Monday, January 23, 2023

For systems, research is development and development is research

The Conference on Innovative Data Systems Research (CIDR) 2023 is over, and as usual both the official program and the informal discussions have been great. CIDR encourages innovative, risky, and controversial ideas as well as honest exchanges. One intensely-discussed talk was the keynote by Hannes Mühleisen, who together with Mark Raasveldt is the brain behind DuckDB.

In the keynote, Hannes lamented the incentives of systems researchers in academia (e.g., papers over running code). He also criticized the often obscure topics database systems researchers work on while neglecting many practical and pressing problems (e.g., top-k algorithms rather than practically-important issues like strings). Michael Stonebraker has similar thoughts on the database systems community. I share many of these criticisms, but I'm more optimistic regarding what systems research in academia can do, and would therefore like to share my perspective.

Software is different: copying it is free, which has two implications: (1) Most systems are somewhat unique -- otherwise one could have used an existing one. (2) The cost of software is dominated by development effort. I argue that, together, these two observations mean that systems research and system development are two sides of the same coin.

Because developing complex systems is difficult, reinventing the wheel is not a good idea -- it's much better to stand on the proverbial shoulders of giants. Thus, developers should look at the existing literature to find out what others have done, and should experimentally compare existing approaches. Often there are no good solutions for some problems, requiring new inventions, which need to be written up to communicate them to others. Writing will not just allow communication, it will also improve conceptual clarity and understanding, leading to better software. Of course, all these activities (literature review, experiments, invention, writing) are indistinguishable from systems research.

On the other hand, doing systems research without integrating the new techniques into real systems can also lead to problems. Without being grounded by real systems, researchers risk wasting their time on intellectually-difficult, but practically-pointless problems. (And indeed much of what is published at the major database conferences falls into this trap.) Building real systems leads to a treasure trove of open problems. Publishing solutions to these often directly results in technological progress, better systems, and adoption by other systems.

To summarize: systems research is (or should be) indistinguishable from systems development. In principle, this methodology could work in both industry and academia. Both places have problematic incentives, but different ones. Industry often has a very short time horizon, which can lead to very incremental developments. Academic paper-counting incentives can lead to lots of papers without any impact on real systems.

Building systems in academia may not be the best strategy to publish the maximum number of papers or citations, but can lead to real-world impact, technological progress, and (in the long run even) academic accolades. The key is therefore to work with people who have shown how to overcome these systemic pathologies, and build systems over a long time horizon. There are many examples such academic projects (e.g., PostgreSQL, C-Store/Vertica, H-Store/VoltDB, ShoreMT, Proteus, Quickstep, Peloton, KÙZU, AsterixDB, MonetDB, Vectorwise, DuckDB, Hyper, LeanStore, and Umbra).


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