Recently, the newspapers and journals were bubbling with articles and editions devoted to various kinds of millennium and Y2K perspective. Some were retrospective and others prospective; some simply comprised lists of ‘greatests’. Interpreting the past with accuracy and insight is challenging, as is predicting the future. Fortunately, many others have already done that. So, instead, I will look at our discipline, cell biology, defined very broadly and to include molecular biology, both prospectively and retrospectively in the context of some perhaps prosaic but pertinent questions about the discipline that are surfacing as the centuries change. Many greats: One approach to summarizing the past is through lists of the greatest participants or classic papers in a given area. These lists appear frequently in areas like physics and mathematics, where progress is, or at least was, heavily influenced by heroic individuals who opened or sustained a field. In these areas, most participants and observers would develop a very similar list of the ‘greatests’, and nearly everyone working in the discipline would know what their contribution was. Is this true in cell biology? Are there names that everyone would know, or a canon of papers that everyone has read? Did the cell biology of the last 50–100 years evolve because of heroic individuals? Or were there only some insightful pioneers, followed by a large number of important accomplishments that occurred in many different laboratories? Interestingly, none of the major journals has compiled a ‘greatest’ list or even a “classic papers” list in cell biology. This is revealing. Perhaps it tells us that there were no great cell biologists - i.e. that the recent, great progress that we have witnessed didn't require great individuals. More likely, however, there are too many - that is, the advances in cell biology tend to be incremental, with many more bright sparks and contained blazes than forest fires. Seminal observations are frequent and arise in unexpected places. Progress may be better measured as the integral of many important contributions and contributors. Thus, cell biology is the product of many many great scientists, who interact, synergize and stand on each other's shoulders. The attractiveness of cell biology lies in this open, frontier culture. And the result is that the pie of success is large and that many have been rewarded. An interesting consequence of our frontier culture is that it is too exciting and fast paced for anyone to take the time to develop a sense of history and accomplishment. Sidney Brenner makes this point in his review of a book entitled ‘The lac Operon: A short history of a genetic paradigm’, by Benno Muller-Hill (Nature 386, 235). Brenner writes: “This book opens with the lament that for young molecular biologists history does not exist, and that they have no interest in the long struggle that has made the subject what it is today. I hold the weaker view that history does exist for the young, but it is divided into two epochs: the past two years, and everything that went before. That these have equal weight is a reflection of the exponential growth of the subject, and the urgent need to possess the future and acquire it more rapidly than anybody else does not make for empathy with the past.” A few years ago I read a list of the names of biomedical Nobel Laureates to some colleagues. They knew only a handful of the names and what their contributions were. It seems that so much is being accomplished so quickly it is hard for individuals to stand out. And the consequent focus on the collective achievement is what makes our discipline so rewarding for so many. But how long will this frontier culture last? The emergence of big biology, through government and private-foundation initiative, is changing the landscape. The rate of progress continues to accelerate. Will one soon require a very big lab to survive? Will creative minds find cell biology fertile territory? There are answers to big science. Most important is to embrace what it produces and look ahead. Another is to develop multi-institutional collaborative networks in which the product can far exceed the contributions of single individuals. And, finally, there are always trails to blaze and syntheses to make. They require little more than hard work, organization, good sense, perseverance, and some luck. Is it almost over? Extrapolating the rapid progress that we are witnessing, can one realistically predict what our discipline will be like over the next few decades? Will the questions that we are investigating now be answered or passe, and, if so, how soon? How long will cell biology continue to be on the center stage? Will there be new, fundamental, concepts or a paradigm shift? What ‘unexpecteds’ might we expect? At meetings over beer and at dinner tables with seminar speakers, the question “Is it almost over?” creeps in with increasing frequency. The concern is that the big picture will be in place soon - that is, the outlines of the fundamental cellular processes will be largely understood at a molecular level. This concern, of course, reflects the depth with which one wants to understand the cell. Clearly, we now know vastly more than we did even a decade ago. There is an emerging sense that a rudimentary understanding of the most basic cellular processes is in sight; one sees this even in the undergraduate cell biology textbooks. Of course, progress will continue. However, the questions about fundamental processes will become increasingly refined, and the answers more detailed - more likely to occupy space in specialty treatises than in undergraduate cell biology