How to Write an Academic Paper

People write many different kinds of things. What you write, and for which audience, will vary and the advice given to writers varies accordingly. The pieces of advice that follow below refer to the kind of writing we do at the university. What concerns us is how to write essays, theses and academic papers. Or, slightly more pretentiously put, we are concerned with the question of how to do research. A paper for an undergraduate class is just the beginning, and much of the advice below can for that reason appear slightly overblown. Come to think of it, that is probably the case. At the same time, it is good to understand the process since it is the same for all kinds of research, from the very first term-paper to PhD dissertations and on to those seminal tomes which senior scientists produce in mid-career.

To write a thesis at a university is to enter a new and at first rather intimidating world. Previously, if you had a question, you would simply look up the answer on-line or search for it in a book. Yet as a researcher your task is to transform yourself from a consumer of knowledge to a producer. You will become an authority and your own source of information. To be an authority and a source of information is a great responsibility. It is a pretentious and perhaps slightly scary position to be in, but it is also very exciting. If you have problems presenting yourself as an authority, you must begin by pretending. After a while you will start to believe in your own hype, and before long you will be able to hold forth with authority on most issues. Welcome to our world!

There are of course many kinds of research and also many kinds of academic papers you can write. Researchers have different goals. Sometimes they primarily want to describe something. To describe something sounds like a fairly easy task, but that depends of course on what you want to describe. When Galileo Galilei in 1609 observed hitherto unobserved heavenly bodies through his telescope, the first and most obvious questions was what he had seen and how to describe it to others. This was clearly not that easy to do. But it is also possible to describe the already well-known in new ways – and that is not easy either. Consider the task that Adam Smith set himself in The Wealth of Nations, 1776, where he presented the economic market as an independent system governed by its own laws. No one had previously described the economy that way. The challenge was to convince others that they should look at the world in a new fashion.

But most research concerns not descriptions as much as explanations. Research is a question of understanding things that have not been understood before; of finding out why things are the way they are and work the way the do. Really good, really fascinating, research is organized like a detective story. In a book by Agatha Christie there is always a person found dead in the first chapter — often a young, scantily clad, woman on the floor or a library. Two questions present themselves immediately: who killed her and why? The rest of the book is then concerned with finding the murderer and the motive. Nothing else matters. Since we always know what detective stories are about, they are easy to read. Together with the detective you simply put the puzzle together. Detective stories are also easy to write — Agatha Christie used to write two or three per year.

A good academic paper should be like a detective story. In the first paragraph there should be a body in a library. The reader, that is, should be introduced to something strange, something that needs to be explained. The rest of the paper should then provide the explanation. Nothing more, nothing less. In this way both the author and the reader are perfectly aware of what the paper is about, and the paper is finished when the question has been satisfactorily answered. In the conclusion, at the end, the researcher gathers all the facts pertaining to the investigation for a final encounter in the library, where he or she goes through the case again, and identifies, to everyone’s amazement, the most important causal variables.

There is thus a great difference between a research topic and a research question. The world is full of topics and as human beings there are always a lot of things that interest us. But you cannot do research on a topic. Topics are too big; they never really start anywhere and they never really end anywhere either. One topic relates to other topics and writing about it we will before long end up with a gigantic topic-web where everything is dependent on everything else. If you try to untangle this web you will become hopelessly confused and you will never be able to finish. There are pathetic examples of scholars who failed to understand this and who write volume after colume before they realize that their lives are too short to finish what they have started.

A question does not work that way. A question you pose and then you answer it. And when the question is answered, the research is done. This is why it is important to formulate the question well. A well-formulated question is a question that can be answered, and hopefully in an interesting way. A badly formulated question is a question that pretends to be a question but which actually only points to a topic. If you are a Ph.D. student this provides a great opportunity to save years of work. The better the question you are pursuing, the sooner you can finish your dissertation and get your life back.

Unfortunately it is quite difficult to formulate good research questions. In many ways this is the most difficult part of your work — representing, perhaps, something like 50 percent of the overall effort. I have written books where it has taken me years to understand what I actually wanted to know. You write and write and since the text grows longer you think you are making progress, but actually you have no idea where the whole thing is going. When the question finally comes to you, it is embarrassing to acknowledge how lost you have been, but it is also wonderful to know that the right path lies straight ahead. After that the work proceeds quickly. It is easy to write once you know what you are doing.

