April 5, 2004
Whither Game Research
I had a great time at the GDC last week. The positive buzz around Façade led me to consider once again the issue of whether the phrase “game research” makes sense. To cut to the chase:
- The game industry currently doesn’t believe in “game research”. You’re either working on a shippable product, or you’re bullshitting around. Shippability implies minimizing risk; minimizing risk implies minimizing innovation.
- There are regions of design space that cannot be reached incrementally. That is, there exist new game genres that can’t be invented through a sequence of incremental, shippable products.
- Academia currently has no funding mechanism (and potentially, no tenure mechanism) to support research inventing new game genres (research that often, along the way, involves solving some hard, first class technical problems).
So neither industry nor academia will do the non-incremental work necessary to explore these hard to reach regions in design space. Who will? To put a finer point on it, how do I fund the next Façade?
“Game research” can mean many different things. For the purposes of this post, I’m not referring so much to game studies, that is, theoretical analysis of games, but to work at the intersection of design and technology in which new game genres are invented. In this style of research there is of necessity a feedback loop between design and technology; design suggests new directions for technical research, while new engines and infrastructures suggest new directions for design.
Interactive drama is an example of a non-incrementally reachable region of design space. Trying to reach one of these regions through an incremental series of shippable products is like trying to get to the moon by climbing trees. When you climb a tree it does get you closer to the moon. As your tree-climbing skills improve you can climb even taller trees. But no matter how good your tree climbing skills are, only a radically different approach, like building a rocket, will get you to the moon. Of course, the first few times you build a rocket, it will explode on the launch pad, or dive into the ocean, or engage in other such shenanigans that so disturb funders and publishers. But if no one builds rockets, then nobody gets to go to the moon. Academia is a good, relatively cheap place to house this high risk, high payoff research.
These hard-to-reach regions of design space can’t be reached by design-only approaches, necessitating integrated work in design and technology. As we’ve discussed here before, interactive drama is an example of this; there is no magic design perspective that suddenly makes interactive drama doable without significant technical research in socially and emotionally believable characters, drama management, and natural language processing. While any one of these research areas is enough to keep you busy, the only way to understand how the three major components integrate, and how these integrated components push and are pushed on by story and gameplay design considerations, is to try and build an integrated infrastructure and a complete experience. This is game research.
Maybe by this point the reader is willing to entertain the notion that it is good for the future of gaming to have people doing game research as I’ve defined it. So now the ugly question where this all falls apart – who funds this activity? I’ve participated in a number of academia/industry panels and discussions over the years trying to figure out what kind of productive relationships might exist between the game industry and academia. In my experience, these discussions have never moved beyond industry saying “if you teach students what we want you to teach, we’ll be happy to hire them when they graduate.” Though I didn’t attend the panel “Towards Relevant Research: Collaboration 101” at GDC this year, from what I hear it was the same old story, with academics falling over themselves to make their students as sweet and juicy as possible (anyone who attended the panel, feel free to post a comment contradicting me; but this is the buzz I heard, and based on my past experiences in such discussions, very believable). While preparing students to work in industry is one function of academia, it is certainly not the sole function. If industry believed “game research” wasn’t an oxymoron, perhaps genuine collaboration on problems (including funding) could happen. At GDC a couple of people mentioned to me that their companies are starting or have recently started a research group; I take this as a good sign for the future of research collaboration. Note that such a research group is different from an engines group. While an engines group may be involved in advanced engineering work on, say, the latest physics engine, this is still work in the service of an established design approach (genre or set of genres). A game research group would create new genres, engaging in a combination of design research and technology research.
As far as academic funding, the battle is still ongoing to define game research at the intersection of design and technology as a legitimate, fundable activity. My own work in game research focuses on AI – as I’ve argued before, AI-based art and entertainment (which includes game AI) really is a new research agenda, not a simple application of existing AI research. In order to fund this work through traditional academic funding venues thus means translating an Expressive AI research agenda into terms that funders of traditional AI research can understand, certainly an uphill battle. To make matters more challenging, the funding must support interdisciplinary teams of artists, designers and computer scientists (ideally, these roles are fulfilled by the same people, but the issue of artist/programmers (1 2 3) is an uphill battle for another day).
