19 Large-Scale Biology

2.1. A Primer on Discovery Strategies—A Tripartite Account

In order to understand how large-scale projects in biology influence discovery strategies and whether they may possibly undermine the epistemic independence of molecular biology labs, we should say something about discovery strategies in general. It is commonplace to distinguish between a phase where a hypothesis or model is generated and a phase where evidence is provided in support of a hypothesis or models are evaluated for accuracy according to certain standards.4 However, some philosophers have realized that such a sharp division does not do justice to the variety of processes that hypotheses are subjected to (Curd 1980; Nickles 1980; Schaffner 1993). These scholars make a distinction between hypothesis formation/generation and hypothesis weak evaluation/development in order to show how the discovery phase is much more complicated (Curd 1980). According to Curd, the discovery phase should be divided in two subphases: a phase of theory/hypothesis generation and a phase of prior assessment of the theory/hypothesis generated. Therefore, we can distinguish three broad, procedural phases of scientific practice: hypothesis generation, hypothesis prior assessment/development, and hypothesis justification/confirmation. The idea behind the phase of prior assessment/hypothesis development is that theories or hypotheses are not generated in the final form in which they are tested (the phase of justification). Theories/hypotheses are subjected to a “period of incubation” (Duhem 1954, 221). In this period of incubation, hypotheses and theories are developed (i.e., the second phase).

Abstracting from the complexities of scientific practice, we can think of discovery strategies as being composed by these three broad phases: hypothesis generation, hypothesis development, and hypothesis confirmation. During the phase of hypothesis generation, scientists construct or build a preliminary hypothesis or model. Such a model will be generated in many different ways, such as from intuitions or by building on previous knowledge. The process of generating a hypothesis has been conceived by some philosophers as irrational (or nonrational) because it is sometimes opaque. The phase of hypothesis development is when the model or hypothesis generated is subjected to modifications because of actual scientific work. While the phase of hypothesis development is often standardized in each scientific discipline according to norms for experiments and topical techniques (inter alia), the phase of hypothesis generation may be seemingly random even within the same discipline. Finally, the phase of confirmation is when a certain model or hypothesis, after it has undergone a great deal of modifications and refinements, is finally considered adequate and detailed enough to be tested.5 This characterization should not be understood as providing an abstract structure to impose on scientific practice, nor does it mean that any discovery episode can be characterized sharply in terms of “first comes generation, then development and finally confirmation.” The process involves reciprocal feedback, and it is iterative.

2.2. The Tripartite Account in Molecular Biology

This tripartite characterization of scientific discovery makes it possible to figure out the contribution of large-scale tools to each phase of scientific discovery and thereby understand the epistemic impact of large-scale biology on molecular biology. Discovery strategies in molecular biology are intimately connected to experimentation, and especially material manipulation. Molecular biologists gather information about phenomena by modifying them, and to modify them one needs to develop standardized techniques to constrain and exploit the internal dynamics of cells, as well as relations between cells.

Molecular biologists are constrained by an experimental system, which is defined as the “integral, locally manageable, functional unit of scientific research” (Rheinberger 1997, S246). An experimental system may be conceived as the particular phenomenon one is investigating, together with the conceptual and experimental apparatus used to grasp its dynamics. Researchers are tightly committed to their selected experimental system: “In analyzing a problem, the biologist is constrained to focus on a fragment of reality, on a piece of the universe which he arbitrarily isolates to define certain of its parameters. In biology, any study thus begins with the choice of a ‘system’” (Jacob 1988, 234).

After the experimental system is chosen, biologists “attack” the epistemic complexity of biological phenomena (i.e., what they have limited access to) by constraining and manipulating the experimental system (both conceptually and materially) in various ways. For this reason, Rheinberger focuses his analysis on the details of epistemic and experimental practices.

Highly complex mechanistic models do not come out of nowhere (i.e., hypothesis generation) and then are tested (i.e., hypothesis justification). In molecular biology, something is established via a system of experiments. Systems of experiments include several types of experiments, from exploratory (Franklin 2005; Waters 2007) to clear-cut theory-driven ones. Even if the system of experiments is complex, we can still identify at least two of the three phases,6 though their relations are quite intricate.

