## July 15-16, 2006

The purpose of the "Birds of a Feather" sessions at the AAAI Fellows meeting is to provide an opportunity for subgroups to discuss particular AI challenges and how to achieve them, then report back to the full group on the outcome of their discussion.  Our expectation is that most groups will report back on a specific AI goal which they feel is ripe for major progress, describe that goal, and explain why it is ripe and how to pursue it.  However, you may propose any topic you like.

Here are some topics already suggested.
If you would like to participate, feel free to contact the organizer, or just sign up at the meeting on July 15.
If you would like to suggest other topics, please send Tom.Mitchell@cmu.edu a brief description and I'll add it to the list.

List of topics (see description of each below)
How relevant is game theory to AI?
Organizer: Yoav Shoham.

In recent years the area of multi-agent systems has seen significant growth. As every area matures it becomes increasingly rigorous, and in the process draws on the most relevant established disciplines. Single-agent theories have drawn on probability, decision theory, and statistics, among others. The primary counterpart of these in the multi-agent systems domain is game theory. And so it is not surprising that one sees increased influence of game theory on multi-agent systems. Indeed the influence is dramatic, and not confined to AI; other areas of computer science have been as influenced (most notably theory, but also networking and other area). The question for AI is whether the sweeping adoption of the game theoretic framework and analysis style is appropriate. Will the basic assumptions of perfect mutual modeling, reasoning capabilities, selfishness -- and the focus on equilibria as the driving solution concept (indeed, on the very notion of a 'solution concept') --  help us build better agents (or, for those who still care, build better computational models of human beings)? The exchange in the forthcoming issue of AIJ on foundations of multi-agent learning exposes some of the views in the community (as well as within game theory), but the topic is not limited to learning theories. My own view is that one cannot make progress in the area of multi-agent systems without deep understanding of game theory, but that this deep understanding also exposes some basic limitations which make it clear that 'as is' game theory's usefulness is limited. I believe that what is required is what might be called "constructive game theory", which accepts game theory's insights into interactive epistemology, but which introduces mutual modeling in a gradual fashion, and in which equilibium analysis is only a limit analysis which is sometimes relevant but often not. But this is a complex issue which I don't pretend to completely understand, and a discussion among us interested parties will be illuminating.

Can we design an architecture for human-level intelligence?

Organizer: Stuart Russell

Modern AI has developed and refined a large set of techniques over the last 10 years, to the point that they are practically applicable in circumscribed domains.  They include:  Bayesian networks, Markov models for planning, Bayesian learning techniques, kernel methods for learning, use of unlabeled data in learning, reinforcement learning.  These are beginning to be connected to more traditional AI representations, generating methods for probabilistic first-order models of representation, reasoning, planning, and learning.

The question is: can these kinds of techniques be integrated and pushed toward a solution of the "human-level" AI problem?  The goal of the discussion will be to address this question by developing ideas for an overall architecture for human-level intelligence, as well as identifying major gaps in understanding or technology.  The group will aim to develop a research strategy for the next ten to twenty years, incorporating both conceptual and institutional considerations.

How Has AI Computational Modeling Contributed to the Study of Other Domains?
Organizer: Kevin Ashley

Computational modeling using AI techniques has long been urged as a tool for empirically investigating issues of interest to non-AI domain experts in a variety of fields, such as biochemistry, medicine, law, ethics, and philosophy. AI, it was hoped, would add tools to domains already susceptible of scientific methods, or introduce scientific methodologies to domains that never had them. When the final history of AI is written, it will be interesting to see how well-founded these hopes have been. It may be intriguing for interested Fellows to discuss the attempts that have been made so far, their successes and failures, and even the criteria for evaluating their success. For instance, have the results of AI investigations been published in non-AI research journals, have they been accepted by non-AI domain experts, to what extent have non-AI-related funders provided support for the work, etc.?

Can we design a never-ending learner to solve the natural language understanding problem?
Organizer: Tom Mitchell

I believe a reachable goal for AI this decade is to build a never-ending learner to continually improve its ability to understand natural language, using the web and other sources for training.  If this in fact happens, it will create an "inflection point" for AI capabilities, by making the world's largest knowledge base (the web) understandable to computers.  This breakout group will focus on the question "How can we mount a community-wide research effort to develop a never-ending language learning system?" and subquestions such as "using what architecture?", "what existing technical ideas should we build on?" and "what are arguably achievable subgoals along the way?"  Much of my optimism on this topic stems from (1) the recent burst of new algorithms for unsupervised and lightly-supervised machine learning for natural language processing, (2) general progress in the field of natural language processing, and (3) the fact that we have available a corpus (the web) which has just the properties one would want for a self-supervised language learning system (e.g., mix of structured tables and unstructured text stating the same facts;  many different  statements of the same fact on different web pages using different linguistic forms),

