Guidelines for your 20.109 research proposal
Writing a research proposal requires that you identify an interesting topic, spend lots of time learning about it, and then design some clever experiments to advance the field. It also requires that you articulate your ideas so any reader is convinced of your expertise, your creativity, and the significance of your findings, should you have the opportunity to carry out the experiments you’ve proposed. To begin you must identify your research question. This may be the hardest part and the most fun. You can start by finding a handful of topics to share with your lab partner. Together you should discuss and evaluate the topics you’ve gathered. Consider them based on:
- your interest in the topic
- the availability of good background information
- your likelihood of successfully advancing current understanding
- the possibility of advancing foundational technologies or finding practical applications
- whether your proposal could be carried out in a reasonable amount of time and with non-infinite resources
It might be that not one of the topics you’ve identified is really suitable, in which case you should find some new ideas. It’s also possible that through discussion with your lab partner, you’ve found something new to consider. Both of these outcomes are fine, but you and your partner should settle on a general topic or two relatively quickly; that way you can begin the next step in your proposal writing, namely background reading and critical thinking about the topic.
A few ground rules are 20.109 specific:
- You should not propose any research question that has been the subject of your UROP or research experience outside of 20.109. This proposal must be original.
- You should keep in mind that this proposal will be presented to the class, so try to limit your scope to an idea that can be convincingly presented in a twelve minute oral presentation.
Once you and your partner have decided on a suitable research problem, it’s time to become an expert on the topic. This will mean searching the literature, talking with people, and generating and critically evaluating some ideas. To keep track of your efforts, you should start a wiki catalog on your OpenWetWare user page. How you format the page is up to you but check out the “yeast rebuild” or the “T7.2” wiki pages on OpenWetWare for examples of research ideas in process.
As you become more expert on your research topic, you'll read a lot about it and you may feel
(a) like there's too much to read
(b) like you have too many ideas and no way to map or prioritize them
(c) like you don't understand what you're reading
(d) all of the above.
One of the best ways to help frame the problem for yourself is to discuss it with someone new. You will have an opportunity during lab to talk with a person from another lab group. This person will offer you a fresh ear to consider your proposal. You can rework your proposal based on the conversations you've had.
Prepare a 12 minute powerpoint talk that describes the research question you have identified, how you propose to study the question, and what you hope to learn. A general outline for your research proposal presentation is:
- a brief project overview (scientific and social context)
- sufficient background information for everyone to understand your proposal
- a statement of the research problem and goals (specific research aims)
- project details and methods
- predicted outcomes if everything goes according to plan and if nothing does
- needed resources to complete the work
- societal impact if all goes well
On the day you present (see announcements on front page for when and where) your team should print out and bring two copies of your powerpoint slides. Black and white is fine and you can print more than one slide per page if you like (4-6 slides per page tends to be ideal for my note-taking). You should also write (and print out) your "talking points" in the comments box of each slide or in a separate document. These are speaking notes for your presentation, and should include short phrases to remind you of the key points to cover on each slide, as well as the transitions you've planned between them. For example, in a previous year's presentation one slide's talking points were:
As you can see from this image, taken from a review on hydrocarbon metabolism in marine bacteria, the alcanivorax species is the first to grow in population after an oil spill, and its growth correlates with a decrease in aliphatic hydrcarbons.
- After most alkanes have been degraded, the Cycloclaticus species blooms while aromatic hydrocarbon levels decrease
- One thing to note is that as soon as they have done their job, both species return to their normal population levels.
- One problem with using Alcanivorax and Cycloclasticus to clean oil spills, however is that they can only be found in specific locations
The next slide (transition statement) began:
To remedy this, we decided to look into other bacteria into which we could move the hydrocarbon metabolic pathways
You don't have to use complete sentences in your own talking points, but the above example should give you a sense of what content is expected.
You will be graded on the integrated success of your presentation: concepts, slides, talking points, and presentation.
FAQ and Addendum
Questions that we got on Day 3, as well as a glance at pre-lab clarifications from previous years, have together made clear the need for updating this assignment description! To avoid confusion for those of you who already read through the assignment, all new material will be placed in this section rather than integrated above.
Q: How '109-like' does it need to be?
A: Your proposal does not need to directly involve research pertaining to DNA damage, cancer or phage-base materials! However, it does need to include a combination of engineering and biology, using at least some techniques / approaches that you have learned in class. For example, determining the role of a specific protein in apoptosis is not a good project (too much biology) -- but engineering a protein sensor to quantify the activity of the protein under different conditions and using that data to predict apoptosis would be an acceptable project.
In general, if you have question about whether your idea satisfies this criteria, ask an Instructor!
Q: What is an appropriate scope?
A: A typical proposal should span a few years, but some stages should be described in more detail than others.
You may not have a good feel for what a three-year project should encompass. It's not important here that you be precise. Rather, you should make sure your project wouldn't span only a few months… or over a decade. If you're still not sure, ask us directly.
