A Taxonomy of R&D Orgs
What Is New, What Is Missing?
“It is a common observation, that mens studies are various, according to the different courses of life, to which they apply themselves; or the tempers of the places, wherein they live.”
– Thomas Sprat, The History of the Royal-Society of London, 1667 (I.9.5)
For more than a century, American philanthropists have created novel research institutions to fill the gaps left by incumbents.
Cold Spring Harbor Laboratory, for instance, was founded in 1890 to provide naturalists and educators with summer access to species and conditions they couldn’t observe at the academy. Andrew Carnegie created his institution in 1902 “to find the geniuses of the Republic and set them to work on the higher problems.”1 From Bell Labs to DARPA, most of the great research organizations of the 20th century developed novel approaches to organizing scientific activity across the dimensions of governance, funding, staffing, and relationships with research users.
But we still have gaps, which is why today’s philanthropists are accelerating the formation of new orgs: the Parker Institute for Cancer Immunotherapy, the Allen Institute, the Broad Institute, the Chan Zuckerberg Biohub Network, the Stowers Institute, the Janelia Research Campus at HHMI, the Arc Institute, and the Francis Crick Institute. Even further outside the existing box are Arcadia Science, Speculative Technologies, and Convergent Research. And more recently, the National Science Foundation announced a new “X-Labs Initiative” to fund new organizations outside of the traditional university system.2
This flurry of activity raises an interesting question: What exactly are the parameters of possible science organizations? And once we identify these parameters, how do we determine which ones to move, in what directions, and by how much?
These questions get more pressing given (the likelihood) that frontier AI labs going public will dramatically increase philanthropic investment in scientific research3 – we must start thinking about the best ways to absorb this additional capital4.
Thankfully, we are not starting from a blank slate. Focused Research Organizations (FRO), a type of “nonprofit startup for science,” is innovating on two axes: 1) These groups focus on one particular scientific mission, rather than many diffuse objectives; and 2) they work over a limited timeframe, rather than pursuing their aims indefinitely.
But focus and time are only two parameters. If there are 10 parameters of R&D organizations, each of which could be merely absent or present, there would be 210 (or 1,024) possible types of organizations. In practice, these parameters aren’t purely binary, so the real possibility space is far larger. Even if many of those combinations don’t make sense (or are impossible to implement), it is likely that there are rewarding and achievable arrangements we haven’t tried yet.
In this essay, which grew out of preliminary notes created by Good Science Project fellow Eric Gilliam, we suggest that there are at least nine parameters of R&D orgs:
With all of these traits in mind, we believe that funders and entrepreneurial researchers might be able to identify “holes” in the R&D ecosystem, in much the same way that Adam Marblestone and Sam Rodriques identified an FRO-shaped hole and gave it a name. We could do the same for any number of scientific problems.
Optimal project timelines
How much time can an organization or research team spend on a project without positive results? The answer to that question dictates the types of projects they can and can’t pursue.
Many university labs do basic research via individual projects that have a high probability of success and can be completed in the length of a PhD program or postdoc fellowship. Meanwhile, a group that is free to work on a line of research for 7-10 years despite having no publishable results in year 5 is obviously working on a very different timeline.
A 2011 metascience paper published in the RAND Journal of Economics compared NIH-funded researchers to those who won a grant from the Howard Hughes Medical Institute (HHMI) and found that HHMI’s funding led to “high-impact articles at a much higher rate.” This paper is often cited as evidence that it is better to “fund the person, not the project,” because HHMI funds researchers based on their track record, while NIH focuses on specifics of proposals.
But there’s more to glean from the paper, which also notes that HHMI grants provide funding for more years than NIH grants and are renewed at a higher rate. Lead author Pierre Azoulay of MIT once told Stuart Buck that he suspects this is the secret to HHMI’s success: long-term grants with a strong likelihood of renewal give researchers enough time to focus on making breakthroughs despite no immediately obvious payoff5.