What can we learn from linguistic semantics about KR&R?
Organizer: Len Schubert  (perhaps this should merge with the above 'never-ending learner for NLP' session)

I think there has been an unfortunate disconnect between research on language and research on KR&R from the beginnings of the AI field.  It is unfortunate because it seems likely that language and mind are closely connected: language is a mirror of mind. I think that to attain human-level AI, we need to look much more closely in that mirror, and transfer the many insights that have been gained in the formal study of language meaning into our work on KR&R.  In particular, all human languages have certain semantic devices that are largely lacking in AI-style KRs. These include generalized quantification, modification, reification, complex event reference, genericity, and uncertainty (in various forms). These are arguably all important for commonsense reasoning, not only for NLU. Also, recent semantic theories for the "dynamics" of language meaning may suggest new inference methods similar to model-elimination and SAT-like (perhaps randomized) methods.
P.S. I don't necessarily see this as a separate topic, but perhaps as "something we need to pay attention to if we want to succeed in building systems that learn by reading"

How must logic be modified for representing common sense?
Organizer: John McCarthy

Languages of mathematical logic have been used to express common sense knowledge and reasoning.  Indeed this was a goal of Leibniz's first proposals.  However, nonmonotonic reasoning is certainly needed, and I think concepts as objects and a theory of partly defined objects are also needed.  A theory of the relation between language and reality is probably needed,  but this can be done within present logic.

Do we need a common framework for investigating architectures?
Organizer: Aaron Sloman

Many AI theorists have proposed different architectures for different purposes ranging from relatively simple architectures for agents in very large multi-agent systems to very complex architectures inspired by attempts to produce individual human-like systems (E.g. Minsky's architecture in 'The Emotion Machine' and my closely related H-Cogaff).

Perhaps we need an understanding of what varieties of purposes AI architectures can have and which sorts of architectures are suitable for which purposes (i.e. which niches). For this we need a language and ontology for describing how niches can vary and, if possible, an agreed ontology and terminology for talking about varieties of architectures, e.g. by specifying types of components, types of representations, types of functions components can perform, ways in which different components can be assembled for different purposes, etc. (Compare the use of electronic circuit diagrams: nobody supposes there is one right circuit but there are agreed ways of talking about circuits and representing them, and analysing their behaviours, tradeoffs, etc.)

Superficially there seems to be some common ontology in the AI community insofar as many people use labels like 'reactive', 'deliberative', 'reflective', 'symbolic', 'subsymbolic', 'layered architecture', 'BDI architecture', 'subsumption architecture', etc. Yet when you look closely it turns out that some of these labels are used in strikingly different ways by different people. E.g. some assume that 'reactive' rules out internal state changes whereas others don't. Some use 'deliberative' to refer to anything that considers options and makes a selection, whereas others require something richer (e.g. a planning or problem solving capability). Some assume that an architecture must be unchangeable, whereas others (like me) assume that if you want to understand human intelligence you will need to consider an infant-like architecture that grows and bootstraps itself into something very different over an extended period.

There are also differences between amounts and types of competences required ab-initio, as clearly demonstrated in natural systems by the differences between precocial species like deer that need to run with the herd very soon after birth without having time to learn much, and altricial species born or hatched helpless and (superficially) incompetent but somehow able to develop much richer and more varied cognitive competences by the time they are adults, e.g. the competences of a hunting mammal. A similar spread of designs may be required for artificial systems, e.g. depending on how much detail can be predicted in advance by the system designers about the application domain and task requirements and how much has to be figured out by the system itself on delivery or after the environment changes as a result of unforeseen events.

There may also be very different architectural requirements depending on how the agent interacts with its environment. E.g. an individual with an articulated 3-D body with multiple sensors and effectors of different sorts interacting continuously with physical structures and processes in a dynamic and potentially dangerous environment requires very different mechanisms from an intelligent system interacting with and controlling a large chemical plant, or a software system interacting with other internet agents concerned only with commercial transactions. Are there some requirements common to all of them?

Is the diversity of niches and architectures for intelligent systems so great that there is no point trying to develop a common framework? Or might we gain new conceptual clarity and improved communication and collaboration by developing such a framework? I suggest that some of the interesting transitions in evolutionary history provide useful clues.  E.g. why and how did the ability to refer to and reason about unperceived or future objects and events, including multi-step futures, arise?  Why and how did meta-semantic competence arise: the ability to refer to things that refer, including coping with referential opacity, etc. How were those related to the evolution of linguistic communicative competence? Which other interesting discontinuities are there?
(There's more here: http://www.cs.bham.ac.uk/research/cogaff/talks/#nokia)

How can a robot learn the foundations of commonsense knowledge from its own experience with "blooming, buzzing confusion"?
Organizer: Ben Kuipers

In 1890, William James wrote, {\em The baby, assailed by eyes, ears, nose, skin and entrails at once, feels it all as one great blooming, buzzing confusion}.''  Even so, after early childhood, we humans describe the world primarily in terms of macroscopic objects, the spatial relations among them, how we can act on them, and how they can act on each other.