I don’t yet know a workable model is for this kind of research. But I hope we find one – otherwise we’ll never get to experience those non-incrementally reachable genres, like interactive drama, that lie waiting to be invented.
April 5th, 2004 at 2:48 pm
Michael — thanks for your thoughtful post. Seems to be something in the air this week :)
I wonder if the realities of funding will force us to create schizophrenic research agendas — we’ll have to find waypoints or moments along the path to the moon that individual grants can fund, while keeping our eyes on the big picture. LEM, heavy lift rocket, efficient propellent, life support, etc. Of course, each of these on their own are massive goals.
April 5th, 2004 at 3:49 pm
Michael, you seem to be faced with a Postmodern dilemma. I’m tempted to be pithy and say something like: aiming for the target isn’t the same as hitting the target. Meaning that if you aim for interactive drama you may hit something else instead. But if you try hitting a target by aiming at something not the target, at what should you aim?
This reminds me of a puzzle from the Hitchhiker’s Guide to the Galaxy game — one that is relatively obscure because it requires that you have figured out how to get the babel fish, something only 10% of people were able to do. When you are playing as Zaphod, you find yourself in a powerboat headed towards a dock on a craggy shore. If you aim for the dock, you’ll crash, but if you aim for the rocks…
April 5th, 2004 at 6:51 pm
Well put, Michael. I’m reminded of some of the discussion in Beyond Productivity. We have these areas of inquiry that are important to our culture — and economically important — and no funding model.
April 5th, 2004 at 7:15 pm
Yes, the road ahead does seem glum. I have a question though, a possible approach: Why aim your work at the producers in the industry? From my experience the entertainment industry — television, effects, tvcs, games — will always do what it can to sell more of their own product. Fear of loss of market share and so on is a large factor in decisions. The consumer on the other hand wants to be entertained. Why not work to produce products that people want to and can buy? Why reshape your invention for a postal service when the recipient is happy to be handed it? I guess the question is: who is the research for?
April 6th, 2004 at 9:29 am
Michael asked, To put a finer point on it, how do I fund the next Façade?
First we should point out that Facade itself was only spottily funded, so it can’t even be used as a case study of how to fund this kind of research. (For the sake of discussion, I’ll go ahead and make the assumption that Facade has achieved enough results that, in hindsight, would have been worth funding at some level.) Michael had received tuition and grad-student stipend for some of the project, the approval for which in itself was due to unusual fluke-like circumstances; also he was able to apply a portion of his startup funds to cover a few months of our work, but overall the project was self-funded; I worked at least two years with zero pay, which is do-able not a very sustainable work model. One reason Facade is taking so damn long to finish is we’ve both eventually had to take jobs to pay our rent, only giving us nights and weekends to finish it up.
And, the truth is it took over five person-years to develop Facade, the bulk by two very experienced, self-managed people. Each of us came into the project with 7+ years of industry experience (I had shipped 6 products) — not your typical grad students who are willing to work in exchange for tuition and stipend, who need a lot of guidance. To have “properly” funded this project would have required several hundreds of thousands of dollars.
Note that a key part of Facade’s value is that it is game research and development — once the research phase was “done” we took the time to author a lot of content, polish it to a playable level, test and debug it. Risky research is hard to fund, but all that development time is probably even more difficult to fund. But without that development effort, the value of the research would be unproven! It’s only by having a reasonably polished, playable system (even if small), will industry folk be able to look at and evaluate the research, and potentially build a new product around it.
Here’s an idea. I like to believe it’s possible that if offered the chance, talented people with industry experience would be willing to leave their industry jobs for a few years and accept a minimal salary (e.g. as low as $40K), working alongside academic researchers, for the opportunity to do real game development R&D. I believe there exist enough developers out there hungry enough to innovate that this could be pulled off. I’d hope that for, say, $250K, a team of 2-3 from industry and 2-3 from academia (a P.I. and grad students) could be assembled for 2 years of hard work, to accomplish some non-incremental innovation. (I would have taken such an offer, and still would!)
If you believe my assumption that for game research to be noticed by industry, it must be used to build an at least minimally authored and polished experience, then short of the model I just described, I’m not sure how much can be accomplished in academia. (I’d love to be proven wrong though.) Industry research labs, e.g. Microsoft, Sony, Interval, seem better suited, although I’m not too familiar with how those projects get approved, how much time and resources they get, how much freedom the team really has, how much in the end gets shared with the public.