In that respect, writing an academic paper resembles giving a speech in front of an audience. If you have something to say, an hour can be short and it is easy and fun to talk. But if you have nothing to say, even two minutes can feel like an absolute eternity. For paper writers too it is essential to win and keep your audience. Compare the working conditions of a stand-up comic who only has a few seconds before the rotten tomatoes start to fly. And once you have lost your audience, it is next to impossible to win it back.

The audience for your academic paper is most likely your supervisor or examiner. Unfortunately, supervisors and examiners are human beings, and this means that they too are likely to have rather limited attention-spans. Moreover, they often have a big pile of papers on their desks and only a couple of hours to read and assess the whole thing. Often they make up their minds very quickly regarding what sort of a paper they are reading, perhaps after reading only a few pages. Of course research should not be judged on such a flimsy basis, and maybe you are lucky and will find a supervisor or examiner who has more patience, but it is a mistake to trust this to be the case.

So why not make it easy for the reader? Make clear already in the introduction to the paper that you are worth listening to. Start by saying what you really have in mind. Put the best points first and use the rest of the paper to explain, deepen and clarify your argument. A “historical introduction” may be useful of course, but chances are that it is not, and in any case it slows you down and makes you lose focus. And do not try to bulk up your paper in order to reach the required word length. Word lengths are bureaucratic, not intellectual, requirements. Good papers are never too short but always exactly the right length. They finish when they have done what they promised to do. They end when they have answered the question they set out to answer. And once you have made your argument, there will always be something you can add to make up the missing words.

And, speaking of supervisors and advisers, you should not make the mistake of taking these job descriptions literally. Although the idea of being “supervised” can sound slightly intimidating, chances are your supervisor cares about your work far less than you think. Similarly, the pieces of advice which advisers give you will not necessarily be all that helpful. It will not take long before you are more of an expert on the topic than your adviser is. It is you, after all, who is doing the research. It is lonely to write things and it really helps if you like your own company. Not everyone is suited to become a researcher, and that, come to think of it, is probably a good thing.

So what do you need to do in order to come up with a good research question? Well, somehow or another you need to learn how to construct problems; that is, learn how to problematize what you see around you. And in order to problematize something you must wonder, and worry, about it. One of my teachers, a very famous American political scientist, used to say: “The problem with students these days is that they read too much. They don’t think!” What he had in mind, I think, was that reading can turn into a pretext for not doing what research really should be about — posing questions and answering them. To read is hardly better than other things that researchers do when they prefer not to work — like gossiping about students or checking how popular they are on Google Scholar. Yet a great advantage of problematization as a research activity is that it can be carried out whenever you have a few moments to yourself — when you are on the bus, say, about to fall asleep or when you suffer through a particularly boring lecture. Switch off the phone, switch on your mind, and just think! If you are lucky, and persistent in your wonderings and worries, you will come up with something that no one else has wondered or worried about before, at least not in the same way. If this is the case, chances are your subsequent research will constitute an original contribution.

It might seem obvious, but the point is easily missed — never write about a question you do not want to find the answer to. If you do not genuinely care about the answer, chances are no one else will care either. The best research questions are simple and obvious and they often sound naive, at least at first. If your question is unclear, ambiguous, or contain more than two qualifying sub-clauses, it is probably the wrong question. Change it to something you can formulate in a more straightforward fashion.

The best questions are always the ones that children ask. Children are good at noticing that emperors have no clothes and they often point to things that grownups miss. The best research questions are childish ones and they constitute a sort of discovery. They require a new way of looking. Children ask good research questions since they have their own, not the grown-up, view of the world. Don’t be afraid to be childish!

I once traveled between Singapore and Laos together with my children. Despite the fact that the two countries are located in the same part of the world and share some historical and cultural influences, they are worlds apart. Singapore is one of the richest countries in the world and Laos is one of the poorest. After having walked around Vientiane, the Laotian capital, one afternoon, my oldest daughter asked: “Dad, why are people so poor here?” That is of course a great research question. Why indeed are people so poor in Laos and so rich in Singapore? There must be some reason but what could that reason be and how would we find it? The Chicago economist Robert E. Lucas asks himself the same thing as my daughter. Is there, asks Lucas, some measure a government can put in place in order for countries that grow slowly to be able to grow at the same pace as those that grow quickly? If so, what would those measures be? And if there is nothing a government can do, why not? “The consequences for human welfare involved in questions like these,” as Lucas puts it, “are simply staggering: once one starts to think about them, it is hard to think about anything else.”

