On his blog "In the Pipeline", Derek Lowe has a contemplative post on the conditions necessary for seeing titans in particular fields, and whether these conditions can be replicated again. Building on examples from organic synthesis, music and art, he makes the case that every field has its heyday and you can never make the same contribution twice. I concur with this viewpoint; it’s possible to discover the structure of DNA, or formulate general relativity, or revolutionize organic synthesis, just once.
Putting it another way, the question to ask is whether the general problem has been solved. The organic chemist Robert Burns Woodward, who has been the foremost candidate for the adjective "genius" as applied to chemistry, is certainly a case in point. He showed us how to synthesize almost any complex molecule, and it’s not possible to see how someone could do that again. Until Woodward did it many believed that it might be impossible to synthesize molecules as complex as reserpine, chlorophyll, cholesterol and vitamin B12, and after he did it there was no doubt in anyone's mind. As Derek notes there are still challenges in synthetic organic chemistry and particular examples abound, but the general problem was solved by Woodward and there is no chance that someone can solve it again. Contrast that with a field like computational chemistry, where the general problem of efficiently computing the free energy of binding of a small molecule to a protein is far from being solved.
Of course this also make a cogent argument for being in the right place at the right time, placing that all-important and inconvenient factor named luck at the center of great scientific discovery. There is no escaping the fact that you can fail to make your contribution to a scientific paradigm simply because you are born a few years too late. A great example is the golden age of physics in the twenties when people like Heisenberg, Dirac, Pauli and Schrodinger others laid the foundations of quantum mechanics. With the glaring exception of Schrodinger, all the others were in their mid twenties and in fact were born within a year or two of each other (1900-1902). Once they invented quantum theory nobody could invent it again. Dirac in particular was not only one of the founding fathers of quantum mechanics but was also the founding father of quantum electrodynamics; thus, the stunning success of that field after World War 2 by Feynman and others built on his work.
This meant that if you were unfortunate enough to be born just a few years later, say between 1906 and 1910, you would miss your chance to contribute to these developments no matter how talented you were. Examples of people in this category include Robert Oppenheimer, Hans Bethe and Edward Teller. All of them, and especially Bethe, made seminal contributions to physics, but they missed the bus on laying the foundations. They matured at a time when the main task of physicists was to apply the principles developed by men only a few years older than they were to existing problems. Bethe and others achieved great success in this endeavor but there was no way they could replicate the success of their predecessors. Quantum mechanics was perhaps a rare example since the time window during which the fortuitous confluence of brilliance, data, geographic proximity and collaboration bore copious fruit was remarkably narrow, but it does underscore the general point that the period during which one can make fundamental contributions to a field might be preciously rare. As a more recent example, think of particle physics. After the discovery of the Higgs boson, how easy would it be for someone just entering the field to make a fundamental discovery of comparable magnitude? What are the chances that a particle as important as the quark or the neutron would again be discovered? It's quite clear that while there's still plenty of important discoveries to be made in physics, one could make a good case that the age of fundamental discovery at the level of the atom might be over.
A similar theme applies to chemistry. Woodward was heads and shoulders ahead of many of his contemporaries but he also had the advantage of being born a few years earlier. Thus, his first synthetic success came with quinine in 1944, a time when many future leaders in the field like E J Corey, Carl Djerassi, Samuel Danishefsky, Gilbert Stork were just entering high school or graduate school. This was still the case when Woodward synthesized two other landmarks, strychnine (1954) and reserpine (1956). Being a titan certainly entails being born with great intellectual gifts but it also benefits tremendously if you are born at the right time. Woodward matured when the conditions in organic chemistry were right for a man of his stature to revolutionize the field. The British chemist Robert Robinson and others had just described the electronic theory of organic chemistry which charted movements of electrons in organic reactions, UV and infrared spectroscopy were coming into vogue and structure determination by chemical degradation had reached its zenith. Woodward combined all these tools to invent a superb new methodology of his own and then applied it to scale hitherto unscaled peaks. He pioneered spectroscopy as an alternative to tedious chemical degradation for determining the structure of molecules and applied sound theoretical principles for making complex molecules. Another specific example is his development of the Woodward-Hoffmann rules; these are rules which allow chemists to predict the course of many key reactions that are of both of pure and applied interest. In formulating these reactions with Roald Hoffmann, Woodward again was in a rather unique position to appreciate both observations arising from his synthesis of vitamin B12 and the widespread dissemination of molecular orbital principles which were ripe for application. After he did all this that was it; while the others also made highly innovative contributions, in many ways they were duplicating his success.
This discussion also has a bearing on the frequent debate about awarding Nobel Prizes to one discipline or another. The fact is that we are very unlikely to see Nobel Prizes in organic synthesis in the future because many of the fundamental problems in the field have been solved. There has not been a general organic synthesis prize awarded since 1990 (Corey) and for good reason. Methodology has been recognized more often, but even the two most recent methodology prizes (2005 and 2011) stem from work done about twenty years earlier. There is of course a chance that some transition metal may further the cause of efficient, high-yielding and environmentally friendly synthesis in a significant manner but these achievements are likely to be rare.
There is a very important lesson to be learnt from all this regarding the education of students in the history of science. Students should never be discouraged from studying particular scientific fields, but graduate students at the cusp of their research careers should be given a good idea of where the greatest opportunities in science lie. There’s still nothing to stop a Phil Baran (widely considered to be the brightest synthetic organic chemist of his generation) from venturing into organic synthesis, but he should do so with full knowledge of what Woodward and Corey have done before him. One way to ensure success in science is of course to work in the “hottest” fields, and while history often has its own peculiar way of defining what these are, it’s sometimes clearer which ones have passed their prime. And it’s important to drive home this point to young researchers.