The small company I recently joined, Zoesis (an spinoff of the CMU Oz project), is a very unusual but I think successful example of doing game research. They recently received a $2M grant from the U.S. Dept of Commerce, that the company is using to do research to create lifelike characters with conversational ability; a portion of early results were publicly demoed two weeks ago to industry folk at the GDC Experimental Gameplay Workshop.
But, overall, if all else fails, I think people will have to take matters into their own hands, and do what it takes to scrounge together funds, savings, art grants, etc., as scrappy independents. The good news is, even if you’re an individual not affiliated with any official institution (academic or industry), if you do useful research with tangible results, you will be welcomed into the academic community (at symposia, conferences) and at some industry venues (e.g., GDC, Gamasutra).
April 6th, 2004 at 1:34 pm
Why not work to produce products that people want to and can buy? Why reshape your invention for a postal service when the recipient is happy to be handed it? I guess the question is: who is the research for?
The point I was making is that there are non-incremental genres waiting to be discovered that, to put it in the language of the marketplace, consumers don’t know to ask for and producers don’t know to build. The research is about new kinds of experiences that, once you see them, you know are powerful, compelling, desirable, but that you don’t know how to think about or build until somebody does it.
First we should point out that Facade itself was only spottily funded, so it can’t even be used as a case study of how to fund this kind of research.
Yes, I’m not saying that how we funded Façade is a model. Rather, I acknowledge that our model for how we made Façade is not sustainable. My post was a meditation on how and whether it would be possible to fund a project like Façade in a sane way. That said, I should point out that as a grad student at CMU, with overhead, tuition, stipend, and various fees, I cost around $70K a year. So the 3 years of my grad career that I worked on Façade cost someone (namely Jaime) $210,000.
I agree with you that doing this research involves building complete experiences, and that involves development. Small, playable, reasonably polished experiences must be built to get the feedback to know if you’re even pursuing the right questions, and what the next questions are. You think to know what to build, and build to know what to think (Roger Schank described AI research this same way). Academia doesn’t tend to reward “mere” development, but there are exceptions (AI architecture work tends to involve a lot of development – OS and compiler research similarly involves a lot of development). If there were game industry folk interested in working as research scientists on a game research project (for less than they probably make in the game industry) for a couple of years, this could be an interesting model. Still begs the question of where the money comes from, however.
If there was an industry research lab doing game research as I’ve described it, I’d love to examine their model. To my knowledge, nobody is doing it.
The main problem with the “scrappy individual” approach is that, unless they’re fairly tapped into the current streams of thought in academic research, they often end up reinventing the wheel (very slowly and painfully) or otherwise not leveraging known approaches and techniques. It’s hard to make a non-incremental contribution without being somehow connected to a research community.
April 6th, 2004 at 5:23 pm
So how does a “scrappy individual” get connected to the research? My primary source the last few years has been first citeseer, then tracking through references for interesting material.
Unfortunately, this means that I am always a good 3 or 4 years behind best case, as that seems to be about how long it takes for the ‘white paper chaff and wheat’ to be separated.
As a programmer in the game industry, keeping up with such research is important to me. The limiting factor is purely time, given the amount of research going on.
April 6th, 2004 at 10:57 pm
Two frameworks for rewarding and funding experimental work are the free market and academia. If you want industry to fund research, you have to play by the rules of the capitalist game, which means help ship a product (game) or start your own studio to purse your crazy ideas. Luckily, academia has less penalty (and financial reward), for trying new ideas. It seems like a lot of game research could be funded in traditional academic frameworks: systems research, AI, graphics, HCI, etc…
Gonzalo Frasca’s Powerful Robot studio is an example of using a commercial studio to produce experimental work.
What I’m hearing, Michael, is that while you think these are fine games, you don’t want to play by these rules exactly. You want to play a new game with slightly different rules, like where big, successful game companies would reward academics for risky research, and universities funded experimental games like they pay for experimental operating systems.
It seems that both of these things are logical ideas, but it’ll take time for them to happen, if they happen at all. Will Wright pointed out that many of these roadblocks are a function of time. Will observed that the game will be totally different once we have a generational wave of cross-pollination: university folks working in the buisness, and ex-game-developers teaching at universities. Think of Fred Brooks.