Robert E. Lucas is a Nobel Prize laureate and clearly pretty obsessive about his research. Most people prefer not to worry about matters such as these, or they trust that there are others who know the answers. This is what makes researchers different from other people. Researchers are people who are kept up at night by their research questions and they never trust that others know the answers to them. Having a research question on your mind is like having a rash. It itches and itches and you cannot stop yourself from scratching. Research, in the end, is nothing but intellectually motivated scratching. Looked at in this way, research might appear as a ridiculous and perhaps as a pointless activity, but try not to itch if you can. After a while you go completely mad.

If you do not know what to write about — and few students do when they start their work — it might help to look for a pattern of some kind. Compare how something varies over time or varies between two cases, countries or regions. The pattern you discover in this way will often need an explanation and the explanation is what your research paper will supply. The simplest way to go about this is to look for some piece of statistics. Why did Chinese export grow so dramatically after 2001? Why is Vietnam attracting more foreign investments than Burma? Why are Finnish schools better than Swedish and the French health-care system cheaper than the American? It might of course be rather flatfooted to only occupy yourself with numbers, but the numbers necessarily require an explanation which is qualitative rather than quantitative. The numbers help you identify puzzles which your research goes on to solve.

There is a very simple way to find out whether you have found a good research question or not. When  a fellow student in your dorm, or perhaps your mother, asks you what you are writing about, let them know. If you can explain yourself in a simple and comprehensible fashion, you probably know what you are doing. And when you explain yourself, look at their eyes. You can always tell from the eyes of a person if they are interested or not. Really good questions will make their eyes light up. Bad questions, on the other hand, make their eyes glaze over. If your friend or your mother then adds something to the effect that “that sounds really interesting,” you know for sure that you are on the wrong track. Good research questions are not “interesting,” they set your mind on fire.

I have stressed the importance of a research questions since everything else involved with the writing of an academic paper follows from them. The rule is simple: it is only that which helps you answer your question that should be included in the paper, everything else you can leave behind. Take the use of sources. There are different kinds of sources — texts, statistics, interviews, artifacts, and so on — but what counts as source material is entirely determined by the question you ask. Web-sites filled with celebrity gossip are not normally regarded as the best sources of knowledge about the world, but if you ask a question concerning how the notion of celebrity has changed in the course of the last century, they will become an important primary source. It is the question, that is, that determines the status of the source and nothing inherent in the source itself. The question will take you to the source and the question will determine how you use it.

In general it is difficult to write about very big questions. Big questions are inevitably complex and have too many aspects, variables and causes. It is a lot easier to write about small questions. The only problem with small questions is of course that they can be quite irrelevant. The best questions are for that reason small but significant. A small but significant question is a question that has a relevance far beyond the material that it asks you to investigate. In one of my books I tried to explain why it was that a combined Anglo-French army, in the year 1860, decided to destroy the palace of the emperor of China, located just north-west of Beijing. The event as such might not have been all that important, but by explaining what the Anglo-French army did it is possible to understand a lot about European imperialism in China, and in other places too, during the nineteenth-century. In fact, I even argued that my research can help us understand U.S. attitudes towards Iraq and other countries the Americans have invaded. Perhaps I exaggerated. I probably did. But I still believe my question worked well – it was relatively small and thereby easy to do research on, yet it pointed to something big and important.

The same conclusions apply when it comes to the choice of “methods” and “theory.” Scientific method concerns which procedures we should employ in order to find an answer to a research question. The choice of procedure will for that reason always be connected to the sources which our question has helped us identify. Some researchers prefer certain kinds of methods; some are stats jocks while others advocate historical or interpretative approaches. But this is just another way of saying that different researchers pose different kinds of questions, questions that forces us to rely on different kinds of methods. Yet it is not possible to say, in a general way, that one method is better than another. It all depends on what it is that we want to know.