The available timeline does not independently determine ambition however — short timelines can coexist with high technical risk, and long timelines with conservative incrementalism. The governance structure (discussed later) also interacts with timelines in ways that can amplify or undercut the flexibility that long timelines are supposed to provide. But the disincentive to work on projects that don’t yield publishable or sellable results for extended periods is a significant constraint in R&D orgs, however it manifests.
Nobel Laureate Irving Langmuir and his research projects at General Electric (GE) illustrate this point. Langmuir was allowed to spend years rather than months on individual research projects, provided they were directly related to the problems of GE engineers and workmen6. The timeline allowed him to be ambitious in ways he could not have been if GE needed a “product” from his work within a year. His explorations often ended in places he did not expect, and several of his research projects ultimately led to new product lines, billions of dollars in revenue for GE, and a Nobel Prize.
How to measure research project timelines
The timeline of expected project payoffs is among the easiest parameters to measure. One can measure it in raw time units — 6-18 months, for example. In other cases, it makes sense to measure time in terms of money: How long can a research organization sustain its burn rate?
Level of user input
A second major trait: the extent to which an organization’s research is motivated by user-specific needs7. This is distinct from the question of who within the organization selects projects. Rather, user input is about whose problems shape the research agenda. For example, as Jeffrey Tsao has argued, the widely admired successes of Bell Labs resulted from its close connection to a technology corporation that needed to transmit information effectively8.
On one end of the user input spectrum is a botany professor who seeks to understand a plant’s life cycle simply because it’s interesting, or a mathematician working on a proof just because it’s elegant. At the other end is a corporate R&D shop myopically researching questions that are precisely relevant to corporate strategy.
Two factors help clarify where an organization actually sits on this spectrum: how well the researcher understands potential users, and whether users can say no to the researchers. For instance, Bell Labs used systems engineers to understand potential users, and GE Research forced even people like Langmuir, at least early on, to understand problems on the applied side of the lab before building anything.
User veto power, meanwhile, shows up clearly in the evolution of ARPA (renamed DARPA in 1972). In the agency’s early years, project managers could build things with users in mind, even if those users did not ask for the technology. In later administrations, however, PMs increasingly needed the promise of follow-on funds from specific users before undertaking a project. These are very different operating procedures that produce different scientific portfolios.
Many of DARPA’s most ambitious projects might be characterized as basic research due to their low probability of success and years-long timelines, but the focus on users distinguished the agency from its university-based counterparts. DARPA’s Autonomous Land Vehicle work, which helped usher in the modern autonomous vehicle revolution9, is a case in point:
A PM worked to thoroughly understand the needs of the Army
The Army did not express interest
The PM built for them anyway
DARPA’s experts built for a user who did not yet understand the product, while keeping that user in mind at every step. Indeed, it is possible to credit part of DARPA’s success to this approach. As Ben Reinhardt notes, “DARPA derisks working off the beaten path for small companies by giving them more confidence that there will be customers for their product – either large companies or the government.”
How to measure levels of user input?
The best way to measure levels of user input might be something like the following set of categorical variables:
Pure undirected. Researchers don’t talk to users and aren’t obligated to justify projects as having practical outcomes.
Holes in the literature with practical justifications. Researchers don’t talk to users but still justify projects as useful to them10.
Build for users with the freedom to ignore them. Researchers talk to users, justify projects as useful to them, but can still say no to users and build something new. (Think application-minded university researchers, confident VC-funded startups, certain corporate R&D shops, and many old DARPA teams, etc.)
Build for users with no freedom to say no to them. Researchers talk to users, justify projects as useful to them, and can’t conduct research that users don’t want. (Research is expensive, and many executives choose to take risks in other areas of the business rather than in their research strategy. As a crude example, if the c-suite thinks customers want a lighter phone, that – and only that – is what company researchers focus on.)
