Frozen Evolution. Or, that’s not the way it is, Mr. Darwin. A Farewell to Selfish Gene.

Box 26 What is to be done?

I don’t know what is contained in Chernyshevsky’s original What is to be done?, nor in Lenin’s treatise of the same name. Not that I’d wish to brag about it, or to even build my career on it (I’m a veteran opponent to communism – I fearlessly paid no attention in classes of Russian Literature and Marxism-Leninism!). In any case, after a meeting last year of the College Academic Senate, at which a certain formerly high-ranking comrade, now a properly elected member of the Academic Senate lectured me about morals – I even got the impression, that such bragging would bring me harm. The truth is that aside from the contents of the Marxist-Leninist treatises, I unfortunately also forgot most of what was poured into my head in high school and later in college. In any case, I am almost certain that the contents of my box are entirely different from the writings of my more famous predecessors. Here I’d like to deliberate the criteria, according to which it is appropriate to choose a topic for scientific research. Be warned, that this is my purely subjective opinion, which I definitely don’t wish to impose on anyone (although, in years to come, I will be diligently checking the knowledge of said opinion in exams of my course Practical methodology of science!). The main criterion, which I applied always and before anything else, was whether the research question interests me. Our life is too short and (intending no offense to Buddhists) only one, so it is the height of folly to waste it searching for answers to questions that don’t really interest us. Sure, it might be nice to tell yourself and others that we’re able to find the answer to the given question before our competitors, but competition can also be carried out solving interesting questions (and one also attracts more spectators). Secondly, I applied the criterion of the probability that I could solve the given problem. That was related to the difficulty of the project, as well as (first and foremost) to whether I had the necessary materials and prior knowledge to solve the given problem. I’d really be interesting in researching the validity of string theory, but when I see an integral (I’m ashamed to admit it, but even a derivate is enough), I cannot help but shudder. Nor do we momentarily have an appropriate particle accelerator in the department. The third criterion is practical. I don’t think that I exactly need to save or at least nourish a “suffering mankind,” but it would definitively bring me joy, if something useful came of my discovery. The fourth and, admittedly, at once the most important criterion, is that I must enjoy the research of the given topic. I definitely enjoy it more, when I’m inventing ways to find, using an ethological experiment, whether Toxoplasma-infected people are more suspicious, than when I was inventing or rather used trial and error to find how to best separate out virions from homogenized trichomonads cells.

Box 27 Why to model in science, and what can and can’t be modeled

In engineering we model primarily to replace a difficult or expensive study of the behavior of certain systems with a much cheap and easier study of the behavior of their models. Usually we try to make it so that the behavior of our model corresponds as closely as possible with the behavior of the modeled system, and we’re glad when we succeed in this. In science, however, we usually model for a completely different reason. With the help of a model we generally try to show what the mechanism of a certain process isn’t like, and so we’re happy when the behavior of the given model is substantially different from the behavior of the real system. The model is actually the realization of our hypothesis as to what the mechanism of a certain process is like – what elements the given system contains, and what relationships are applied between these elements. When our model behaves differently than we imaged, it means that our hypothesis likely wasn’t true, which means that we have to discard our hypothesis or more often modify it. We’ll embody the new hypothesis in another model, which we’ll again subject to our test. When we discover a model whose behavior corresponds very well with the behavior of the real system, meaning that we observe in it processes analogous to those in the real world, we should actually feel disappointed (usually we aren’t, because men are vain creatures and dislike their proposals being rejected). When the model’s behavior corresponds with that of the system, it signifies that we couldn‘t disprove the given hypothesis, and therefore that the hypothesis could be true. But we won’t be certain, because the same behavior can produce many very different models.