As shown in Boem and Ratti (2016), the discovery process and systems of experiments in molecular biology comprise a sui generis, ramified, and intricate hypothetico-deductive system (HD-system). Systems of experiments in molecular biology usually develop and shape hypotheses about the way a particular phenomenon is produced and maintained. There is an emphasis on causal narratives,7 which is typical of mechanistic models (Glennan 2017). The flow of reasoning is intricate, but we can still use the HD-system to make sense of it. The first step is a general guess about a biological system, such as how it is produced or maintained. This is the phase of hypothesis generation. Here, the experimental system is decomposed into entities and activities that are deemed important for the production or maintenance of the phenomenon under scrutiny (Bechtel and Richardson 2010). This is when we “choose” the experimental system and have expectations from it based on previous research, intuitions, and other items that philosophers of science in the past have labeled as psychological, sociological, or historical. In molecular biology, this is when the laboratory leader, to use Knorr-Cetina’s expression, places bets for future research. However, because these guesses are so broad and general, several and often contrasting predictions may be derived. In order to ascertain which predictions are in accordance with the nature of phenomena, one manipulates the experimental system via experiments (à la Hacking 1983) in order to stimulate it to “reveal” more information. Some initial predictions are discarded, while others are transformed into more precise hypotheses. Some predictions “contribute—through additional information they generate—to shape and refine the hypotheses about the functioning of the experimental systems” (Boem and Ratti 2016, 150). Next, other experiments are repeated to observe reactions of the experimental systems. Then, some hypotheses are further developed and others are discarded. This process continues, virtually, ad libitum: “[t]his is a sort of progressive and ramified (but not-linear) deductive process, developed by poking and prodding experimental systems” (Boem and Ratti 2016, 150).

Therefore, hypothesis generation is the first step toward an intricate composition of experiments leading to a final model. Hypothesis development is the phase that contributes the most to mechanistic models, and it is when systems of experiments are instantiated to develop a hypothesis. One may argue that generation and development are nearly equivalent. However, during hypothesis generation one need not provide strong evidential reasons for a hypothesis or commit to exploring it. It is striking how little evidence about molecular details is required—details are what biologists look for later on in the process. For instance, if previous studies had noticed that a protein, if mutated, disrupts a particular molecular pathway, one might generate a hypothesis simply from this unconstrained observation. However, neither the actual activity of the protein nor the specific way it is mutated (or even how the pathway was disrupted) have been uncovered in detail. This is the gap that biologists try to fill after generating a very general hypothesis about the way the protein is important to make sense of the phenomenon observed. The first guess is the most important—the choice of strategy, such as decomposition/localization (Bechtel and Richardson 2010) or backward/forward chaining and schema instantiation (Craver and Darden 2013), will depend on it. Next, because of the nature of the system and the techniques at our disposal, we modify and manipulate the experimental system accordingly, to stimulate it to reveal more until our initial guess can become more and more precise—until we have an adequately detailed mechanistic description of what the protein does. In the phase of hypothesis development, some reasons must be provided in order to pursue and develop one specific hypothesis rather than another.

2.3. Using the Account to Explore the Epistemic Dimension Between Small Labs and Large-Scale Projects

Having laid out this general picture of how discovery strategies work in molecular biology, we now can investigate how large-scale biology had an impact on the epistemic strategies of small-scale molecular biological labs. Note that we are not exclusively interested in the way knowledge generated by molecular biologists is influenced and constrained by large-scale biology. If we only have the typical notion of epistemic dependence from analytic epistemology (Hardwig 1985), then the knowledge generated by molecular biologists is clearly but uninformatively dependent on the data generated by large-scale projects. Although the natural sciences exemplify this common phenomenon, here we are interested in the extent to which large-scale biology projects dictate to small labs in molecular biology what to do in the three phases of discovery, and thereby constrain the knowledge that they can generate. In other words, we are interested in how large-scale biology channeled the way molecular biological knowledge is generated and developed.