Current AI systems, especially robotic systems, typically have foundational concepts of space, motion, objects, and actions programmed in by human designers and programmers.  These systems can learn maps of individual spaces, or the properties of particular objects and the categories that they can be organized into.  But the foundational concepts themselves come from the minds of the human designers.

Is it possible for a robot to start from pixel level'' interaction with its world, and learn high-level concepts of space, motion, objects, and actions, without those concepts being programmed in by a human programmer?  The robot's pixel level'' consists of the basic elements of a camera image, of a laser scan, of an individual sonar return, and even the incremental steps of the motor signal.  As AI researchers, we confront this problem directly, especially if we attempt to build intelligent robots that interact with the physical world through their own sensors and effectors.

From a pragmatic point of view, this type of learning will become increasingly important as robots become more complex and longer lived, with greater varieties of sensors, and operating in environments unfamiliar to human experience.  However, the question also raises deep issues at the foundations of artificial intelligence and the philosophy of mind.

New Challenge Problems for Research in Heuristic Search
Organizer: Richard Korf

Heuristic Search was one of the first AI techniques, and research in this area remains vibrant today.  Much progress in this area has come from researchers thinking about how to solve particular concrete problems.  The classic example of this is the game of chess.  In other areas, problems such as the sliding-tile puzzles, or the N-Queens problem, have motivated a great deal of research.
Often when a new problem domain is introduced, it stresses the current stock of algorithms in different ways, resulting in new algorithm developments.  The purpose of this session is to encourage participants to share some of their favorite test domains for two or multi-player games, single-agent path-finding problems, and constraint-satisfaction problems.

Research on Integrated Systems for Human-Level Intelligence
Organizer: Pat Langley

There seems wide agreement that AI would benefit from increased
efforts on integrated intelligent systems, with the ultimate goal
of developing agents that exhibit human-level behavior. However,
there are also powerful biases in place that discourage work along
these lines. To encourage progress toward human-level AI, we must

(1) What testbeds would help motivate research on integrated systems
and support their scientific evaluation?
(2) How can we develop architectures for intelligent systems that
incorporate ideas from diverse disciplines such as logic,
psychology, statistics, and linguistics?
(3) How can we obtain more substantial - and widely distributed -
funding for research at the level of integrated systems?
(4) What mechanisms would foster publications about integrated systems,
which are harder to describe than component algorithms?
(5) How can we educate future generations of AI reseachers so they
have the knowledge needed to work toward human-level AI systems?

We should generate tentative answers to each of these questions for
wider discussion within the AI community. The responses should not
favor one theoretical framework over another, since the issues we

Promoting AI
Organizer: Eugene Freuder

There are a number of "practical" issues related to promoting our field. Of course, the AAAI organization and others work on these all the time; but a little brainstorming in a birds of a feather session here might be fruitful, especially if it inspired follow on activity. Among the questions we might address:
- How do we capture public excitement and attention?
- What are our community "infrastructure" needs and opportunities?
- What is the role of "grand challenges"?
- Can we organize "virtual laboratories" with a broad range of AI expertise from collaborating institutions?
- Can we generate better support for international collaboration?
- Can we improve our relationship to industry?
- Can we further encourage interaction among subcommunities?
- Can we influence government funding priorities and procedures?
- What can we learn as a community from the successes and failures of the first 50 years?
- What are the greatest challenges and opportunities facing the AI community?
- Where would we like AI as a field to be in 5 years, in 10 years, in 20?
- Do we have any recommendations for our national and international organizing bodies?
- Are there additional activities the Fellows would like to organize amongst themselves?
- Is there a more active role for the Fellows, as a group, to play in the AI community?

Is it time to resurrect the orginal Shakey Robot project using currnent technology?

Organizer: Marty Tennenbaum

The goal would be to finally achieve the original ARPA deliverables (circa 1972) of performing ill-constrained tasks such as "fetch me a cup of coffee" or "tidy up the room". The proposed discussion would focus on what's been learned in the past 30 years that would justify giving it another go. Participants could include members of the original Shakey team in attendance (e.g., Peter Hart, Harry Barrow, Nils Nilsson, and myself) as well as current generation roboticists (e.g., Sebastian Thrun, Rod Brooks).