Type of Research projects Part 2: Hypothesis-driven versus hypothesis-generating research (1 August 2018)
One fundamental way to distinguish between projects is dependent on whether the project is hypothesis-driven or hypothesis-generating.
In hypothesis-driven research, we basically come up with a hypothesis that might explain a certain phenomenon. The hypothesis is usually based on doing prior research (published research or work in your own laboratory) and requires that you read, analyze and come up with a new idea. Or your supervisor may have done this for you. But it is important that eventually you come up with your own hypotheses.
When you then start to test the hypothesis, there are several things that could go “wrong”.
Firstly, it might be very challenging (for instance technically challenging) to set up the experiments to test the hypothesis. Hence, the technical challenges of testing a hypothesis is certainly something to think about and ask about. Bear in mind, however, that by setting up a new lab techniques, you actually learn a lot. But it is important to consider the timeframe that is available to you to do your research when discussing the methodological challenges.
Another thing that can happen is that someone else (in a different lab) confirms your hypothesis first (while you are still working on it). This is commonly referred to as “getting scooped”. Getting sccoped usually severely impacts your prospects of publishing your work in a reputable journal. On the other jand, as an undergraduate this should not be too much of a concern because your main objective is to learn how to do good research. And if your research works out well, you can still publish in a smaller journal, even if someone else has reported similar findings. After all, scientific knowledge rests on the ability to reproduce research findings.
Lastly, your hypothesis can turn out to be wrong (which sadly is the most common outcome). In fact, according to the scientific method of evaluating a hypothesis, the aim is to design an experiment with the goal to disprove the hypothesis. If we repeatedly fail to disprove the hypothesis, we have provided evidence in favor of the hypothesis, which may then become a theory. The reason for this is that in most cases it is impossible to actually prove a hypothesis, because there are usually alternative explanations for positive findings.
As an example, let’s say you want to prove that drug X induces cell death by activating protein Y. To test this hypothesis, you may do an experiment where you knock out protein Y and test if drug X still induces cell death. If you find that drug X still induces cell death even though protein Y is absent, you have obviously disproved your hypothesis. In contrast, if drug X no longer induces cell death, it is possible that drug X normally really induces cell death by activating protein Y. However, it is also possible that protein Y is not the direct target of drug X. Protein Y may be necessary for the drug to be taken up by cells or for cells to be able to undergo cell death. Hence, you have to design more experiments to rule out potential alternative explanations.
So let’s say you did your experiment and the hypothesis turned out to be wrong? What comes next? The first question is always, did you do the experiment correctly, or is there a problem? What is especially important here are your positive and negative controls, as they tell you whether your experiment actually worked and whether you indeed measured what you wanted to measure.
The next question then is, can you come up with a new hypothesis that could explain the phenomenon you are studying? And are you able to test the new hypothesis? If you are at the end of your allocated project time, then there is clearly not enough time to test a new hypothesis. Sometimes, though, showing that a hypothesis is wrong can be of interest, too, for instance if your finding refutes a widely believed mechanism. So in short, it is good to discuss questions like “What if the hypothesis is wrong?” and “Is there an alternative hypothesis?” with your supervisor at the start of the project. Because then there is still time to think about alternative hypotheses that can be studied.
The opposite of a hypothesis-driven project is a hypothesis-generating project. Here you also have a general research question (which could be need-driven or curiosity-driven – see part 1 of this post). But you don’t have a hypothesis. Maybe you cannot find one because there is not enough information out there about your research question, or you don’t want to be confined by the current scheme of thinking. Instead, you try to come up with a brand new hypothesis by pursuing a non-biased approach. This often times involves some kind of screen. For instance, you could identify genes that are upregulated, downregulated or mutated in a certain cancer. This can lead to the hypothesis that one of the identified genes is involved in tumor formation and could be a potential therapeutic target. You could also do a screen where many genes are individually knocked out, knocked down or overexpressed in order to identify novel genes involved in some phenotype. Hypthesis-generating research could also involve using “omics”-related technologies, such as proteomics or metabolomics. These techniques can be used to identify novel proteins or enzymes involved in a disease, or to find biomarkers for a specific disease. Some screens or hypothesis-generating experiments are very creative and innovative, which can increase your chances to come up with truly novel hypotheses and to make novel discoveries (see part 3, technology-driven versus technology-utilising projects).
Here is an obvious example for a hypothesis-generating project that I cam across recently:
What are the advantages and disadvantages of hypothesis-driven and hypothesis-generating projects?
In hypothesis-driven (hypothesis-testing) projects, the hypothesis might obviously turn out to be wrong, which can be very depressing. On the other hand, if the hypothesis is true, it can be truly exciting and you are on your way to new discovery and publication!! In fact, the possibility to think of a new hypothesis and then testing it out in the lab has always been one of the most exciting things in research for me.