Modeling is a tremendously powerful tool. It enables us to quickly and cheaply refute (more accurately, to make improbable) a large number of hypotheses, and thus to concentrate on testing those more likely to succeed. Additionally, creating models allows us to specify and elaborate our often somewhat vague hypotheses. An intuitive visualization, that something should work like this and this, achieves a defined outline only after conversion into a mathematical or numerical model; and often we still have to alter it during the very creation of the model (frequently we must decide on very significant details, which we didn’t tackle during the verbal construction of our hypothesis). For example, in my book Frozen Evolution: Or, that’s not the way it is, Mr. Darwin, I expressed the hypothesis that sexually reproducing species with an inability to fit the model of natural selection may have a paradoxical advantage in quickly changing environments. Evolutionarily plastic asexually-reproducing species are in danger of opportunistically adapting to a short-term variation in environmental conditions, and after a return of the conditions to normal, they won’t manage to adapt to the original conditions quickly enough, thus dying out. Precisely this could be the reason why most known species reproduce sexually. Only during the modeling, which was conducted by Petr Ponížil, did it become apparent that I must decide whether plastic and non-plastic species compete directly for a common resource, or whether they just coexist independently. The results consequently showed that apparently only in the second case could the evolutionarily non-plastic species win over the plastic species. They also showed that it is more advantageous for the success of the non-plastic species when the changes in environment are cyclical (this I did not expect); and that jump changes are more favorable than continuous changes for the success of the non-plastic species (this I expected, but it pleased me anyway).

We can model any process (phenomenon, property). One must realize, however, that we never model an object or system, but always only the certain specific behavior of the given object or system. The command “Model the watch!” is nonsensical – it isn’t clear, whether we’re supposed to model how the watch will behave after a crash from a speed of 200 km/h into a brick wall, or after being placed into 70% sulfuric acid, or whether we just want to know why its hands tick regularly. All of the mentioned processes would require completely different models. Technically, we can study the behavior of mathematical models, either analytical or numerical or perhaps even mechanical models (for example in aerodynamic or hydrodynamic testing). In science the mathematical models are most applicable, and for a biologist, whose qualification prerequisites almost inherently include mathematical illiteracy, numerical modeling it is useful above all. Modern computers and modern programming resources are immensely powerful and allow even modeling amateurs to model. Nevertheless, to this end I’d recommend to taking up cooperation with a professional. Modeling on your own harbors one serious hazard – it’s addictive.

Box 28 How to measure the quality of science

It’s hard. The value of a scientific discovery is usually seen only in retrospect, and just for an individual discovery it’s often difficult to determine who contributed to what extent. The quality of science produced by certain researchers, by a certain research team or institution, can be weighed based on the examination of individual scientific papers, the response to these papers and the scientific reputation of the researchers (according to awards received, invitations to be a plenary speaker in conferences, and so on). But such individual evaluation is pretty demanding and in the conditions of a medium-sized country would require the formation of an international team of evaluators. On the other hand, this approach would be hardly objective. For example, in our small Czech pond we all know each other too well, and personal ties would likely have a greater effect on the evaluation than did the objective quality of the study. In most cases we must therefore rely on auxiliary, indirect criteria, which we take to at least approximately reflect the quality and quantity of the research. A simple criterion is the number of publications, which the evaluated scientist (team) produced in a certain period. Another indirect measure reflecting the quality of research is the number of references of the article of the given author in the articles of other authors. This value reflects, above all, the author’s age (this can be avoided by counting only the references of articles published in a particular time period); as well as the extent of his social network (this cannot be helped, but it is questionable, whether it would even be desirable); and finally the significance of the published papers for other authors – nobody would reference unimportant works (unfortunately, they would reference erroneous ones, albeit in a negative context, but we wouldn’t differentiate this during the evaluation). When evaluating the number of publications it is possible and fitting to take into account also the quality of the journals in which the papers were published. A simple criterion of the quality of a journal is its JIF, or Journal Impact Factor, the impact which is the average number of references to one article within its first two years of publication. Of course, in individual fields there are different procedures for referring resources; so basically one can’t compare the quality of journals nor certainly of researchers from different fields; but that isn’t necessary very often. Today the most popular indirect measure of the quality of a researcher is likely the Hirsch index (h-index). We obtain it by ordering the papers a scientist published in a given time period, from most referenced to least referenced. We determine the h-index as the number of papers h cited at least h-times. An h-index of 20 was achieved by a researcher who, in a given time period, published 20 papers, each of which was referenced at least twenty times. An advantage of the Hirsh index is that it is little affected when an author references his own publications in his other papers (auto-reference) or when, among many low quality papers, he somehow manages to publish one high quality, or rather highly referenced, paper. Nevertheless, a highly referenced and scientifically valuable paper doesn’t have to be one and the same. For example, my most referenced article is a study describing a computer program for molecular phylogenetics. The program is definitely useful – for this reason others use it and reference the article – but the scientific value of the article is relatively low. Indirect measures for evaluating science, offered to us by today’s scientometrics (a field which pursues the measuring of scientific quality), are imperfect, but we have no better ones, so thank goodness we have at least these.

