When I started grad school, I approached it sort of like you describe here — looking for "gaps" and looking for "hot topics" and looking for "really interesting arguments." That seemed to be how one ought to approach it, because we were always praising books that tackled something "really new" or had a "sexy argument" or whatever.

I came to conclude this was a bogus approach. Why? Because sometimes gaps are there because there isn't much to say or it isn't that interesting, because a topic hot today is not hot in 5 years (when your thesis will be finished, if you're lucky!), because the argument needs to come after the work is done, not before. I see a lot of grad students chasing the idea that to succeed they need to hyper-specialize and simultaneously hitch themselves to some bigger scholarly trend. Having run a job search I have seen how this results: a lot of more or less uninteresting thesis topics that are more or less interchangeable, hyper-specific, not very promising if you're not super invested in them already.

The approach I ended up taking was to write a lot of serious seminar research papers (something like 4 a semester) my first two years of grad school, and then look back at them. Which papers did I enjoy writing? Which topics did I find I continually enjoyed circling around? What was the big theme that defined what I liked to work on? In the end, it was really damned obvious: I liked nuclear weapons topics and I liked secrecy in particular.

So I went to my advisor and I said, "I want to write my dissertation on the history of nuclear secrecy." And he said: "hasn't that been done?" And I said: "not really — I mean, obviously the theme comes up in other works on nuclear history, and people have touched on it, but there is no big 'history of nuclear secrecy' book out there, and that seems like something worth doing." The other question I got is, "can you even do this? Are there sources?" and from the seminar papers I knew the answer was, "well, sure, there are sources — and any topic is going to have some limitations on sources, I can just work around those."

Which is to say: I picked a relatively broad topic (it's not as broad as "the history of nuclear weapons" or "the history of secrecy," but it's also not as specific as a chapter or paper might be, like "the history of classification debates surrounding laser fusion in the 1970s"), one that touched on a lot of literatures but was also its own "thing," and didn't worry about the argument. The argument(s) came as a result of the research, not the other way around (it takes some faith in one's self to imagine finding new things to say, but we're all different scholars, so we all have something different to observe and talk about).

Anyway. This has been my go-to advice to grad students for a long time. Find a fairly broad topic that you find endlessly interesting. Because you're going to be stuck with it for a long time (much longer than 5 years, because you are going to be "that scholar" for many years afterwards, whether you like it or not). Don't worry about being overly clever about the argument. Don't excessively worry about "filling a gap in the literature" (as my undergraduate advisor once noted, "sometimes there is a gap for a reason"), though of course if one is going to tackle something that has been tackled a million times before, make sure you're bringing something new to the table. (Though if "a million times before" means no one has worked on it much in 20 years, that's a great opportunity — you have a built-in audience, and if you can bring something new to that debate then you get to "own" it.)

But my other advice is that you should write as many research papers as is physically/financially possible in your first two years of grad school (e.g., before you are technically "dissertating"). You can't really tell whether a topic is good, or fun, or enjoyable until you've tackled it in a serious way. There were some research papers I wrote than I though, "damn, I could write a whole book on this!" There were others (I'm looking at you, historiography of psychoanalysis) where I thought, "I will never think about this topic again." I tried a lot of different things, to get a real "taste" of research (some of my history paper topics: random number generating machines; how people have tried to visually depict how nuclear weapons work; nuclear weapon patenting policies; Polish nationalism and Marie Curie; latter-day readings of Freud's views of child abuse; cartographic representations of racial groups in the 19th and 20th century; the differences between the approaches of Charles Darwin and Francis Galton to problems of heredity and human society; invocations of the history of eugenics in discussions about the Human Genome Project; epistemological issues in using declassified documents... some of these panned out, some did not! One became [my first peer-reviewed publication](http://alexwellerstein.com/publications/wellerstein_patentingthebomb(isis).pdf), which was a good sign that I enjoyed working on it).

Finding a good topic is as much about understanding yourself as it is about the subject matter. Because you have to write it, in the end, not the discipline or the "literature." And you have to have some faith in yourself, in the end.

I learned Turkish which locked me into Turkey. I knew I wanted to study something having to do with religion, because that's what interested me since my first year of college. I thought probably something broadly about religion and politics. My first proposal was totally different from what I ended up doing: I wanted to study comparative secularism, and how the legal structures of secular states (Turkey, France, India) ended up benefiting moderate forms of the dominant religion, in part because of their assumptions of what constituted "religion" as a legal category. By ~2012, secularism was quickly becoming less important in the Turkish consciousnessness, fights over "pseudo-secularism" in India were fading, and Ahmet Kuru had written a book about secular governments comparing the Turkey, France, and the US. I explored other topics, like how people experienced "lived religion" and what religion meant to people in Turkish cities, but that became less interesting as well, because I couldn't get at what I wanted to with the methodology I had (I am a sociologist, so was considering ethnography). I eventually started thinking about the opposite of secularism in Turkey: political Islam. It's something I kept seeing in my everyday religion stuff, something that people kept bringing up, how Erdogan had "freed them" and let them be religious. This got me wondering about how this happened, where were all these religious voters before Erdogan and the AKP came in 2002? This led me to read a lot of old ethnographies to understand how Party cleavages used to be, which led me to 1) figure out how cleavages (i.e. political divisions) used to be, and 2) to figure out how exactly these cleavages shifted from an earlier set based on local networks to the present set based on religion and ethnicity.

So I have had three main topics: the first was based on first me hearing a friend describe her deep love for Turkish secularism and it sounded like a cult, I wanted to learn more. As I learned more, I saw this was a pattern not unique to Turkey but fit with other cases I knew. I dropped this topic as it seemed less relevant. Then I just started looking around at things I didn't know: all my friends were secular, and talked about the religious as a distant "them", so I became curious. I dropped this topic as it became unsatisfying. Then finally, I had a question I wasn't satisfied had a good answer ("how did this people used to vote?, and why do they vote this way now?") so I dove deeply into that.

