Experiments so crazy they just might work (UPDATED)

Have you ever done an experiment that’s very unlikely to produce an interesting result, but if it did, it would have a huge impact? An experiment so crazy it just might work?

Back when I was a postdoc, a couple of colleagues of mine did an experiment to test whether fruit flies can actually incorporate genes from the yeast they eat into their own genomes. It was completely crazy–there was no reason to think fruit flies could do this, and plenty of reason to think they couldn’t. But nobody had ever actually tested it directly, and if it turned out that fruit flies could do this it would be a massive result. Turns out that they can’t do it, sadly.

I think conducting such experiments is much like buying lottery tickets, or gambling in a casino. You expect to lose money doing those things. And it’s a really bad idea to spend money on lottery tickets or gambling that you’d be better off spending on something more important, like food and shelter. But if you have some cash you can afford to lose, and you find lotteries or gambling more fun than other forms of entertainment, then sure, why not have a go?* Similarly, even someone with a secure, long-term funding stream probably shouldn’t spend all of it conducting crazy experiments. But if you’ve got a bit of money and effort to spare, and a crazy idea that would be fun to test even if it doesn’t work out, why not have a go?

I do think there’s a line between crazy and too crazy. For instance, if you’ve already tried the experiment several times and gotten the same result every time, trying it again and hoping for a different result is probably too crazy. After discovering the symbiotic origin of mitochondria and chloroplasts, my understanding is that Lynn Margulis spent many years looking for genetic material in other organelles. Early on, that probably wasn’t a crazy idea at all. But after looking for a while and not finding anything, it probably transitioned to being a crazy idea. And then after still more futile searching, it probably transitioned to being too crazy. A bet that’s favorable at 10 to 1 odds, and unfavorable-but-fun at 1000 to 1 odds, can be neither favorable or fun at zillion to one odds.

Note that an experiment can seem crazy if you don’t understand the rationale for it. If you don’t understand Einstein’s theory of relativity, it seems crazy to do an experiment testing whether time slows down when you’re on an airplane. That an experiment can seem crazy to someone who doesn’t understand the rationale for it can occasionally provide opportunities for sharp people to do low-risk high-reward experiments. The experiment isn’t really crazy, and so is low risk, but others see it as high risk and so are really impressed when it works. Darwin’s famous prediction of the existence of an as-yet-undiscovered long-tongued moth wasn’t an experiment, but it illustrates what I’m talking about: the prediction seems crazy only to someone who doesn’t understand evolution. The analogy here might be to people for whom playing the lottery actually isn’t crazy at all, because they’ve figured out how to game the system.

My pet idea for a crazy experiment (two, actually) involves dormancy emergence decisions in lysogenic phage. A lysogenic phage is a virus that, when it infects a bacterial cell, can choose to go dormant. The phage remains in that state until being induced to emerge from dormancy, for instance by signals that the host cell is stressed and may die, thereby dooming any dormant phage. The emerging phage hijacks the host cell’s genetic machinery, makes a bunch of copies of itself, and lyses the host cell to release its progeny. Phage also occasionally “spontaneously” emerge from dormancy, which is conventionally thought of as a “mistake” or “accident”, but may actually be a form of bet-hedging against unsignaled host mortality risks (e.g., the host cell getting eaten by a protist or something). My first crazy idea is to see if you can select for an increased rate of spontaneous lysis by imposing unpredictable, unsignaled mortality on host cells. This would be a test of whether spontaneous lysis is actually adaptive bet-hedging rather than a mistake. It’s not totally crazy, for the reasons I just described–there is an arm-waving evolutionary argument that suggests the experiment might work. But I think the idea runs sufficiently against the conventional wisdom among people who work on phage that it qualifies as crazy. My second crazy idea is to impose predictable but unsignaled mortality on host cells, say by killing a large proportion of them with chloroform at 100-hour intervals, to see if you could select for phage that can keep time while dormant. If hosts are dying like clockwork every 100 hours, but with no advance warning, that should, all else being equal, select for phage that remain dormant for something like 99 hours. I can see the Nature paper now: “Evolution of phage with an internal alarm clock”! 🙂 (I emphasize that I haven’t thought super-hard about either experiment. I haven’t gotten beyond casually chatting about them with a few phage evolution folks. So I really don’t know if these experiments are crazy or too crazy.)

I’ve been trying to think of crazy experiments that actually worked, but so far I’ve been drawing a blank. That arsenic-based life study looked like a candidate at one point, but of course it’s been refuted now. (UPDATE: Tabletop cold fusion is another example of a crazy experiment that initially looked like it might have worked but turned out to have failed. And while SETI is an arguably-crazy attempt to find extraterrestrial life that has so far failed, you can argue that spinoffs from it make it at least a partial success.) Note that accidentally stumbling onto something unexpected while doing non-crazy experiments doesn’t count as a successful crazy experiment. That’s like finding money on the sidewalk, not like playing and winning the lottery.

Have you ever done an experiment so crazy it just might work? Can you think of any crazy experiments that actually did work?

*These remarks are not meant as a serious analysis of the many issues surrounding gambling. I’m intentionally ignoring things like the possibility of getting addicted. It’s merely a simple analogy to clarify the circumstances in which I think crazy experiments can be worth doing.

4 thoughts on “Experiments so crazy they just might work (UPDATED)

  1. Pingback: Friday links: good cartoons of bad arguments, and more | Dynamic Ecology

  2. A thought: does Rich Lenski’s long-term evolution experiment (http://telliamedrevisited.wordpress.com/2013/12/14/what-weve-learned-about-evolution-from-the-ltee-number-4/) count as an experiment so crazy it just might work? “Let’s just start up a dozen replicate lines of initially-isogenic E. coli, subculture them daily, and see what happens.” Still trying to decide if I’d consider that a low-risk or high-risk experiment. In some ways it’s low risk, because it’s open ended–lots of different possible outcomes would be interesting, for different reasons. But in some ways, it’s high risk. Many of the possible interesting outcomes (including but not limited to those that actually occurred!) would’ve been thought unlikely back when the experiment started, while I bet the risk of getting something fairly uninteresting might’ve seemed pretty high back at the start. And while the experiment turned out to be massively rewarding, I’m curious how rewarding Rich thought it would be (or what distribution of possible rewards he foresaw) when he first started it. Well, since Rich is now blogging and on Twitter, it should be easy enough to find out! 🙂

  3. Pingback: In praise of side projects | Dynamic Ecology

  4. Pingback: Tell me again what “risky” or “potentially transformative” research is? | Dynamic Ecology

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