Wealthy users buy a portion of research time at a higher rate. Researchers sell a small fraction of their capacity to a top-tier user for a 10x rate and within those confines function as a tightly controlled corporate R&D team. That arrangement allows for research organizations’ remaining capacity to function much more autonomously.
Size of discretionary funding
Although it sounds painfully obvious, it matters whether a research team/lab/org has the discretion to decide what to research, rather than being tied down to objectives and milestones written down years before.
The slogan “fund people, not projects” reflects the importance of discretionary research budgets. Forcing a lab to run to the NIH so that it can follow up on results that look a little strange is a rate-limiter on the number of shots a lab can take. This is particularly true when the funder makes decisions based on a peer review panel that is inherently biased against projects viewed as speculative.
Inconsistent grant renewals can incentivize researchers to manufacture discretionary funding under the radar by applying for grants to support work that is largely complete, then redirecting the new funds toward riskier explorations. This practice is widespread enough that it even might amount to a shadow system of discretionary budgets!
An extreme case can be found in DARPA’s Computing Center of Excellence block grants to departments at Carnegie Mellon University, Stanford, and MIT. In the early years, the money was largely for the departments to use as they saw fit, though DARPA had many ongoing projects and expected expenses to be covered by those budgets. But it was also understood that these departments would use a large portion of this money to conduct new, useful research that would pay dividends to the DARPA ecosystem.
The conversion of discretionary funds into exploratory research depends heavily on whether the organization’s governance structure allows individuals to spend autonomously – how much added friction do researchers encounter when deploying the budget? A lab could have large discretionary spending capacity on paper but lots of bureaucracy surrounding expenditure which may mean that the funds are discretionary in name only.
How to measure discretionary research budgets
Within a single era and field, the actual dollar amount a researcher could spend per year at their discretion is a reasonable measure. However, across time or fields, a better metric might be the additional number of experimental rounds or researcher-hours the money can buy. Sometimes, it may also be useful to measure the percentage of a research group’s funds that are discretionary.
Career incentives, attracting talent, and personnel models
Every organizational model implicitly selects for a certain type of researcher.
Bolt, Beranek and Newman (BBN), “the contractor that did the most work to bring the ARPAnet into existence,” attracted many of its best people from Lincoln Laboratory where researchers had become accustomed to seeing their ideas sit on a shelf until industry was ready to productize it. In BBN’s model, people could build, test, and deploy rapidly. This expectation selected for a relatively rare sub-type of researcher who was comfortable moving between basic research and systems engineering.
Similarly, the early ARPA-funded computing departments offer another case. ARPA’s block grants to CMU, MIT, and Stanford funded the creation of a new type of technical position. The research scientist and research engineer roles that emerged in these departments were permanent (or semi-permanent) staff whose careers were focused on building and maintaining the large-scale systems on which the research depended. This personnel innovation was perhaps as important to program success as any particular technical insight.
Also important: how the incentives of key research staff are different from the lab’s top decision-makers, and how that may affect recruitment and talent selection. It’s one thing for a tenured professor to declare that their field doesn’t focus enough on building and maintaining entirely new instruments, and then attempt to do exactly that. However, even if their grad students and postdocs agree with them, spending five years writing two papers in an unfashionable area might prevent them from also getting tenure.
This principal-agent problem is partly a function of who staffs the lab and on what terms. In the traditional university model, the pyramid mostly exists as such: a tenured PI at the top, a few postdocs in the middle, and a base of graduate students who do most of the bench work. This structure has its benefits in that it keeps labor costs low while training the next generation of would-be scientists, but it also means that most lab-members cycle through on relatively short timescales (4-7 years for students and 2-4 years for postdocs). Institutional, tacit, knowledge flows out continuously, and career incentives point trainees toward safer questions that would yield publishable projects instead of ambitious, long-term work. Importantly, the entire system assumes that the primary career path for research staff is to become PIs themselves (which is true for only a shrinking fraction of trainees).