texts. The approaches and concepts will become more deeply linked to chemistry and physics, eventually focusing on subtleties of mechanism and structure. Some of these details will change our basic concepts dramatically; but the frequency of such occurrences will dwindle. These details are also necessary for the applications of cell biology that are beginning to emerge and for a true marriage of cell biology with the molecular world. This level of inquiry and detail, or increasing reductionism, may not sustain the interest of or resonate well with many of our colleagues. However, for others, it's just the beginning and is opening doors for a cadre of new colleagues trained in physics and chemistry to enter with fresh ideas, insights and technologies. Will it ever end? But is it almost over? Do we really know how cells do what they do? How is the thicket of seemingly redundant pathways and networks, molecules, and supramolecular assemblies coordinated spatially and temporally? Which of the many pathways and redundant mechanisms revealed in culture are utilized in vivo. How are cellular phenomena, as revealed in the spatial and temporal coordination required for cell division or migration, for example, integrated? How do groups of cells integrate and coordinate to effect tissue function, embryonic development, and pathology, for example? As we begin to observe cellular phenomena in situ, they can appear very different from those observed in culture. The compensation and redundancy seen in knockout, transgenic or mutated organisms also reveals a diversity of possible mechanisms. It seems that the cell has different ways of doing the same thing. How does the cell do it normally, and when, if ever, are the other mechanisms used? We have tended to focus the majority of our efforts on a few cell types. What about the other cells? How do they do it? These questions are especially pertinent in developmental biology and pathobiology, where the cellular environments are changing; they also point to a class of challenging, important new avenue of investigation. As the canon of cellular phenomena becomes understood at an increasingly refined level, it provides the basis for explaining integrative phenomena. It also becomes the source of interesting and important practical applications. In this way, cell biology can become the language for understanding complex integrative phenomena like learning and memory, behavior and personality - areas in which the genome project and genetics might merge to provide unique insights. In addition, cell biology is the source of endless practical applications and, in some sense, sits in the center of a booming biotechnology industry that includes novel therapeutic strategies, designer animals and plants, tissue replacements, biomaterials and biosensors. The possibilities here seem endless. What does genomics bode for cell biology? A great deal of opportunity. Do sequences, homologies, binding interactions, changes in expression, and even knockouts provide a satisfactory understanding of function? Isn't the genomic bottleneck the assignment of cellular functions to different genes? In its essence, gene function can be viewed as a cell biological issue and perhaps not fully amenable to high-throughput analysis. Thus, the genome project promises to keep cell biology on the center stage. And maybe, therefore, we will have too much to do. The devil is in the detail: A major product of the successes in cell biology is a mind-numbing number of facts, particulars, data and details. The volume of information and detail that we are generating in genome studies and cell signaling, for example, unsettles some. Will the molecular paradigm, which has been so successful and brought us here, lead us to the next level? In the reductionist paradigm, the cell can be viewed as a complex chemical system that obeys the laws of physics and the principles of chemistry. In this view, one needs to know the relevant chemical properties for all of the cellular components. Once this is known, the cellular dynamics and equilibria can be computed, and ultimately cell behavior modeled. For small systems and isolated processes, this has had an important predictive value and has been insightful and revealing. Most importantly, it uses the principles of chemistry, which is a common language that is known and understood by nearly all participants. Can this approach be usefully extrapolated to a highly complex system like an entire cell? It may take a while, as it poses some interesting challenges. How many complex differential equations, which must cover both temporal and spatial distributions, would be involved? How accurately will the concentrations and rate constants need to be measured? How does one deal with the non-ideal nature of the cell interior and exterior? The differential equations required to describe the systems of interacting pathways or networks found in a cell will necessarily be very complex and contain many terms. How does the error in measurements of the rate constants and concentrations, for example, propagate - that is, given any reasonable measurement error, can one derive anything that is meaningful and useful? The situation is complicated further by the nature of the cell. What are the effective concentrations (the activities) of the components? How does one address reactions that are occurring on surfaces or macromolecular assemblies that can be dynamic? These are formidable challenges. Chemistry faces them continually, as do other sciences that deal with complex phenomena. Natural phenomena have strong roots in the principles of physics and the concepts of chemistry. Yet the mathematics