Some years ago, I attended a seminar by a young postdoc who spoke about an extension of the standard model of particle physics. Known as “physics beyond the standard model,” this is a research area where theory is presently way ahead of experiment. In the hope to hit something by shooting in the dark, theorists add stuff that we haven’t seen to the stuff we know, and then explain why we haven’t seen the additional stuff – but might see it with some experiment which is about to deliver result. Ie, the theorists tell experimentalists where to look.
Due to the lack of observational evidence, the main guide in this research area is mathematical consistency combined with intuition. This type of research is absolutely necessary to make progress in the present situation, but it’s also very risky. Most of the models considered today will turn out to be wrong.
The content of the seminar wasn’t very memorable. The reason I still recall it is that, after the last slide had flashed by, somebody asked what the motivation is to consider this extension of the standard model, to which the speaker replied “There is none, except that it can be done.”
This is a remarkably honest answer, especially since it came from a young researcher who had still ahead of him the torturous road to tenure.
You don’t have to look far in the blogosphere or on Amazon to find unsolicited advice for researchers for how to sell themselves. There now exist coaching services for scientists, and some people make money writing books about “Marketing for Scientists.” None of them recommends that when you’ve come to the conclusion that a theory you looked at wasn’t as interesting as you might have thought, you go and actually say that. Heaven forbid: You’re supposed to be excited about the interesting results. You were right all along that the result would be important. And there are lots of motivations why this is the one and only right thing to do. You have won great insights in your research that are relevant for the future of mankind, at least, if not for all mankinds in all multiverses.
It’s advice well meant. It’s advice for how to reach your presumed personal goal of landing a permanent position in academia, taking into account the present mindset of your older peers. It is not advice for how to best benefit scientific research in the long run. In fact, unfortunately, the both goals can be in conflict.
Of course any researcher should in the first line work on something interesting, well motivated, and something that will deliver exciting results! But most often it doesn’t work as you wish it should. To help move science forward, the conclusion that the road you’ve been on doesn’t seem too promising should be published to prevent others from following you into a dead end, or at least telling them where the walls are. Say it, and start something new. It’s also important for your personal development. If you advertise your unexciting research as the greatest thing ever, you might eventually come to believe it and waste your whole life on it.
The reason nobody advises you to say your research project (which might not even have been your own choice) is unexciting is that it’s difficult if not impossible to publish a theoretical paper that examines an approach just to come to the conclusion that it’s not a particularly convincing description of nature. The problem with publishing negative results might be familiar to you from medicine, but it exists in theoretical physics as well. Even if you get it published, and even if it’s useful in saving others the time and work that you have invested, it will not create a research area and it’s unlikely to become well-cited. If that’s all you think matters, for what your career is concerned it would be a waste of your time indeed.
So, they are arguably right with their career advice. But as a scientist your task is to advance our understanding of nature, even if that means concluding you’ve wasted your time – and telling others about it. If you make everybody believe in the excitement of an implausible model, you risk getting stuck on a topic you don’t believe in. And, if you’re really successful, you get others stuck on it too. Congratulations.
This unexciting seminar speaker some years ago, and my own yawn, made me realize that we don’t value enough those who say: “I tried this and it was a mistake. I thought it was exciting, but I was wrong.” Basic research is a gamble. Failure is normal and being wrong is important.