Being attuned to the incentives that drive their ideal hire can help research groups structure their orgs accordingly. At the Janelia Research Campus, Gerald Rubin limited lab sizes, restructured the postdoc pyramid, and hired research scientists as permanent staff to circumvent the problem of lab staff turnover.
The Institute for Advanced Study indexes for a different type of person by bringing on a mix of permanent faculty and rotating visitors, on one- or two-year appointments. In their case, they benefit from the short appointments of talent because it brings fresh perspectives – but it only works because the IAS is not executing multi-year engineering projects that require stable teams. FROs take yet another approach: hiring for a specific mission with a defined endpoint. Staff know that the organization may not exist in 10 years, let alone five. This explicit uncertainty weeds out one type of person while simultaneously attracting people who are genuinely excited about the research problem at hand.
How to measure various mixes of incentives and goal types
Measuring the incentive alignment of research staff and decision-makers is exceptionally difficult. Despite knowing the consequences of misalignment and some effective strategies for avoiding it, we have no good method for measuring whether everyone in a lab has bought in and is sufficiently motivated to take the kinds of risks that fuel discovery.
On the personnel side, several dimensions are worth tracking:
Composition of research staff: What is the ratio of permanent research staff to trainees? An organization that is 80% trainees operates very differently from one that is 80% permanent.
Expected tenure of key personnel: A lab where the average postdoc stays 2.5 years has a fundamentally different institutional memory than one where the average research scientist stays 12 years.
Career paths available within the organization: Can technical staff advance without moving into management or leaving for a faculty position?
Diversity of roles: Does the organization employ roles that support the research mission without being on a PI track? The range of roles an organization supports is often a strong predictor of the range of projects it can undertake.
Revenue strategy
Where a lab gets its funding, how that money is allocated, and what its funders value, all shape what gets done. Moreover, it is often easier to categorize R&D groups based on who funds them than on whether they are “basic” or “applied,” or housed within a university or the private sector11.
MIT, for example, had eras in which the majority of its research funds came from private-sector or government contracts rather than federal R&D grants, and the Institute hired accordingly. We now live in a different era, with tens of billions of dollars annually going to academic teams through project-based funds, approved by academic panels.
One common revenue strategy today is relying almost entirely on NIH or NSF project grants, which means doing work that excites the PhDs who sit on review panels. Meanwhile, venture-funded companies are at the other extreme, with revenue strategy almost entirely driving the technical agenda.
The most interesting cases, however, are organizations with hybrid revenue strategies, which are more readily comparable to one another than to standard R&D firms or most university labs. For example, the CMU Robotics Institute is more easily compared with a novelty-seeking firm like BBN than Marvin Minsky’s computing group at MIT. Both the CMU group and BBN’s computing groups:
Were novelty-seeking
Worked on practical projects and products for real users
Were managed more like small, flexible firms than university labs
Both groups spent much of their time serving an ambitious, applied funder like DARPA, raised nonprofit grants to offset less applied explorations, and would work with traditional companies if the work excited their researchers. Even though CMU could not turn a profit, while BBN sought a modest one, both were clearly optimized for doing cool work over maximizing revenue12.
How to measure revenue strategy
Revenue strategy is harder to reduce to a single metric than timelines or team size. One method could be to track two dimensions: the diversity of funding sources (single funder vs. many) and the degree of funder control over the research agenda (block grants vs. tightly scoped contracts). If we plot on these two axes, HHMI investigator labs (many funders, low control) exist in a very different quadrant from a corporate R&D lab reporting to a single business unit (one funder, high control).
Degree of focus on a single mission
Scientific organizations differ in their level of focus on a particular goal or mission. Focused Research Organizations (FROs) are organized around a single scientific problem or question, such as conducting synthetic biology in non-model organisms. In contrast, Bell Labs pursued a kaleidoscope of projects. As Bell veteran Walter Brown once wrote, “One of the great features of Bell Labs was that there were so many experts in so many different fields within it.”
