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National Research Council (US) Chemical Sciences Roundtable. Reducing the Time from Basic Research to Innovation in the Chemical Sciences: A Workshop Report to the Chemical Sciences Roundtable. Washington (DC): National Academies Press (US); 2003.

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Reducing the Time from Basic Research to Innovation in the Chemical Sciences: A Workshop Report to the Chemical Sciences Roundtable.

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4DARPA's Approach to Innovation and Its Reflection in Industry

Lawrence H. Dubois1

SRI International


Today's world is changing rapidly, providing exceptional challenges and opportunities. As shown by recent events, it is increasingly complex and chaotic with seemingly small actions triggering massive changes. In addition, the rate of technological change is accelerating at what some would say is an exponential pace based on principles such as Moore's law, Metcalf's law, and Schumpeter's waves. An outcome of this change is that our work is becoming more interdisciplinary. Information technology is impacting chemistry, physics is impacting biology, and nanotechnology is pervasive in many disciplines.

How does one manage and control these changes? How does one harness this complexity and growing multidisciplinarity to solve critical problems for society? For approximately 50 years the Defense Advanced Research Projects Agency (DARPA) has played a leading role in turning innovations in technology into new military capabilities. In fact, most military and many civilian systems today can trace their origins to funding from DARPA. These include the Internet (ARPANET), high-speed microelectronics, stealth and satellite technologies, unmanned vehicles, and a wide variety of new materials. What are the driving forces, culture, and processes employed by DARPA to accelerate technical innovation, and how can these same techniques be used effectively in academia, national laboratories, and industry?


In order to understand DARPA, one must understand the context in which it operates. DARPA is the central research and development organization of the Department of Defense (DOD) and has a very specific mission: innovation in the defense of our country. Other agencies and offices in the defense and intelligence communities play different and complementary roles. The same is found in all large institutions. Peter Drucker2 explained that there are three types of changes that occur in all complex organizations. The first is systematic continuing improvement, which the DOD calls training and experimentation. The second is based on building tomorrow's systems using today's proven techniques and technologies. The DOD views this as evolutionary requirements-based research and development as practiced by, for example, the Office of Naval Research and the Army and Air Force Research Laboratories. The third type of innovation required by any healthy organization is innovation with a goal that makes obsolete and to a large extent replaces even the most successful current products and processes. For the DOD the function of radical innovation is carried out by DARPA.

Innovation is more than invention—it is invention turned into practice, and it requires a fundamental change in operations. Innovation is a very slow process in most organizations, and it is especially slow in large institutions where continuing success can breed a risk-averse atmosphere. Furthermore, radical innovation is risky and requires real leadership, dedication, and protection from above. How does one do this consistently in an organization like DARPA that invests over $2 billion per year in advanced research and development?

Despite its ties to the Pentagon, DARPA's strategy is to remain small and flexible and to quickly exploit emerging technologies and situations. DARPA has a broader horizon than most commercial analogs, such as working with venture capital firms, but it is more focused than traditional university-based research. DARPA is not bound by military requirements (official military doctrine) but rather responds to military needs. For the most part, DARPA emphasizes high technical payoffs for which success may provide dramatic advances in military capabilities. This usually entails taking high risks and focusing investments in a few critical areas. In this sense, DARPA is more like an investment firm since it has no long-term investments in “bricks and mortar” (no in-house research labs) and no established constituency that it must “keep fed.”

DARPA is a small, relatively flat organization with approximately 120 technical staff, 220 total employees, and only one level of management between the program managers and the director of the agency. This allows ideas to flow very quickly. Projects, program managers, and even the agency director rarely last more than 3 to 5 years, and there are seldom renewals. This constant flux of programs, program managers, and directors leads to a rapid generation of new ideas. Because of limited resources, there is competition for funding the best new ideas, both internally and externally. Each project is managed by a proactive program manager, and quality performance is rewarded with increased funding. In order to accomplish this, DARPA has highly flexible contracting and hiring practices that are atypical of most of the federal government. DARPA contract agents can issue contracts, grants, and various other transactions. Staff can be hired from industry quickly, at wages substantially above those of typical government employees.3

DARPA has a set of very strict investment criteria. There are seven key questions that must be answered by each program manager and that in turn must be answered by individual project leaders or principal investigators:

  • What are you trying to accomplish?
  • How is it done today and what are the limitations?
    • What is truly new in your approach that will remove current limitations and improve performance? By how much? A factor of 10? 100? More?
  • If successful, what difference will it make and to whom?
    • What are the midterm exams, final exams, or full-scale applications required to prove your hypothesis? When will they be done?
    • What is the DARPA “exit strategy?” Who will take the technologies that you have developed and turn them into a new capability or a real product?
  • How much will it cost?

