So before starting my career as a Taxi driver or a McD fry cook, I have the opportunity to do some research.
However I find that I am not particulary good at it. It's not exactly the lack of ideas, but rather the mechanics, the approach and probably everything else. Lack of proper education on the matter doesn't help.
In your opinion, what are the crucial steps for good research? What have you learned from experience? What would you teach your young self starting out?
The idea is still the key thing to doing anything worthwhile.
The execution turns the good idea into a good paper and contribution, so you will just have to work hard to learn and carefully apply what you need, there is no way around that. This is a hard slog, but it is worth it.
But the good idea is the key to it all. So if you are willing to work hard at the other stuff, you will be fine.
I would go with: persistence, diligence, patience, persistence and blind faith.
1 Simple real life examples are the way to go .
There are different ways to do theory. But first you pick a topic. Something that interests you. Preferably something from the real world, not from a paper. Even if you choose a topic based on a general paper and not based on a real life situation, you need to have a simple real life example in mind: to fix ideas, to get the intuition of why things should work, to guide modelling choices, and even to help understands the mechanics of whatever model you will end up using. You need a toy real life example.
2 Try to reach an audience .
Nowadays, it may also be important to ask from the very beginning: will your paper result in any testable implications? can your model be estimated? is there data for the kind of environments you have in mind? or, at the very least, does your paper generate any important policy implications? There are very important theory papers that fail in all these regards, but not a lot and usually only theorists care about these papers. If you are writing a job market paper, you want to be able to motivate your work in front of a general audience, and if your model doesn't lead to policy implications or empirical exercises, then you won't be able to engage non-theorists.
3 You are not the first to think of your idea .
Unless you are working on some obscure thing that nobody cares about. There will be related literature. You may even find some paper from the 80s that "does everything you wanted to do". If every time this happens you drop your idea and start over, you won't get anywhere. There are a couple of things to say about this:
(a) It is OK to have related papers. Forget the stories about how Nash only cites Kakutani and vNM. You are not creating a new literature. You are making a solid contribution to the existing literature. And no matter how similar the work of others is to your idea, it is never complete and there is always work to be done. People are still publishing papers and re-writing theorems about Savage (1954)'s model. So don't drop the topic at the first sign that someone "has done it".
(b) Still, the more you can differentiate your work from the work of others, the better. That is why, prefereably, your topic shouldn't be too narrow and it is better to be based on a story and not on a model. Because then it is easier to adjust your work to build upon the existing literature. If your original idea was to see what happens to X's model when you drop assumption A, then it might be the case that someone else has done exactly that. If your idea was to see what happens in situation X under circumstance A, then even if other people have asked this question they have probably modelled differently. In any case, remember that you have already paid the fixed cost of learning the mechanics and literature of a subsubfield and you may want to stick to the area even if you drop the topic. (Not saying you should always stick to your idea, sometimes you have to admit defeat, but you should resist the initial fatalit urge that we all get the first time we discover related literature).
4 Something always comes out.
Unless you are doing trivial work that nobody cares about, chances are you will bet stuck at some point. At least for a few weeks. This is were you need he persistence and the blind faith. At this point it is crucial that you meet with your adviser regurarly even if you don't have anything to show. THis will help you to keep working, even if you are not producing anything, it will motivate you to produce something because you don't want to show emptyhaded again, and it will help to deal with the anxsiety and guilt that all gradstudents feel at some point. If you shoudl be worried, your adviser will tell yo...See full post
Theorist, I agree with your post for applied theory. But for hardcore theory, you might need more than a toy model and real examples.
Of course you are right. Most of the time an example is not enough (there are exceptions like: cheap talk, rubinstein '89, spence) and the general result matters. My claim is that it pays to start from an example and, many times, either the example will be enough or the general result will follow naturally from the example.
Consider for instance a successful JMC from this season: Misha Panov from GSB. His paper is about "interspection" and forward reasoning in extensive form games. I think it it "hardcore" enough. However, from what I hear, Mr. Panov is a pretty good poker player. And his paper is a description of what happens in a poker game: there are good players and bad players, and when you see somebody do something unexpected, you update your beliefs about how good a player he is. I don't think he started thinking about this idea by reading Battigalli and Siniscalchi, he probably thought of this idea while thinking about a poker table.
When people think of bad reputation, they think of Valimaki and Ely (2003)'s example, not about the general case covered in Ely, Fudenberg and Levine (2008). Sure the general papers about perturbations and global games are important, but a lot of credit still goes to Rubinstein's (1989) simple example. I think that in many cases the example is more important than the general result.
look at where past theory candidates ended up. you think you can beat the odds? unlikely
yeah I know. I just wanna have fun while I can and maybe do something worthwile for someone. Afterwards I'll drive a cab, as I said.
lol as if I had any illusions, come on, I am reading EJMR
The idea is still the key thing to doing anything worthwhile.
The execution turns the good idea into a good paper and contribution, so you will just have to work hard to learn and carefully apply what you need, there is no way around that. This is a hard slog, but it is worth it.
But the good idea is the key to it all. So if you are willing to work hard at the other stuff, you will be fine.
I don't fully agree with this. Yes, good ideas are important, but execution is also essential, and very hard. Moreover, ideas develop as you work on them, so it's not clear in what sense the idea exists independent of the execution.