Cheap access to space: lessons from past breakthroughs
by John F. McGowan
|This lack of progress certainly does not appear to be due to lack of funds. Are we doing something wrong?|
The space community remains frustrated by the extremely high cost of space access. Most potential uses for space such as space solar power or asteroid mining remain impractical largely due to the cost of space access, which is usually estimated at thousands of dollars per pound to orbit. The high cost of space access has largely limited profitable space applications to information applications such as communication and surveillance that are increasingly vulnerable to rapid advances in Earth-based information technology.
The solution is (obviously) to improve power and propulsion technology to greatly reduce the cost of space missions. Then the space community can afford to do many things in space that are now impractical.
Since 1970 attempts to develop improved power and propulsion systems by space agencies, military agencies, and many private organizations have had negligible success. Even the recent success of SpaceX has only replicated the state-of-the-art orbit-capable rocket.
This lack of progress certainly does not appear to be due to lack of funds. Many billions of dollars have been spent on research and development of new power and propulsion systems. In fact, history records a number of remarkable cases where new power and propulsion systems were developed on very small budgets, although usually over many years. Are we doing something wrong? Can we learn anything from the methods used in the research and development of new power and propulsion systems during the eighteenth and nineteenth centuries when many of these remarkable low-budget advances occurred? The rest of this article explores the lessons for cheap access to space from these historical successes and suggests a way forward.
All major scientific discoveries and technological inventions that I have studied in sufficient detail to determine whether large amounts of trial and error were involved, in fact involved large amounts of trial and error over a period of five to twenty years. The number of trials during a major discovery or invention is probably somewhere between hundreds on the low end and thousands, even tens of thousands, depending on exactly how a trial is defined.
The cost per trial and the duration of each trial is an extremely important factor in the total cost of achieving a major invention or discovery. Octave Chanute and the Wright Brothers were able to achieve powered flight on a very small budget where better funded efforts like Samuel Langley and Hiram Maxim’s attempts failed, in part because they kept the cost per trial very low. They flew gliders made of canvas and wood at low altitude on beaches where crashes would have limited cost, no one was killed, and no expensive engine was destroyed during the trial. The gliders could be repaired and/or modified quickly, often in less than a day. Langley destroyed a small steam engine in each of his infamous failed trials. He only had money for a handful of trials, which empirically is almost always too few to succeed. In contrast, Chanute and the Wright Brothers probably conducted hundreds of trials each year for several years. Keep in mind that Chanute was conducting trials of his glider designs in Gary, Indiana well before he met the Wright Brothers. The Wright Flyer was a lineal descendant of Chanute’s glider design.
In the case of space and rockets, the current cost per trial is very high, on the order of $50–100 million for a single launch attempt of a medium to large rocket. If one considers failed projects such as the X-33 as trials, these purported “cheap access to space” projects have cost hundreds of millions, if not billions, of dollars each. With these mega-projects, the cost to perform the hundreds or thousands of trials probably needed to succeed becomes anywhere from $10 to $100 billion, even approaching $1 trillion.
Similar kinds of economics probably apply to other power and propulsion mega-projects like tokamaks or the giant inertial confinement fusion experiments. It is true that a tokamak can be modified without building an entirely new tokamak that now costs billions. But the cost per trial even to modify a giant machine like a tokamak or inertial confinement fusion reactor prototype must be huge—millions of dollars—for most modifications.
What the space community needs to identify are technologies and approaches that have reasonable costs and durations for each trial. In the case of chemical rockets, this might mean, for example, small-scale rockets. In the case of fusion, this might mean focusing on non-mainstream approaches like electrostatic fusion where working devices like the Farnsworth fusor can be constructed for a few thousand dollars. This might bring the total cost to actually make a breakthrough down to a few million dollars where either government funding agencies or private sources of funds could actually finance the necessary research and development.
There is more to successful research and development than trial and error. Brute force trial and error — the famous monkeys pounding on keyboards producing Shakespeare — is not adequate. There is certainly a lot of thought and creativity that goes into major discoveries or inventions, but there is also a lot of trial and error.