Let’s say that in 5 years many big game studios have research divisions, for some definition of research, and universities are funding experimental game development, for some definition of games*. Both of these sound like logical steps to me. What would be a surprising and desirable variation on that arrangement? Is anything more even desirable? Why? Would something like the Media Lab (a corporate research DMZ, to paraphrase Negropante), but for games, be desirable to both parties? Are advances in the digital game medium intrinsically linked to academic research programmes in ways that the development of other practices, such as film, aren’t?
* I think Facade is a new genre and only barely resembles a game. Not that it isn’t interesting, but the game industry’s first interest would be in stripping it for parts (character AI, for instance). Unless, of course, you and Andrew make a ton of money, or everyone and their mom plays it.
April 7th, 2004 at 1:02 am
Are advances in the digital game medium intrinsically linked to academic research programmes in ways that the development of other practices, such as film, aren’t?
It seems that creating new computer game/play/art genres — certainly of the ambitious sort that interest Michael — is more like creating new methods of capturing, editing, and projecting moving images than it is like using existing ones for alternative means. It’s the same reason that those interested in funding this work can’t do it by establishing the equivalent of the independent film economy (“Why not work to produce products that people want to and can buy?”).
Will this always be the case?
April 7th, 2004 at 1:06 pm
(1) Has anybody tried the NEA or the NEH yet?
(2) What about assembling P.I.’s from different fields and creating an *internally* “schizophrenic” research budget, then clabbering together some mixture of grants? My girlfriend (a Victorianist) and I have this idea, see, to create a Regency marriage-plot simulator, like Facade with a telos. I figure you would need one Victorianist and one speech-act theory inclined linguist as P.I.s (and maybe an A.I./HCI specialist) and then a bunch of grad students, and you could reasonably apply for grants to fund the different aspects of the research, and still produce something. Just tell them you’re investigating “modes of extending current theory by generating an experiential space for experiment.” It’s not that different than the Hypercube/HyperAtlas I’m involved with (http://www.chicagoschoolmediatheory.net). Now, granted, we haven’t won any grants yet, but we are just finishing the first round of applications.
April 7th, 2004 at 3:06 pm
re: Chaim and noah’s remarks on games and film practices
It is hard to look at Hollywood and talk about whether the industry has advanced due to academic work, versus whether academic work thrives because of the industry. It is a medium that reached a certain critical mass several years ago, to the point where the industry can support writers whose scripts are never made, producers who make sitcom pilots that are never seen, and actors who make a living as extras. Most of this is due to a generous but rarely unspoken of philosophy, that if you spread your profits around you will attract a lot of loyal and talented people.
With all the buzz that the game industry is about to surpass/has already surpassed Hollywood in term of box office receipts, I have doubts that it has reached the same critical mass. If it had, I think you would see a lot more interest in academic programs, a more legitimate independent games movement, and, last but not least, /better journalism/.
But I also think that computer games, as a subject for study, is far too narrow. I’m still working on my New Forms Manifesto.
April 8th, 2004 at 12:02 am
Michael wrote: The main problem with the “scrappy individual” approach is that, unless they’re fairly tapped into the current streams of thought in academic research, they often end up reinventing the wheel (very slowly and painfully) or otherwise not leveraging known approaches and techniques. It’s hard to make a non-incremental contribution without being somehow connected to a research community.
Brian wrote: So how does a “scrappy individual” get connected to the research? etc…
Aha, a solvable problem, that doesn’t require much money! I think you’re both right, that it currently feels like too much work for those not fully plugged-in to the research community to get much benefit from it, unduly handicapping the process.
Imagine an academic project whose goal it is to encourage and woo industry folk to do game research, by providing them with clear, edited summaries and paper links of the history and latest applicable research of game-oriented technology — character AI, procedural animation, emotion, learning, etc. As an example of the format, this could be a more detailed version of Michael’s oft-cited 1997 Review of Interactive Drama and Believable Agents, and/or a sort of an academic, broader, deeper version of Steven Woodcock’s annual Game AI: State of the Industry.
