Designing Research Projects¶
I never assign projects—I don't think it works effectively.
We should invest more time designing and killing projects, but avoid premature termination. Early-stage ideas are fragile and often hard to fully recognize.
Key principle: Difficulty and importance are uncorrelated. Strive for projects that are both easy (that is, have an angle of attack) and impactful. Often 10x more impact isn't 10x harder.
The Project Management Paradox¶
Designing projects is difficult because we must make the most important decisions when we have the least knowledge—at the project's start.
In knowledge work... the task is not given; it has to be determined. "What are the expected results from this work?" is the key question in making knowledge workers productive. And it is a question that demands risky decisions. There is usually no right answer; there are choices instead.
Peter Drucker
Cognitive Challenges¶
When dealing with complex problems, several cognitive reactions impair our judgment:
- Emergency reaction reduces our ability to step back and assess objectively
- Irrationality increases failure potential through strong influence of context and background knowledge
Due to these cognitive biases and the project management paradox, we must actively set aside sufficient time to think about what problems to work on and how to address them.
Project Selection Factors¶
When choosing projects, consider multiple factors:
- Lab's research interests
- Potential knowledge gain and question importance
- Task difficulty
- Our experience level
- Available time
Different projects suit different career stages. For PhD students, the first project should be a "second master's thesis"—clearly scoped work leading to publishable results quickly.
Consider this framework from How to Choose a Good Research Problem:
After this foundation, longer-term projects become more suitable.
Research Velocity¶
For many research questions in our field, getting rapid signals proves valuable. Build small prototypes (simpler/smaller datasets, smaller/simpler models) to quickly gain intuition about direction and identify the most important variables. Look at this slide deck for ideas about research velocity.
Remember: Ideas are cheap, evidence is expensive. Science is the art of the soluble—can you test the idea?