Part One: Defining Your Project

You of course will be working on a project, and whatever it is, in your project you have to launch a two-pronged attack on your subject. You must make both a conceptual effort and an empirical effort. These two parts of your work feed off of each other, since the thinking defines what you want to look for in the way of evidence, and serves to draw out meaning from the evidence you see, while exposure to the evidence often serves to focus and redirect your thinking. Although the two sides proceed hand in hand, there is bound to be a heavier emphasis on the conceptual side at the beginning of a project and on the empirical side in its later stages.

How do you go about choosing a project? Your project should develop out of a concern with the biggest issues; you have to think about them in a serious way, and a project develops as a specific way to get a handle on the issues you are interested in. So you have to get your thinking about those fundamental problems to start moving, but how do you do that? In principle, the answer is simple enough: you basically start with the biggest questions--what makes for war, or for international stability in general?--and gradually move down the ladder of concreteness: how do you account for the coming of peace, at least among the great powers, during the Cold War period? What, you are then led to ask, was generating the conflict in the first place? What issues are so important that people could conceivably risk going to war over them? And this directs you to yet greater concreteness: the German question, the China question, the nuclear question, etc. And then, as you start to learn about these issues, you ask increasingly specific questions: what was going on in the Taiwan Straits Crisis in 1954-55, or with German rearmament around 1950? Why was this very specific thing done, or that? If policy shifts, the problem is first to nail down exactly how it shifts, and then explain why it shifts. You now have questions narrow enough to be studiable. Moreover, by having these specific problems result from a thought-process of this sort--that is, by having established a linkage between great issues and very specific historical problems--you guarantee that the conclusions you reach from studying these concrete issues will have some bearing on the much broader questions. In other words, you automatically endow your work with real meaning, and you avoid the great sin of "antiquarianism"--i.e., luxuriating in the details of the past for their own sake. For an example of how to do this, take a look at the first three pages on my piece on the July Crisis in my book History and Strategy.

In other words, you keep your eyes on a problem or set of problems; you are not just choosing a topic. Your research effort is then question-driven. This has the effect of providing some guidance for you as you go into the sources. You are not just plunging into an enormous ocean, but you are looking for very specific things: namely, answers to questions. Please pardon this series of mixed metaphors, but it's like a chemical stain drawing out what's important in a biological specimen: the relevant material is thrown into relief, you can separate the wheat from the chaff (so you don't have to waste a lot of time going through garbage)--in short, you have some mastery over the great body of material with which you are confronted.

Also, approaching things in this way--not as the gathering of material on a topic, but as the targeted and systematic answering of a set of questions--will naturally shape the structure of the final product that will emerge from your work. By answering questions--the answers to which are not obvious in advance--you will be making your work interesting to the reader. You will be dramatizing what is important about it, why it is worth the reader's time to go through it. You will be making it possible for the reader to assimilate your findings. I'll be talking more about writing later on, but for now let me just say that it's vital that you take effective presentation in this sense as one of your primary goals, since over and over again prodigious research (as reflected in Ph.D. dissertations) is wasted because of an author's inability to present work effectively--that is, because an author has been poorly taught and simply overwhelms the reader with detail, instead of constructing an argument, where detail is cited only to the extent that it is needed to support conclusions.

But if this is in theory the way to go--that is, concerning yourself with the biggest issues, and working down the ladder of concreteness until you have something studiable--the fact remains that it's often very hard to do something like this entirely on your own. After all, it's not like you're the first person ever to think about these issues, and it would be foolish not to pay attention to what other people have had to say about these questions, and how they have gone about trying to answer them. And indeed it's very to think through these big issues in a kind of vacuum.

In fact, you never do historical work entirely for yourself. Scholarship is a social process. It's standard practice to draw on, and to react to, other people's work. You read the historical literature in this area. Sometimes you read things you fundamentally disagree with. Sometimes you're just uneasy with a given line of argument. It strikes you as too facile, too simple. But how do you go about sorting out the issue--that is, how do you draw out the question in such a way as to make it studiable? I once had a student who was uncomfortable with the argument I made (in the "Wasting Asset" piece in the History and Strategy book) about the link between the shift in the strategic balance from 1950 to 1954 and the toughening of American policy across the board--on Berlin, Korea, Indochina and so on. This whole argument struck him as too pat. To test the interpretation, I suggested that he look in detail at U.S. policy on some regional question I had not examined--e.g., Yugoslavia, or Turkey, or Iran. What would the U.S. have done if push came to shove and the USSR had attacked one or another of those countries? If I was right, the Americans would have been very cautious in 1950 and much tougher beginning in late 1952. If I was right, the toughening of U.S. policy should have preceded the change of administration in January 1953--implying that the shift was structural, and not just due to the change in personnel. If there was no major change, or the change only took place when the new administration took office, then my interpretation would have been questionable, and his initial misgivings would have been borne out. But if I turned out to be correct, he would have been able to see for himself that the interpretation I had laid out had real explanatory power. And the issue had been framed in such a way as to become studiable. In this way, someone else's interpretation can become a kind of springboard for your own work.

