid cell, and several hundred thousand to several million grid cells. Tons of numbers, and how many increases every time we run a climate model at better (meaning smaller grid cells) resolution.
Yet 12 or so is, in some sense, 'enough' for temperature. (Another 12 for pressure, maybe a bit more for each of wind and humidity.) The sense starts here: if you look at temperatures around the globe, most of what you see is climate -- that the poles are cold and the tropics are hot. So we subtract out climate in looking at the global temperature field.
After doing that subtraction, you can see that areas that are warmer than usual tend to be fairly large, millions of square km. Ditto the areas that are cooler than usual. Continue with that sort of analysis and you also notice that the warm areas are usually balanced off by cold areas elsewhere. Keep doing it and you see that the same areas tend to be counterbalancing each other. These are areas that you can look at and know even thousands of km away whether it is warmer or cooler than usual. The El Nino-Southern Oscillation is the best-known of these patterns.
Once you get rigorous about doing this, which I will be for a later post, you find that if you pick the right areas, once you've chosen about 12, you can put together the entire globe to fairly good accuracy. This is the root of methods to reconstruct paleoclimate from information sampled from only a modest number of locations around the world.
But I look at it and think, and wonder ... if you can describe something with only 12 numbers, global surface temperatures in this case, then there should be some way to model it with only that many variables. If only we were clever enough?
So one thing I'd like to see some funding for is these sorts (I'm sure I'm not the only one with such ideas) of basic research ideas. They're ideas that will probably take a few years to develop, and most will never pan out. But they're also the ideas that will revolutionize the field if they do pan out. Current support for science has gotten very short term in its view. If you can't be sure to publish a paper or three per year from a grant, you are very unlikely to get it. Fields therefore get very 'play it safe' in what they attempt to do.
EGU 2015, my impressions
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