We would like you to demonstrate both some breath and some depth in this proposal. For example, if you propose molecular and/or in vitro work, you would want to be able to say a few words about in vivo experiments, beyond the words “in vivo” – such as being aware of a useful model system. As for depth, you should define a few experiments in detail. What controls would you use? What potential outcomes do you expect, and how would you deal with the different possibilities? If your sample looks like your negative control, how would you modify your approach? If the sample looks pretty good but not great, how might you tweak your design? If you can't get good validation data at all, is there an alternative method to try, perhaps one that is more time consuming but more sensitive? If your synthesis fails, do you have a back-up plan? Keep in mind the outcomes matrices we made for experiments like transformation after ligation.
Q: What does novel mean?
A: We don't expect you to be Angie Belcher. But we do expect you to go beyond a direct analogue of a single existing publication.
Like a few other things in life: we know it when we see it. The level of novelty we expect in 20.109 is difficult to define precisely; it may be easiest to do so by example. You might find a useful method or interesting device that was recently published, and apply it to a totally different context, which would likely require some novel engineering design choices. You might combine improvements/approaches from multiple papers in a single area, but in novel ways that require you to make unique choices with respect to experimental set-up and validation ("add molecule X from paper 1 and molecule Y from paper 2 at the same time" is not okay, but "co-deliver drug fusion from pH-sensitive nanoparticle" might be). You might investigate a mechanism of why something worked the way it did in existing research. Or you might genetically engineer a novel biological device.
Briefly, you should be able to define a specific research gap, and a plan to address it that includes some novel methodological and/or synthetic elements.
Q: How soon should we settle on an idea?
A: Depends... on your interests, strengths, and work habits.
There is a trade-off here that you can keep in mind. You might spend weeks coming up with a great, truly novel idea, and then find yourself with too little time to prepare your slides and polish your delivery or perhaps even to define your methods in sufficient detail. On the other hand, you don't want to wed yourself to an early idea that turns out to be flawed or boring -- to you! It is normal to change your idea one or more times. If you settle on an idea very late, you'll have a challenge ahead of you. However, experience shows that it is better to present a project that you are passionate and knowledgable about than one that you have come to resent.
Q: What is "overview" versus "problem and goals"?
A: The overview is a brief, holistic summary of the project, while the problems and goals define specific stages of the research.
As the rubric states, one way to approach the overview is to describe both social and scientific context. Working with a previous year's example, the social context was the need for improved treatment for diseases of the cornea due to a shortage of donor tissue, while the scientific context was overcoming limitations of corneal culture -- such as apoptosis -- that lead to poor wound healing.
The problems and goals should be more specific, but still somewhat high-level. Taking Module 1 as an example, aims would be something like "Prepare truncated GFP constructs," "Validate flow cytometry assay in a cell line," and "Test recombination frequency under various conditions," NOT "Digest backbone and insert," "Ligate construct," "Transfect into cells," etc. A typical project will have three or four high-level aims.
Q: How specific should we be about "resources"?
A: Read the rubric :) We are not looking for an itemized spreadsheet. Do specify unique elements where you can.
Q: Can our proposal be purely computational?
A: This is a hard question -- and one that often falls under the 'Is this 109-like?' category. In general, you should not propose a purely computation project -- this isn't 20.320. However, here are a couple examples that do satisfy the 20.109 requirement:
- The Bidkhori et al model did not account for receptor trafficking. Perhaps you want to create a more realistic model of NSCLC signaling pathways. What experiments would need to be conducted (and how would they be controlled and quantified in the correct way) in order to parametrize the receptor trafficking? Is it necessary to account for other receptors? How would you do that experimentally?
- The Cancer Cell Line Encyclopedia contains an enormous amount of publicly available data about cell proliferation. What if you are interested in cell migration? Are there modeling techniques that could be applied to that data set along with experimental techniques that you could perform to harness that data and learn how cell migration is controlled?
In short, you must have some experimental component to your research proposal. You may use experiments to inform a model or a model to inform experiments -- but the experiments must be a large focus.
Q: Do you have an example?
A: Kind of.
Shannon prepared a partial draft/outline of a written version of a proposal, linked here. Please pay especial attention to: the use of figures; statements pertaining to both social and scientific context; specific research aims; background, definition, and alternatives for a few experiments; a clear knowledge gap and central question.
Finally, some general tips for idea development (early and late stage):
- Read a recent review paper in an area that interests you. This approach is one of the quickest ways to develop sufficient expertise as well as an eye for existing research gaps.
- Talk to faculty who are experts in an area that interests you. More fun and interactive than reading a review paper for honing in on research gaps! But don't expect them to do all the work for you. The more research you do in advance, the more productive a conversation you will be able to have.
- In later stages, faculty may also be a resource for appropriate methods to use: How do people usually measure X? Is there an animal model for Y?
- If a recently published finding inspires you, read the discussion section carefully. What do the authors envision with respect to future work?
- Give yourself enough time (and sleep) to let your creativity emerge!