Our hypothesis is that there are two broad possibilities based on the way we have decomposed the context of discovery of molecular biology. First, large-scale biology might facilitate or accelerate the work of autonomous small-scale biology labs, for instance, by providing resources that are used within the phase of hypothesis development. This is the phenomenon of standardization that yields experimental shortcuts. We call these large-scale project facilitators. In this scenario, we claim that labs retain a relative epistemic independence and autonomy, because they are free to choose the starting point of their research (i.e., hypothesis generation). Second, large-scale consortia can provide, in principle, resources not just to pursue and develop hypotheses that small labs independently generate, but rather they provide the hypotheses themselves, together with justificatory reasons to pursue them. This means that small independent labs are not really free to pursue their own hypotheses; there is an (epistemic) authority that decides what is and is not worth pursuing. Ideally, such consortia explicitly provide justificatory reasons to pursue certain hypotheses rather than others. We say that these consortia are epistemically centralizing, because they tend to dictate the very starting point of research strategies.8

To explore these possibilities, we discuss the HGP (section 3), which, in our opinion, exemplifies large-scale facilitator projects. In section 4, we hypothesize that TCGA is an example of an epistemically centralizing project and evaluate the merit of this conjecture by means of computational analysis.

3.1. Criticisms of HGP

Many biologists were fiercely opposed to the HGP for a variety of reasons.

First, the involvement of DOE looked suspicious to many biologists: they did not want to collaborate with physicists who worked for large-scale military projects in the past, and they did not want HGP to become a “program for unemployed bomb-makers” (Mueller-Wille and Rheinberger 2012, 198).

A second reason was that biologists were uneasy with the proposed scale of the project. The project was interpreted as an attempt to turn biology into a “big science” discipline like physics, and this was seen “as a threat to their discipline” (Morange 2020, 342). As Strasser reports, molecular biology was “little science par excellence” (2019, 195), and even if experimental biologists had participated in other centralized and collective efforts before HGP (such as GenBank or the Atlas of Protein Sequence and Structure), their “ethos” (to borrow Strasser’s terminology) was still individualistic. In order to get an idea of this attitude, Strasser lists the concerns raised during a meeting at Rockefeller University in 1979 to discuss the creation of a centralized sequence database. Among the others, molecular biologists were concerned that a centralized facility would resemble too much postwar-big-science-physics facilities, which was in direct opposition with them “taking pride in the smaller scale of their laboratories” (2019, 201). While this episode is not about HGP, it sheds light on the ethos of molecular biologists. It is also interesting to note, as Mueller-Wille and Rheinberger rightly point out (2012), that big science in biology turned out to be quite different from big science projects in physics, “which were typically organized around a very large scientific instrument” (2019, 201). Unlike in physics, big science in biology developed with “patchwork” and distributed character around different “genome centers” (Hilgartner 2017). But independently of the nature of big science in biology, HGP seemed to subtract resources from small, independent labs, which were seen as the real engines of molecular biology. For instance, Davis said that the “human genome initiative is competing with the initiatives of investigators in other areas” (1990, 342). Rechsteiner explicitly noted that “HGP diverts funding from university laboratories to centers, thus having a negative impact on training future scientists” (1991, 455). Weinberg added that this could demotivate investigators from more “traditional” style of research: “[r]unning laboratories focused on small-scale, hypothesis-driven research has become unattractive for many young people” (Weinberg 2010, 678).

A third (and more related to the point we want to make) set of criticisms to HGP has to do with the value of the project itself. For instance, Weinberg suggested that sequencing the genome would not answer any particularly interesting question about human biology: “we may understand less about ourselves at the end of this project than when we began” (Weinberg 1987).14 Davis (1990) was more precise and suggested that it is hard “to see how a complete sequence could be useful for understanding the organization of the huge human genome” (343). Critics saw HGP as “mediocre science” (Rechsteiner 1991, 457) for similar reasons. Moreover, the criticisms concerning the value of HGP reproduced an old and well-known opposition between experimental and collecting efforts. Strasser (2019) characterizes this as an opposition between two “ways of knowing,” and while he convincingly shows that the two ways of knowing have been successfully integrated, still old and recent actors used the opposition as a powerful rhetorical tool. For instance, Rechsteiner said that “the finest science is characterized by (. . .) elegantly designed and competently performed experiments (. . .) HGP is little more than a massive data collecting effort” (1991, 459). As Strasser concisely puts it, collecting and comparing “were often regarded as archaic by experimental biologists” (2019, 214). Even in 2012, Alberts raised similar concerns for another large-scale project (ENCODE): “the grand challenges that remain in attaining a deep understanding of the chemistry of life will require going beyond detailed catalogs” (2012, 1583). The epistemic goals of big science and small science were seen as in tension, rather than complementary.

