In the previous Research project posts, we have discussed the types of research questions and how we go about addressing these questions by testing or generating hypotheses. In the final part, we discuss how we can go about testing or generating our hypothesis.

 

There are basically two approaches to test or generate a hypothesis. There is the technology-utilizing and the technology-driven approach. I guess the terms are rather self-explanatory, but keep in mind that there is a spectrum in terms of using or developing new technology to answer research questions. The one obvious advantage of a technology-utilizing project is that you can get data and come to conclusions quickly. In the simplest way, you are using methods and procedures that are already well established in the lab and that someone else teaches you how to do. It gets a little more challenging if you actually have to set up methods by yourself. It takes longer to get results this way, but you pick up important skills in resourcing, critical analysis and trouble shooting, which are very useful. But there is also the type of project where you spend a major part to develop a new and innovative assay to test hypotheses or do generate new hypotheses. Sometimes setting up of the new assay could be the project itself. Bruce Alberts (of “Molecular Biology of the Cell” textbook fame) makes a very strong case for technology-driven research in an article published some years ago, which I encourage to read.

But to summarize, the article is the story of how Bruce Alberts initially failed his PhD exam and what he learned from it. Bruce Alberts noted that most researchers “… were pursuing obvious experiments that were simultaneously being carried out in other laboratories. These scientists were constantly in a race. It had always seemed to me that, even if they were able to publish their results six months before a competing laboratory, they were unlikely to make truly unique contributions.”

 

As a PhD student, Bruce Alberts wanted to do things differently by, instead of picking an obvious hypothesis, coming up with a daring and risky one. His hypothesis was less based on available information but more on intuition and it occupied most of his PhD. If the hypothesis were to be proved correct, he likely would have made a big impact. But the hypothesis proved out to be wrong, and as a result, he had no impact, and in fact nothing significant to report for his PhD studies.

 

For his postdoctoral research, he then pursued a totally different strategy. He writes:

 

“I wanted to continue to focus on how DNA is replicated for my postdoctoral work in Geneva. But what strategy should I choose? The months of analysis triggered by the wake-up call of my PhD failure finally produced an answer. I would look for a unique experimental approach, but one that would have a high probability of increasing our knowledge of the natural world, regardless of the experimental results obtained. After a great deal of soul-searching, I decided that I would begin by developing a new method — one that would allow me to isolate proteins required for DNA replication that had thus far escaped detection. I knew that the enzyme RNA polymerase, which reads out the genetic information in DNA, binds weakly to any DNA sequence — even though this protein’s biologically relevant binding sites are specific DNA sequences. If the proteins that cause DNA to replicate have a similar weak affinity for any DNA molecule, I would be able to isolate them by passing crude cell extracts through a column matrix containing immobilized DNA molecules.

 

Arriving in Geneva in late 1965 with my PhD degree finally in hand, I found that by drying an aqueous solution of DNA onto plain cellulose powder, I could construct a durable and effective ‘DNA cellulose’ matrix. A large number of different proteins in a crude, DNA-depleted extract of the bacterium Escherichia coli bound to a column containing this matrix. Moreover, these DNA-binding proteins could be readily purified by elution with an aqueous salt solution. Using this new biochemical tool and a large library of mutant T4 bacteriophages obtained from Dick Epstein in Geneva, I discovered the T4 gene 32 protein after moving to Princeton a year later as an assistant professor. This proved to be the first example of a single-strand DNA binding (SSB) protein, a structural protein that plays an important role in DNA processes in all organisms (see Nature 227,1313–1318;1970).

 

The strategy of investing in method development and then using this new method for a major series of experiments would be employed over and over again during the next 25 years of my career as a research scientist. As a result,my laboratory almost never felt that it was in a race with other laboratories, and our successes were sufficient to satisfy both me and many of the graduate students and postdoctoral fellows who would join my laboratory. It seems strange to recall that we may owe all it all to one very unhappy PhD thesis committee at Harvard, nearly 40 years ago.”

 

So think about this strategy, especially if you are embarking on a longer term research project.

 

These are my thoughts on the different types of research projects. At the end, you might ask, so what is a good research project? This depends a little on which stage of your career you are in. For undergraduate students, in my opinion the best project is to test a specific hypothesis using established experimental approaches. At least some of the methods should be set up and validated by the students themselves. This way, the students get a sense of doing real research and are hopefully learning some important skills, such as planning experiments, analysing and interpreting results, trouble-shooting. Bad projects for undergraduates are in my opinion projects where the students don’t have their own project but “shadow” a PhD student or postdoc or “help” with big projects. The problem with these projects is that the motivation can be low because the level of ownership and responsibility and the ability to contribute creatively are often limited. I also think that projects that focus on developing a tool or helping to design complicated assays for hypothesis-generating experiments are not ideal because these projects often focus more on technical details than on scientific inquiry.

 

Of course, this is only general advice, because after all, every project is different. So ultimately you have to ask yourself, am I excited about the project, and also discuss with the supervisor the “what if it doesn’t work” question.

 

For postgraduate students and postdocs, various other factors play a role when choosing a research project, such as: How novel is the hypothesis or approach? What is the potential impact? What is the possibility of getting scooped? Does the project align with my long term goals? Etc.

 

Have fun with your research! And don’t forget, the fun doesn’t come from just doing experiments, but from doing them well, getting interesting results, solving your problems yourself, coming up with your own ideas, discussing your ideas with others. But don’t expect all these to happen right away. They take time and effort.

 

 

Where does your research project sit in this table?