Big data and experimental biology: the complementary roles of hypothesis-led and blue skies research Free

In their recent editorial, Franklin and Handel (2024) offered a significant broadening of scope for Journal of Experimental Biology (JEB):

Fundamentally, perhaps one of the most substantial changes is that we no longer require a research paper to test a hypothesis; instead, it is sufficient for it to address a significant question of relevance to JEB's areas of interest. We feel that this will allow for more discovery-based studies to be considered for publication in JEB.

What is the significance of this statement, and is it a good thing? In this Perspective, I will argue that this relaxation should open the door (formally) to a new class of innovative and influential research.

In the classical view of experimental science, hypotheses have always been revered. According to the scientific method (of which there are several philosophical flavours), a hypothesis is generated based on the available knowledge of the time, and is tested to destruction (Fig. 1). Incidentally, a hypothesis is not necessarily directly testable; rather, a good hypothesis allows the formulation of a prediction; and a good prediction is one which is testable. These topics have been discussed in more detail elsewhere (Elliott et al., 2016; Fudge, 2014). If the hypothesis cannot be disproved, it is added to our knowledge database, until such time as it is disproved (Popper, 1935). In fact, the scientific method was formalized rather earlier than Popper, by Ibn Al-Haytham while under house arrest in Cairo, between 1011 and 1020, in his epochal Book of Optics (see Sabra, 1989). Although the limitations of the scientific method have been long discussed (and indeed it has been described as a myth; Thurs, 2015), it still holds sway today. In a valuable variant – ‘strong inference’ – Platt (1964) argues that we are better formulating multiple hypotheses than formulating predictions that distinguish between them. Then, in a nod to the logic of a great detective, ‘When you have eliminated all which is impossible, then whatever remains, however improbable, must be the truth’.

However, do we – and should we – always rely on the hypothesis-led approach in real science, explicitly generating and testing hypotheses to learn more about the world? As experimental biologists, our interest is in how animals function, and I suggest that, in reality, most of us formulate and test ideas, rather than hypotheses. For example, the question ‘how can small insects fly?’ was answered not by deducing the clap-and-fling hypothesis de novo, but by detailed kinematic analysis of insect flight (the ‘big data’ of its day), leading to the development of a radically new hypothesis (Weis-Fogh, 1973). Thus, although hypotheses are loved by journals and grant agencies alike, there is a place for hypothesis-free (or idea-led or question-led) research, particularly in extending our understanding beyond our logical line of sight.

How can we gain genuinely novel insights into biological phenomena? I think big data can help us, and (used properly) they can bring a huge advantage to the investigation: freedom from experimenter bias. To illustrate with an example from my field, one could formulate a hypothesis on the role of the Malpighian tubules in insect osmoregulation: based on what is known in mammals, one might hypothesize that the Na⁺/K⁺-ATPase (the ‘sodium pump’) is vital for function of the Malpighian tubules. One would then use the best available drugs (ouabain, digitalis) or reagents (antibodies for immunocytochemistry and western blots) to test this hypothesis. This is a perfectly valid approach, and one which has certainly been published in JEB and elsewhere (Leyssens et al., 1994; Torrie et al., 2004). However, let's now look at the limitations: the hypothesis was generated based on the available literature of the time, the researcher's awareness of it, and their choice of sodium pumps as the most important thing to be studying. The outcome would depend on the availability of reagents to test the model at that time. Such research is logical and incremental, but is vulnerable to unconscious bias in the experimenter's choices. This confirmation bias can limit the scope of a scientific investigation by ‘narrative fallacy’ (Taleb, 2007), the natural tendency to connect unconnected data to produce a ‘story’ that helps make sense of the world.