How do DARPA program managers differ from those in other funding agencies, and how do their efforts reduce the time it takes to go from basic research to innovation? First, the role of a DARPA program manager is different than that of most of his or her colleagues in larger, more traditional government funding organizations. In the Defense Sciences Office of DARPA, program managers must be proactive “techno-scouts” constantly searching for the next big technological opportunity. He or she is constantly talking to potential new contractors as well as possible users of any new capability. Once a new opportunity is identified, the goal is to grow this discovery with a judicious amount of money and technical talent and a modicum of oversight to catalyze the creation of a new capability. Since the tenure of a typical program manger at DARPA is on the order of 4 years, this must be done very quickly. Thus, efforts are highly focused, and goals and military needs are clearly understood by all up front. To accomplish this, DARPA program managers are given both the responsibility and the authority to act. There is both technical and fiscal flexibility, where the goal is to develop a new capability, not to fund someone's pet project for years.

The Defense Sciences Office is technically diverse and highly interactive, which naturally leads to collaboration and multidisciplinary projects. Many of the most interesting opportunities are at the interfaces between conventional disciplines. This working environment is conducive to such activities. Multidisciplinarity is also accomplished through the teaming of universities, service and federal laboratories, small businesses, large industry, etc. This allows one to develop a portfolio of technologies by combining basic and applied research with development and demonstration. By working synergistically with industry and pairing experts in fundamental research with those charged with producing a product, technology is transitioned more rapidly from the laboratory into the marketplace. As noted above, projects do not go on forever, and therefore DARPA program managers are always developing an appropriate exit strategy. Thus, DARPA technical staff work closely with business/ industry leaders and department acquisition officials to ensure a market pull for the technology. Transitioning a research program into a long-term funding opportunity for the same group of contractors by another government agency is not the preferred exit strategy.

Program management at DARPA is a very proactive activity. It can be likened to playing a game of multidimensional chess. As a chess player, one always knows what the goal is, but there are many ways to reach checkmate. Like a program manager, a chess player starts off with many different pieces (independent research groups) in different geographic locations (squares on the board) and with different useful capabilities (fundamental and applied research or experiment and theory, for example). One uses this team to mount a coordinated attack (in one case to solve key technical problems and for another to defeat one's opponent). One of the challenges in both cases is that the target is continually moving. The DARPA program manager has to deal with both emerging technologies and constantly changing customer demand, whereas the chess player has to contend with his or her opponent's king and surrounding players always moving. Thus, both face changing obstacles and opportunities. The proactive player typically wins the chess game, and it is the proactive program manager who is usually most successful at DARPA.


The traditional method of technology development where lengthy proposals are written and submitted to an august group of peers for review is incredibly time consuming and leads to a very inefficient use of resources. In this case, research by competing individuals working in isolation leads to a vast array of potential technologies and discoveries, only a fraction of which are ever combined to form useful new products and/or processes (see Figure 4.1). Most published papers sit idle in the archival literature with few, if any, references. Movement of technology out of the research lab and into the marketplace is generally slow. An example of this lengthy process is the development and application of new materials. Materials development is typically highly empirical and appropriate, and coordinated experiments and modeling are rarely done early on in the research process to answer critical questions an end user might have. The disconnect between researcher and application engineer is reflected in the amount of time needed between an idea and an end product. For example, to build a reliable part out of a known alloy requires a minimum of 36 months. This is short compared to the time it takes to change ship steel (7 to 10 years), apply lightweight composites (more than 15 years), or develop ceramics for engines (more than 20 years).

FIGURE 4.1. The traditional approach to technology development.


The traditional approach to technology development.

