How to Win the Nobel Prize and Change the World

This book has aimed to point you towards skills and habits that can make your creative research career more successful and, just as importantly, more satisfying. The motivations people have for pursuing research vary widely. It is rare, however, for researchers to devote months or years to a problem that they know is obscure and to hope that no one in their professional community or elsewhere will ever care about their results. Instead, almost every researcher hopes that someone somewhere will care about their work and perhaps even use their results in a positive way.

The ideas in this concluding chapter are adapted from the book A Beginner's Guide to Winning the Nobel Prize by Peter Doherty, an Australian immunologist who shared the Nobel Prize in Medicine in 1996 for his work on how our immune systems recognize and act against viruses. The chapter title is a deliberately inflated version of Doherty's tongue-in-cheek book title. In his book, Doherty points out that he can't actually tell anyone how to win a Nobel Prize, although (unlike me) he can at least talk about the topic from firsthand experience. Hopefully, you will keep reading even with the caveat that the title of this chapter shouldn't be taken too literally.

Peter Doherty was born in 1940 in Brisbane, Australia. After attending his local public high school, which shared a tongue-twisting name with the suburb of Indooroopilly where it is located, Doherty studied at the local university to be a vet. Developing an interest in research, he moved to Edinburgh in the UK to complete a PhD. In 1970, he returned to Australia to do postdoctoral research. It was this work, performed within just a couple of years of his PhD, that won Doherty and his postdoctoral supervisor, Rolf Zinkernagel, the 1996 Nobel Prize. Just like Fiona Woods, who we met in Chapter 1, Doherty was chosen as Australian of the Year, in his case in 1997.

Doherty's book and the title of this chapter use the idea of a Nobel Prize as a shorthand for work that has long-lasting significance and meaning. In scientific publishing, the term "impact" has taken on a narrow meaning associated with the number of times a paper is cited in a short period after it is published. Many scientists use the resulting "impact factors" to help decide which journals they want to publish in. Instead of fixating on the number of citations a paper gets, I urge you to think about the impact of your work using the everyday meaning of this phrase. Will your work change how people in your field think about something? Will your work be useful in some way to people outside the tiny group of people studying your specific problem? Does your work spark creative connections that allow someone to solve a related but different problem? These kinds of questions are the real measure of impact, and they point to impact being hard to quantify and taking place over long periods of time. The more than 20-year delay between Doherty's postdoctoral work and his Nobel Prize is one example of this time lag.

The discussion above about significance and impact centered on achieving these goals in your research. There are also many professional and personal activities that are significant and impactful without being centered on technical outcomes of research. Your research might train undergraduate students in careful work and logical thinking, skills they go on to use in a broad range of careers. You might devote your energy and talent to advancing education or life prospects for a community who is traditionally disadvantaged. Your training might allow you to become involved in influencing local or national government policy. All of these areas, and others you can probably add to the list, have the possibility of leading to real significance and impact. Many of the research-motivated ideas we explore in the rest of the chapter are also highly relevant to non-research endeavors.

Try to Solve Major Problems and Make Big Discoveries

Doherty's first piece of advice seems almost tautological: if you want to make a lasting impact with your research, work on an important problem. This advice is not just a Zen Koan from a master researcher; it can be a helpful way to frame the choices you must make about problems you could work on. This advice forces you to think about what makes a problem important. One way to address this issue is to imagine that your specific research project is completely and wildly successful. What would this look like? Whose lives or future work would be influenced by your research results? If this daydreaming exercise convinces you that your project has enough potential upside to be worthwhile, then it is also healthy to imagine what problems could stand in the way of that success. If the most positive outcomes you can dream up even as a wild-eyed optimist seem limited, perhaps the project isn't attacking what Doherty calls a "major problem".

In the early 1980s, it was accepted wisdom that ulcers were associated with high-stress hard-charging lifestyles. To give just one pop culture example, one of the Madison Avenue executives in Mad Men is depicted as suffering from an ulcer, which he and his doctors assume is from his lifestyle. In 1982, two doctors at a hospital in Perth, Western Australia, Barry Marshall and Robin Warren, had a startling idea; they suggested that ulcers were caused by a bacterial infection. Let's evaluate the value of doing research on this idea from the "importance" metric outlined above. If the research was wildly successful, there is no doubt that many people would benefit, so from this perspective, it was potentially a worthwhile problem. At the same time, however, finding something that overturns many decades of medical wisdom seems exceedingly unlikely. Marshall and Warren submitted a paper with some preliminary results to an obscure Australian medical conference. The paper's reviewers ranked it in the bottom 10% of papers for the year, and it was rejected.

Despite the initial lack of enthusiasm for his work, Marshall remained convinced that it was worthwhile exploring the connection between bacteria and ulcers. In 1984, he performed an experiment that surely would not be approved by any present-day ethical review board by drinking from a Petri dish in which he had cultured Helicobacter pylori (H. pylori). Within three days, he developed nausea and his mother noticed another symptom of digestive problems, halitosis. Just a few days later, Marshall experienced vomiting and severe stomach inflammation. After waiting another week and enduring an endoscopy that showed H. pylori had infected his stomach, Marshall started taking antibiotics. This dramatic experiment gave direct evidence that gastritis could be caused by bacterial infection, that is, that gastritis was an infectious disease. This insight revolutionized the treatment of gastritis and ulcers. In recognition of their work, Marshall and Warren were awarded the Nobel Prize in Medicine in 2005.

Medical breakthroughs such as the work of Barry Marshall and Robin Warren are appealing in part because their impact is easy to understand. Most research, including most biomedical research, has impact is less obvious ways even when it is successful. Doherty's advice to "solve major problems" can nevertheless be helpful in setting long-term goals for your work. Like "write my thesis", "solve a major problem" is not a useful item to put on your daily to-do list. As with any significant long-term goal, breaking the overall task into well-defined actions is critical to connecting your ambition to make big discoveries with the day-to-day realities of creative research.

 
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