Is there a way to ask the organism what is important in the functioning of a tissue? I suggest that big data achieve this goal; for example, the use of genetic screens. Such screens can identify genes of relevance to a certain process or phenotype from unbiased phenotypic screens of panels of mutants. Work from my lab can illustrate the importance of this unbiased ‘fishing trip’ approach. The insect ‘kidney’ comprises independent Malpighian tubules. By the late 1970s, the best available classical morphology, histochemistry and physiology of the day had identified three regions and two cell types in the Malpighian tubules (Wessing and Eichelberg, 1978). By using enhancer trapping (a technique by which reporter genes are randomly inserted in the genome, and their expression patterns documented) it was possible to show that the Drosophila tubule actually comprises six regions and six cell types, and that these domains are almost invariant in size (Sözen et al., 1997). Pleasingly, all data since, including a landmark single-cell RNAseq study two decades later, have aligned with these genetic domains (Li et al., 2022; Xu et al., 2022). The ‘fishing trip’ thus allowed an unbiased and original view on tubule structure and function that (so far) has withstood extended hypothesis testing by the classical scientific method. In fact, the insights from a screening approach can be seismic in scale: most of the structural framework of our understanding of developmental biology is based on genetic screens of Drosophila embryos (think pair-rule genes and homeotic mutants; Nüsslein-Volhard, 1996); similarly, most of what we know about circadian rhythms can be traced back to an insightful and pioneering screen (Konopka and Benzer, 1971).

Genetic screens are largely the province of genetically tractable organisms (the so-called ‘model’ organisms), and may feel remote from a typical physiologist's chosen problem area; however, it is important to note that in all the examples above, the insights gained have proved transferrable to other organisms, and even to humans. Genetics should thus be seen as a valuable complement to the physiological approach, when it can be invoked.

Our journal focuses on multicellular organisms, particularly those of the Kingdom Animalia. This choice provides an amazing richness of complexity and beauty for study, and which has certainly entranced me throughout my career. Multicellular organisms have adapted to their environments by specializing groups of cells, or tissues, to perform specific roles that improve overall fitness. The effective founder of the field of comparative physiology, August Krogh, realized that particular organisms might display these traits to extreme levels that make them ideal for study, and for the generation of general insights (Krogh, 1929). So, our central question ‘how do animals work?’ might be rephrased as ‘what are the most important specializations of my tissue of interest that contribute to the success of the organism?’. The central dogma (that genetic information flows from DNA to RNA to proteins; Fig. 2) can help us toward this unbiased view.

Of course, the minimal central dogma must be decorated with provisos and codicils (e.g. epigenetic marks, RNA stability, post-translational modifications). However, sampling at all stages of the central dogma can be useful, depending on the problem domain. To understand how tissues operate within an organism, the genome is least useful, as it is present in nearly every cell. Investigating the proteome has its own issues, relating to sensitivity, quantification and bias against membrane proteins. The metabolome is closest to function, but is highly dynamic (i.e. noisy). The key issues with interrogating the metabolome are that not all proteins are metabolic enzymes, and that an instantaneous metabolome requires flux information to be informative. So – although all of these levels of investigation are superior for their own problem domains – for labs such as mine at least, transcriptomic datasets seem to provide the most comprehensive, unbiased insights; the following sections therefore focus on the use of transcriptomics in the use of non-hypothesis-led research.

For the large domain of questions where transcriptomic data can provide ‘blue skies’ insights, how can they be analysed? Firstly, a microarray or RNAseq experiment, coupled with Gene Ontology (GO) analysis does not cut it, and hasn't for a couple of decades. GO is useful (Aleksander et al., 2023; Ashburner et al., 2000), but the shortcomings of GO annotation and nomenclature are well documented (Rhee et al., 2008; Wijesooriya et al., 2022). For example, many of the high-level GO terms are too general to mean anything; I have reviewed articles that pronounce solemnly that expression is enriched for ‘metabolic process’ or ‘response to stimulus’. This is such a waste of opportunity! If you are reading this, then you are an experimental biologist, and the excitement comes when the data are used to construct models to test. For example, our original expression analysis of the Drosophila renal tubule did not finish with a list of enriched gene expression but instead demonstrated the utility of these gene enrichment hit lists with physiological and histochemical assays (Wang et al., 2004), producing in turn some novel insights about tissue organization.