In order to circumvent some of the inefficiencies inherent in traditional funding organizations, the concept of a technology road map has been developed. Unfortunately, a road map is not always an appropriate solution. While road maps have several good points, including providing direction, defining distances, and supplying a plan to get from point A to point B around obstacles, they do not provide a complete explanation of how research or even technology development should be done. For example, a road map assumes that everyone starts from the same place and that the destination remains fixed. In other words, there is no competing solution being developed and user needs do not change. It also assumes that no new roads will be built or that an airplane will be invented. Road maps can stifle creativity and do not account for serendipity.

An alternative to the standard method of performing research is termed the “end-game” approach and is typical of many DARPA-funded programs (see Figure 4.2). By first defining the desired product or process and the anticipated technology needs, research teams can better coordinate their efforts and a higher rate of return on technology development can be realized. The results of fundamental research are tied to the needs of the technologists, who then build on this information to further create new and useful knowledge. Basic research, applied research, and development and demonstration play a role at all levels in the process since there is a tight feedback loop between discovery, whether planned or serendipity, and end use. Frequent contact between technology developers and technology users, with the DARPA program manager playing the role of “technology midwife” at times, ensures that useful discoveries will move more rapidly from the research laboratory into the marketplace.

FIGURE 4.2. The “end-game” approach to technology development.


The “end-game” approach to technology development.

The development of a practical liquid feed for a direct methanol oxidation fuel cell provides a useful example. The reaction chemistry (CH3OH+1.5O2 → CO2+2H2O), and much of the basic technology has been known for decades. Despite substantial investments by both industry and the government, little progress was made. By using the end-game approach, DARPA program managers drove the process to rapid success—they obtained a several order-of-magnitude improvement in performance in a matter of a few years. Catalyst discovery and optimization, an understanding of fundamental electrochemical kinetics and modeling, and polymer membrane chemistry all played a key role at different stages of the process (see Figure 4.3). In contrast to the more traditional approach to technology development, it is the coupling of the research teams from academia, federal laboratories, and industry as well as across different disciplines that led to this rapid success.

FIGURE 4.3. Research and development issues in the development of direct methanol oxidation fuel cells.


Research and development issues in the development of direct methanol oxidation fuel cells.


Once a good idea—a true “golden nugget”—is found, effective technology transfer is a multidimensional process. Many of the key components for successful technology transfer are outlined in Figure 4.4. Some of these may be enhanced or driven by a funding organization, while others must be led by parties more closely involved with the technology. Just lobbing the technology “over the fence” and hoping someone picks it up rarely works. The key to success is knowing what to do. Should the project further enhance an existing technology with a well-defined market or should it commercialize a completely new product or process? Are there licensing possibilities into a well-established industry or is it necessary to build a large infrastructure in order to compete effectively? Is the starting point a profitable company with an existing manufacturing capability or the formation of a new company from the results of university- or national laboratory-based research?

FIGURE 4.4. Necessary aspects to enhance technology transfer once a potentially good idea (“golden nugget”) is identified.


Necessary aspects to enhance technology transfer once a potentially good idea (“golden nugget”) is identified.

The license versus venture decision is a critical one when trying to accelerate the movement of basic research into the marketplace. A number of important factors come into play. For example, licensing works best for the development of an improvement to an existing product or process. In this case, there are typically a handful of established players in the market and generally the barriers to entry are high. Alternatively, if development of a revolutionary technology creates a new complementary product opportunity, licensing may also be the most appropriate method of bringing an innovation to market. Frequent and early contact with the expected user is critical to moving technology to the market more rapidly. The movement of people—for example, students in the case of university-based research—also speeds this process. It is said by many that effective technology transfer is a contact sport, and the more contact the better.

Starting a technology venture is more difficult and longer than licensing a new technology, but the payoff can be much greater. For most ventures the market needs must be sizeable, on the order of $1 billion. Venture capitalists typically want a very large opportunity, for which a company can be valued at greater than $100 million in less than 5 years and for which significant market share is possible. They expect a return on investment of 30 to 40 percent per year and breakeven in a reasonable time. The venture community is generally risk averse and is willing to take market risk but not technology risk. Thus, most venture-funded technologies are at a fairly mature stage. In addition to technology, a compelling competitive advantage and solid intellectual property protection are needed. Technical and business champions are a must, as is a dedicated team. Despite the typical work ethic at a venture-backed start-up, all this takes a substantial amount of time. Again, frequent feedback from the market is critical to accelerating success.