NASA falls somewhere in the middle. Its overall mission of space exploration and aeronautics research is broad, but it often organizes itself around specific projects. On the more focused end, the Allen Institute for Brain Science works on understanding the complexities of the human brain, but it’s not as narrowly scoped as an FRO because it approaches that goal from multiple angles (cell types, neural circuits, BCI, etc.).
The degree of focus interacts with several other parameters in our taxonomy. An organization with a relatively narrow focus can get away with a less diverse talent pool since it doesn’t need expertise across many fields. This is not true for broad-mandate organizations (like Bell Labs) that benefit from the cross-pollination of ideas between specialists across many domains.
How to measure the degree of focus
This isn’t an easily quantifiable metric, but we can bucket organizations into three rough categories:
Focused on one mission or a specific scientific question (such as FROs)
Focused on a number of related missions/questions
No specific focus, or focused on the broadest possible set of related questions (i.e., anything that affects communications).
It may also be worth distinguishing between stated focus and operational focus. An organization’s charter might describe a broad mandate, but if a charismatic leader is directing most resources toward a single problem then the org is operationally focused. In other cases, organizations nominally focused on a single topic can drift into covering an increasingly wide range of related questions, especially as the teams get larger.
Size of organization and/or research teams
What do we know about the relative productivity of small versus large labs? What happens to a lab’s productivity if it grows from 5 to 10, or from 10 to 20, or from 20 to 50, or even to 149 lab members, as is the case for Nobel winner David Baker?
Research on this topic has yielded mixed results. Smaller teams tend to produce more disruptive research and are more likely to introduce new ideas, while large teams are better at developing existing technologies (Wu et al., 2019)13. We suspect that the nature of the research problem should dictate the team size.
Size also interacts with several other parameters. For example, larger organizations require more formal governance structures: a lab of five people can operate on informal consensus, but a lab of 50 cannot. Size impacts the talent model: larger organizations can support a wider range of specialized roles that smaller labs often can’t afford to fill. And on size and focus — a large organization can sustain many different research threads simultaneously, but it can also suffer from diffusion of effort and bureaucratic overhead that a smaller group avoids more easily.
How to measure size
The size of an organization or team is easy to measure but hard to categorize, as per the Sorites paradox. There may be little difference between five and six people, but there may be a huge difference between a lab of five and one of 50. It may, therefore, be best to think of lab/org size as broad buckets with fuzzy boundaries:
A small lab/org of five to 10 people
A medium-sized lab/org of 20 to 50 people
A larger org of 100+ people
Governance and project selection mechanisms
One of the ideas we have implied many times over thus far but haven’t spelled out yet is the influence of the person or people making decisions in an R&D org. It is their choices that non-trivially impact the other parameters discussed thus far (those that have mostly been concerned with what shapes an org’s agenda).
Two organizations can have identical timelines, budgets, and user relationships, and nevertheless produce radically different research portfolios simply because of how governance works.
Projects can be selected top-down, relying on a few well-informed individuals with high conviction. Whole-genome shotgun sequencing reflected Craig Venter’s belief in what was technically possible and scientifically important. In the DARPA model, a single program manager (typically a domain expert on a short rotation from academia/industry) has wide latitude to identify a problem and form a research program.
Meanwhile, Janelia Research Campus’s governance structure was designed by Gerald Rubin to be more bottom-up. Lab heads are given substantial freedom to pursue their research directions, but they undergo rigorous review every five years, with the expectation that they will periodically change research directions.
In other cases there is a happy middle ground to be found. At the early Broad Institute under Eric Lander, large-scale projects with collective payoff (such as developing the genome-wide association study [GWAS] infrastructure) were driven forward by institute leadership and individual researchers continued to retain autonomy over their own scientific questions. Directors like Mervin Kelly at Bell Labs also set broad thematic directions while leaving substantial room for researchers to determine their own specific projects within that framework.