that backs them up does not readily yield to highly complex phenomena. Maybe different approaches - perhaps one based in the complex-systems theory that is so familiar to engineers - will provide an alternative. Where's the big picture? Are there other ways of dealing with our flood of details and particulars? There is a call for mathematicians, computer scientists, engineers and/or theorists to help bring order to this information flood. Can they make sense of this complexity? Are there overarching and unifying concepts that will allow us to think in generalities, rather than in particulars? There may already be some unifying concepts. One is the genetic paradigm, which views a cell's behavior as a consequence of its expressed genes. The geneticist's point of view has already provided an important, empirical and quantitative way of looking at cellular and organismal phenomena. This view of a cell or organism, or even a disease like cancer, differs greatly from that of a biochemist, which focuses on mechanisms and specifics. In some respects, it shifts attention away from the particulars and sticky mechanistic issues, and thus can be simplifying. Genetics has been a very powerful driver in many areas, not only as a tool to determine function but also as a way of looking at a process. The marriage of genetics with developmental biology is only one of many examples. A number of other examples derive from modeling. The Hodgkin-Huxley equation is one prominent and useful example. It models the axon as an electrical entity. For other purposes, the cell has been likewise treated as a mechanical entity and modeled in the jargon of mechanics. There are other ways of modeling the cell and its component processes - for example, through signal and systems theory, network and graph theory, Boolean algebra, and statistics. Each of these treatments can be meaningful and useful to those well versed in that particular discipline. But are these useful to those not versed in them? Is there a unifying theory or model that avoids a proliferation of models. How does one connect them to our chemical roots? In physics, the simplest is accepted as correct. Cell biology has a different reality. It is derived evolutionarily, and therefore, the simplest model may not be correct or even useful. Perhaps, in the future, there will even be a synthesis - like the periodic table or quantum mechanics for physics and chemistry - that allows us to deal with the mega-detail that we are generating. Big surprises in small packages: To date, cell biology has progressed rapidly because of its qualitative nature. Differences in localization are often characterized by fluorescence intensities that are described qualitatively as brighter or dimmer or as more or less localized. Similarly, differences in expression are often characterized by the intensity of bands on western blots or SDS gels; these are often described as bigger or smaller. Many changes are, in fact, very large, and this level of characterization is likely to be adequate. But have we missed anything? Is there a need for more quantitative measurements? When differences in expression are analyzed by gene array, where does one draw the line? Is a tenfold change more significant than a 2–3-fold change? Many measurements would not detect changes that are only 2–3-fold, and in others we have tended to ignore them. We wouldn't see such a small change in fluorescence intensity by eye, for example, nor would we readily identify changes in concentration that arise from differences in localization rather than expression. Ignoring small changes assumes that biological readouts are not highly poised. But is this true? Systems that have interacting components, undergo conformational changes or enzymatic modifications, or are part of amplifying cascades, for example, can be highly poised. Thus 2–3-fold changes in expression or in substrate/ligand concentration can have effects that are very large. Of course, the converse follows as well. Large changes might have only modest consequences - for example, if one is well removed from the Kd. Examples of small changes having large effects and vice versa are common features of complex systems and are now beginning to appear in the cell biology literature. It seems likely there will be many more as our measurements become increasingly quantitative. Downstream signals: What can one make of all of this? (1) This is a very, very good time for cell biology. Questions that have loomed for decades and centuries are becoming understood in a meaningful way. The progress is breathtaking; it wasn't this easy only a couple of decades ago. (2) Many are participating in the success; they are all contributing to something useful and important. (3) The devil is in the detail but so are the opportunities. (4) Big science is here to stay - perhaps a consequence of our success. As investigators, we need to embrace it and look ahead. (5) The only constant in our research will be change. We will need to be flexible in our approaches and questions. (6) We must translate our progress to the public through education and the popular press in ways that sustain their interest and support and attract new minds to our discipline. (7) The surge in new technology will continue to drive our progress, which will come to nearly anyone who works hard, chooses a good problem, and takes a reasonable approach. (8) We need to develop strategies to deal with the information flood; it won't ebb soon. And the anticipated simplifications from the mathematicians, computer scientists and modelers may take quite a while. (9) Enjoy your successes. This might be about as good as it gets.