In many respects, work at SRI International mirrors the way DARPA manages programs. SRI, one of the world's premier contract research and development organizations, has been delivering innovative science and technology solutions to governments and businesses worldwide for over 50 years. Like DARPA, SRI brings multidisciplinary teams consisting of technical depth spanning many fields, along with business and market insights to meet complex challenges. These teams are led by technical champions, individuals who have the passion to make something important happen and who work across traditional organizational and disciplinary boundaries. Since SRI uses its research for organizations like DARPA to develop commercial opportunities, it is focused on moving technology rapidly from the research laboratory into the marketplace. Staff at SRI endeavor to have all of the elements outlined in Figure 4.4 in place in order to reduce the time it takes to move basic research from the laboratory and turn it into a true innovation.

SRI has created a number of tools in order to help its staff speed the technology transfer process. These include the NABCs, a simple way to capture the true impact of an effort. N stands for the customer, client, or market need. This can be commercial, government, or societal. A is the compelling technical approach, which can be new science, new engineering, or new theory. B is the benefits that would accrue if one were successful. C is the worldwide competition, reminding the primary investigator or project manager to check who else is doing similar work so that other efforts are not duplicated. The key to success is not just developing a great technical approach but a thorough understanding of the market needs and the competition. This includes not only where the competition is today but also where it will be when the new product or process comes to market. Note the similarity between the NABC formalism used by SRI and the seven questions asked of all DARPA program managers.

SRI has developed a series of specialized “watering holes” or gathering places where staff can present and vet their ideas in an open, mutually supportive forum (NABC presentations). Typical watering holes span multiple disciplines and include business development staff in addition to scientists and engineers. As ideas mature, SRI has developed an online Business Development “Cookbook,” a how-to guide to move technology into the marketplace and to build relationships with government and commercial clients. The SRI Internal Ventures and Licensing Board reviews, evaluates, and nurtures emerging business opportunities and provides a forum where business leaders can supply feedback on emerging technologies and markets. A formalized royalty and equity-sharing program that rewards staff for the value they create is an added incentive to help speed commercially successful products and processes into the market. Reinvesting the remainder of the funds received from licensing or equity in new equipment and facilities helps to keep the facilities at SRI state of the art. This helps to deliver more technology more quickly to the customers and to attract talented staff.


Blindly funding the technology transfer process is clearly not the most effective answer to improving the ability to move technology out of the laboratory and into the marketplace. Funding, which is always a limited resource, must be invested wisely. Based on my experience at Bell Laboratories, DARPA, and SRI International, I suggest three cross-cutting themes that affect all of the issues outlined above and seriously enhance or impede the speed with which technology commercialization can occur: (1) focus on important problems, (2) keep the end in mind, and (3) empower funding organizations. Since the vast majority of basic research in this country is funded by the federal government, these recommendations focus on government funding organizations. Nevertheless, many of the key points apply to private sources of capital as well.

Focus on Important Problems

Important and also interesting problems are all around us. There are many examples in health care and medicine, the environment, transportation, telecommunications, and defense. Chemistry has and will continue to have a major impact in these fields. Today's problems are inherently multidisciplinary and a challenge to our current university structure. This challenge must be met by any funding organization.

For example, in the area of defense the world is changing rapidly. No longer are we fighting the Cold War, and new threats are emerging everywhere, as evidenced by the increase in terrorism, the proliferation of chemical and biological weapons, and the advent of information warfare. At the same time, our adversaries have access to our latest technologies and there is increased pressure on the military to cut costs. It is very clear that the DOD is no longer the technological leader in such fields as advanced electronics and information technology and that it will never be the leader in the burgeoning field of biotechnology. These ideas do not come from any classified government documents but from reading newspapers like the New York Times or the Washington Post and from watching CNN.

Against this backdrop, chemistry can play a key role. Chemistry and chemical engineers can develop new materials and actuators for unmanned and robotic platforms and can use biomimetic or bio-inspired principles for sensors to detect the chemical signatures of land mines, chemical weapons, or biological weapons. They can also control micro- and nanostructures to improve ballistic protection, develop new therapeutics to counter the effects of emerging chemical and biological warfare agents, and develop self-healing materials to repair our aging platforms. These are but a few of many possible important problems in the defense arena where chemists can not only perform great, intellectually challenging science but also make a real impact on people's lives. Similar lists can be made for many other fields.

