## Course Overview * Audience: graduate students (or beyond) already engaged in research - Not: undergrads * General Goal: practice thinking about research, but not navel gazing - No one-size-fits-all solution, but many methods - Make explicit a lot of implicit understanding and know-how - Produce work that will valuable for you throughout your PhD: a dissertation proposal, a groundbreaking research agenda document, a faculty job application, a set of research papers, a startup pitch, a nonprofit collective charter, or ... * Concrete Goal: explore the boundaries of some research sub-area of interest to you - Or even define a new sub-area * Non-goals - Not: to identify research that will maximize research paper output - Not: to preordain a career path, or to say that one career path is better than others * Diverse readings - Across computer science: AI, cryptography, networking, programming languages, etc. - Outside of computer science: philosophy, math, sociology, history, etc. * Challenging - Conceptually: will challenge you to think in new ways - Practically: a consistent (not bursty) moderately-high reading and writing load * I want to learn more from you than you learn from me - Also: I'd like you to learn more from each other than you learn from me - But most importantly: I'd like you to learn the most by yourself through the work ## Perspective * Who am I to even be teaching this? - I have an unusual background and set of interests * I could not have taught this course even a few years ago - My perspectives have changed - My interests have changed - The *world* has changed (most importantly) * Missing subtitle of course: Crafting a Research Agenda in the post-X era - where X = modern? - where X = truth? - where X = science? - where X = ??? * Computer science's trajectory as a field: - Rapidly developed in the post-WW2 era, a unique period in human history - Yet until ~20 years ago, CS was inward focused: 80-20 inward-outward - Now, CS is outward focused: 20-80 inward-outward - This has not been widely understood, and has profound implications for our field ## No Method * There is no one method to crafting a research agenda * Don't believe everything ***you*** think - Also don't believe everything you read, even from famous / eminent people - But don't reject everything either * Broken notion: craft a research agenda (or software project, or science experiment) - Then do it * New notion: craft a research agenda and then... - You might throw out the whole agenda - You might realize its premises were wrong, or goals were wrong, or techniques are ill-suited - This is fine, and expected * Why bother crafting an agenda, then? - The *process* of crafting the agenda is key - Eisenhower: "plans are worthless but planning is everything" - Your agenda can frame a research space, influence others, bring in collaborators and resources - It's ok if the document doesn't hold up with 20/20 hindsight; nothing does * The public agenda and private agenda will be different - Public agenda is what you might write in a vision paper * Private agenda is a meta-agenda, with thoughts on "navigation" - Goal is more of "how to navigate" rather than "charting the path from A to B" - "Discover the road as you walk it"; you may not end up where you planned - What are possible blockers/hurdles to this work? How do you test them, move past them? - What are avenues to explore at each potential research crossroads? - What are multiple hypotheses/ideas to consider for each sub-problem? - What happens when something inevitably goes wrong? - What are some possible unknown unknowns; how might they affect problem framing, the work process, the data sets used, etc.? * Research entails prediction: - Ordinary engineering doesn't involve prediction: application of known needs to known problems - Research requires predicting enabling technology, needs, problems, and more - We often don't realize we have mentally internalized predictions about the future - "Program or be programmed": either we are conscious in our choice of predictions or risk accepting problematic and self-motivated predictions from others - No one prediction about the future can be right -- the world is complex and nested - It makes sense to hedge our bets - Where do "problems" come from? How can we select which ones to work on? - Our orientation towards the future is central to these questions - These are central topics of this course ## "Normal" vs. "Revolutionary" Science * Our goal is to go beyond "normal" science - Aspire to "revolutionary" science - However, "normal" science is needed for "revolutionary" science * "Paradigm shifts" and "revolutionary" science are not solely major changes - Both happen at many scales - Impossible to categorize all research as strictly "normal" or "revolutionary" * You will get plenty of practice doing "normal" science as a PhD student - Here we aim to discuss something bigger * Research trends in CS are like economic bubbles - [Where is your research area in this chart?](https://en.wikipedia.org/wiki/Jean-Paul_Rodrigue#/media/File:Stages_of_a_bubble.png) - Individual researchers often occupy different points in this chart * The world _demands_ of us something beyond "normal" science at this very not-normal time ## Systems and Meta-systemicity * Understanding research from a systems perspective - Not: computer systems, but: conceptual and rational systems - And moving beyond specific systems to a meta-systematic perspective * We are told we operate in a world of rationality as researchers - A fair bit of our discussion will be on why this is often not the case - "There must be an answer" is a common belief * Research sometimes employs/requires meta-systematic thinking - Thinking this way takes practice * There is no clear line between systematic and meta-systematic thinking - Lots of shades of gray ("nebulosity"), another theme we will discuss - Key is to not get stuck in one way of thinking ## Doing, not just thinking, in a Community of Practice * How to do good research can't be learned from a book - Nor is thinking sufficient - Nor is dreaming about grand results sufficient - You must ***do*** it, *with others*; lots of hard work - Not unique to research: many things are this way * Example: Computational Agroecology - I now do a fair amount of research on applying computing to sustainable agriculture - I was trained in networking, but don't really use any of it here - I never formally studied the ostensible background topics: agriculture, sustainability, AI, etc. - I learned the agriculture and sustainabiilty perspectives by doing, embedded in a community of practice (urban agriculturalists, mostly hobbyists but some professionals) - I brought my own perspectives and techniques to bear * You, and your work, get better through those around you - Cultivate your community ## Advancement at the Limits of Understanding * Just "doing" is insufficient; not all work is explicit or conscious - Combination of conscious and subconscious work required * Example: Wagner's cryptanalysis in the hot tub * Example: ideas in the shower * Easy to have false insights if you don't put in the work - No shortcuts * Hard to have insights without allowing room for the subconscious - Fixating on rational, conscious methods is limiting ## Activities for the Semester, and Beyond * Read widely, not just in the research literature - The literature is a lagging indicator of where research is, sometimes as much as 4 years out of date (why?) - You don't want to just read the "best" work or the "best" venues - Example: SMT - Also: read what innovative researchers are themselves reading, so go find out - Also: read very broadly, because you never know what might spark ideas * Don't just read, talk with people - The most cutting edge ideas are difficult to articulate in writing - New ideas can come out through discussion rather than written dialogue * Read technical *and* non-technical writing - Read technical to learn new techniques for problem solving - Read non-technical to consider new problems or problem framings or contexts * Don't rely upon others to lay out a vision for you - Point: You'll just be building their vision - Counterpoint: don't just ignore everyone and do your own thing - Synthesis: build a community of researchers around a common vision * Take a lot of notes, not just of ideas but also of what you read - Never know what ideas might connect ## Course Mechanics * Create a new folder in the shared Google Drive folder in the format "Full Name -- CSCI 654" - In this folder you'll put all your materials * The first document you should now create in your folder is "Full Name -- CSCI 654 -- Responses" - Clone the template doc and put it in your folder - This is where you'll be writing reading responses, newest on top - For each class date, should be heading for each class (notes taken in class discussion) and separate heading for reading responses ## Five Whys * Ask why five times to try to get to root causes - We'll apply this later ## Activity * In groups of 2-3, discuss what "research" is. Do not look it up online, in a dictionary, etc. - What is research *to you* ***in your experience***? (Not what you've been told it is, or read that it is, or think that it should be.) - Ask each of the following five times about research: what? who? where? when? why? how? - Take notes in your new document