We suspect that the rise of AI might affect organizational governance in a number of ways, by making it easier to cooperate across teams and individuals, or by making it easier to run an organization that is relatively flat and non-hierarchical.
How to measure governance and project selection
Governance is arguably more categorical than continuous. These categories might include:
Distributed peer review: Projects are selected by committees of peers evaluating proposals.
Individual decision-maker: A single person, such as a program manager, lab director, or founder, has broad authority to shape research programs.
Managed autonomy: Org leadership sets broad themes or priorities, but individual researchers have freedom to choose specific projects within those constraints.
Full researcher autonomy: The researcher decides what to work on, with support from organization resources, with minimal institutional direction.
Openness and IP strategy
It is also important to consider the incentives created by the prospects of the research once it leaves the lab.
As we have mentioned before, BBNs made great use of researcher dissatisfaction with seeing their ideas go unused: “While MIT and Lincoln Labs were great research environments, many who defected to BBN felt the nature of academia forced them to leave their best ideas as under-developed prototypes or “applied” ideas in papers.” Policies on openness thus, in some way, select for personnel. Scientists from the academic system may be reluctant to move to places where they cannot publish while others prefer environments free of scooping risk.
For example, researchers working on the Human Genome Project were subject to the Bermuda Principles which required that all human genomic sequence data above ~1kb be released within 24 hours. This meant that those joining the public project had no competitive or strategic advantage despite their early access to results.
Beyond talent, how freely an organization shares its findings or how aggressively it protects them can have many implications for how the org operates.
Modern day examples include Arcadia Science which has committed to making all of its research papers, protocols, datasets, and code freely available. At the other end, pharmaceutical R&D defaults to strict secrecy – sharing results only through patent filings and carefully managed publications.
In contrast to the necessary secrets firms hold in competitive industry, AT&T’s regulated monopoly made sharing knowledge essentially costless. Because patents were bargaining chips rather than exclusionary tools, researchers at Bell Labs could publish prolifically14 even as AT&T maintained a strategically necessary patent portfolio.
Similarly, DARPA-funded research is often published openly (much of it does take place at universities), but the agency also funds classified programs and generally maintains a complex relationship with IP generated under its contracts. Early-stage research is often quite open, while work approaching deployment may become more restricted.
There are also trade-offs to consider regarding the speed and breadth of downstream impact, because open findings can be built on by the rest of the world, while proprietary ones may have a large commercial impact but narrower scientific effects (at least in the short-to-medium term).
How to measure openness and IP strategy
Openness can be measured along several dimensions:
Publication policy: Does the organization publish freely or selectively?
Data and materials sharing: Beyond papers, does the organization share raw data, code, protocols, or other tools?
IP stance: Does the organization patent aggressively, defensively, or not at all? What purpose do the patents primarily serve? Organizations like universities often also patent reflexively through their technology transfer offices without much strategic intent, which is yet another category.
Secrecy constraints: How much of the work is classified or otherwise restricted from public disclosure?
Concluding remarks
Our purpose in providing this non-exhaustive list of traits and our thoughts on how they may be applied/how they interact with each other is to emphasize the largeness of the possibility space of potential scientific organization.
Certainly, some gaps exist for good reasons: an organization with very short timelines, no user focus, and no discretionary budget may not be able to do anything interesting. Other gaps may reflect a failure of institutional imagination. Do certain possible organizations not exist because that particular combination of parameters is incoherent? Or because no one has tried?
We suspect there may be some important scientific problems that could be addressed but aren’t, simply because we have yet to identify the right organizational structure to support the research. That meta-problem is likely solvable, and we hope our taxonomy motivates philanthropists and researchers to give it a shot.
We’d like to thank Eric Gilliam, Zac Hill and Ben Reinhardt for their comments and feedback. Any errors within are ours.
