I am often asked to review research proposals and aid in the research of others. Some of these projects are excellent, others not so much. Below is my unsolicited advice to students embarking on research projects:
1) There is nothing wrong with research that lacks a hypothesis, but instead is focused on investigating unknown aspects of the biology of an organism.
This "taxon-centered research" (West-Eberhard 2001) has mostly fallen out of favor in academia, though, so good luck finding an adviser or committee that will support this work. (Matthews 2015 has an excellent article on this, calling natural history studies "the raw material from which great syntheses or robust conservation decisions
are made.") One of the keys to doing this successfully is to choose a species that is not extremely rare (thus, making it too difficult to find and/or already the subject of a great deal of intense study) or too common (having been studied in detail, already.)
In Ohio, the state-listed amphibians and reptiles are the subject of ongoing research by many dedicated folks. But there are a lot of species for which our knowledge is sorely lacking. Do some literature reviews, talk to knowledgeable people, and find "your" species.
Here are a few readings I would recommend on this subject:
2) While research without a hypothesis may be acceptable, research without an objective isn't research.
By far, the most common mistake I see students make is deciding on a technique, then trying to find a question to answer using that technique.
Radiotelemetry, trapping, surveying, GIS, and collecting samples for genetics are all tools for conducting research. But calling these techniques "research" is akin to swinging a hammer and calling yourself a carpenter. Adding more tools and collecting more data in hopes that you'll be able to make something of your work in the end, is the single greatest trap to avoid as a student.
Take the time to really think about how you hope to contribute to the pool of knowledge about a particular species, habitat, or system. This includes reading everything you can on the subject. Only then should you begin to ask what data you need to collect and the best way to collect that data. Often the best research comes from individuals who pose an important question, then find a novel (and often low-tech) technique for gathering the data to answer that question.
Two quotes from grad-school professors that stick in my mind: (1) "Don't measure the world and hope that something significant comes from this;" and, (2) "Do less, but do it better."
3) If you want your project to have a conservation focus, ask yourself the following question: "If the results fall to one extreme or the other, or somewhere in between, how might this impact on-the-ground conservation and/or management?"
Or, to put it even more simply: Will the species/population be more likely to persist as a result of my project?
I have seen quite a few so-called "conservation" projects that, no matter the results, can have no impact on conservation. That doesn't make the research bad, as these projects may help in our scientific understanding of such things as ecology, evolution, and genetics. But that, in and of itself, doesn't make it a conservation project. In the worst-case scenarios, some of these projects can siphon resources away from pressing issues facing an endangered species and produce results that will only make an interesting epitaph on the gravestone of the species.
Our tendency to continually study declining species, instead of implementing solutions, has lead to what some have termed an "implementation crisis" in conservation. Some of my favorite readings on this subject:
Whitten, Holmes, and MacKinnon. 2001. Editorial: Conservation biology: A displacement behavior for academia? Conservation Biology, Vol. 15, No. 1. pp. 1-3.
Knight, Cowling, and Campbell. 2006. An operational model for implementing conservation action. Conservation Biology, Vol. 20, No. 2. pp. 408-419.
Balmford and Cowling. 2006. Fusion or failure? The future of Conservation Biology. Conservation Biology, Vol. 20, No. 3. pp. 692-695.
And while it is a business management book, anyone interested in overcoming the implementation crisis should read:
Pfeffer and Sutton. 2000. The Knowing-Doing Gap: How Smart Companies Turn Knowledge into Action. Harvard Business School Press.