Perhaps this “Academic Game Research Review” could be done periodically, every year or so. It would take some time to prepare the first version, and then take a person-month or two each subsequent year, but the work could be shared among a group of academics. It would have to be funded (I don’t know, $20K up front, then $10K/yr? something relatively cheap), otherwise it becomes a thankless task that would never get done. Perhaps it could be funded under the auspices of trying to build academia-industry connections.
Given such a resource, it could encourage motivated industry people to become “scrappy independents”, and nurture them, as well as help out developers working at game companies.
Additionally, imagine holding a yearly 2-day Game Research Outreach Workshop, to which industry folks are encouraged to come, where the yearly Review is presented, avenues of R&D are suggested, and brainstorming and Q&A could happen.
In a nutshell, make it a lot easier for experienced game developers to apply and build upon academic research.
April 8th, 2004 at 3:37 am
I have my doubts about Chaim’s imagined research being funded by the game industry in 5 years. As long as publishers are sequel/hit-driven, and developers forced to toe the line by publishers, I don’t think the industry has any way they’re going to fund their own internal research. You will have people like Will Wright able to get his company to fund his games, which may effectively be research, but that’s a special case.
(I’d certainly like it to be otherwise; four or five years ago I canvassed a couple people I knew in the industry about the idea of funding me to spend two years working on doing something liek non-incremental believable character research; but given the lack of guarantee of any useable results, I couldn’t get any bites. Maybe if I could have found eight different companies and hit them up for $10K each (using Andrew’s $40K number) it would have been possible, but I didn’t know that many people who’d have had that much confidence in it.)
There’s an opportunity for _independent_ game development to do really novel stuff, since that stuff mostly _is_ just self-funded. Unfortunately, it’s difficult to do large amounts of content that way, and it’s hard to actually market and try to self-fund, so most indies don’t take many more risks than mainstream developers. So I think we’re kind of doomed to the Facade model: developers who try to push things do it self-funded, and only do it once (or once in a while).
On the third hand, I think the game industry doesn’t even do incremental improvements to the sorts of things we’re interested in, so getting people working on _that_, whether in the industry or in academia, would be nice.
Also, I agree that things like Michael’s paper are really useful. (In fact, I wish I’d heard of that paper five years ago, instead of a week ago–although in practice it looks like the incremental research I’m doing on story generation is still unexplored, anyway.) Good luck getting the industry to pay for it, though.
April 8th, 2004 at 6:33 pm
Let’s say that in 5 years many big game studios have research divisions, for some definition of research, and universities are funding experimental game development, for some definition of games*. Both of these sound like logical steps to me.
I agree with Sean that this is not a logical or necessary outcome, but will have to be actively nurtured. Many universities will have game programs, but much (most? all?) of the research will be either game studies research or design research, where you assume no new technology. The kind of research I’m talking about involves a combination of technology and design research. And this is what makes it different from Powerful Robot – I think Gonzalo would agree that Powerful Robot isn’t doing CS research. Of course you can develop new genres through design experimentation, using established idioms in Flash or c++. But, as I argued above, there are regions of design space that can’t be reached only via design ideas. And its far from clear to me that game studios will really have groups doing this mixture of CS and design research.
I like the idea of a Game Research Outreach Workshop. Also, I’d like to point out that my review of interactive drama and believable agents is a out of date now. It’s really time to write another one.
April 8th, 2004 at 9:15 pm
Michael, when will you learn to abuse your power? Now is the time to find a graduate student to update your review of interactive drama and believable agents.
April 9th, 2004 at 2:08 am
With no disrespect intended, I think it’s a bit ironic that a discussion of research into unconventional game content is so wrapped up in such traditional notions. Why do we limit our definition of industry to game developers and publishers?
Let’s face it, these folks have a vested interest in preserving the status quo: it’s far cheaper and more predictable to exploit existing, proven genres than to go about rocking the boat trying to come up with new ones that’ll force them to rework their production pipelines, marketing efforts and revenue projections. “what about being first to market with that new blockbuster hit?” you ask. Doesn’t matter. It’s easy enough to buy or replicate a newly proven genre, and you’ll make more money in the long run than you might have lost on the original property. And you can do it without tainting your reputation with the string of failures that have to exist if innovation is to happen.
Simply put, not only is there less risk in following tried and true formulas, there’s virtually no risk in not trying anything new.
