- The Specific Question. There's some particular piece of physics in an established area that isn't well understood, and after reading the literature and thinking hard, you've come up with an approach for getting the answer. Alternately, you may think that previous approaches that others have tried are inadequate, or are chasing the wrong idea. Either way, you've got a very specific physics goal in mind, a well-defined (in advance) set of experiments that will elucidate the situation, and a plan in place for the data analysis and how different types of data will allow you to distinguish between alternative physics explanations.
- The New Capability. You've got an idea about a new experimental capability or technique, and you're out to develop and test this. If successful, you'll have a new tool in your kit for doing physics that you (and ideally everyone else) has never had before. While you can do cool science at this stage (and often you need to, if you want to publish in a good journal), pulling off this kind of project really sets the stage for a whole line of work along the lines of The Specific Question - applying your new skill to answer a variety of physics questions. The ideal examples of this would be the development of the scanning tunneling microscope or the atomic force microscope.
- The (Well-Motivated) Surprise. You're trying to do either The Specific Question or The New Capability, and then all of the sudden you see something very intriguing, and that leads to a beautiful (to you, at least, and ideally to everyone else) piece of physics. This is the one that can get people hooked on doing research: you can know something about the universe that no one else knows. Luck naturally can play a role here, but "well-motivated" means that you make your own luck to some degree: you're much more likely to get this kind of surprise if you're looking at a system that is known to be physically interesting or rich, and/or using a new technique or tool.
Sunday, August 12, 2007
Kinds of papers
I've seen some recent writings about how theory papers come to be, and it got me thinking a bit about how experimental condensed matter papers come about, at least in my experience. Papers, or more accurately, scientific research projects and their results, seem to fall into three rough groupings for me:
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16 comments:
I think you missed an obvious one. You try to answer a specific question or develop a new technique, but it doesn't work. However, you have to graduate soon because you can no longer admit to anyone how long you've acutally been in graduate school. So you put together a few crappy papers that tell some sort of awkward story and then bury them in a paper graveyard of a journal.
Not that this has ever happened to me, but I have a friend :)
I have another type you forgot. You try to observe an effect someone thinks may occur, but you don't observe it. You then make up data claiming you observed the effect and many others and publish 2 papers a week on all the made up data. Write this type paper at your own peril!
mkg - I hear ya. I was actually talking with one of my students recently about how in some sense the worst situation is if an experiment kind of sort of equivocally works. That is, the effect being measured seems to be there, but only with a signal to noise ratio of about 1.5. That's tough, because you have to figure out whether improvement is possible or not. If an experiment really doesn't work, and has the good grace to do so quickly, and it looks like a dead end, you have to figure that out and move on. I learned that in grad school: a necessary ingredient for research success, at least for me, is a high attempt frequency.
aaron - boy, you really were vicariously scarred by the Schon affair, weren't you.... How are things out there these days?
Aaron, that can be improved: Let your postdoc do all you say and be a co-author. Similar pay off, but smaller risk.
I agree, Doug, that a high attempt frequency is important. I also wonder about the proper balance between sticking to the original grand research goals and pursuing potentially interesting effects noticed along the way. I'm amazed at the discipline some groups show in sticking to the original mission. Their students might publish only a few really nice papers, but if you look into their theses you find that they're loaded with other fantastic data.
Most of my grad school papers were really side stories that spun off of a grander research goal. The project that yielded the most papers (and was also the most time consuming) did not achieve its original goal, but did provide some other nice stories. I often wonder if we would have had more high profile papers if we'd focus more on the big carrot rather than exploring and writing papers about effects we saw along the way.
why do you mean by high attempt frequency?
I am new to this blog world. I am a grad student in physics and enjoy your blog.
What about the research projects that are taken upon only because there is money for that particular area? This happened to me not too long ago. I joined a group where the PI is chasing the -never to be found, if you ask me- glory. After a while, I realized the projects were not going anywhere (there has been one student for 7 years, few months ago got his first paper and his graduation date is still unknown) so I switched to another group. Anyways... I just think some professors don't really care/know what they are doing anymore. Does that count as a kind of paper?
sorry, not why, what do you mean?
Thanks for the comments.
By "high attempt frequency", I mean that in my experience it's good to have several things to try in the lab, or at least to have experiments designed so that even if the main (extremely hard but important) goal is not achieved, some kind of decent science still gets done. Situations where it takes three years to set up a measurement and then the effect isn't there, or there is some noise problem or something, are really bad, both practically and psychologically.
There are definitely some people who set their research agendas by exactly which way the funding winds are blowing. That's necessary at some level (that is, you do need to get some money to pay students), but I'd much rather work on well-motivated science. To turn it around, though, if a professor has money for a specific project, then students supported by that money really do have to work on that project. There's always some freedom to pursue new things that crop up in the course of research, but money from funding agencies has to be spent appropriately....
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That is, the effect being measured seems to be there, but only with a signal to noise ratio of about 1.5. That's tough, because you have to figure out whether improvement is possible or not. http://www.dating-bride.com If an experiment really doesn't work, and has the good grace to do so quickly, and it looks like a dead end, you have to figure that out and move on.
Not a bad analysis, I was reading it with delight.
You don't mention about an other one kind of paper.
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