The following quotation is from Thomas Edison in The Electrician (London) Feb. 17, 1883, p. 329,
This disquieting message, and the reason behind it, ring true today. Edison's point is that everybody wants to believe in a better battery (or other energy device, for that matter), so there are rich opportunities for deception. Some deceptions are violations of thermodynamic laws, but fortunately these do not travel far. The more durable deceptions are wishful interpretations of experimental data, sometimes supported by interpretations that are logical, but rely on optimisitic assumptions or untested steps. Ideas in other fields of science that are equivalently weak tend to be dismissed quickly. For energy materials, however, many dubious ideas survive for years before they are exorcised after considerable effort and cost. The argument in favor of pursuing them is that the energy problem is so important that no stone should be left unturned, even if the dirt around it looks pretty ordinary, or if even if the stone has been turned over before. There can be real problems when these ideas lead to financial investments in new technologies, however. Overexuberance about early results has hurt people. They feel "swindled" and attribute the early enthusiasm to a "latent capacity for lying."
Fortunately, energy materials science is a rich topic, and there is much honest and important work for research universities. Historical observations show that the development of battery materials is by "punctuated evolution," where 1) large jumps occur with the discovery of a new class of material, followed by 2) advances that are improvements to the basic structure and composition. Both processes are essential. In the 1970's, the original effort on Li batteries was with pure Li anodes, but these proved too unstable. A major jump occurred when graphite was used as the anode material in the 1980's. Some tuning of the graphite was important for improving safety and capacity, but these evolutionary advances were relatively quick. In contrast, commercial cathodes based on LiCoO_2 have compositional variations and methods of processing that took some time to develop. The full process is replaying itself with olivine LiFePO_4, which was a major jump, but refinements to microstructure and composition are underway today. What about tin oxide, nano-silicon, or germanium anodes? These are known to offer very high energy density, at least twice that of graphite, but they need evolutionary advances to survive.
Materials science can contribute to both the big jumps and the optimization steps in the punctuated evolution of energy materials. The big jumps less predictable. Many have been tried, but most do not work, and hence there are relatively few battery systems in use today. Predicting entirely new material systems may best await advances in science -- today the big jumps come from experimentation, often by "serendipity" or by "Edisonian testing" of numerous candidate materials. Evolutionary advances can be predicted more reliably today, or at least they can be tested in more definitive ways. Variants of materials can be tested by differential measurements, where apples are compared to other apples, so to speak. The variations can often be posed as hypotheses, so the work can be guided by the scientific method. By posing good hypotheses, the field of materials science can advance with improvements in the materials. New understandings can suggest new compositions or microstructures that may have superior properties.
There are many opportunities to study energy materials and obtain results relevant to their performance. Such research can build our understanding of the thermodynamics of energy materials at the level of the electrons, and this is where the future generation of materials scientists will make their big contributions. To this end, we select problems where we can provide unique insights from our mastery of experimental scattering methods, or our computational tools for electrons and thermodynamics. We do have a few patents on energy materials, but these are not the a-priori goals of our work. What we do is "use-inspired basic research," but we want it to be original science with lasting value. We do our best to pose problems as hypotheses, and test them systematically with strategies so that either outcome is interesting. For graduate students this leads to quality thesis work, not just the optimistic turning over of stones. For the broader impact, our work gives bounds on energy material performance, understandings of why these materials work, and suggestions for how properties can be improved.
So be careful about telling me that you want to develop a new nanomaterial that will make you rich by solving societal energy problems. Instead, are there promising directions in the science of energy materials that interest you? It is possible to do solid science that addresses important issues in energy materials. The truth offers its own rewards.