I agree very much with /u/restricteddata about figuring out a broad subject that interests you, and I wanted to emphasize the other half of that: following your nose within that subject. I think Islam being more hireable than, say, Judaism, and religion and politics being more hireable than "everyday religion" did play some role in my thinking, but I also just ended up finding those more interesting: sometimes there are gaps in the literature for a reason, sometimes topics are hireable for a reason. I think being driven by things I had real questions (and eventually answers) about was a real benefit to me.

Could I piggy back on this to ask a vaguely related question? I'm currently doing a phd in cardiovascular science (in the UK for reference). We start working on our phd topic from the beginning of our PhD and spend 3ish years doing experiments and generating data and then normally 4/5ish months writing up at the end. Obviously a history phd is completely different though. How do you approach it? What's a normal day in the life of a history phd student?

To be honest, everyone comes to this in totally different ways. I would reiterate exactly what restricteddata said- if you approach this problem from the "what are the gaps?" mindset, you'll just disappoint yourself and get stressed, because you'll feel overwhelmed as you search your brain for a topic and then get disappointed once you start digging into the topic and realize that other things have been written about it.

Here's the other thing you have to keep in mind: sometimes a good topic is one that needs to be re-explored or reinterpreted. It's great to have a sexy thesis about an obscure topic, or an ultra-theoretical subject (the performativity and spatiality of the historical archive, just to make something up randomly lol) but sometimes people just don't care about that. Good questions are sometimes based on topics already explored. If you are interested in the topic, the quality of the research will naturally unfold and your interpretation/analysis will still have its own unique subtleties and differences. As you write, if you can find out what those subtleties are and then accentuate them and highlight them, you should be able to distinguish yourself from other scholars on the topic.

Like restricteddata, i began very broadly and then worked my way in too (history of republicanism in Spain). Lucky for me, I wanted to focus on its origins and beginnings and I was lucky enough that the topic had not been explored very much at all (which i found absurd, as that is a major topic in Spanish history). So, I was a bit lucky.

The key thing is to just read and read and read (which you'll do plenty of, believe me) and over time, it'll be easier to pick a topic because you'll get a sense of what you like and what you think you can do. You need to enjoy it, because writing a diss is tough work and it's no fun if you don't like the topic. And remember: a good dissertation is a done dissertation so don't feel too bad if your topic isn't the most unique thing in the world.

I found a source (by the vague process of interlibrary loans finding a book at sort of random) that intrigued me, and opened my eyes to a problem that historians hadn't dealt with recently. I couldn't understand the source I read, and thought it was important enough to spend time figuring it out.

I wrote up my problem, and granting agencies gave me scholarships for a few years to read archives in which I really explained that first source to my own satisfaction. I wrote an obnoxiously long dissertation, which I'm sure roughly 10 people read. I've never really done anything with that, but in the archives I found a bunch of other stuff, which has allowed my career to move forward.

I've never been motivated much by how my career might go. (I mean, if I'd have been a careerist, surely I'd work somewhere else than in a university. I could have traded bonds for a living, which would have been more lucrative than my current job.) I stumbled into something. I think it often works like that. Granting agencies, with their "motivate your interest according to the current intellectual fashion", are just a test of your basic creativity at bulllshitting, and putting forward an intellectually coherent program. Only academic administrators take them seriously, really, and most academic administrators are only respected by themselves. For the honest, get engaged in a problem, a source, or something else that catches your attention.

I'm sorta-kinda historian as I did my thesis in an organization science department. I was originally looking for a case that could illuminate a phenomena I was interested in (how constraints or scarcities influence the development of technology), and a professor in my department loaned me a book-length history of one invention that was supposedly born from such a scarcity.

I just sort of followed it from there, going through the same archive the book had used, and garnished it with material I was able to find from other archives.

1. Think of a place or type of place you'd like to work in. So, for instance, a country you'd want to live in for a few stretches, at least to start.
2. Cross reference that with places you have a comparative advantage, if at all present (language, people you know, friends/family who live there). Find ways to express those advantages in a professional-sounding manner, so that it's clear you have a way of getting things done in subject x in country y.
3. Figure out a way to bend that to a thematic focus that is interesting to you, enough so you can write about it and get into grad school with an advisor you want to work with (following the "what have they produced lately" rule to verify if they are still on things that interest you).
4. Change your thematic focus accordingly, as you find out things have been done or aren't what you really want to do. This last step sounds hard, but if you put in the time to your reading and writing in coursework, it will be apparent pretty quickly when you come across things that work for you.

The important thing is to find a way into the grad school/advisor relationship you want to be in, with the acknowledgment that it may be a temporary stepping stone to what you actually end up doing.

My rules were pretty pragmatic and simple:

1. writing a thesis will take a large chunk of my time and effort. what topic Im sufficiently passionate about to sustain the effort?

2. Almost all interesting topics are already milked dry. What topic can i pick that was not done over extensively, yet there is enough data to use for a thesis?

3. Will the topic I picked spark academic interest, popular interest, or the interest of my promoter? (At least 2/3 of those must happen).

4. Is there a way I could expand the topic of my thesis into a publishable book, a series of lectures, or in other way leave an academic legacy out of it? Or is it a dead end?

By far, the greatest two strategies on how to improve the research for my thesis was sharpenning my internet-skills (you would be surprised how many historians fail to use Google to its full potential) and trying my best at learning the basics of the most common academic languages: Latin, English, German, Russian, and enough French/Italian to at least pick on the key words. There IS literature and artefacts and iconography to fill the gaps in your initial research, but its often 3 translations away and at the page 7 of your Google search.