I have written about the rise of human as a first-class model organism, and am an enthusiastic user of this outbred, large vertebrate, which can walk right into pre-funded phenotyping centres (hospitals). However, some scientists are (somewhat flippantly) predicting ‘the demise of all non-human model organisms’ completely, only conceding the necessity for using mouse in impossible-in-human verification experiments. Although such positions tend to be put forward in jest, their underlying argument resonates: given our obsession on human health, and how much we can do humans – with broad outbred genetics, iPSC cell lines and organoids – why should we bother with other systems?
This is dangerous thinking, mainly because it vastly overestimates our knowledge of biological systems at atomic, molecular, cellular and whole-body scales. Like all areas of science, our grasp of biology is variable in depth: there are a few areas we know surprisingly well, for example our quantum grasp of some specific enzyme catalysis, or the behaviour of groups of molecules relaying a signal in the cAMP signalling pathway. But these are mere pinpricks of light in an otherwise obscure landscape.
There is a seemingly solid foundation of at least the total parts lists by using genomes: good representation of the entire human genome, and a respectable catalogue of human protein-coding genes (though many annoying-to-nail-down details need sorting). But this gives us a false sense of security about our knowledge, both because this list is not complete in its details, but far more importantly, the list is just the start of understanding life (human included) and we are nowhere near the end of this journey.
Even with a complete parts list of proteins in humans, we are still clueless about what vast tracts of well-characterised protein coding genes actually do. For about 8000 proteins we have a good idea of at least one of their roles; for another around 7000 proteins we have some hints. But even this knowledge can be very partial. For example, the Huntingtin gene we know is involved in Huntington’s disease via a trinucleotide expansion – yet we have almost no knowledge of its molecular function. We know other genes are key mediators in disease, for example C9orf72 in amyotrophic lateral sclerosis (of ice bucket fame), yet we know very little about about its cellular or molecular function. And this patchy knowledge gets far worse as we move away from proteins. Every year it feels like a new class of non-coding RNA is defined, but pinning down functions for them (including potentially no function, the hardest thing to show) is elusive, beyond some individual cases.
Imagine we knew the full parts list of proteins and RNAs, and their individual functions. Somehow these proteins go on to make cells, and the cells form organs. Huge unknowns dominate the landscape of cellular structure and mechanism. For example, the massive, Death-Star-like Vault complex has a large RNA component, hangs around in the nucleus and is quite easy to visualise with electron microscopy – but we have no firm idea of what it is doing. Or take the host of vesicles and membrane-bound structures zipping around every cell. Presumably they’re doing some kind of cellular ‘housekeeping’ (specific to different cell types), but we’re gloriously ignorant of the details. How do they know where they’re going? How does the right thing get into the right vesicle? As soon as you start poking into even the easiest-to-observe cellular phenomena, there are a surprising number of unknown components and their interactions.
Research into nearly every combination of cells turns up far more questions than answers. Even ‘simple’ multi-cellular systems, like the gut, have mysterious ways of ensuring that the right cells divide and differentiate at the right time. In more complex systems, interactions between cells give rise to clearly observable (sometimes model-able) phenomena, for example beating heart muscle, or the capture and excretion of toxins.
We observe that assemblies of cells arise during development, but can only just begin to describe their behaviour, sort of. As for our level of ignorance about the four-billion-structured mass that is the human brain… let’s just say there is much work to be done.
The massive intellectual effort it takes to elucidate the human system from atomic to organ scales is analogous to discovering, climbing and mapping the entirety of the Himalayas in detail. In the dark. With constant storms. It is challenging, tricky and demands both innovation and a huge attention to detail – and done by a large number of people. We are in the foothills of this task now – and it will take many more decades.
Just another vertebrate
In the main, humans are ‘just another vertebrate’ – just one of evolution’s run-of-the-mill metazoans (albeit with a high-end brain), part of the great, wandering trail of cellular life on Earth. Despite the diversity of the final life forms, evolution is mainly a tinkerer at the molecular and cellular level, rather than radical innovator. Huge, key macromolecules, such as the Ribosome, have basically the same fundamental structure and function from seeming the very first living cell. This is true also in development; for example, amazingly, the developmental program that sets up the humble fruit fly’s pulsating tube of 36 cells – its proto heart – is quite similar to the one that determines our (or even more impressively, the giraffe’s) – million-cell behemoth of cardiac engineering.
