The said truth is that it is the greatest happiness of the greatest number that is the measure of right and wrong.

Jeremy Bentham (1748–1832)

The “greatest happiness principle” propounded by 19th century Utilitarian philosophers such as Jeremy Bentham and John Stuart-Mill directs that “right” actions are those which do the greatest good for the greatest number. Even if this philosophical principle has fallen into disrepute, having found its purest expression in the totalitarian excesses of fascism and communism, utilitarianism seems like a promising moral foundation, at least for public health medicine. However, medical research tends to be driven by the intellectual interests of individual researchers and rare diseases appear more often on grant applications than can be justified simply by the number of people affected. A commonly stated defence is that by understanding the pathophysiology of rare diseases we will learn something of importance about more common conditions. Are there good examples from neurology to support this approach?

Most genetic diseases are rare whereas most common diseases are considered to be “complex”, by which is meant that there are both genetic and environmental contributions. For example, a number of rare monogenic diseases lead to stroke, including CADASIL due to mutations in NOTCH3 and Fabry’s disease caused by mutations in alpha-galactosidase.¹ An important test of the general value of such genetic findings is whether sequence variations (polymorphisms) in these genes, which are presumed to alter gene expression or function, are found more commonly in populations of typical stroke patients than in the rest of the population. So far, it seems that variations in NOTCH3 do not appear to predispose to either stroke or migraine, although, as a result of underpowering of studies and the inherent heterogeneity of stroke, the question has probably not been adequately answered. Unfortunately, none of the monogenic stroke loci emerged as “hotspots” in a genome-wide association study suggesting that, in an Icelandic population at least, the causes of monogenic and sporadic stroke are not the same. Homocystinuria may be a notable exception as both a cause of monogenic stroke and for which functional polymorphisms in the gene are a risk factor for stroke in the general population (although with a 1.2-fold increased risk, the effects of individual genes are likely to be small); there is even a treatment, folic acid, which may lower stroke risk, though this is yet to be proven in randomised trials.

Late-onset neurodegenerative diseases represent an emerging public health crisis for the developed world. Sporadic, age-dependent conditions such as Alzheimer’s disease, Parkinson’s disease and motor neurone disease (MND) or ALS are presumed to have a complex aetiology, though there is currently no convincing evidence for specific genetic or environmental factors. The vast industry of molecular genetic and animal model research in these diseases is focussed on much rarer monogenic analogues of the commoner conditions which, even if they share some of the characteristics, are by definition not the same entity. A mouse harbouring a mutation in presenilin-1 can never be “a mouse with Alzheimer’s disease” simply because the latter is a sporadic progressive degenerative disease of the elderly human brain, an organ separated from the mouse brain by 75 million years of evolution. Perhaps it is no surprise that, despite the fact that a number of transgenic mouse models of Alzheimer’s disease recapitulate the molecular pathology of plaques and tangles, none provides a good model of the cognitive phenotype. Furthermore, the genes underlying rare variants of common diseases, such as the presenilins and the amyloid precursor protein in familial Alzheimer’s disease, do not in general appear to be the same genes as those that confer risk of the associated sporadic disease, such as Apoe4 in typical Alzheimer’s.

It is still possible that rare disease models could lead to the identification of useful therapies; however lessons from other neurodegenerative diseases suggest that caution is required. Although only 2% of MND patients harbour mutations in the SOD1 gene, a very significant proportion of all the molecular pathological research in MND is based on a single transgenic overexpression mouse (G93A). Clinical trials of potential therapies targeted at the mechanisms of motor neurone death in this mouse (apoptosis, microglial activation, oxidative stress, excitotoxicity and many others) have resulted in a series of expensive and uniformly negative clinical trials in humans. Part of the reason is that our basic science colleagues have been slow to realise that clinical trials require blinding, randomisation and adequate power—even in mice.² However, the less comforting possibility, as someone once pithily remarked, is that humans with MND may not be a good model of the mouse disease.

Generalisation from a rare genetic form of a neurodegenerative disease to the more common sporadic variant may simply not be possible. Given the methodological difficulties in creating models of late onset sporadic disease in humans, however, we are destined for the time being to continue with the tools available to us. Rare diseases affect our patients and therefore deserve our attention. Along the way we are likely to learn something of scientific value about the nervous system. However, whether this information will help to prevent or cure the major neurological causes of death and suffering remains an open question.