The tiny number of model organisms constrains research in ways that must be acknowledged and addressed, warns Jessica Bolker.
For most experimental biologists, life revolves around a handful of species: the mouse (Mus musculus), the nematode worm (Caenorhabditis elegans), the fruitfly (Drosophila melanogaster) and the thale cress (Arabidopsis thaliana). We assume that model organisms offer universal insights, and funding agencies largely support work on a shortlist of favoured species (www.nih.gov/science/models).
Scientists who submit grant proposals for a project using a standard model organism need not use up space to explain their choice. By contrast, choosing a less common model that is uniquely suited to the research demands a lengthy justification to convince sceptical colleagues. Proposals for projects in unusual species are often returned with the suggestion that the applicant use a standard organism instead, because any worthwhile question should be accessible in a well-established model.
Investments in research with a handful of models have returned rich dividends in basic knowledge and medical progress. And many careers, labs and journals are built on the primacy of the fly, mouse and worm1.
But studying only a few organisms limits science to the answers that those organisms can provide. The extraordinary resolving power of core models comes with the same trade-off as a high-magnification lens: a much reduced field of view. For instance, traditional models for developmental biology — such as the fly — were chosen because their phenotypic traits directly reflect their genotype, with minimal environmental input. These models are poorly suited to questions asked by scientists in emerging fields such as ecological developmental biology — 'eco-devo' — which focuses on external influences on developing phenotypes.
Such limitations have serious consequences. Disparities between mice and humans may help to explain why the millions of dollars spent on basic research have yielded frustratingly few clinical advances1,2,3,4. Narrowing the research focus too far limits basic understanding, in ways that can lead directly to clinical failures. For example, an experimental treatment for multiple sclerosis that, in inbred mice, improved symptoms of induced disease produced unpredicted — and sometimes adverse — responses in human patients. The inbred mouse model failed to represent the genetic and immunological diversity of human cells, a shortcoming that was obvious in retrospect2.
It is time to think more critically about how we use models. This means articulating tacit assumptions, such as the adequacy of rodent models to fully represent specific human diseases. It means looking hard at how we select and use our favoured model species, and acknowledging both their strengths and their limitations. And it means mainstream funders and journals welcoming work in non-standard organisms.
Models of convenience
How did a handful of species become central models? Sometimes it was more about convenience than strategic planning. Drosophila rose to prominence in the early 1900s in part because its short generation time was handy for student projects and its four pairs of large chromosomes were ideal for the study of eukaryotic genetics5. Yeast, mice, chickens and other domesticated species became lab favourites because they were already familiar and accessible. The existence of lab populations of frogs (Xenopus laevis) for use in pregnancy tests led to their recruitment as a model for developmental research.
As model-based science grew, these few species became increasingly dominant, despite the sometimes haphazard way that they had initially been chosen. We have now reached a point where, if researchers cannot tackle a problem using a familiar species, they may not study it at all1.
Take modern developmental biology. The field has centred on small, rapidly developing organisms with short generation times — most typically, Drosophila and C. elegans. Much of our current understanding of developmental principles is based on experiments in these species. However, evolutionary selection for rapid development has broad implications. It seems to favour stronger genetic control during development and less plasticity (or flexibility). Compared with related species, development in the models is less responsive to external signals, whether adaptive or disruptive. Because plasticity and the role of the developmental environment are particularly hard to study in key models, these areas receive comparatively little attention6.
A similar narrowing has occurred in biomedical research. In the case of Parkinson's disease, potential treatments are often assessed by measuring motor function in a lesioned rat. But the rat model does not clearly represent other significant symptoms of Parkinson's that occur in human patients, such as cognitive decline. This may steer some researchers away from these aspects of the disease.
Similar biases rooted in the use of particular models may also contribute to the 'translational disconnect' with regard to neurodegenerative diseases such as Alzheimer's and amyotrophic lateral sclerosis3,4. The inability of highly inbred and often genetically modified rodent strains to fully represent the diversity of human patients and symptoms has called the power of such models into question, even within the research communities they serve1,2,3,4,7.
At the same time, the effects of apparently trivial environmental variations, such as the details of mouse handling, are often overlooked8. Aggression is the key behavioural phenotype in male mice lacking the enzyme neuronal nitric oxide synthase. This was not observed — and could not be seen — until animals were housed in groups rather than in standard individual cages9. Few lab models explicitly account for the environment of organisms, despite increasing recognition that this may affect the outcome and replicability of experiments7.
“To study environmental influences, we need to study species in which such factors matter.”
In short, if we frame a research model or system too narrowly, leaving out key causal elements such as environmental influences, we cannot hope to construct a complete picture of the mechanisms that underlie crucial variations, for example in development and disease. To study environmental influences, we need to study species in which such factors matter. So the traits that define a successful model must shift as the questions for which we use them evolve.
Choosing a research model should be more than a matter of convenience or convention. Scientists need to ask more questions — about the goals of a specific experiment, how suitable a given model is to reaching those goals, and what environmental or other external factors might be relevant to how well the model works. For a given question, it is crucial to determine which aspects of human biology are essential (for example, our genetic diversity, unique characteristics of our immune system or particular disease symptoms) and assess how well they are represented in a candidate model (see 'Choosing the right candidate'). Where mismatches appear, we must limit our inferences from animal studies accordingly, and consider when and how to move to research in humans. For some kinds of biomedical research, it may not matter that the damage or symptoms in the model developed by a different pathway to that which occurs in patients — orthopaedic injuries are one example. But in other areas, such as epidemiology, it matters a great deal.
Recognizing that standard models have limitations does not mean we should give them up. Rather, we should deliberately account for their limitations as part of study design — for example, by analysing the role of a gene in mouse strains with different genetic backgrounds. No single species, no matter how highly engineered, can ever serve as a universal model: every species has unique features that may be assets or faults, depending on the question being asked. For instance, the lack of developmental plasticity in Drosophila and of genetic variability in inbred rats limit what these models can tell us about ecological effects on development, but make them powerful tools for studying gene function during development.
We also need to broaden our range of models to include species such as Antarctic icefish, comb jellies, cichlids, dune mice and finches that are naturally endowed by evolution with features relevant to human diseases10. Studying the basis of unique adaptive traits in these animals may yield insight into human disorders such as osteoporosis, cataracts and cancer.
Immediately and practically, the US National Center for Advancing Translational Sciences in Bethesda, Maryland, should support the development of new systems for investigating problems that are not tractable in currently favoured models. It should also fund investigations into fundamental questions about model-based research (see 'Choosing the right candidate'). The resulting insights would help scientists to select the best models for advancing basic and applied research, and strengthen the bridges between them.
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