All these issues (involvement of DOE, concerns about big science and centralized efforts, and criticisms of the scientific value of the project) are eminently cultural, and they affect the perception of the epistemic dimension of HGP. As Knorr-Cetina (1999) shows, the knowledge culture in molecular biology is framed in the epistemic and political authority of the laboratory head, which makes each small lab (somehow) epistemically independent to place bets on research projects as he/she sees fit. Even though the HGP did not turn out to be as centralized as large-scale physics, the attempt to make biology a big science was interpreted as a threat to the independence of small labs. To use the terminology introduced above, some molecular biologists were worried that HGP would become an epistemically centralizing project. In other words, the fear was that DOE or the NIH would set research goals or long-term plans that eventually would involve small labs, threatening their independence by forcing them to follow the lead of large-scale biology. To frame this concerns in terms of our account of discovery in biology, the question is: in which phase of discovery HGP had the major impact? Did it dictate research agendas of small labs by imposing itself in the phase of hypothesis generation (i.e., an epistemically centralizing project), or did it just become one tool among the many in the phase of hypothesis development (i.e., a facilitator project)?

3.2. Real Impact of HGP

The HGP did not, in fact, undermine small-labs’ independence in the way some envisioned. Instead of setting new priorities or research agendas, it facilitated the old gene-hunting agenda of “normal” molecular biology; in other words, it has been a facilitator rather than a centralizer. The HGP merely facilitated and made more efficient what small labs were pursuing independently. Simple examples that reflect common activities in laboratories are easy to find. Having an infrastructure that provides you with the entire sequence of a genome can help you in designing better primers when doing a PCR. “[W]hole-genome sequences are now available for many species. Thus, it is possible in principle to electronically estimate the likely specificity of candidate primer pairs, and one common approach is to search for and then avoid segments of the intended amplification target that are too similar to other sequences” (Untergasser et al. 2012, 2). Having a complete genome sequence aids researchers in designing primers that are more specific to target sequences. A similar example is provided by microarrays, which are instruments to measure the expression of thousands of genes. Microarrays are microscope slides printed with thousands of spots in specific positions. There is a probe attached to each spot that is a sequence of fifty to one hundred base pairs complementary to a selected mRNA. After collecting mRNA molecules from samples, you discover whether they attach via complementary base-pairing to the probe. But microarrays may have tens of thousands of probes; to design them you need to have as much sequence as possible to avoid redundancies and imprecision, which can be done if you have the entire genome sequence.

These and other examples show that the resources provided by the HGP did not undermine the authority and independence of small molecular biology labs. Instead, they facilitated their work. In particular, the HGP offers resources that facilitate hypothesis development, by making existing experimental techniques faster and more efficient. Rather than wasting time in preparing your experimental apparatus, the HGP can help biologists cutting corners (in a good way). The HGP helps molecular biological research be faster and more efficient where biologists want and need it. Rather than using a trial-and-error approach to design primers or probes, the HGP helps you to avoid redundancies. These experimental shortcuts are incredibly useful in the phase of hypothesis development. From this point of view, HGP transform long and painful processes into routine procedures.

But these points were already clear to acute observers back in the 1980s and 1990s. A famous case is Walter Gilbert who, in a piece entitled Towards a Paradigm Shift in Biology (1991), contrasted two ways of attacking problems in biology. The first is to identify a gene by using various techniques, and then try to understand its function by experimental means. But with HGP, all genes “will be known” and “the starting point of a biological investigation will be theoretical [i.e. a theoretical conjecture]” (1991, 99). Therefore, biologists will continue to choose their own starting point and pursue their own interests, and HGP will make this process more efficient: “The actual biology will continue to be done as ‘small science’—depending on individual insight and inspiration to produce new knowledge—but the reagents that the scientist will use will include a knowledge of the primary sequence of the organism, together with a list of all previous deductions from that sequence” (Gilbert 1991, 99). To use our own terminology, hypotheses will be generated independently by small labs, but the way they are developed will be aided by HGP.

