Abstract
Scientists currently strive to obtain reliable data on the properties of astrocytes in situ, and pari passu to define what the term astrocyte should encompass. As is the current fashion, they are also required to propose in a formal sense hypotheses for astrocytic function that serve as guides for such research. It has become the fashion to raise up “hypothesis-driven” science and denigrate descriptive science that lacks this formal introduction as merely cataloguing. Terms such as “fishing expedition” are often used pejoratively to describe scientific studies that are viewed as simply collecting data with no end in view. This seems as though it would be rather rare and would anyway describe the efforts of a rather inexperienced angler who does not have sufficient experience and skill to determine the types of fish that are likely to be caught where he or she is planning to fish.
There is no dispute as to whether the postulation of hypotheses will lead to experiments. The real question, however, is whether always starting with hypotheses leads to more discoveries and a better-organized, more reliable database. To be consistent, this would have to be resolved scientifically; to test this hypothesis in the usual carefully controlled fashion with defined measures of whether so called hypothesis-driven science provides better data or more insights than so called non—hypothesis-driven science. It would be a simple exercise for the research professional to restate this question in the form of a hypothesis and develop a research plan to address it. To put it into practice, however, will rapidly lead to complications. For example, we would first need to define what non—hypothesis-driven science actually is and how it differs from the hypothesis-driven science.
The lack of a formal hypothesis does not mean there is not some end in view. It may simply be that in the hypothesis-driven variety we take a positive view that we can guess pretty well what the mechanism or relation is, whereas in the latter case, we leave the question open and will come to this later because we believe we don't have enough data to form a sensible hypothesis. I would hope that an individual scientist's opinion, as an expert in his or her field on this issue, would be respected and not dismissed out of hand. You obviously need a background of reliable observations (that is, facts) to propose a hypothesis, and it may well not be clear to another observer when you are ready to propose it. The criticism on a case-by-case basis would be that any reasonable scientist, given the state of knowledge, should be able to come up with a reasonable hypothesis for the area of study under question. This is, in practice, unpredictable and when successful is referred to as scientific intuition. I will assume that everyone agrees that randomly obtained data, however reliable, with no question in mind (although by chance it may come up with important data leading to insights) is not acceptable because it is simply too much of a gamble, and this leaves one very uncomfortable.
The two astrocyte-related hypotheses that I will cover to illustrate the problems of this common current practice are as follows: 1) that glucose enters the CNS via the astrocytic processes where it is converted by aerobic glycolysis to lactate which then serves as the principle source of energy for neurons (Magistretti et al., 1994;Pellerin and Magistretti, 2003;Voutsinos-Porche et al., 2003), and 2) that the processes of astrocytes that surround blood vessels at the levels of the arterioles affect smooth muscle contractility and therefore blood flow by releasing vasoactive agents. (Anderson and Nedergaard, 2003;Simard et al., 2003;Zonta et al., 2002).
In a recent commentary regarding their well-known astrocyte-neuron lactate shuttle hypothesis (ANLSH), Pellerin and Magistretti (2003) write, “The important point here is not so much to decide, based upon the actual pieces of evidence, whether an hypothesis is right or wrong but rather to point out what is heuristically valid in it, what we have learned, what remains to be assessed, what new hypotheses can be proposed, and which experiments are critical for this.” An alternative viewpoint was written some 330 years ago by Isaac Newton: “For the best and safest method of philosophizing seems to be, first to enquire diligently into the properties of things, and establishing those properties by experiments and then proceed more slowly to hypotheses for explanations of them. For hypotheses should be subservient only in explaining the properties of things, but not answered in determining them; unless so far as they may furnish experiments. For if the possibility of hypotheses is to be the test of truth and reality of things, I see not how certainty can be obtained in any science” (Christianson, 1984).
Now, Newton was responding to criticisms by Ignance Gaston Pardies, a French Jesuit and professor of Rhetoric at the Collège de Louis-le-Grand in Paris, of Newton's work with prisms that demonstrated that the simplest explanation of the well-known visible spectrum is that white light is a mixture of primary colors with different refractions. This is clearly a hypothesis in the best sense of the term that has been raised to the rank of a theory because it has been repeatedly shown to be a valid explanation of all sorts of optical phenomena, with now, of course, a much deeper understanding of what is going on. This is very different from the astrocyte-neuron lactate shuttle hypothesis where things are very much up in the air, as Pellerin and Magistretti do point out.