What this biological unity means for us as scientists is that we have our pick of systems to work in, even if they have very different properties to humans, and can still have confidence that we are understanding humans in molecular detail. We can attack the hideously complex task of untangling life at all scales from many different directions.
The agony of choice
So which of the millions of species and thousands of tractable systems (including human!) should you use to tackle a biological problem? This is the ultimate agony of choice. My contribution to easing some of this pain: here are three rationales you might use to choose a system that will ultimately have an impact on our understanding the biology of humans.
1. To discover key facts about molecular and cellular life, including humans
Because of the unity of life by evolution, there are many systems for which one can have one’s pick of species and be confident the vast majority of knowledge will map to human. For example, whichever species you study to understand the eukaryotic ribosome in detail, the core components will work pretty much the same. So choose the system(s) that provide the easiest material to use, or the best system to manipulate. The same applies for things like the Map kinase cascade, vesicle transport, microtubule function, liver function across multiple cells, or short-term associative memory in neuronal structures.
The information gained by studying these systems will map easily to human proteins/cells/organs, with only minor modifications. Choose your organism partly for the ease of studying the molecules/system of interest, ensuring that the system you are studying is ‘clearly homologous’ to human.
For studying molecular and intra-cellular components, choose one of the yeasts or human cellular systems (human is a fine system!). For developmental and multi-cellular schemes, you could choose worm, fish, fly or Xenopus, among others. For organ-level systems you probably want a vertebrate (more directly homologous organs), but you can be confident about choosing a more exotic species if it really provides a novel angle on a particular system (e.g. the structured nictonic acetylcholine receptors of electric eels, the giant snail neuron, Takifugu’s minimal-vertebrate genome).
2. To elucidate key principles of biology
Certain systems are particularly good for elucidating the key principles underlying biology. We don’t often know what a ‘good understanding’ of a complex system is: what you need to know to understand a signalling pathway, or development, or how a neuronal system works, for instance. For this kind of work you need to be able to dominate a system completely, usually by all means possible so you can build up layers of knowledge and test different schemes experimentally.
For this rationale, it needn’t be the case that the components of your system will be directly homologous to human; rather, the argument is that the type of phenomenon you’re looking at is present in both species. Take the very un-human, stereotypical development of C. elegans, in which every individual has exactly the same set of cells. It is really worth studying in detail, precisely because you can have an intellectual dominance of the worm developmental scheme in a way that is near impossible in other systems. Similarly, the ability to manipulate and monitor the living fly or worm brain is exquisite not because we expect to find directly homologous neuronal circuits in humans, but because it helps us find out what we need to know to understand neuronal circuits fully (or, if we’re honest, at all well).
This argument bears out, from quantitative ways in signalling pathways (e.g. in bacteria and yeast) through developmental to neuronal processes. Here, the choice of organism is driven by the technologies and measurement modalities, and as such will often be ‘traditional’, well-established model organisms with many experimental techniques. However there are some scenarios where using the diversity of life really helps understand principles, usually by providing an insight into evolution. For example, studying primitive metazoans, with proto-muscles and proto-nervous systems provides, via evolutionary arguments, a huge insight into the evolution and role of these cells.
The third rationale is by far the most open: experience over the past 100 years of research has shown that completely serendipitous discoveries sometimes lead to radical new technologies. The current poster child for this is CRISPR/Cas9, which is the now-ubiquitous gene-editing enzyme, which arose from research into bacterial immunity. But there are many others, from PCR to the discovery of the apicoplast in the malaria parasite.
For people who want to ‘think strategically’, choose the area of research with an outcome in mind. The successfulness of just “exploring” might sound lazy, but nevertheless, the truth of science is that you can’t predict what you will find. Using arguments of serendipity gives carte blanche to a molecular biologist to simply follow his or her nose. However, given the entirely open field, in practice one has to have an ‘eye-catching’ reason to explore some aspect of biology, and a good nose to convert this quirk of biology into insightful knowledge.
Biology doesn’t disappoint, though, for possibility: the Alaskan tree frog, which freezes solid over winter (including their heart stopping) and then revives; the Mexican Axolotl, which can regrow an entire limb as an adult; the tardigrades, which can be revived from complete desiccation, even after a hard-vacuum exposure; soil bacteria, in all their chemical weirdness… there is no shortage of eye-catching stuff.