Therefore, a project like the HGP did not reshape the priorities of molecular biology or put small laboratories in a position of epistemic inferiority. Instead, it helped them achieve whatever they aimed to achieve. The resources of the HGP (and other large-scale projects in biology) take the form of a map: “a data resource comprehensive, complete, closed-ended – to be used my multiple groups, over a long time, for multiple purposes” (Eddy 2013, 261). The map makes it possible to navigate genome complexity in order to better understand cellular complexity.

4.1. Exploring the Claim

TCGA has the potential of dictating which hypothesis or research question should be pursued: “the viability of a project in small biology would be entirely dependent on the big biology infrastructure and its potential to bring into light promising target from an immense sea of data” (Ratti 2016). To test this hypothesis, we designed a computational analysis to ascertain whether TCGA has in fact been the driving force described in the previous section. Given the cancer genes that we know today, we should observe a peak in their analyses starting in 2008, which is the publication year for TCGA pilot project (Cancer Genome Atlas Research Network 2008). Subsequently, we expect to observe groups using TCGA resources to explore the nature of new cancer genes. It is difficult find informative proxies to test this claim. We contemplated two options.

First, we could analyze when known cancer genes were cited. If TCGA affected the prioritization of cancer genes for small laboratories, some cancer genes should disproportionately appear in the biomedical literature after 2008. Using this approach, we obtained the mapping between publications on PubMed and individual human protein-coding genes from the National Center for Biotechnology Information, and added the publication year as listed in Medline. In parallel, we obtained a list of currently known cancer genes from the Network of Cancer Genes project (Repana et al. 2019). Next, we counted the number of occurrences in publications for each cancer gene within the publications published until the year 2008 (the year of the first publication of TCGA) and between the years 2009 and 2015 (the last year for which bibliometric data is available). Comparing the number of publications in these two time frames, we observed a strong correlation (Figure 19.1, Spearman: 0.88), which suggested that the extent of scholarship on individual cancer genes had changed little after the first publication of TCGA. Notable exceptions to the general trend are IDH1 and IDH2. The role of mutated IDH1 in multiple cancer types was described and popularized between 2006 and 2010 by a series of publications (Sjöblom et al. 2006; Yan et al. 2009; Zhao et al. 2009; Paschka et al. 2010), which included one publication of the TCGA (Verhaak et al. 2010). This finding supports our hypothesis that large-scale efforts can dictate subsequent small-scale research on individual genes, but also demonstrates that these are rare events.

We extended our analysis backward in time to see if scholarship on cancer genes might have been more dynamic in the past by computing the relative contribution of each cancer gene to the literature on human genes in each year. To avoid counting single publications with several genes multiple times, we counted publications containing multiple genes as 1/(number of contained genes) toward the count for each of the contained genes. Finally, we obtained for each five-year observational period the median contribution of each gene, and normalized it with a naive null model in which each human protein-coding gene would be studied equally. We did the normalization by taking the ratio of the observed annual contribution and the contribution anticipated by the naive null model, and subsequently performed a log2-ratio. On this analysis, a value of +1 would indicate that a given cancer gene would be studied twice as much compared to a culture where researchers would randomly publish on individual genes, whereas a value of –1 would indicate that a given cancer gene would be studied half as much. Recapitulating our earlier observation, we see that different cancer genes tend to be studied to a varying extent (Figure 19.2). However, we also observe that 86 percent of the cancer genes have a log2 ratio above 0 in at least one time interval, and 60 percent do so for the most recent time interval. This suggests that, cumulatively, small laboratories study cancer genes more frequently than other genes.

Detailing the temporal changes, we see that only 19 percent of the cancer genes peaked after 2010. Instead, we notice that 61 percent of all cancer genes peaked before the year 2000, with the time span between 1995 and 1999 having been the peak time for the largest amount of cancer genes (26 percent). This demonstrates that the most recent years, which coincided with TCGA, did not lead to a surge of research on cancer genes. Another conclusion that we can draw from this analysis is that most cancer genes were already known prior the completion of the HGP and the start of TCGA, with several known in the 1980s continuing to be among the most studied cancer genes more recently. We suspect that the decreasing contribution of these genes toward the annual literature may be explained by these cancer genes having been identified early on, while only a small subset of human genes had been identified yet; subsequently, they contributed less to the annual literature as new cancer and non-cancer genes were being identified and studied.

