The below provides definitions and explanations of “domain scanning” and “epistemic translation”, in an attempt of adding further gears to how interdisciplinary research works.
Domain scanning and epistemic translation
I suggest understanding domain scanning and epistemic translation as a specific type of research that both plays (or ought to play) an important role as part of a larger research progress, or can be usefully pursued as “its own thing”.
Domain Scanning
By domain scanning, I mean the activity of searching through diverse bodies and traditions of knowledge with the goal of identifying insights, ontologies or methodsrelevant to another body of knowledge or to a research question (e.g. AI alignment, Longtermism, EA).
I call source domains those bodies of knowledge where insights are being drawn from. The body of knowledge that we are trying to inform through this approach is called the target domain. A target domain can be as broad as an entire field or subfield or a specific research problem (in which case I often use the term target problem instead of target domain).
Domain scanning isn’t about comprehensively surveying the entire ocean of knowledge, but instead about selectively scouting for “bright spots”—domains that might importantly inform the target domain or problem.
An important rationale for domain scanning is the belief that model selection is a critical part of the research process. By model selection, I mean the way we choose to conceptualize a problem at a high-level of abstraction (as opposed to, say, working out the details given a certain model choice). In practice, however, this step often doesn’t happen at all because most research happens within a paradigm that is already “in the water”.
As an example, say an economist wants to think about a research question related to economic growth. They will think about how to model economic growth and will make choices according to the shape of their research problem. They might for example decide between using an endogenous growth or an exogenous growth model, and other modeling choices at a similar level of abstraction. However, those choices happen within an already comparably limited space of assumptions—in this case namely neoclassical economics. It’s at this higher level of abstraction that I think we’re often not sufficiently looking beyond a given paradigm. Like fish in the water.
Neoclassical economics, as an example, is based on assumptions such as agents being rational and homogenous, and the economy being an equilibrium system. Those are, in fact, not straightforward assumptions to make, as heterodox economics have in recent years slowly been bringing to the attention of the field. Complexity economics, for example, drops the above-mentioned assumptions which helps broaden our understanding of economics in ways I think are really important. Notably, complexity economics is inspired by the study of non-equilibrium systems from physics and its conception of heterogeneous and boundedly rational agents come from fields such as psychology and organizational studies.
Research within established paradigms is extremely useful a lot of the time and I am not suggesting that an economist who tackles their research question from a neoclassical angle is necessarily doing something wrong. However, this type of research can only ever make incremental progress. As a research community, I do think we have a strong interest in fostering, at a structural level, the quality of interdisciplinary transfer.
The role of model selection is particularly important in the case of pre-paradigmatic fields (examples include AI Safety or Complexity Science). In this case, your willingness to test different frameworks for conceiving of a given problem seems particularly valuable in expectation. Converging too early on one specific way of framing the problem risks locking in the burgeoning field too early. Pre-paradigmatic fields can often appear fairly chaotic, unorganized and unprincipled (“high entropy”). While this is sometimes evidence against the epistemic merit of a research community, I tend to want to abstain from holding this against emerging fields, because, since the variance of outcomes is higher, the potential upsides are higher too. (Of course, one’s overall judgement of the promise of an emerging paradigm will also depend more than just this factor.)
Epistemic Translation
By epistemic translation, I mean the activity of rendering knowledge commensurable between different domains. In other words, epistemic translation refers to the intellectual work necessary to i) understand a body of knowledge, ii) identify its relevance for your target domain/problem, and iii) render relevant conceptual insights accessible to (the research community of) the target domain, often by integrating it.
Epistemic translation isn’t just about translating one vocabulary into another or merely sharing factual information. It’s about expanding the concept space of the target domain by integrating new conceptual insights and perspectives.
The world is complicated and we are at any one time working with fairly simple models of reality. By analogy, when I look at a three-dimensional cube, I can only see a part of the entire cube at any one time. By taking different perspectives on the same cube and putting these perspectives together—an exercise one might call “triangulating reality” -, I can start to develop an increasingly accurate understanding of the cube. The box inversion hypothesis by Jan Kulveit is another, AI alignment specific example of what I’m thinking about.
I think something like this is true for understanding reality at large, - be it magnitudes more difficult than the cube example suggests.Domain scanning is about seeking new perspectives on your object of inquiry, and epistemic translation is required for integrating these numerous perspectives with one another in an epistemically faithful manner.
In the case of translation between technical and non-technical fields—say translating central notions of political philosophy into game theoretic or CS language—the major obstacle to epistemic translation is formalization. A computer scientist might well be aware of, say, the depth of discourse on topics like justice or democracy. But that doesn’t yet mean that they can integrate this knowledge into their own research or engineering. Formalization is central to creating useful disciplinary interfaces and close to no resources are spent to systematically spreading up this process.
Somewhere in between domain scanning and epistemic translation, we could talk about “prospecting” as the activity of providing epistemic updates on how valuable a certain source domain is likely to be. This involves some scanning and some translation work (therefore categorized as “in between the two”), and would serve the central function of a community mechanism for coordinating around what a community might want to pay attention to.