There is no doubt that post-genomic research can be eye-wateringly expensive. However, for some purposes, meta-analysis of existing datasets may provide novel insights – this approach has also been endorsed recently by JEB (Franklin and Hoppeler, 2020). Of particular utility are gene expression datasets; for example, of fly or mouse (Chintapalli et al., 2007; Geffers et al., 2012; Krause et al., 2022; Leader et al., 2018). If you want to find out how a tissue works, and a suitable dataset already exists, a list of genes specifically expressed in that tissue is a great place to start. The quality of the resulting paper is in large part measured by the quality of the predictions that can be made from the analysis.

Is hypothesis-free science antagonistic to the scientific method? Absolutely not! Unfortunately, both grant agencies and less enlightened journals are not favourable towards what they decry as ‘fishing trip’ proposals (Haufe, 2013). However, when such studies are undertaken, they are intrinsically hypothesis generating. A gene that shows expression that is utterly limited to a specific tissue has clear predictive value; for example, the urate oxidase gene is uniquely expressed in the renal tubule of Drosophila, strongly suggesting that the conversion of urate to 5-hydroxyisourate (a necessary part of the purine catabolism pathway) occurs only in this tissue – a clearly testable hypothesis (Chintapalli et al., 2007; Wallrath et al., 1990) that would not have been developed without the serendipity of a big dataset. Whether the unbiased study is a genetic screen, a transcriptomic analysis or collection of a comprehensive dataset, a well-conceived experiment will naturally point towards new lines of work and new ideas that can be formalized in hypotheses.

Gene-based discovery can produce very large hit lists. One could, of course, pick the ‘juiciest’, most interesting, genes for further study, but this risks reintroducing experimenter bias. How do we choose ‘juicy’ genes, other than based on our own experience and preconceptions? My lab has recently developed an impartial tool, ‘DigiTally’ for prioritizing such datasets (A. D. Gillen, S. Keenan, M. Akram, M. Skov, A. J. Dornan, S. A. Davies and J. A. T. Dow, unpublished), whereby multidimensional scoring identifies both interesting and experimentally tractable candidates. Interestingly, the Perrimon lab is thinking along similar lines (Mohr et al., 2023).

Clearly, gene-based downstream testing is relatively straightforward when one is working in a model organism. For a range of select species, from yeast to fly, from worm to mouse, there are mutant organisms available that can allow the functional dissection of a gene with quite beautiful precision. But this does not mean that the new biology is confined to such genetic models. As a recent Special Issue of JEB argued, the advent of precise genome-editing technologies, such as CRISPR, allows the democratization of comparative physiology, whereby any organism can be considered a Krogh model (Dickinson et al., 2020; Matthews and Vosshall, 2020): ‘Building on the availability of sequence data, genome-editing techniques are becoming available for a broadening array of species, allowing hypotheses to be tested experimentally’ (Dickinson et al., 2020).

This convergence has helped to address the ‘phenotype gap’ for informative models such as fly and mouse (Brown and Peters, 1996; Bullard, 2001; Dow, 2003, 2007); that is, the mismatch between tractability of a model organism to genetic manipulation and big data approaches, and its historical study by physiologists. Thus, physiological skills and approaches are not superseded by post-genomic biology, but are essential for its progress.

In conclusion, although hypothesis building and testing remain central to the scientific method, let us welcome the potential for idea-based discovery to provide unbiased, breakthrough insights into the questions that we care about. In this Perspective, I hope to have convinced you that big data, in particular, has strong merits in this regard. Furthermore, public deposition, data re-use and meta-analysis are wonderful vehicles (though not the only ones) to provide such ‘blue sky’ insights into how a tissue functions and contributes to organismal success. In fact, such work has already featured in JEB – as an editor for many years, I can't think of many articles that featured formally defined null and alternative hypotheses in their Introduction. I therefore welcome this liberalization of thought, and where it can lead. Perhaps – rather than the ability to formalize hypotheses – the most important qualities for a successful biologist are the knack of having hunches that turn out to be correct, green fingers in the lab and a certain stubbornness. Or, in the words of Nobel laureate Barbara McClintock:

‘If you know you are on the right track, if you have this inner knowledge, then nobody can turn you off. No matter what they say’.