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Education and outreach

Courtesy: Peter Ginter/Superstock
12 Oct 2017
Taken from the October 2017 issue of Physics World

Philip G Judge, Isabel Lipartito and Roberto Casini share their thoughts for the budding research scientist, on how to choose meaningful research

Being an academic researcher and studying the natural world is a rewarding and unpredictably productive quest. But, as is true with most things, it can be difficult to sculpt a fruitful career if you are unclear of the research landscape or of your own motivations. If you are considering becoming a professional researcher, then it’s vital to know what the scientific pursuit involves, what it means to be an academic today and, most importantly, what field of study you are most inclined towards.

As a newly qualified academic, picking your first major project can be a daunting task. Are you to simply accept the wisdom of a potential adviser? Most of us do precisely that. But make no mistake, the first research project you pick will often determine the trajectory of your career. Much is at stake and the choice is never easy. Indeed, this is more true today than in the past. As is the case with many other vocations, scientific research is changing in response to powerful external influences. From societal pressure to deliver something “useful”, to public scrutiny and scepticism fuelled by social media; from the denial of facts in favour of opinion, to funding agencies that demand “deliverables” – it can be a balancing act as you try to pursue your scientific goals while also measuring up to various standards. Indeed, picking the right field, and then finding a meaningful project, is no mean feat.

Every researcher hopes for a career that is based on sound foundations, but also includes a chance of making genuinely new discoveries. In its purest form, scientific study has the simply articulated goal of seeking a better understanding of nature. Nothing else is necessary, unlike technological research, whose goal is to develop better technology. What, then, makes something “scientific”? The ability to experimentally test a potential idea is paramount. Whether it is a physical experiment that you carry out, or a gedanken (thought) experiment that you propose, these are imperative to identify an acceptable theory. So, something counts as “science” when an idea is tested via experiment, pitting it against the real world. Your theories must also be refutable; for if they are not, they are often considered as unscientific (though some believe this “Popperian” view to be too stringent.)

As a researcher today, it’s also highly likely that your experiments will use computational methods. Some numerical experiments, which involve testing hypotheses against computer-generated data, have led to major discoveries (for example, in the field of nonlinear dynamics). Other numerical approaches seek to simulate data for comparison with real data. Computer-generated data have obvious limitations, but so do experimental data. Real experiments are limited by circumstance – we do not live long enough to witness a galaxy merger, or watch the lifecycle of a star or, for that matter, even the natural evolution of large animal species. On the other hand, numerical data are not on the same footing as actual data, if only because current computers always return deterministic solutions. Before quantum computers arrive, we can in principle never simulate reality.

As history has shown, many exciting discoveries – from penicillin to dynamite – have been made through mistakes and blunders. A good research environment will implicitly give permission to fail, at least some of the time. Mere curiosity has led to discoveries of semiconductors, the laser and nuclear magnetic resonance, all of which have revolutionized the modern world. Curiosity-driven research without foreseeable outcomes must remain an imperative. Nobel prizes have been awarded across the spectrum of both curiosity-driven and goal-oriented work.

Another lesson comes from Thomas Kuhn who, in his 1962 book The Structure of Scientific Revolutions, argues that advances occur mostly through “incremental science” or modest changes to existing ideas; until a discovery is made. Such a discovery will eventually overthrow a previously accepted framework, creating a “paradigm shift”. Very few professional scientists get to change paradigms, but you should strive to do just that. Unfortunately, though, this idealistic viewpoint is certainly naive, as very few organizations would fund research that plainly states this as a goal.

Funding organizations naturally tend to promote research that makes use of facilities (experimental and computational) and tools previously developed at great expense. So, potential scientists should be aware that the motivation behind their project might be more tool-driven than question-driven. Today’s entire academic environment is optimized to make incremental advances. Risk-averse work attracts funding, and publishing such work is easier than publishing genuinely new ideas, which receive harsher scrutiny. Both accolades and tenure are awarded for having a large number of publications under your belt, a metric that is used to attract further funding…and so the cycle continues. Rarely does a scientist with just one paradigm-changing paper compete in this environment.

But to make research stand out among peers, young researchers should ensure their choice of project allows for some genuinely new work. An element of risk is necessary in all research, to make genuinely new discoveries, and to avoid a disappointing start to your career. Work that fails to produce testable ideas or new questions, or leads to little advancement of knowledge, might be considered as such.

So, before you pick your next research project, ask yourself, and perhaps your supervisor, these questions:

  • Are you mostly interested in natural science, or technology, or both?
  • Is the proposed project driven by a basic question or by the tools at hand?
  • What in the project is genuinely new, or what is unknown in the field?
  • How much does the research programme allow for truly unexpected outcomes?
  • How much risk does the project entail?
  • How will numerical calculations connect with reality, and how will a numerical experiment be judged to be successful?

If you can come up with satisfactory responses to most of those questions, you should have an interesting and fruitful project to hand. For those starting out on a research career, do get some experience as an intern at a lab or university where you may be interested in working. Make sure to pick a research area that you find compelling, as tenacity is a great virtue in research. Beware of advisers who seem to treat graduate school as a revolving door – they are often focused on quantity of results, publications, the number of students graduating and other “metrics”. Grant yourself licence to take risks, to fail and learn from your mistakes. Lastly, don’t forget to enjoy the excitement of new discoveries.

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