Tips for developing original philosophical ideas?

In our newest "how can we help you?" thread, a reader asks:

At least once a week, I have an idea that I think could be developed into a publishable paper. But ninety-five percent of the time, the relevant idea has been published already, usually within the last four years. Is this a common experience? Am I doomed to accidentally reproduce others' work on an almost daily basis for the rest of my academic career? Do any of you have advice for generating original philosophical ideas, or for how to quell the ever-present fear that absolutely everything worth saying about philosophy has already been said (or is about to be said, this month, by someone from NYU)?

Good questions. This happened to me a lot early in my career, particularly in grad school, but it doesn't seem to happen to me much anymore. If I had to put my finger on the reasons why, I think it's probably two-fold.

First, the longer one goes in one's career, the better of a sense one may get of the philosophical terrain that has already been mapped out. You've read a lot more, seen the literature develop, and so on.

But second, the further I've gone along in my career, the less my publishable ideas have come from reading philosophy books or articles. Most of the ideas I've come up with that haven't been taken already have come from simply thinking about day to day life and various problems in the world around me. When you read the philosophical literature, you're typically reading preexisting debates where various positions have already been mined and developed. In contrast, the world around us is always changing in unexpected ways, with new phenomena (social media, large language model AI, etc.) always cropping up that haven't necessarily been mined philosophically as much.

So, I guess that would be my tip: focus a bit less on the literature, and more on what philosophically interests you about the world! But this is just me.

What do you all think? Which strategies for developing original philosophical ideas do you find fruitful?

Comments

[Hermias]

“The highest mountains.
The oldest books.
The strangest people.
There you will find the stone.”
- Terence McKenna

I think it can help to read around a few different topics and try to map them over each other, or free-flowingly just write crazy sentences with philosophy words and then later go back over rationally and see if there's anything good in there, if anything can be said for it, e.g. "if veganism is right, then aborting kittens is bad, if aborting kittens is bad then aborting human fetuses is bad."

[keep going]

I just tend to explore issues and questions I find interesting, and I naturally tend to form opinions about them. Sometimes, those opinions turn into original publishable ideas. Lots of times, I hit a dead end and come up with something that someone else has said in a much better way than I ever could. It's frustrating. But's that just the name of the game. Even still, I always keep every rough draft I've ever written and all unused material. Sometimes it will find its way into a paper eventually.

[anon]

This is a bit of a boring suggestion, but I do think it helps: when you're interested in a book or paper, look it up on Google Scholar, then click the link to see who has cited it, then scroll through titles and read abstracts if necessary. This helps you get a sense of what's been done already - in a small area, the one you're thinking of right now. Only let yourself ponder "new" ideas related to book x or paper y after doing this.

[Assc prof]

I agree with Marcus. One great heuristic for developing paper ideas: can you explain their interest to another philosopher without mentioning *any* literature?

[use your anger.]

One route: find a recent paper that you think is obviously mistaken, explain why it's mistaken (whether directly or indirectly).

[Keep going]

To add again to this thread if I may, I think Marcus’ advice is spot on, which I’ve seen him make many times on this blog. First write ‘your paper’ and then situate it within the literature. This serves two purposes. First, it ensures that you are writing ‘in your own voice’, something my supervisor coached me to do early on. Graduate students tend to write papers as an overview of the literature and try to show their mastery of it. I find that more experienced people do the opposite. They present their own ideas and then work in the literature around that idea. I think this is a good practice. Second, it helps you to develop you’re own ideas! I think you’ll actually be surprised to find that even if you think an idea you have has already been done, you’ll notice subtle but substantive differences between your own take on the idea and what someone else has done. Of course, this might just constitute a ‘micro move’ in the literature. But I think these moves are worth making, least of all because very few of us (myself included!) are likely to make few macro moves or lead the literature in entirely new directions. But that’s fine! Let the big names at NYU make the big moves. And then fill in the gaps in important but smaller ways. I think over time you’ll find a smaller niche in which your work will be significant, at least to you. What’s wrong with that?

[go concrete]

If you work in a field like philosophy of science, which purports to be empirically informed, then a great way to develop new philosophical ideas is to start reading empirical research. If you are interested in collaboration in science, read the research on it, by sociologists, historians, etc. Then you will have something concrete to guide your philosophy.

[Shay Allen Logan]

My advice: don’t check whether it’s been thought of. Write it up first and let the referees decide whether it’s novel. If it’s not, whatevs. Doing the writing will make you understand the thing way better anyways. If it is, awesome! You win!