What about hypothesis-generating projects. Because these projects take a non-biased approach, these projects are more likely to come up with ground-breaking new mechanisms or concepts. On the other hand, hypothesis-generating research usually involves a longer process. You have to first generate the hypothesis, which requires setting up of the experimental system and assay and then to carry out the assay or screen. If you manage to find a new hypothesis, you still have to test the hypothesis to come to an impactful conclusion.
Both types of projects can yield very exciting discoveries. Hypothesis-driven discoveries tend to be very exciting if the hypothesis is very daring (and hence by default risky). In hypothesis-generating research, as mentioned above, the novelty and impact of a discovery is dependent on how creative and innovative the experimental system and design is. Another important factor is how relevant your experimental system and readout is with regards to the phenotype or disease you are studying. For instance, you could try to identify new genes involved in tumorigenesis by measuring proliferation of cancer cell lines grown in monolayer cell culture. However, the results you obtain are likely much less relevant compared to using a more physiological system, such as 3D-cell culture or in vivo tumor models. Of course, there is a trade-off in that more relevant models are usually more difficult to set up.
Some of you might say, I don’t care what kind of project I do, I just want to do an interesting project. What makes a project interesting? Any project starts with an overriding question. Different labs ask different questions. Some labs ask big questions, some ask smaller questions. The types of questions they ask are often related to their resources (e.g. grant money, expertise, technological tools). But what makes a research project interesting is not really how big or important the research question is. For instance, someone might be leading an effort to coordinate help for thousands of flood victims in a developing country or just help out a single family affected by the flood. How passionate one feels is not really dependent on the number of people that we help. What makes us passionate about something is the emotional attachment we feel towards the task. In research, the emotional attachment is dependent on the hypothesis and the way we go about testing the hypothesis, because these are our own contributions to addressing the research question.
As we already mentioned, you (or your supervisor/mentor) can either come up and test a hypothesis to address the research question or you design an experiment to generate a new hypothesis. What makes a project interesting is dependent on how novel and exciting your hypothesis is and how cool the method is that you use to go about testing your hypothesis. For instance, it is well known that protein aggregation is involved in neurodegenerative disease. If you do a project to determine the identity of aggregated proteins in different neurodegenerative diseases, that is probably not very exciting. On the other hand, your project would probably become much more exciting if you come up with a brand new hypothesis for how protein degradation causes neurodegenerative diseases and test it. Or you might develop a novel way to experimentally induce the aggregation of specific proteins in the brain in mice or some other model organism and test if this is sufficient to cause neurodegenerative disease. The only way to come up with exciting hypotheses and cool ways of testing them is to read and think a lot, and this is why these two activities are so important.
For examle. recently I was reading a paper on high throughput identification of mutations in lung cancer. (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC5003022/pdf/nihms-801008.pdf) My attention went immediately to the list of gene mutations that they identified to see if based on my own knowledge, I can come up with a hypothesis about how a specific mutation promotes cancer. That would make the paper really interesting for me. (But unfortunately I couldn’t…)
As we said above, hypotheses can fail, and there is usually a negative correlation between how exciting a hypothesis is and how likely it will work out. That is why for PhD students it is important to have a mix of safe and risky projects. In the safe projects, you test a hypothesis that is most likely true, based on evidence in the literature (but probably less interesting because it is only a minor step forward) or you do a hypothesis generating experiment that employs a well-established method (which usully translates into a rather tedious exercise). The risky projects involve testing a bold new hypothesis (that has a high likelihood of being wrong) or developing a challenging new way to generate a hypothesis that will be conceptually new.
A new hypothesis should in theory be grounded on evidence that has been published or been generated in your lab. Often times, though, hypotheses are not very clearly grounded on facts or are not even very clearly defined. The researcher may just have an instinct, based on his experience, that something is important in a certain phenomenon. Although this sounds a bit non-scientific, many discoveries stem form instinct hypotheses, and in fact these can be very exciting if they yield novel insight.
Sometimes researchers even pursue hypotheses that contradict published evidence. This could be due to two reasons: (i) They didn’t read the literature (or they did, but somehow overlooked it), and (ii) they may have looked at the published evidence and they didn’t believe it. After all, a lot of papers that are published are partially or completely wrong. The reasons for that can be manyfold (and this is a topic on its own). But as Francis Crick said, “A theory should not attempt to explain all the facts, because some of the facts are wrong.” The technique he was referring to here is called rule-bending, and it is an important technique because it actually allows us to come up with truly new concepts and ideas.
Finally, sometimes while testing a hypothesis, you make an interesting side observation that may lead to a new hypothesis. And this may even become your main project, if curiosity leads you there. This is fine, and good. Many great discoveries have come from side observations.