This isn’t speculation but a message I’ve heard repeatedly in personal conversations with CTO’s at EA and elsewhere.
If you want to go where the money is, look for those companies most likely to benefit from the kinds of siesmic shifts in the industry that come about as a result of new the genres you’re researching.
Case in point: I currently work for a large network computing company, (okay, it’s Sun Microsytems) having spent a number of years in academic research. We are currently sponsoring a project at Cal-(IT)2 that proposes to do exactly the kind of research that both you and I believe the games industry will not support, namely experiments with new game genres and the technologies necessary to make them happen.
“Why would we do such a crazy thing?” you ask.
Well, think about it. We makes our money supporting network infrastructure. The folks at Cal-(IT)2 are interested in using heterogenous networks and devices (think cell phones to supercomputers) to explore new game genres. If they come up with a revolutionary new genre that spawns a hit, that drives demand for greater network infrastructure. If they produce no new games, but the results of their work inform existing genres, that drives demand for greater network infrastructure. If they develop nothing of value, it’s still a tax deductible donation. Anyway we look at it, we can’t lose, right?
So to your next question, “Why don’t we just sponsor technology research?”
I say: Because new technologies don’t expand the market for applications, but new applications do expand the market for technologies.
Not that we’re prepared to sponsor any and all game research; there are specific areas we are more interested in than others. That said, I do think it’s worth expanding one’s definition of the “industry” when considering where funding for game research might come from.
April 9th, 2004 at 11:12 am
Athomas, what you write about looking for funding in other places, like computing companies, certainly makes sense. Michael and I had a similar conversation at GDC. I’m glad you’re part of a group that’s pioneering new models.
No disrespect intended to those CTOs, but I’m a bit amused by the statement, It’s easy enough to buy or replicate a newly proven genre, and you’ll make more money in the long run than you might have lost on the original property.
Now, I have the impression that The Sims has done pretty well — to put it mildly — so we could say its new genre is proven. Where are the replications? Seems those knock offs are taking a little while to get to market. Which makes it seem to me as though the people who came out with The Sims actually are getting “the benefit of being first to market with that blockbuster hit.”
Do the folks you were talking with see the case of The Sims differently?
April 9th, 2004 at 1:45 pm
Actually The Sims is a prime example of what I see as the attitude of a significant chunk of the industry toward innovation.
If you look at the history of Maxis you’ll note that Will Wright had released 9 games at a company he started himself because no one would publish SimCity when he first created it. It wasn’t until 8 titles (and 13 years!) later, after these games had already become hugely popular, (and Sid Meier’s Civilization had further established the genre), that EA finally acquired Maxis.
Arguably, The Sims represents an important but still incremental change to the existing genre of open-ended, non-competitive, social simulation games that Will pioneered, but had, nonetheless, been long established by the time the game was released.
One of the reasons we don’t really see any direct knock-off’s of the Sims may be that the genre is so well established at this point that there are quite a few directions one can take while sticking to the same proven formula. Atari’s Roller Coaster Tycoon series and Microsoft’s Zoo Tycoon series are just two examples of hugely popular games that have probably suffered little from not having years of minimal or mediocre (commercial) success while trying to break new ground.
April 9th, 2004 at 3:29 pm
Robin Hunicke has some comments about this thread on her blog.
April 9th, 2004 at 3:43 pm
Why do we limit our definition of industry to game developers and publishers?
In fact my current source of funding is from Intel for reasons similar to those you list for Sun. AI-heavy entertainment genres (e.g. interactive drama) chew mips (more than graphics ever will). This drives the need for faster processors.
So “technology centric” funding is one possibility. Along those lines… Athomas, I have proposed some work, not currently funded, in online social learning for believable NPCs in massively multi-player, that is networked, worlds. Perhaps Sun is interested… :)
But, hopefully, technology-centric funding won’t be the only source of funding for this kind of work. I’d like to see the game industry step up to the plate as well.
April 9th, 2004 at 4:31 pm
Athomas, that’s an interesting insight into how some in the game design community see The Sims. That might explain why there aren’t more identifiable knock offs. I’m pretty sure, however, that the general public sees it as almost the only entry in the “games you play with simulated people” genre.
