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How to formulate a good research problem? Part 4

Is it worth seeking out authorities in the world of science? Is it possible to find the perfect research problem – one equally interesting and connected with the actual challenge? Answers to these and many other questions may be found in interview with Professor Piotr Sankowski, the President of IDEAS NCBR. Enjoy the reading!

23 November 2022

  1. A good research problem – what does it mean exactly? How can it be described?

PS: To give a satisfactory answer to these questions, we also have to decide what defines good research. For me, the crucial part is thinking about what the results may be applied for. We need to stress, that I do not mean applied “here and now”. The verification of usefulness of the results of fundamental research may take many years, but it is certainly much easier to publish research that is related to real challenges. And in my opinion, they are simply more interesting. At the universities, particularly in Poland, we are often unable to effectively combine these two parts, that are, in fact, parts of the same story. On one hand I know researchers, who strongly believe, that “the real science” should not have use. On the other hand, many persons concentrate on the work on applications with no research aspect. I think a nice illustration of this is a quote by Louis Pasteur: “There are no such things as applied sciences, only applications of science.”

This matter is an important part of the answer to the question of a good research problem, but it is not all. When choosing the research problem you should be guided by certain pragmatism, i.e. assess your chance for success. The severity of the problem is usually inversely proportional to the difficulty of solving it. That is why we need to find this perfect point for us, where we solve the most interesting problem that we have a chance to solve yet. This compromise, as it usually is with compromises, is not simple at all. Few researchers can do it instinctively, many come to it over the years, along with the growing experience.

  1. What are young researchers’ most common mistakes when looking for a research idea?

PS: In recent years, I have been meeting more and more young researchers whose research interests are fully formed before their master’s degree. To my surprise, at that point they already know what subjects they want to explore and in fact they do not want to discuss what is worth doing or listen to the older colleagues’ suggestions. As I previously mentioned, the choice of research problem is difficult and both experience and intuition increase the researcher’s chance for success. To certain point such approach is understandable – it results from major science authority crisis in Poland. Few scientists are in world’s big league. Why would these young scientists draw inspiration from them or consult them? Even though I can understand such approach, in my opinion it may be a mistake. It is worth taking some time and look for a mentor at the world level. Luckily, there are more and more fantastic scientists who decide to work in Poland. Experience in effective research is crucial in science, where problems often take years to solve.

WE HAVE SET OUT TO INCREASE THE R&D POTENTIAL IN THE FIELD OF ARTIFICIAL INTELLIGENCE.
  1. Where to look for inspiration?

PS: I think I need to repeat myself – in discussions with other researchers. It is worth going to conferences and other scientific meetings, checking what respected scientists have to say and what problems they find interesting. You should not be afraid to ask questions, because each scientist will gladly explain his research.

  1. How has the process of formulating a research problem changed over the years? What did it look like at university, during your doctorate, and what does it look like now?

PS: When I started my research work, I was more inclined to focus on one research problem. This may be a mistake made by other young scientists as well. Focusing on a super important problem and assuming, that we are writing this one most important work very rarely works. It is much better to start with a couple of reasonable projects or to change the research problem, when it turns out, that we see no progress at work. In science, it is often the case that problems that seem simple at first also lead to profound results or further generalizations. It is not that starting work on such a problem, we will not get meaningful results. Once we start working on them, some of them will turn out much more interesting than we thought in the beginning. It is difficult to predict exactly how the research will turn up and what the results will be. It may turn out, that one of these written works will be in fact particularly good. It is a little like in statistics, i.e. in a few throws of the dice, a six will surely come up, but if we throw only once, the chances of it are small.

  1. When thinking about a research problem, do scientists take into account any external factors? Does what is happening in the world or the ease of obtaining financing affect this process?

PS: Personally, I take into consideration the usefulness of my research. This aspect is important to me, even in the part being in the domain of fundamental research. I would like to be able to imagine, that their results might be applied somewhere. I think, that in my case, this approach is the key to obtaining financing.

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