The same argument applies to the question of “theory.” Students are often stressing themselves out regarding “theories” — what they are and how they should be used. Theory sounds complicated and it is theory, we are sometimes told, that distinguishes academic writing from all other kinds of writing. In order to be scientific — in order to sound smart — “you have to have a theory.” Usually students are introduced to the theories they can choose between already in their introductory classes when they learn how various famous researchers have gone about explaining the world. The study of international politics provides an illustration. Here there are Realists, Pluralists, Idealists, Liberals, Constructivists, Feminists, Structuralists, Post-structuralists, Marxists and a large number of other -ists, and all their writing seems to take place within one or another of these intellectual camps. To write theoretically thus becomes to adopt one of these perspectives. We chose a theory much as we chose how to dress ourselves in the morning or decide what to eat for dinner.

But this is not how it is supposed to work! A theory is not something that we choose separately from the questions we ask. A theory is like a tool which allows us to carry out a certain job. One theory can be like a hammer, another like a screwdriver or a saw. If we want to build a bookcase we should not use a pneumatic drill, but a pneumatic drill will be very useful if we want to redo our driveway. In exactly the same fashion, the questions we pose will determine the theory we need to rely on. And in many situations there are several theories that might fit the bill. In that case, we test the alternatives against the data we have discovered. A person calling herself a Realist, Pluralist, Marxist, Feminist or whatever, is a person who only can think in one fashion. For a person who only has a hammer, everything looks like a nail. Such a person lives in a very limited world. Such a person has a problem. Good research forces us to think in many different ways and to use many different kinds of tools. Often at the same time.

But this is nothing to lose sleep over. Try instead to simply forget what they taught you regarding “theories” in your methods classes. And you should under no circumstances add “theories” to your work in order to sound more “scientific.” You do not sound scientific as a result, only pretentious and a bit daft. Instead, go back to the question and start there. When you have found your dead body in the library, look for the kinds of intellectual tools that can help you catch the murderer. Once you do this, the theoretical arguments will come flowing back into the analysis by themselves and without you having to worry about it. Theory is nothing but another name for thinking, after all, and once you start thinking seriously about your research question, you will come to theorize without even noticing it. When you finally have provided your explanation, and everyone is happy and convinced, there is nothing more for you to do. Adding more “theories” will not make the paper better, it will make it worse.

There is, we said, no essential difference between the kinds of questions that researchers ask and the questions that normal people, or children, ask. We now understand that there is no essential difference between the answers researchers and normal people come up with. The difference is rather that research has to be much more carefully executed. Good research takes into consideration more information, more alternatives, and it is always subject to criticism from other researchers. We draw conclusions on certain grounds, but the grounds must be exposed so that they can be criticized by others. This makes research into something different than beliefs, which need no proofs. It also makes research different from mere opinions, which are based in a certain person’s outlook on the world. Good research gives better answers than what normal people provide, but the answers are not of a different kind.

I sometimes say that I do research since I never could deal very well with intoxicants. Just like intoxicants, however, research has the power to alter your understanding of the world and it can also make you feel very good about yourself. Suddenly you realize something that no one else has realized before. As a result you feel not only smart, but invincible. You rule the world. But before long the buzz will always dissipate and you are left with a headache, and your usual self-doubt, and then you realize that the deadline for the paper is tomorrow and in the end you are happy just to hand in the damn thing. But of course research is never actually about you. Instead it is always a collective enterprise. Everything we do, and ever can do, depends on the contributions of others. Research is also one of the most noble activities in which you can engage as a human being. It is a matter of our desperate attempt to explain and understand the world we all have ended up in. As a researcher — even as a writer of an undergraduate term-paper — you are a part of this great, shared, all-too-human, project of exploration. Research takes place elsewhere in society too but it is only at the university that research is a main preoccupation. So why not take the opportunity to write a really good academic paper?

Erik Ringmar, Ibn Haldun University, Istanbul, Turkey.

Read more:

Collingwood, R. G. An Autobiography. Oxford: Oxford University Press, 1978.

Lindblom, Charles E. Inquiry and Change: The Troubled Attempt to Understand and Shape Society. Yale University Press, 1992.

Lucas, Robert E. ”On the Mechanics of Economic Development,” Journal of Monetary Economics, vol. 22, no. 3, 1988.

Polanyi, Michael. Tacit Dimension. Peter Smith Publisher, 1983.

Popper, Karl R. Conjectures and Refutations: The Growth of Scientific Knowledge. London: Routledge, 2009.