Friday, March 20, 2015

Priority in science is mostly a mirage

It seems these days that there are a lot of CRISPR priority fights out there, with the biggest being the patent dispute between Doudna and Zhang. Got me thinking about why we place so much emphasis on priority.

As scientists, it is a deeply engrained goal to be first. First to think of an idea, first to work it out, first to publish the idea. And in our culture, the one who does it first typically gets all the credit, sometimes even if they just “win” by a couple of months (although sometimes other factors come into play). It is what separates those perceived as the most shiny stars from the rest of us.

But think about it. If you’re working on something and get there just a few months before someone else, are you really that much more shiny than the next person? If the goal is to win a footrace, sure, you win. But if the goal is to create knowledge, the world would essentially be unchanged if you had never existed. Sobering. And true for the vast majority of us.

I think a pretty rational definition of a really original advance is something that if the researcher had not existed it is likely to have taken a really long time before anyone else would have come up with it. Almost by definition, such an advance is much more likely to come from one person. Like maybe RNAi. Or PCR. Although who knows? Maybe someone would have figured out these same things a few years later. I’m consistently surprised at how often you think you’re working on something completely alone only to find someone else hot on your heels. I think there are two reasons for this. One is that as technology and knowledge develops, the time becomes ripe for some discoveries. Like once sequencing was around, the discovery of several new long non-coding RNAs was essentially an inevitability. The other reason is that there are just so many smart people out there these days. With so many scientists, it’s virtually impossible that nobody out there is thinking about the same things you are. Even in math, which historically has worshipped at the altar of the solitary genius, often has multiple names attached to many new theorems. Which makes the exceptions all the more remarkable, like Yiteng Zhang’s amazing theorem about bounded gap primes or the discovery that primes is in P by a small group in India working largely independently. Kudos to them!

This is not to say that “meat and potatoes” science is not important. In fact, I think the steady, cumulative effects of incremental advances of the entire scientific community mostly outweigh the contributions of those few geniuses, especially in biomedical sciences in the current era. Somehow, I find this very reassuring and in many ways freeing: if you realize that we parcel out winners and losers in this race based on essentially arbitrary factors–and probably our innate desire to create heroic narratives–then it’s okay to just continue doing what you’re doing and not worry about it. In the long run, nobody really wins or loses, and science will continue moving, regardless.

So what is the strategy if you want to do something really original? Well, if the goal is to make a discovery that would take a long time to happen if you did not exist, then you can either do something really original or something that nobody cares about. Often one and the same!


  1. " Well, if the goal is to make a discovery that would take a long time to happen if you did not exist, then you can [do] something that nobody cares about. ."

    I guess I am on the right track, then :-)

  2. Interesting post. I think the whole issue of priority in science can be damaging. This is because we have a habit of putting published papers on a pedestal (of enshrined truth). So you can have a situation of two groups, each with a manuscript on the same thing, racing to publish. It's very arbitrary, but one paper is accepted. The group has won and now the other paper is useless. I'm only slightly exaggerating here.
    It's often said that "it's better to be right than first", but I'm not sure how realistic this advice is these days. Especially with so many scientists (as you point out) pursuing similar lines.

  3. Arjun, I agree that in case of CRISPR and many other biomedical discoveries, especially those requiring much resources, assigning priority is not possible.

    That being said, many scientists think of a minority of expectational cases, such as general relativity or Feynman diagrams, in which the priority of the conceptual insight is quite clear, at least in my opinion. These are the most shiny examples of scientific triumph, so it is utterly unsurprising that they create a seductive expectation. Virtually everybody fails that high expectation but that does not stop ambitious people from trying to create a make-belief greatness.

    I do agree that nowadays for almost all scientists, the probability of doing research of the originality and advanced-thinking of general relativity or Feynman diagrams is very close to zero. However, I think that there is a wide distribution in terms of how likely it is contribute a genuinely new idea, and our choice can move that probability anywhere from zero (do the next step in CRISPR research) to significantly above zero ... if you choose well your "neglected" area, it is not necessarily unimportant. Perhaps our main difference of opinion is in how much above zero the probability is: it's impossible to put a number on it but I think it is high enough to be worth our best efforts.

    1. I agree completely. I think it's a choice to try to do something original, and it's a good choice to make. Then again, if you want to try and "win" on the current fad, that's fine, too. That is also progress. I think it's a matter of style.

    2. And let's not forget that evolution by natural selection was worked out independently by Darwin and Wallace!