The below provides definitions and explanations of “domain scanning” and “epistemic translation”, in an attempt of adding further gears to how interdisciplinary research works.
Domain scanning and epistemic translation
I suggest understanding domain scanning and epistemic translation as a specific type of research that both plays (or ought to play) an important role as part of a larger research progress, or can be usefully pursued as “its own thing”.
Domain Scanning
By domain scanning, I mean the activity of searching through diverse bodies and traditions of knowledge with the goal of identifying insights, ontologies or methods relevant to another body of knowledge or to a research question (e.g. AI alignment, Longtermism, EA).
I call source domains those bodies of knowledge where insights are being drawn from. The body of knowledge that we are trying to inform through this approach is called the target domain. A target domain can be as broad as an entire field or subfield or a specific research problem (in which case I often use the term target problem instead of target domain).
Domain scanning isn’t about comprehensively surveying the entire ocean of knowledge, but instead about selectively scouting for “bright spots”—domains that might importantly inform the target domain or problem.
An important rationale for domain scanning is the belief that model selection is a critical part of the research process. By model selection, I mean the way we choose to conceptualize a problem at a high-level of abstraction (as opposed to, say, working out the details given a certain model choice). In practice, however, this step often doesn’t happen at all because most research happens within a paradigm that is already “in the water”.
As an example, say an economist wants to think about a research question related to economic growth. They will think about how to model economic growth and will make choices according to the shape of their research problem. They might for example decide between using an endogenous growth or an exogenous growth model, and other modeling choices at a similar level of abstraction. However, those choices happen within an already comparably limited space of assumptions—in this case namely neoclassical economics. It’s at this higher level of abstraction that I think we’re often not sufficiently looking beyond a given paradigm. Like fish in the water.
Neoclassical economics, as an example, is based on assumptions such as agents being rational and homogenous, and the economy being an equilibrium system. Those are, in fact, not straightforward assumptions to make, as heterodox economics have in recent years slowly been bringing to the attention of the field. Complexity economics, for example, drops the above-mentioned assumptions which helps broaden our understanding of economics in ways I think are really important. Notably, complexity economics is inspired by the study of non-equilibrium systems from physics and its conception of heterogeneous and boundedly rational agents come from fields such as psychology and organizational studies.
Research within established paradigms is extremely useful a lot of the time and I am not suggesting that an economist who tackles their research question from a neoclassical angle is necessarily doing something wrong. However, this type of research can only ever make incremental progress. As a research community, I do think we have a strong interest in fostering, at a structural level, the quality of interdisciplinary transfer.
The role of model selection is particularly important in the case of pre-paradigmatic fields (examples include AI Safety or Complexity Science). In this case, your willingness to test different frameworks for conceiving of a given problem seems particularly valuable in expectation. Converging too early on one specific way of framing the problem risks locking in the burgeoning field too early. Pre-paradigmatic fields can often appear fairly chaotic, unorganized and unprincipled (“high entropy”). While this is sometimes evidence against the epistemic merit of a research community, I tend to want to abstain from holding this against emerging fields, because, since the variance of outcomes is higher, the potential upsides are higher too. (Of course, one’s overall judgement of the promise of an emerging paradigm will also depend more than just this factor.)
Epistemic Translation
By epistemic translation, I mean the activity of rendering knowledge commensurable between different domains. In other words, epistemic translation refers to the intellectual work necessary to i) understand a body of knowledge, ii) identify its relevance for your target domain/problem, and iii) render relevant conceptual insights accessible to (the research community of) the target domain, often by integrating it.
Epistemic translation isn’t just about translating one vocabulary into another or merely sharing factual information. It’s about expanding the concept space of the target domain by integrating new conceptual insights and perspectives.
The world is complicated and we are at any one time working with fairly simple models of reality. By analogy, when I look at a three-dimensional cube, I can only see a part of the entire cube at any one time. By taking different perspectives on the same cube and putting these perspectives together—an exercise one might call “triangulating reality” -, I can start to develop an increasingly accurate understanding of the cube. The box inversion hypothesis by Jan Kulveit is another, AI alignment specific example of what I’m thinking about.
I think something like this is true for understanding reality at large, - be it magnitudes more difficult than the cube example suggests. Domain scanning is about seeking new perspectives on your object of inquiry, and epistemic translation is required for integrating these numerous perspectives with one another in an epistemically faithful manner.
In the case of translation between technical and non-technical fields—say translating central notions of political philosophy into game theoretic or CS language—the major obstacle to epistemic translation is formalization. A computer scientist might well be aware of, say, the depth of discourse on topics like justice or democracy. But that doesn’t yet mean that they can integrate this knowledge into their own research or engineering. Formalization is central to creating useful disciplinary interfaces and close to no resources are spent to systematically spreading up this process.
Somewhere in between domain scanning and epistemic translation, we could talk about “prospecting” as the activity of providing epistemic updates on how valuable a certain source domain is likely to be. This involves some scanning and some translation work (therefore categorized as “in between the two”), and would serve the central function of a community mechanism for coordinating around what a community might want to pay attention to.