One of the things that Chanute did was to conduct a very thorough survey of all historical attempts to fly resulting in his book Progress in Flying Machines. Chanute was interested in flying from his youth but set aside the interest to pursue a successful career as a railroad engineer (he made a sizable fortune). Railroads were the “high tech” of the nineteenth century. He collected articles on flight all through his life. Once he retired, he combined this collection with further research to produce his book.
|If one considers failed projects such as the X-33 as trials, these purported “cheap access to space” projects have cost hundreds of millions, if not billions, of dollars each.|
What Chanute did was study all of the failures—and the few successes—to date. By studying them all he was able to identify a number of patterns. First, the few successes or near successes involved fixed-wing vehicles, not attempts to emulate the flapping wings of birds. Second, he determined that the key problem was what he called “balance”, that the planes were unstable and often flipped over or crashed, which led to the eventual development of the Wright Brothers’ wing-warping mechanism and, more importantly, the aileron.
It does not seem that there is a comparable analysis of the problems with the many attempts to achieve cheap access to space to date. There is no Progress in Cheap Access to Space book or web site today.
There is a tendency to blame the persistent problems and failures on specific technical excuses, e.g. we failed to tighten a bolt (SpaceX for one failure), rather than identify deeper systemic problems. This happened with Langley’s attempts. He blamed the crashes on faulty construction and assembly of his “aerodromes”. He apparently never realized the aerodromes were unstable even though he knew Chanute.
It often takes a comprehensive look at a large number of failures to identify a consistent pattern or underlying problem. This is probably one of the reasons for the large amount of trial and error in most breakthroughs and the substantial calendar time that elapses.
In the case of the many cheap access to space attempts of recent decades, it’s difficult for me, as a (mostly) outsider, to identify the underlying problems. My educated guess is that both NASA with its huge budgets and the “alt.space” community are encountering manufacturability problems where consistently reliably and cheaply producing components and systems is very difficult. Because rockets explode catastrophically due to small errors, this is difficult to overcome even though recent advances in computer-controlled machine tools should offer a resolution.
But the proper procedure is not to jump to conclusions, but to do what Chanute did and systematically review the many trials and failures. This is something that space enthusiasts can do on a shoestring budget much as Chanute did a century ago. This can be done both for chemical rockets and more advanced systems like fusion power.
In mechanical invention it has often been possible to use cheap, lightweight, soft, easily modifiable materials for rapid prototyping during the research and development phase. This is what Chanute and the Wright Brothers did with gliders made of canvas and wood. In other areas of mechanical invention, clay, cheap plastics, wood, paper, cloth, and a range of other materials have been used during the research and development process to keep the cost and duration of trials as low as possible. With rockets and other high-performance power and propulsion systems, this is often difficult or impossible. Hard, durable, resilient, often costly materials such as metals are needed because of the high energies, pressures, temperatures, and other stresses involved.
Historically, in this case, scale models have been used during the research and development process. James Watt was able to develop the revolutionary separate condenser steam engine on a very small budget over several years. The Newcomen steam engines of Watt’s time were the size of small buildings and quite costly to build or modify. Watt started building scale models of the Newcomen engine for teaching purposes at the University of Glasgow. Significantly, these models were useful only for teaching purposes. A small Newcomen engine is not as efficient as a large Newcomen engine and was not practical for actual power generation.
|There is a tendency to blame the persistent problems and failures on specific technical excuses, e.g. we failed to tighten a bolt, rather than identify deeper systemic problems.|
The Newcomen steam engine exhibited economies of scale. The surface area of a steam engine scales with the square of the size, while the mass and volume of the steam engine scales with the cube of the size. Consequently, larger steam engines can retain heat and function more efficiently than small steam engines. The original Newcomen steam engines were extremely inefficient even at large scale. It was not until many years later that small practical steam engines such as the ones that Langley used for his aerodromes became feasible. However, the scale-model Newcomen engines were ideal for teaching and also for research and development. By experimenting with the scale models that could be done quickly and cheaply, Watt eventually conceived of the separate condenser, which radically improved the efficiency of the full scale Newcomen engines and paved the way for the steam era.
Major advances in power and propulsion technology today probably require following Watt’s example of working with small scale models (or possibly small component tests) rather than full-scale working devices. Full scale engines and reactors like tokamaks, orbit-capable rockets, and so forth are both costly and time consuming to build or modify, making the per trial cost extremely high. Even if economies of scale make the scale model prototypes impractical as final production systems, much like Watt’s teaching models in the eighteenth century, the research and development of better power and propulsion systems needs to use smaller systems as prototypes—ideally inexpensive tabletop devices.
To achieve cheap access to space, the space community must focus on the cost of each trial and the total cost of the many trials that are usually needed to make a major technological breakthrough. Even promising technologies that have a high per-trial cost are unlikely to result in the desired improvement in cost and performance. Rather, the space community must identify and use those technologies and methods that offer low trial costs and durations. This will make the large number of trials needed for a major advance affordable and doable.