The second option for an illuminating proxy to probe the impact of TCGA on research involved restricting ourselves to 223 genes that had been reported and experimentally verified within the first 2008 publication of results by TCGA. These were then tested to see whether they would become more or less studied over time when compared to all other genes (Figure 19.3). Using the same time frames for the number of publications per year, we compared cancer genes against all other genes by ranking genes according to the number of publications; the gene at the 100 percentile corresponds to the gene occurring in the most publications. For both groups, the median percentile of all 223 cancer genes is 92 percent, confirming that cancer genes are already heavily studied when compared to all other genes. However, we did not observe any difference in the ranks when comparing the two time frames (Wilcoxon: 0.49). This, too, suggests that TCGA had a surprisingly small impact on the genes studies in cancer.

4.2. Why TCGA Has Not Been an Epistemically Centralizing Effort

There may be several explanations for why we did not confirm our initial hypothesis. First, a concern could be raised that we did not consider the technological advancements brought forth by projects such as TCGA, and this may be the most important contribution of the project. As Eddy (2013) claimed, there are no “big experiments” in biology; large-scale projects yield both maps and ways of stimulating technological development in a field. In this respect, TCGA’s most important contribution lies in the way it has developed new tools and technology. This is a constant in projects such as HGP or TCGA: “[g]enome research thus generated not only scientific products, but also the means for their production” (Mueller-Wille and Rheinberger 2012, 201). Plutynski (see chap. 18) notices that “there were in fact many different kinds of goals at play in TCGA,” and in addition to scientific goals, “TCGA promoted improvements in speed, accuracy, and lower cost of sequencing” (section 2). Improving sequencing technologies is just another way in which large-scale projects can be “facilitators” by improving the hypothesis development phase for small labs.

Another reason is more empirical. Since the majority of cancer genes were discovered between 1980 and 1999 (and hence before the cancer genomics era), it just turns out that the number of cancer genes is limited and researchers were lucky to discover many of them before the advent of next-generation sequencing. Therefore, we should not expect a sudden increase in the number of cancer genes studied after 2008 because most had already been discovered. According to this hypothesis, TCGA guided small-scale studies, but only for such a small set of cancer genes that it would have been missed by our statistical analysis—or by enabling conceptually distinctive hypotheses that transcend from individual genes. Moreover, we cannot exclude the possibility that overall research on cancer genes might have decreased without TCGA due to competition with other fields of biomedical research. Also, our hypothesis might have been incomplete in regards to TCGA because the disease-relevance of genes is not by itself sufficient to dictate subsequent small-scale studies.20

But our initial hypothesis is not without merit, and it may turn out to be more accurate in the future. As mentioned in the introduction, there are ongoing attempts to undermine small-labs’ autonomy in the way we described. One example is the Illuminating the Druggable Genome Consortium (IDG). This consortium promotes research on rarely studied genes that belong to gene families that are considered to be important and malleable to pharmacological interference. IDG is supported by the Common Fund Program of the NIH and is formed by multiple academic centers and collaborates with the National Center for Advancing Translational Science. Together they follow several strategies. First, they provide information resources (Nguyen et al. 2017). Second, they solicit funding calls for specific genes prioritized by them.21 Third, they engage in community outreach and partner with Nature Reviews Drug Discovery to regularly highlight the genes prioritized by IDG to their readers.22 Another, not yet formalized, example stems from the International Mouse Phenotyping Consortium, a large-scale consortium that mutates mouse genes to monitor mice for phenotypic changes. One of their insights is that many genes that affect the physiology of mice have not been subjected to small-scale studies. Besides publicizing the genes on social media,23 this consortium, and like-minded biomedical researchers, also recently called for a deep-genome project to characterize all human genes and their mouse orthologs in detail (Lloyd et al. 2020). Our analysis framed in the tripartite account of discovery shows a way in which it is possible to monitor how large-scale biology is impacting small-scale biology.

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