By understanding the broad market needs irrespective of any individual technology, one naturally focuses on important, interesting, and technically demanding problems. The consequences of this include the following:

  • In a university setting, research becomes more relevant to students and staff. Problems are inherently multidisciplinary, and students learn naturally from their colleagues in other departments.
  • There is a demonstrative value to society that enhances the ability to move basic research rapidly into the marketplace and therefore enhances the potential for real economic value creation.
  • Increased government and industrial investment in research and research infrastructure allows access to more advanced research tools.

Because the field now has more impact, there is a natural, positive feedback loop causing the field to grow and become more important. Witness, for example, the growth in funding for the National Institutes of Health.

Keep the End in Mind

The specifics of the end-game approach to research management were discussed above, and the advantages are many:

  • Investment is more focused, and return on investment is more easily viewed and measured.
  • Value to society is more clearly demonstrated because the goal is well defined from the start. Thus government funding can be expected to grow.
  • Correlation between investment and scientific and economic progress becomes clearer. This is especially true when proactive program management is tied in (see below).
  • The chemical industry can become more engaged in basic (university) research because outcomes are more relevant to industry, leading to more jobs for students and new and faster innovation.
  • Research and teaching integrate naturally because not only do students see the relevance of their work, they also are being trained for the “real world.”

Empower Funding Organizations

In order for an “end-game” research management program to be successful, funding organizations that play more proactive roles are required. For example, funding organizations must provide a clear need, priorities, and well-defined goals to both their constituents and their customers. The staff of the funding organization must understand both government and societal needs and be able to mix strategic (global) and tactical (directed) research and development. This means a mixed-risk approach should be used, combining appropriate amounts of basic research, applied research, development, and demonstration. The funding agency must support teaming and the effective use of scarce experimental resources through, for example, partnerships with national labs, not-for-profit organizations, and commercial companies. The government should encourage the use of corporate or individual donations of funds and equipment to tie the public and private sectors closer together and to enhance the training of students in state-of-the-art facilities. Funding organizations should also work closer together to gain critical mass and to minimize any duplication of effort. In order to make appropriate funding decisions in a timely manner, government funding agencies must optimize the use of multiorganizational panel review, peer review, and the intelligence and “gut feel” of individual program managers, whose technical judgment and expertise should be valued.

Since technology is not standing still, government program directors must have both the technical and the fiscal flexibility to review and change funding between and among scientific and engineering disciplines. While these decisions are difficult to make, leaving the tough choices to technically unqualified bureaucrats and legislators will not be in the best interest of our future. Similarly, resource allocation such as spending on equipment versus salaries, or funding of “big” science versus “small” science, also should be made by those most technically qualified. By making connections between research groups and fostering an atmosphere of collaboration, government program managers could also provide a very valuable service—enhancing technology transfer. This does not entail commercialization of technologies per se, but it ensures that there is a free flow of knowledge from those who generate it to those who will ultimately need it. Finally, if research is not progressing appropriately and fields are “getting stale,” program managers should have the freedom and ability to terminate projects and invest the resulting funds more productively elsewhere.


While these three recommendations may appear to be somewhat radical, organizations such as DARPA have used these techniques to very effectively move technology rapidly into the hands of those who need it most. Although these approaches may not work for everyone, they have been proven over time to be very effective. They require funding organizations to be proactive and to rely on the skills and judgment of their research managers.


Michael Schrage, Massachusetts Institute of Technology: I have actually followed a lot of DARPA's work over the years, and there is one question by which I am really struck. DARPA has always been a multidisciplinary agency, so how do you, as a program manager, strike a balance between the way a project is defined versus how you facilitate and translate between different disciplines?

Lawrence H. Dubois: It helps when you have money because it enables you to do a lot of different things. One example is at a principal investigator's meeting we will bring people together and have a series of lectures/discussions. People ask questions. Maybe initially you have the physicists asking questions of physicists and the chemists asking questions of chemists, but then we will typically do something a little out of the ordinary. For example, we will rent one of those boats that go out on the Potomac River from 5 o'clock until 10 o'clock at night. Everybody is on the boat at sea and you have to talk to somebody, right? There is food. There is drink. We have played paint ball games and laser tag. We do anything we can to break down barriers between people. That is just an example of what we will do to help people communicate, and it does take time.