We are actively looking for bright minds to develop these lines of inquiry with us: if this is you, reach out to us at aish@analoguegroup.org and stuartbuck@goodscienceproject.org.
How to cite: Stuart Buck, Hiya Jain, and Aishwarya Khanduja. “A Taxonomy of R&D Orgs: What Is New, What Is Missing?” Good Science Project and Analogue Press, July 31, 2026.
From Carnegie’s private correspondence dated December 20, 1901.
For more, see the Overedge catalog maintained by Sam Arbesman, as well as Second Renaissance, a living archive of scenius created by Analogue Group.
From Nan Ransohoff’s article on The third wave of American philanthropy: “Some directional napkin math suggests that adding up philanthropic pools from just three sources – (1) the OpenAI Foundation, (2) Anthropic founders, and (3) Anthropic employees – translates to an additional ~$37B of intended annual spend…[this] figure is based on today’s [May 2026] valuation of OAI/Anthropic and a pretty modest 10% per year spend target. US charitable giving is around $600B per year. Putting this all together: $37B – $100B of new philanthropic funding, which would be a 6-17% increase in annual philanthropic spending relative to today’s $600B/year in the US. Practically speaking, a philanthropic ecosystem that can already disburse $600B/year can likely absorb another $50B without much trouble. The real question is whether there are $50B worth of initiatives that are compelling to these funders. If not, the dollars won’t get spent.”
For a look into a decision tool for funding mechanisms, see the Institute for Progress’ Atlas of Innovation. It focuses on three questions: how clearly can you state the problem, how clearly can you state what a solution looks like, and can you identify who should do the work.
“In its stated policies, HHMI departs in striking fashion from NIH’s funding practices...HHMI Investigators are initially appointed for 5 years, and in the case of termination, there is a two-year phasedown period during which the researcher continues to be funded, allowing her to search for other sources of funding without having to close down her lab. Moreover, HHMI investigators appear to share the perception that their first appointment review is rather lax, with reviewers more interested in making sure that they have taken on new projects with uncertain payoffs, rather than insisting on achievements.” [This is also a governance property].
“Langmuir was mostly free to explore as he saw fit. But it should be noted that he was obligated to strike off on his explorations inspired by an existing course of research on a GE product with known limitations/bottlenecks that needed to be overcome.” From Eric Gilliam, in this FreakTakes essay.
User input can be directed, as in people state their needs to researchers (think early DARPA), or aggregate where impersonal signals like price, revenue, willingness to pay reveal demand (like many early stage start-ups).
That challenge had implications for everything from information theory to the quantum surface interactions within silicon transistors.
ALV itself was effectively cancelled in 1988 and never delivered a usable battlefield system. But the research capacity that emerged from it (including CMU’s Navlab program, the lidar and computer-vision work at ERIM, SRI, and Martin Marietta) helped move forward the contemporary autonomous-vehicle industry.
From the famous Steve Jobs interview with BusinessWeek, (May 25, 1998): “Our job is to figure out what they’re going to want before they do. I think Henry Ford once said, ‘If I’d ask customers what they wanted, they would’ve told me a faster horse.’ People don’t know what they want until you show it to them.”
Revenue strategy obviously overlaps with user input: when the funder is the user, the two parameters converge heavily. But they also diverge often enough to be worth tracking separately, particularly in hybrid-funded organizations where different funding streams push the research agenda in different directions.
That is why BBN could recruit the best from Lincoln Labs, who were often fed up with having to leave their best prototype ideas on the shelf until industry was ready to use them years later.
“BBN’s computing efforts would go on to earn BBN praise from many former MIT researchers, later being described as “the third great university of Cambridge,” “the cognac of the research business,” and the true “middle ground between academia and the commercial world”... They [researchers] could simultaneously work on the hardest problems and build useful technology.” From Eric Gilliam, in this FreakTakes essay.
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I believe the correct response is "Hnnnnnnnnghhhhh" :D