April 9th, 2004 at 6:44 pm
You may be right. I haven’t sampled the general population, but my daughter, who is a big fan of The Sims, SimCity, Zoo Tycoon and others of the genre, does tend to lump them all together into the same general category. When she and her friends play the Sims, they spend most of their time building houses and then let the Sims run around, adjusting the environment in order to keep the Sims happy. When they play Zoo Tycoon, they do the same thing, only on a different scale. I think she’d agree that the experiences were qualitatively different, but she’d probably feel the same way about the comparison between Zoo Tycoon and Sim City, but she probably wouldn’t characterize them as wholly unique and distinct activities.
I’m not saying there isn’t a distinction, or that the distinction isn’t socially relevant. However, from the publishers point of view, now that they’ve honed in on the audience for these games, they don’t need to replicate The Sims in order to successfully market new games to the same demographic.
April 9th, 2004 at 8:18 pm
Michael wrote: I’d like to see the game industry step up to the plate as well.
Who exactly do we think the game industry is? Most of the money is in the hands of a few publishers – the rest, spread around in companies that are trying to maintain/scale despite hit-or-miss sales numbers, continually changing technology, and all the problems inherent in large-scale software development.
If there was a surplus of funds, it might go to a local university – but for the most part (and understandably) it would go to bonuses. Working your ass off is common in the industry, and being paid for it is not. When there’s money, I’d say the creators have first dibs.
So… looking at recent events at CMU/GTech/USC we see that EA, Microsoft, Sun and Intel are the big funders of long-term research in game tech and genre-expanding experiments. Educational funders, government funders and some private investors can also be wooed. And they all want some piece of the IP, so it isn’t just free money.
Either way, the focus will always be providing solutions that can be funded by the interested parties – and “innovation” isn’t really a solution – it’s a result of lots of incremental hard work. Most of which, as we all know, fails pretty miserably.
So can’t we just do the hard work (and the failing – sigh) and see what we hit (as Ian and B. Rickman suggested at the beginning)? What makes us any more special or deserving of consideration than the systems researchers I mentioned in my post from the other day?
I mean – I know we rock the pants off systems researchers, but still. We have more style, but that doesn’t mean people should be falling all over themselves to fund our brilliant ideas. If anything, it means more/better fan mail (and some pretty pants-less systems folks).
April 9th, 2004 at 8:19 pm
While I can’t make any promises, I am definitely interested in proposals for research around innovative content that uniquely leverages or pushes the limits of the network, so send me what you’ve got…
As for the game industry stepping up to the bat, I think it all comes down to how one defines “the industry” If we’re talking developer/publishers than it could be a while, if ever, before they really begin to support this area. However if you look at the number and types of companies involved in the production and distribution of games, actual developers and publishers are only one component of an increasingly complex value chain.
In the last year alone, since I started at Sun, I’ve seen the industry undergo a radical shift that I think most people are completely unaware of. Wireless operators have made games, and now multiplayer games, one of their principal service offerings to the customers. Wireline & broadband providers are now seriously committed to implementing games-on-demand as a value-added service on their networks (in order to drive demand for high-speed access) which will pave the way for serial content and sophisticated network gameplay. Major communication infrastructure companies, whose names you’d recognize, are looking at either supporting, or becoming, Game ASPs. While the effects of this have yet to be felt by the consumer, there are a large number of companies, whose individual revenues dwarf that of the entire games industry, now devoting substantial resources to shaping the future of this business. Not to mention the number of companies looking at games and game technologies as models for applications within their own industries.
All in all, we are in the beginnings of what may be some of the most dramatic changes in the games business to date, and, without revealing more than I can say, two years from now the “industry” will look very different from the way it does today.
The fact that this should coincide with the upsurge in critical theory and experimental research in games has made it, for me at least, a pretty exciting time to be in the “industry” :)
April 9th, 2004 at 9:03 pm
Oh, and I completely forgot to mention the rise of the game tools & middleware market, which, in the last few years, has gone from being extraneous to useful to essential, adding yet another interesting link in the games value chain.
April 10th, 2004 at 6:24 am
Robin makes great points about where the game industry might first choose a surplus of money, as well as how a few large companies have initally chosen to invest in academia.
It occurs to me that almost all the participants in this discussion are American. I’ve noticed that in Europe it seems a bit easier to get funding for game research. And although I don’t often see game research coming from Asia, at least in the conference circles I dwell in, obviously game production is huge there (Japan, S. Korea).
