The conditions under which research is performed have an enormous impact on science, and are rapidly changing. Even if our influence on these conditions is small, we think it worthwhile to briefly mention some key issues that might have dramatic effects on the future of neuroscience research.
What Kind of Neuroscience?
It has been argued that neuroscience is now at the stage of physics in the 1920s when large-scale projects became the best way forward. Large-scale, industrial science employs hundreds of scientists to perform invariant, standardized assays in the service of collecting large data sets with little experimental variability. Indeed, several large-scale biology projects have been very successful, as best exemplified by the human genome project. It is fascinating to consider large-scale projects that might be useful for neuroscience, for example:
- a systematic cataloging of neuronal cell types in all major brain areas using a combination of electrophysiological, molecular, and microscopy methods
- the generation of conditional alleles and corresponding cre-recombinase expression lines in mice for all neuronal genes
- a neuronal ENCODE project that maps the expression patterns of all genes in brain with the corresponding promoter elements
- a complete 3D reconstruction of a vertebrate brain to determine its complete wiring diagram, analogous to what was done for C. elegans by electron microscopy
Such large-scale projects require large budgets, a top-down approach, and a long-term commitment. They have the potential of being transformative by influencing the types of experimental manipulations that can be performed by neuroscientists working at many levels and that therefore can enhance the sophistication of the questions that are being addressed. It would obviously be very powerful to be able, in specific cell types, to express activity sensors, to turn on and off synaptic function and/or plasticity, and to manipulate specific cells’ activity in a precise, temporally controlled fashion. The large-scale projects we mention (also see Malenka, 2002
) might provide the foundation for achieving these goals. However, such projects are also risky from a cost-benefit perspective.
At this time, we are painfully ignorant about some of the most fundamental questions in neuroscience. How is a single memory encoded by synapses and circuits? How can it last a lifetime? How does activity in specific neural circuits allow the brain to recognize an apple? What neural circuits mediate joy or sadness? It is unclear whether the answers to such questions will arise from large-scale projects, or rather will require attracting the smartest and most creative young scientists to our field to individual projects that they control. Projects such as analyzing the region-specificity of synaptic plasticity, examining the mechanisms involved in such plasticity, and testing the role of plasticity in specific behaviors are likely more effectively performed on a small scale since it cannot easily be scaled up. Overall, the issue boils down to the question of what approaches, in a resource-limited environment, are most cost-effective and most likely to yield important advances.
A related issue is how much basic versus translational (i.e., applied) neuroscience is appropriate. Recently, major opportunities for understanding diseases arose, and political pressures for making use of these opportunities are mounting. It is unclear, however, whether applied neuroscience with a specific goal is more cost-effective than basic, undirected science investigating the underlying biology. Most scientists concur in the need to address medical problems and be guided by diseases. Thus, the challenge will be to organize an appropriate mix of basic and applied neuroscience in each of our laboratories to optimize productivity in the service of the society that provides the resources to conduct the research in the first place. Taking successful projects such as the discovery of the role of hypercholestrolemia and the LDL receptor in atherosclerosis as an example, the ideal situation may be if the direction of basic science is informed by clinical findings, without basic science being forced to work on explaining only these findings. Instead, the hypercholerstolemia example suggests that basic science can be most effective if it unravels the underlying biology that can then form the fundament for clinical applications.
How to Promote Interdisciplinary Research?
Work on synapses will increasingly require interdisciplinary approaches, since these provide the most complete insights. The stunning new methods of the last 20 years, from molecular manipulations (e.g., mouse genetics and RNAi) and electrophysiological assays (e.g., patch-clamping, tetrode recordings) to sophisticated imaging approaches (e.g., two-photon microscopy) have enabled advances that would have been unthinkable when the first issues of Neuron appeared in 1988. This wealth of advances, however, also causes problems.
- Because credit is shared in interdisciplinary research, it is difficult to recruit collaborators. Outside of large-scale projects that receive abundant funding and have defined roles for individual investigators, interdisciplinary collaborations often fail when the participants cannot agree about the distribution of funds and credit.
- Since interdisciplinary research involves techniques that not all participants in a project understand, quality control between collaborators can be difficult. Methods are sometimes insufficiently validated, and their limitations misunderstood. This can lead to conclusions that go far beyond the presented data.
- Publication of interdisciplinary research is difficult. Many papers no longer have any “Experimental Procedures” of note, making an interdisciplinary understanding more difficult. Reviewers are often asked to judge all methods used in a single paper, even if they are familiar with only a few of the methods, leading to either too harsh or, more often, too lenient evaluations.
- In interdisciplinary projects, techniques are often not scrutinized equally and sufficiently, leading to the inappropriate use of techniques that are not yet mature. While it is important to push the envelope and develop novel approaches and hypotheses, exciting new techniques also have limitations, and exciting new findings are sometimes wrong.
Science can be considered “truth by consensus,” and can only progress if all scientists can understand each others’ data. On top of the problems presented by a broadening armamentarium of methods, the difficulty in publishing negative results—especially negative results that contradict previous papers—makes reaching such consensus difficult. Journals often have little interest in hearing that one of their papers is being questioned by other scientists. Moreover, ruling out a hypothesis is often viewed as uninteresting, even if essential for progress.
It would obviously be best not only for interdisciplinary research, but for all neuroscience, if disagreements about data and conclusions could be presented and discussed in a frank, forthright manner. The mechanisms by which to do this are unclear. The Neurotechniques section of Neuron is an example of a useful approach to the presentation and discussion of state-of-the-art methods. Additional initiatives that focus on the advantages and limitations of novel approaches and methods will certainly help promote research productivity. Better documentation of experimental procedures would help. The best mechanism for letting scientific communities know about results that are being questioned and becoming controversial is less clear, especially since publicly questioning results and conclusions is often taken personally. Nevertheless, as more and more sophisticated but complex methods are used to probe brain function and more studies involve the use of multiple different approaches, it may benefit the neuroscience community to think about what mechanisms will best help evaluate our progress and determine what should be actively pursued and what should not. Peer review at the journal and granting agency levels has functioned well over the past decades, but may need to be supplemented by additional mechanisms. One possible avenue would be to create a new category of review in which opposing sides of an issue directly argue their cases, supported by data, with the possibility for readers’ comments. Although impossible for a printed journal, such an avenue may be feasible for a web-based journal.