Another example uses technology demonstrations, where every team brings their technology and demonstrates it. Each team will have a little booth or table, and the requirement is that somebody from your team has to go work with somebody else on another team to help set up their demo. It doesn't matter how simple the task; the goal is to help people talk to one another.

Finally, from a programmatic standpoint, one of the critically important procedures we used in the Defense Sciences Office of DARPA was that when we hired a new program manager we did not let him or her run programs in their area of expertise. For example, if someone is an expert in semiconductor processing, they were not running programs in semiconductor processing. They wouldn't do something totally foreign like medical applications on the battlefield, but it would be an area that is a little outside of their comfort level. It allowed a program manager to ask “stupid questions.” In an unfamiliar field, one could ask “Why do you do it that way?” or “How do you do that, and what does that really mean?” If this were the manager's area of expertise, he or she would be “banned” from asking those questions. When you pull people outside of their comfort level, and the funds are there to back you, everybody wants to educate you. That is another way of breaking down a lot of these communications barriers.

Michael Schrage: One quick follow-up on that. You came up with the program's end points. What is the tradeoff between how rigorously you define the end points versus emergent specifications and emergent prototypes from the team you put together? How is that negotiated?

Lawrence H. Dubois: It goes back and forth. You have this goal sitting out there, but you can't reach the goal without a team. For example, the team says, “You know, we need more models. We've got these concepts, but the model is wrong. Larry, I have a suggestion. Could you find somebody who can help on the modeling side because we don't think we can reach the goals without it?” There is definitely iteration between the team and the program manager. However, in many cases I have seen program managers be pretty adamant by saying, “Okay, these are my goals. You go figure it out.” It really pushes the team; if the team members don't figure it out, they may not get additional funding. DARPA truly pushes both its program managers and its contractor base.

Richard J. Colton, Naval Research Laboratory: Is your description of this program something that all of the offices of DARPA subscribe to? Was this methodology developed by DARPA when it was established, or is it the way to operate DARPA according to Larry Dubois? Also, previously DARPA was very much a bottom-up organization, but it is rumored that DARPA is now more top-down. Can you comment on that under the new management?

Lawrence H. Dubois: Sure. First, the Defense Sciences Office was very different from most other offices, partly due to the kind of people we hired. We brought in a much more technically diverse group of people than any other office. In addition, each office tends to take on the character of the office director. My philosophy was very much bottom-up. I would sign almost anything that anybody put in front of me as a funding document. I might argue with them. I might get them to rewrite it or change the scope of work, but ultimately I would sign it because you have to trust your program managers. That is very different than some of the other office directors who were very much top-down managers. In this case program managers tended to be an extension of his or her ideas. DARPA does change depending on the character of not only the program managers and the office directors but also the director of the agency. I think that the new director has made DARPA more of a top-down organization, and program managers execute what it is that he likes. Like anything else, however, the way DARPA is run will continuously evolve because the director will be there for only a few years.



Lawrence Dubois joined SRI International as vice president and head of the Physical Sciences Division in March 2000. Prior to that, he spent 7 years at DARPA, finishing his tenure there as director of the Defense Sciences Office, which is responsible for an annual investment of approximately $300 million toward the development of technologies for biological warfare defense, biology, defense applications of advanced mathematics, and materials and devices for new military capabilities.


Peter F. Drucker. 1998. Management's new paradigms. Forbes (October 5):152–177.


DARPA has at least two ways to bring new staff in from industry in addition to hiring as government employees. The first is the traditional Intergovernmental Personnel Act route. The initial step in this process is to associate the candidate with an eligible institution (e.g., college or university, federally funded research and development center, not-for-profit, etc.). According to the act, DARPA may hire qualified personnel from these organizations for a limited period without loss of employee rights and benefits. Appointments are generally from one to a maximum of 4 years. This process works and is how the author was initially hired at DARPA.

More recently, DARPA has been granted Experimental Personnel Hiring Authority under Section 1101 of the Strom Thurmond National Defense Authorization Act for Fiscal Year 1999. Under this authority, DARPA can directly hire up to 40 eminent scientists and engineers from outside government service for term appointments up to 4 years. These appointments may be extended to 6 years in specific cases. This authority significantly streamlines and accelerates the hiring process.

Copyright © 2003, National Academy of Sciences.
Bookshelf ID: NBK36337


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