The other day, after the weekly meeting everyone in my lab attends, I asked young postdocs and research students to stay on, and presented them with an exercise with made-up research. Many of the participants found it rather interesting and useful, so I'd like to recapitulate the exercise.
Here is the imagined situation. We created transgenic mice with gene A and found that heterozygotes developed mild obesity and diabetes from 3 months of age. Analyses have not shown any other abnormalities so far. Pancreas has not been analyzed either. We know that the blood pressure was not different from that of wild type.
We then created homozygotes of the transgenic mice and found that all the homozygotes develop very high blood pressure after 6 weeks of age. Dissection revealed pigmentation of kidney.
Q1: What would you do? (What would you investigate?)
Q2: Suppose you have decided to investigate the cause of the hereditary high blood pressure, what would you do first?
Q2-1: The transgene can be differentiated from endogenous genes, because, for example, it is tagged.
Q2-2: The transgene cannot be differentiated from endogenous genes, because, for example, it is not tagged.
Q3: The hereditary high blood pressure line was separated from the transgenic line of gene A. Then, high blood pressure line and wild-type mRNA expression was analyzed using GeneChip. As a result, it was discovered that the expression of gene C in homozygote was reduced to 1/5000 compared to that in the wild type. Gene C was found to be adhesion factor upon investigation. Knockout mice have been made by others and there has been report indicating liver dysfunction. What would you do next? Choose the course of your action from the following three.
1) Liver dysfunction in mice with high blood pressure strongly suggests that it is caused by gene C. Therefore, I would investigate the presence of liver dysfunction in homozygotes.
2) If gene C is the cause of the high blood pressure, expression of gene C should be present in the kidney. Therefore, I would examine the distribution of the gene C expression.
3) None of the above.
These were the three questions I asked, but I gave one question at a time, and we discussed the answer.
For Q1 I said, "The analyses of heterozygotes and homozygotes are both good. But if I were to pursue this research, I would put more focus on the analyses of homozygotes because there is the possibility of insertion mutation. My choice of focus is also because there is a possibility of obtaining results that might lead to the elucidation of the mechanism of essential hypertension (which is a big social and medical problem)." It is a question of sensing the larger and deeper implications one's research might end up contributing to.
There is probably no right answer to Q2. It is more of an exercise in figuring out ways to directly prove causality. I talked about efficiency in research—what is required of each one in conducting a research. A research should be reproducible, simple (not complicated), economical, quantitative, and of high standard.
Neither of the first two choices for Q3 would directly prove the causality, so the third choice would be the correct answer. The reason is…. Well, you can think this over.
And the following week, I talked to everyone in our lab, a little more on a related topic using a 400-meter track running as an analogy. If you think of a research endeavor as 400-meter track run, the goal (paper acceptance, let's say) is not visible at the time of starting the race.
Obtaining positive data on which to base your paper would be tantamount to reaching the first corner of the track. The sense of knowing larger implications of you research, as I mentioned above, is needed, as well as the ability to select the right data to pursue. In other words, the key to approaching the first corner is hypothesis-building and an ability to start producing data to substantiate it.
The ease with which a runner can go from the first corner to the second corner depends on the runner's basic athletic strength, which, in terms of researches, corresponds to the researcher's comprehensive research ability and creativity. Once you reached the second corner, the third corner is in view.
The third corner, perhaps, corresponds to the time when a researcher start writing a paper. So, what is important then? Yes, the requirements of the way research is conducted which I mentioned above are to be borne in mind: reproducible, simple (not complicated), economical, quantitative, and of high standard. During the back straight of a research, the research should not be too dispersed, nor should it be too focused on a particular area, to the extent of completely loosing the larger view.
During the back straight of your research, your research should have progressed and matured to the extent that you are able to articulate what your research is all about, and that you know the relevance of your research in the context of a larger, more inclusive scientific view. This is, of course, also an important phase in which you lay the foundation for the next paper to come. You should make sure to stay the course and not sidetrack, finding yourself among the spectators instead of running on the track.
Things don't get any easier when you have reached the third corner of your research. In the actual track race, too, this is where the race often gets intense; the leading runner losing his/her position is not uncommon. You abilities as a researcher will be put to test before you can submit your paper at the fourth corner and reach the goal where your paper is accepted.
There are plenty of papers without a clear message as to what the palpable benefit of the research is, or in what way the scientific community will be benefited by the research in its pursuit to deepen the understanding of biology. It is not an easy effort to write a paper that would be cited for many years to come. Writing of such a paper starts around the third corner, and it will wear you down, but the reward of true satisfaction is also there when you finally reach the goal.
Hope you find this helpful.