And it's not just historical work that you should be reacting to. You read works by economists, or by journalists, or especially by political scientists, that relate to what you are concerned with. What questions are they interested in? What insight does that work give you into the big issues? You don't have to agree with what they say to find this work of value. Often, it's the process of coming to terms intellectually with work you don't agree with, and trying to figure out why exactly you think other people are wrong, that's of greatest value. In particular, when you don't agree with something, it's useful to think about whether it's possible to have an empirical test whose outcome will show who's right. If no such test is possible, then you have to wonder whether there's anything real in dispute, or whether it's just an argument about words. But if you can set up an empirical test, the outcome can be quite revealing, especially if it turns out you were wrong. This was my experience, for example, in doing the work that led to the "Wasting Asset" article. I was reacting to certain basic claims that some of my political scientist friends had made, and it turned out (to my amazement) that they had been right and I had been wrong. Incidentally, everyone interested in this general subject should read Thomas Schelling's Arms and Influence at least once, and also Robert Jervis's "Cooperation under the Security Dilemma" article (from World Politics, January 1978), although I think a deeper understanding of this body of literature is extremely valuable. Again, for a little example of how references to this literature can help frame and orient historical study, let me cite a passage from my own work, the first few pages of my piece on the Cuban missile crisis, also in the History and Strategy book.

There's a method for "processing" this literature--that is, both the historical and the more theoretical literature--and this is the method that should be used with certain types of source material as well. This is the method of critical textual analysis. When I say that it's essential that you approach your material critically, I am not saying that you should be hostile to what you read. The point of the method is not to be nasty, but to be able to assess these writings--to draw out what is valuable and at the same time identify what is defective in what you read--and to do this much more rapidly than would be possible if you processed this material in the more normal way. People have been programmed from the first day they enter kindergarten to believe the things they read--to start at the beginning of a text and to read through to the end, absorbing as much of it as they can. Students, in other words, are programmed to be sponges: think of how the lecture system works in higher education. But one simply cannot believe what one is told on faith. Moreover, one cannot appreciate what is really good in a text if one reads it passively; indeed, what is excellent about a particular piece of work only becomes clear after you've seen writers dealing with similar, and especially with related, topics producing work that is defective in one way or another. When you do this sort of thing, in other words, you're developing a set of values about what constitutes good as opposed to bad work that you can then internalize and apply to your own work: "so and so has screwed up in such and such a way, and I'm not going to do that," and "boy, this is really good for the following specific reasons, and I'm going to try to do things like that, I'm going to add that to my own intellectual equipment." These things will carry particular weight because they're concrete and specific. If you do this enough, the general points--that is, the general, internalizable, values--will take shape in your mind more or less automatically.

It is therefore absolutely essential that you learn to read actively and not passively. The method is in principle simple. You take a text and ask: what is the author driving at? What is the point here? Does this text have a thesis--that is, a core argument--or is it a kind of mindless narrative with no point at all? If there is an argument, what is the key evidence cited in support of it? Does that evidence actually prove the point it is supposed to prove? Or is there no real evidence at all--is it just an argument by assertion? Is the argument of the text internally consistent--i.e., what do you make of its logic? And to get at the thesis, you look first at the key places where an author shows his or her hand: the introduction, the conclusion, the chapter titles, the title and subtitle of the book, the first and last paragraphs in each chapter, the first and last sentences in each chapter. Read these things first and ponder their meaning. Think also about how the various claims made add up to an overall argument--how a general thesis rests on a few key subarguments. In other words, what is the architecture of the argument? Then, looking at the table of contents, try to figure out where in the text one is likely to find the strongest proof of these central claims, and read those sections with great care, trying to figure out whether the basic conclusions are supported or not, but skimming over material that is irrelevant to the analysis of these central claims. This technique, which you can only develop through practice, will prove invaluable as a way of gaining mastery over these texts. It will also result in a great saving of time and energy for you.

In the process of doing this reading and thinking about a general problem, certain narrow problems naturally emerge. One of the key issues, for example, in the interpretation of the Cold War has to do with nuclear weapons. How real was the nuclear threat? To what extent, in what sense, and in what way, did this form of military power weigh on international political life? Massive nuclear arsenals were of course built, but would nuclear forces ever have been used? The question can be "operationalized"--i.e., made studiable--by focusing on the Eisenhower period. Eisenhower, at the level of rhetoric at least, placed a heavier reliance on nuclear weapons than any other American president, but how seriously is his strategy of "massive retaliation" to be taken? Some scholars find it hard to believe that any American president, under practically any circumstances, would have ordered a full-scale nuclear attack on the Soviet Union, except perhaps in retaliation for an all-out attack on the United States itself. They sometimes argue explicitly that the Eisenhower strategy was ultimately a gigantic bluff. Is this claim correct? How does one get to the bottom of this fundamental issue? The best we can do is to focus on the Eisenhower administration's behavior in a crisis--the Berlin crisis, for example. Would the U.S. government in 1959 really have resorted to nuclear escalation if the crisis had come to a head and if that was the only alternative to capitulation? You might not be able to reach an answer with anything like absolute certainty, but if you have access to enough evidence, you can always say more than zero, and sometimes a lot more than zero; that is, you can form an opinion on the subject which you can hold with a certain level of confidence, and which certainly goes well beyond pure speculation. But it is the method, and not this particular issue, that is important here: what you are doing is zeroing in on a specific historical problem as a way of getting a handle on the great issues that you are interested in sorting out.

Go to Part Two