And if the referees get it wrong and you end up publishing an idea someone else already had, then again whatevs. Some wheels are worth reinventing.

[Sympathizer]

Without fighting the hypothetical too much, I do think sometimes this comes down to mindset. I (a grad student) experience the rollercoaster of exhilaration at a new idea followed by defeat at discovering someone's already said something similar pretty frequently. But when I lamented to a slightly more experienced philosopher about it, they just responded "why should that person get the last word on the subject?" I try to have that mindset now. I think that especially for young philosophers, there's a risk of 1) having a good idea, 2) realizing that something in that ballpark has been said and then 3) discarding the idea altogether. My sense is that I (and probably other young people) have a habit of discarding the ideas before giving them the chance to discover what's different about them. Sure, there are cases where I read the *exact* thing I thought of. But there are other cases where pushing past the initial feeling of "shoot, they got there first!" is the central task.

[Michel]

I'd like to echo Marcus, keep going, and go concrete, in particular:

-Read widely
-Write first, then around (you'll find gaps! I once thought I was scooped about the history of a phenomenon, only to find that 'histories' of it went to the 19th century and no further!)
-Go to the cognate research or public-facing discussions, and see what interests people there, and how you can help

I'd also add: look at CFPs for conferences and publications. Not because you should submit tot hem--though you could--but because they'll give you a sense of what topics people are interested in, and you can mine them for ideas.

[Patrick Lin]

It's important to recognize that "original" can mean different things and in different degrees.

An idea itself could be wholly or partially original, or you might have an original critique about a pre-existing idea. Or the connection you draw between two old ideas could be original, e.g., extending the trolley problem to robot cars, or applying just-war theory to novel weapons that challenge the paradigm. Or the way you explain an old idea could be original and very helpful (so it's worth doing), incl. organizing and mapping out a debate.

And probably lots of other ways to be "original." You do you.

[Amma]

No advice to add. just want to say you’re not alone. It’s so frustrating. At one point I felt scared to even start a new paper because I’d think, what’s the point someone already probably said it. I just kept going. Eventually I had ideas that no one had written (or honestly maybe they have but I’ve done my due diligence which is more than you can say for plenty of our colleagues). You’ve heard it before I’m sure, but the fact that ideas you’re coming up with yourself are getting published is an encouraging sign that when you do have an original idea it’ll be a good one. Chin up!

[goblin]

@use your anger

This strategy seems dicey. Generally the only journals that are willing to publish reply papers are the ones that originally published the paper *that* you're replying to. If they say reject it then that's a tremendous amount of work for comparatively little benefit.

[still use your anger]

@goblin. I didn't mean write a "reply," I meant use the wrongness as something to start your own a thinking and, in turn, your own paper. A couple of my papers started like that, and they aren't "replies."

[the anti-rank guy]

I would suggest de-emphasizing "ideas" as the OP seems to focus on in the post. What happens in my case is like the following (I hope to provide perspectives!): I come up with a paper project, either by reading or by talking to someone (usually both). Not once a week! Maybe a few times a year. Then, if the project is carried out successfully, which takes weeks or months of investigation, I get a paper that is hopefully publishable. In this process, I don't think ideas play a dominating role. Sometimes there isn't an idea at all to begin with other than the project itself, other times there is an idea, but the project fails. Ideas do happen, but for me, they happen in small ways during the writing. Occasionally I do end up with a paper that someone has written in some other way. But most of the times, I end up with a paper that enriches the literature. OP, does this help? I am not sure but I hope it does somehow.

BTW, not against OP, but I am uncomfortable about mentioning someone from NYU. I know OP does not mean it seriously, but I don't think it likely that someone from NYU will write your idea more so than anyone from anywhere.

[academic migrant]

Sometimes there are genuine risks of not being "original" in a very vague sense. I got several rejections in different journals from the same reviewer (who copied and pasted the same review without checking whether the manuscript had any updates) citing that someone else has already argued for the exact same conclusion (despite the conclusions being rather different).

Mentioning this, however, as a positive story. Papers can argue for similar conclusions, but from different ways. Sometimes it involves showing that other papers had done a fine but imperfect job. Sometimes one just needs to show that there are further and possibly different practical implications for similar but sufficiently different ideas. We should try to avoid being those narrow minded reviewers, but with enough luck, your idea may still be publishable if you can show the value of having it in the literature.

And just to add, I think it is rather common to have similar original ideas. We are often involved in a common struggle, responding to issues we face together in the same society.

[You know the answer]

Is the question “How to be brilliant?” I cannot think of a single other interpretation of the question—and I intend this in a helpful way, to be perfectly clear.