It is almost too easy to find interesting things, and we could probably take much more advantage of serendipity. One can only speculate on what can be learned from these examples, which is fun in itself (suspended animation? new chemical fuel stocks? re-growing entire limbs?). It all comes down to the fact that we know evolution has been far more inventive than our collective imagination could ever be.
Starting from disease
Some may bristle at the idea of trying to understand human disease by uncovering more basic biology in model systems. For those who start from the standpoint of human disease, it can seem as though basic researchers do not have their priorities straight – every missed opportunity to cure a disease (in particular a disease that might be close to a patient advocate’s heart for personal reasons) can feel like a mistaken prioritisation of funds and effort.
A less personal argument centres on how new technologies have radically improved our ability to focus. With the resurgence of human genetics at scale, iPSCs, organoids and other features, there are plenty of opportunities to study the human system directly – so why not simultaneously study things with a clear connection to human disease? Surely such research would uncover interesting aspects of basic biology and elucidate basic biological processes along the way?
The counterpoint to this view is that one needs a mixed portfolio, because we can be confident that there are massive tracts of things we don’t know, and we know that each species and approach wont be good for all of them.
My fear is that a single-minded, human-disease-first perspective – at the expense of all other approaches – will deliver gains on the diseases for which our current molecular and cellular knowledge is already adequate – but then stall.
How many diseases are in this class of “tractable given current knowledge”? It’s hard to know the percentage, but it’s definitely low – our collective knowledge is poor. More importantly, we don’t know which diseases will ultimately be tractable. Having chased down only the most promising cases, we might valiantly throw ourselves against sheer cliffs of ignorance about the mechanisms of the rest. With a better mix of approaches, we’d be creating paths along and ladders up those cliffs, making our quest to cure diseases a more manageable one.
Starting from basics
Those starting from basic research often want to be honest about their own motivation. Most basic researchers are just curious about how life works. They hope that their research will have benefits, often with a track record of this happening, sometimes in surprising ways. However there is sometimes a distasteful process of having to artificially construct an argument to link their proposed research to disease. Much like the early explorers, they want to study systems simply in the pursuit of knowledge, sure that it will take them somewhere interesting but without any idea where it will take them – or how that might change things – but knowing that what they discover is likely to be useful.
I sympathise with this point of view and appreciate its intellectual integrity, but it opens up an apparent split with translational research, and encourages people to consider these two worlds as being apart.
There are two reasons I feel that this “separation” of basic from translational molecular biology is wrong. Firstly, ‘translation to health’ and ‘basic research’ are not in opposition. Because of the unity of biology at the molecular and cellular level, these are fundamentally intertwined intellectual processes. Collectively, we should not need artificial arguments to link them. Secondly, we all have a moral imperative to contribute our skills to efforts that benefit society, and the ultimate process of changing healthcare practice due molecular understanding should be something we can all support.
Importantly, healthcare is a massive part of the economy, taxpayers and charities want real change and they are happy to fund it. Sustained change to the quality of our healthcare, enabled by molecular understanding, will only be delivered (and intelligently applied) with the on-going engagement of basic science.
Tribal science is unhelpful
Crude arguments that play “translation” and “basic research”, or “human disease” and “fundamental discoveries” off each other are depressing. The idea that humans are the onlymodel organism for the future is simply misguided mischief, and opens up the dangerous possibility that people might actually start to believe it – and it’s just as frustrating to hear some people claim that one can only do translational, healthcare related science in humans, and no profound basic discoveries will emerge from human investigation. Taking an extreme position to make either point is annoying, but it belies an underlying tension that needs to be resolved. I think these arguments are more about conflict between of tribes of scientists who are now interacting more and more. There is also an element of jockeying for position, both as individuals and as tribes. We need to get beyond this.
Balance is best (but not easy)
A ‘balanced portfolio’ sounds great, but there is no straightforward recipe for compiling one. What does the best ‘balanced portfolio’ of research look like? How much “pure” disease focus on humans, and what else to add? A tablespoon of yeast, a teaspoon of serendipity and a dash of electric eel? What part of that portfolio would a particular funding agency, charity, institute or scheme take on? How to assess a slew of wildly different proposals, each with different rationales?
There are no easy answers to these questions, but we do need to realise that the lines between ‘basic’ and ‘translational’ research are now fully blurred – both are essential parts of the same process of understanding life, with massive spill-over effects across many practical aspects of our world, our health above all.