Box 29 Planning and preparing experiments

The most important part of a research project is its preparation. One must first resolve what he actually wants to determine during his study, or what question he wants to answer. We’re dealing with perhaps the most important phase of project preparation, during which the researcher must decide whether the given question is even worth being pursued, whether there isn’t already a known answer and whether he is the right person to pursue it. Always in this phase it’s necessary to conduct a thorough literature review, to find what’s already been written about the given topic. In the next preparatory phase one must choose an appropriate method for answering the given question and plan out the project, making clear when and where the study will be carried out, as well as who will work on it and how. The project must address not only how the data will collected, but also how they will subsequently be pre-processed (what will be done, for example, about missing or outlying values) and how the pre-processed data will be assessed. It is an unforgivable error, which can definitely come back to bite you, if during the project preparation you don’t decide ahead of time how specifically you’ll evaluate the data. For it can easily happen that we neglect to record some important information and finally won’t be able to correctly evaluate the data. Next is the phase of the project’s technical preparation, which involves procuring all the necessary material, learning to work with the equipment and preparing the protocols. The protocols contain tables used to record data during the experiment, and are prepared ahead of time by the researcher; afterwards he records the actual progress of the research in his laboratory notebook, whether it’s a paper or an electronic lab notebook, e.g. an Excel or Open Office spreadsheet. The latter is easier to navigate, namely in the case that one is working on multiple projects – using an automatic filter he can easily control all the recorded data related to a particular project. For a more complicated project it is often appropriate to first carry out a pilot study and test whether it’s possible to carry out the project as planned originally, or whether it’s necessary to modify or entirely scrap our plans – as would happen, for example, if we found using a study power analysis that the studied effect is so weak that to prove it we’d require too many experimental animals. What follows is carrying out the actual study, pre-evaluating and controlling the obtained data and finally evaluating the data. For more complicated studies the pre-evaluation and evaluation of the data often involves as much or even more work than taken up by the experiment itself. Usually it’s also the most challenging phase for the expertise of the respective scientists.

Box 30 Animal Testing

Unfortunately, biomedical research can never entirely do without animal experiments. Moreover it often cannot even do without testing on humans. If the effectiveness of a new drug or medical procedure is to be verified, it is clear that eventually there must come the phase of testing on human volunteers. Some animal testing can be replaced by testing on tissue cultures (if we want to know how a certain substance or physical factor influences the viability of individual cells). In most cases we have to conduct the experiment on animals in the end anyway, because there exist many factors which have an entirely different effect on the functioning of cells and the functioning of multicellular organisms. In the same way, it is not possible to replace an animal experiment with a mathematical model. The model can only serve a didactical purpose – using the model we can “painlessly,” inexpensively and quickly demonstrate to students the course of certain processes. The model can also sometimes reveal that conducting a certain experiment is useless, that the pursued effect is so weak that we basically cannot prove it in the laboratory. In some cases it is possible to replace an experiment with observation in the wild. There it’s not necessary to infect reindeer with Echinococcus tapeworms and observe whether the infected individuals become the prey of wolves; it’s enough, using a suitable serological technique, to find what percent of the reindeer in a normal population and what percent of reindeer that become wolf prey are infected. During animal testing, even with the best intent, we cannot avoid more or less harming them. That we’re doing it in the interest of science or mankind, and that it was approved by the respective Institutional for Animal Care and Use Committee, may be an extenuating circumstance, but it doesn‘t diminish the guilt. As my colleague Jan Zrzavý says, science cannot do without animal testing, but those who do that testing, should perhaps know that they’ll finish in the fiery pits of hell. Before any experiment, one must deeply consider whether its possible outcome is important enough to justify our carrying it out; whether it really enables us to obtain the expected results; whether there exists another way to obtain them; what is the smallest number of animals we must include; and how to minimalize the animals’ suffering.