The makings of a revolution
Before I finish rambling about this week, I need to tell you about some of the keynote speakers at NETS and what they helped me realize.
Sam Dupont delivered a sweeping overview of ocean acidification research, offering his unique perspective on how far the field had come and where it still had to go. He made the bold statement that we (the scientific community) had been approaching ocean acidification research all wrong and needed to shift our perspective. He described the old way of doing experiments as "stamp collecting" to depict the endless enumeration of facts that resulted. Single studies would focus one or two species, expose individuals to predicted future pH levels, and observe the effects. In the end, we were left with a whole bunch of predictions that didn't really have that much to do with each other.
Later that same day, Tjalling Jager said many of the same things about environmental risk assessment models; that we had been going about them all wrong. Previously, one would model the adverse effect of a pollutant on an organism, then another, then another. These separate models would have to be combined with predictions of where pollution would occur in order to quantify environmental risk. The result was disjointed and far from realistic.
What probably struck me the most was that both speakers offered similar alternatives to the previous stamp-collecting methods. Instead of accumulating facts, both put the focus on mechanisms. We as the scientific community should understand not just what happens but how it happens, because once we are able to understand the mechanisms, we can build much more realistic models of the world.
You know, I used to be a stamp collector. Actually, I was probably worse than a stamp collector because I treated science like police work. I tried to find evidence for every little detail. I wanted to test well-worn hypotheses in new locations and new environments, thinking this was progress when in fact I knew full well what would happen. It wasn't until I got a kick in the teeth from my adviser in Oregon that I actually realized what I was doing. He articulated the problem to me quite clearly, but it still took a while for me to re-wire my thinking. I'm probably not even finished with the process yet.
I had some excellent conversations this week with Chuck Fisher, another keynote speaker at NETS and a prominent deep-sea biologist. He told me about monitoring the recovery of deep-sea corals from an oil spill, and even though he and his team were continually finding new coral sites, he said he found it more important to monitor closely at a smaller number of sites. Investigating a large number of sites didn't actually add new information to the analysis because the same principles were shown over and over again.
See, this is the part that it took me so long to realize: you might not actually learn that much by surveying and experimenting in new parts of the world. Whenever I plan a scientific study, I need to be able to articulate exactly why I'm doing it, and explanations like "because it's cool" and "because we don't know anything about it" are simply not enough. There are a heck of a lot of things in the world that we know nothing about. I need to be able to articulate why the particular unknown I have chosen is more important than any other unknown I could possibly study. If I can't articulate this, then my chosen unknown is probably just another stamp.
Maybe the ideas I'm trying to express here are old news to some of you, but it was a big deal to me when I finally got it. It started to sink in sometime over the summer. I actually remember one day when I was just cleaning my apartment and letting my brain turn. I had become fascinated with the cultural anthropology of Polynesian peoples during a trip through the South Pacific, and I found myself wondering why their languages had diverged from each other in the way that they did. I started subconsciously drafting a thesis proposal to study Polynesian linguistics (you know, in my second life where I'm a cultural anthropologist), and all of a sudden I heard the voice of my Ph.D. adviser. It was loud, and it was conscious. "I don't care that it's cool," my brain said. "I don't care that it's unknown. Go tell me what you can learn about everything by studying this."
It's a great feeling when you finally get something. I don't just mean that you're able to spit the words back; I mean you feel it in your gut. I know now that designing a good study is not a matter of heaping all the knowledge in the world into a pile and then standing on top of it. It's more like pulling just the right Legos out of the box and fitting them together in a way nobody has ever thought of. The makings of a scientific revolution are not to be found in a stamp collection of facts. The makings of a revolution are hidden in keynote speeches, in the buzz of conversation, in perspective shifts, in mechanistic models, and in the brains of those bold enough to step out of the crowd.
Sam Dupont delivered a sweeping overview of ocean acidification research, offering his unique perspective on how far the field had come and where it still had to go. He made the bold statement that we (the scientific community) had been approaching ocean acidification research all wrong and needed to shift our perspective. He described the old way of doing experiments as "stamp collecting" to depict the endless enumeration of facts that resulted. Single studies would focus one or two species, expose individuals to predicted future pH levels, and observe the effects. In the end, we were left with a whole bunch of predictions that didn't really have that much to do with each other.
Later that same day, Tjalling Jager said many of the same things about environmental risk assessment models; that we had been going about them all wrong. Previously, one would model the adverse effect of a pollutant on an organism, then another, then another. These separate models would have to be combined with predictions of where pollution would occur in order to quantify environmental risk. The result was disjointed and far from realistic.
What probably struck me the most was that both speakers offered similar alternatives to the previous stamp-collecting methods. Instead of accumulating facts, both put the focus on mechanisms. We as the scientific community should understand not just what happens but how it happens, because once we are able to understand the mechanisms, we can build much more realistic models of the world.
You know, I used to be a stamp collector. Actually, I was probably worse than a stamp collector because I treated science like police work. I tried to find evidence for every little detail. I wanted to test well-worn hypotheses in new locations and new environments, thinking this was progress when in fact I knew full well what would happen. It wasn't until I got a kick in the teeth from my adviser in Oregon that I actually realized what I was doing. He articulated the problem to me quite clearly, but it still took a while for me to re-wire my thinking. I'm probably not even finished with the process yet.
I had some excellent conversations this week with Chuck Fisher, another keynote speaker at NETS and a prominent deep-sea biologist. He told me about monitoring the recovery of deep-sea corals from an oil spill, and even though he and his team were continually finding new coral sites, he said he found it more important to monitor closely at a smaller number of sites. Investigating a large number of sites didn't actually add new information to the analysis because the same principles were shown over and over again.
See, this is the part that it took me so long to realize: you might not actually learn that much by surveying and experimenting in new parts of the world. Whenever I plan a scientific study, I need to be able to articulate exactly why I'm doing it, and explanations like "because it's cool" and "because we don't know anything about it" are simply not enough. There are a heck of a lot of things in the world that we know nothing about. I need to be able to articulate why the particular unknown I have chosen is more important than any other unknown I could possibly study. If I can't articulate this, then my chosen unknown is probably just another stamp.
Maybe the ideas I'm trying to express here are old news to some of you, but it was a big deal to me when I finally got it. It started to sink in sometime over the summer. I actually remember one day when I was just cleaning my apartment and letting my brain turn. I had become fascinated with the cultural anthropology of Polynesian peoples during a trip through the South Pacific, and I found myself wondering why their languages had diverged from each other in the way that they did. I started subconsciously drafting a thesis proposal to study Polynesian linguistics (you know, in my second life where I'm a cultural anthropologist), and all of a sudden I heard the voice of my Ph.D. adviser. It was loud, and it was conscious. "I don't care that it's cool," my brain said. "I don't care that it's unknown. Go tell me what you can learn about everything by studying this."
It's a great feeling when you finally get something. I don't just mean that you're able to spit the words back; I mean you feel it in your gut. I know now that designing a good study is not a matter of heaping all the knowledge in the world into a pile and then standing on top of it. It's more like pulling just the right Legos out of the box and fitting them together in a way nobody has ever thought of. The makings of a scientific revolution are not to be found in a stamp collection of facts. The makings of a revolution are hidden in keynote speeches, in the buzz of conversation, in perspective shifts, in mechanistic models, and in the brains of those bold enough to step out of the crowd.
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