Can anyone from those parts of the world share their thoughts or experiences on how to fund game R&D?
April 10th, 2004 at 10:16 pm
There are actually a few Sims knockoffs, such as Space Colony and the German Singles.
April 11th, 2004 at 12:14 pm
Sorry I missed the discussion, I was crusing Denmark for a few days. This is certainly a wonderful discussion and I think that it should be taken further, here and in other spaces. To sum up my position, I do not have any hopes for the industry to massively move into interesting research any time soon. They are interested in money, not innovation. Innovation will come when money is at stake. As simple as that. Sure, some big players may have their research labs and a few people will have some serious fun, but that’s about it. Innovation, if it happens, will come from the smaller players. Certainly, that is the strategy that I have been following at Powerful Robot, but it only allows us to do very short experiments within very short time. Surely, it allowed us to experiment in political videogames and I am certainly very happy with the results. However, for any result to be significant, we need hundreds of small independent studios/teams taking risks. Hundreds, if not thousands. How many people in the world are doing such things? Maybe a hundred, maybe a few thousands, maybe more. We may never know, actually. Why? Because many independent game developers are just young, brilliant people trying to get a job in the industry (and that is a perfectly acceptable agenda,btw). We need to gather more independent researcher/developers/artists and exchange our ideas, work together even if we still work independently. Innovation will come from people with an agenda: advergamers, researchers, military, people in porn, political institutions, educators. The industry simply wants to entertain ourselves and get their benefits (again, that is perfectly fine with me). The sad truth: making games is hard, takes money and time. We need hardworker people, with time and money. Otherwise, things will take an awful long time to change. And that’s about it.
April 12th, 2004 at 9:15 am
For me, and for many other researchers and independents, the solution is to go open source. This is what academic research is in the first place, so it is not like, revolutionary or anything. One just has to make the $$-eyed university directors see that we are not in business to make money, but to give ideas away.
With large-scale open-source game projects, we can stand on each others’ shoulders and create platforms that can compete with the commercial products, and give independent game developers and artists a real chance to innovate. All it takes is one – 1 – multi-purpose, modular platform and open-source 3D tools like Blender.
Then we don’t have to worry about licences, or about which commercial platform to train our students with, or about becoming stifled by industry non-disclosure agreements.
Game innovation (SpaceWar!, Adventure, Rogue, MUDs, and all those SIGGRAPH papers) used to be open source. A strong, academically supported OS game platform would be immensely valuable, not just to us and our students, but to game designers and artists everywhere.
If anyone out there is interested in becoming part of an open-source game/MMOG platform working group, then please don’t hesitate to contact me.
April 13th, 2004 at 3:28 am
Given who you are relative to our field, I presume you’ve seen this, but thought I’d put it out there just in case:
P.S.: Not sure if y’all have noticed yet, but this whole blog thing is hella’ cool. How else could I spontaneously participate in a public dialogue with someone I’m citing extensively in my B.A. Thesis who *isn’t* on the faculty at Chicago?
April 13th, 2004 at 8:40 pm
$14 Steadycam txtkit – Visual text mining tool and game research [via grandtextauto] Mogi – GPS camera phone hunt…
January 18th, 2005 at 6:44 pm
August 18th, 2008 at 5:47 am
Sorry to raise this post from the grave!
I’ve just stumbled across this one, and I wonder how people feel that this might have changed?
I am *very* hesitant to describe the current situation as a “post-Portal” landscape, but we are now at a time where experimental games have got the prime-time they deserve. PSN and XBLA opens people up to new experiences, games like Flow and Braid are games that most people would never have played before.
Hopefully XNA can help sidestep some of the certification entanglement and get more experiments out there. Academia, whether games research or games studies, should already be keeping a firm gaze, and a feedback loop needs to take place. Who liked Flow? Why did they like it? Can we begin perform games research on a worldwide scale, transmitting play data back to a public database to be mined and studied by institutions all over the world?
Unlike in 2004, it’s clear that the audience for something fresh is there, even if they only experience it for five or ten minutes on a free demo. Five or ten minutes time from even a relative handful of people (say 100 000) could lead to some really interesting results.