But the question that I am addressing is why there is a modern insistence on the supremacy of hypotheses compared with Newton consigning them to a subsidiary role. Has the philosophical basis of the scientific method changed? Clearly the astrocyte-neuron lactate shuttle hypothesis arose from previous work. Pellerin and Magistretti thought these were sufficient to codify them into an hypothesis in 1994. But why did they propose a hypothesis? Did it help their thinking? If so, then it was a personal tool that did not need publicizing at that time when the evidence was (and still is) inconclusive. Did it lead to more experiments? Indeed yes, so for this aspect of Newton's statement it was a good thing. But the authors could simply have said we need to know more about how glucose is handled by the brain. It has to enter from the blood and will therefore first encounter an astrocytic process, so we will study how glucose is handled by astrocytes. Wouldn't the result be the same? The point I would like to make is that hypotheses tend to lock us into an either/or situation. This is the concern of the quote from Pellerin and Magistretti. Namely, that their hypothesis was never intended to be either/or. However, readers will tend to accept the hypothesis as stated without the caveats. After all, if there are caveats, then it is not a very precise hypothesis and is difficult to refute experimentally, which, as Karl Popper has pointed out, is logically all you can do with hypotheses anyway (Lindh, 1993).
So why hypotheses? They can definitely suggest new experiments, often clarify thinking, and make easy targets for grant reviews. However, Newton said that they should not determine anything, and this is particularly so for the merit of any proposed research whose usefulness can, a priori, only be guessed at. Hypotheses also clarify, as Newton fully realized: “And therefore because I have observed the heads of some great virtuoso's to run much upon Hypotheses, as if my discourses wanted an Hypothesis to explain them by, & found, that some when I could not make them take my meaning when I spake of the nature of light & colors abstractly, have readily apprehended it when I illustrated my Discourse by an Hypothesis” (Christianson, 1984).
The underlying observation for both hypotheses 1 and 2, which have been known since the times of Golgi (1885) and Ramón y Cajal (1913), is that the blood vessels in the central nervous system are surrounded by astrocytic processes, and we now know that this can be close to 100% (Virgintino et al., 1997). This fundamental fact has given rise to many hypotheses, ranging from development of the blood-brain barrier because of signals derived from the astrocytes as the central nervous system develops to the ASLNH hypothesis. It seems that all material that does not diffuse between the astrocytic processes will have to pass through the thin astrocytic processes or diffuse through the entire astrocyte. Now the spaces between the astrocytic processes are of the order of a few hundreds of angstroms wide. They could still form a major short circuit path as the membranes would be a major resistance pathway for polar substances unless there are sufficient carriers on the astrocytic processes, such as the Glu-1 carrier. There is also the question of why there are a high density of high affinity Glu-3 transporters on neuronal membranes (Leino et al., 1997) if the sequence is as follows:
Pellerin and Magistretti (2003) point out that this sequence is not obligatory, and parallel pathways can coexist, but then it will be very difficult to test this hypothesis because there are no limits to the degree to which deviations may be explained away.
The proximity of astrocytic processes surrounding blood vessels also suggests a role in the control of blood flow (Anderson and Nedergaard, 2003;Zonta et al., 2002). For this, it is necessary for the control to be exerted at the level of the arterioles because the capillaries lack the smooth muscle needed to cause contraction or relaxation to change the blood vessel diameter (Edvinsson et al., 1993;Traystman 1997). Note here that there must always be some basic tone to keep the arterioles at an intermediate diameter from which they can constrict or relax (Traystman, 1997). This hypothesis seems to be on firmer ground than the ASNLH. Indeed, Mulligan and MacVicar (2004) reported that Ca2+ in perivascular astrocyte processes leads to constriction of contiguous small arterioles via release of arachidonic acid. The astrocytic ensheathment of central nervous system blood vessels originates as blood vessels penetrate the brain parenchyma early in development from the arachnoid to the brain parenchyma and carry with them the glia limitans that are astrocytic processes. Interactions between the astrocytic sheath and the vascular endothelial cells are thought to be responsible for the formation of the interendothelial tight junctions that form the blood-brain barrier, which occurs at around the end of the first trimester in man (Abbott, 2002). However, if the role of the astrocyte is purely developmental, then why does the vascular ensheathment persist through adulthood? Presumably, they are then converted to physiologic roles or a constant astrocytic influence is needed to maintain the blood-brain barrier. Clearly, the former can be the ASLNH (Magistretti et al., 1994), pH control (Tschirgi, 1958), control of ingress of compounds such as glucose and amino acids or egress of waste metabolites (Pardridge, 1997), and control of [K+]o and blood flow (Newman, 1987;Zonta et al, 2002).
These theoretical possibilities need to devolve into specific testable proposals that can be labeled as hypotheses, for the sine qua non of hypotheses, whether you are not too enamored of them or you cannot work without them, is that they have to be testable and that means in a direct and relevant manner and system. Evidence that there are the right lactate transporters (Allaman et al., 2000;Pellerin et al., 1998) is clearly only circumstantial and also needs to be shown in situ. Although cyclooxygenase-dependent products have been shown to be involved in vascular dilation in slices when astrocytes are directly stimulated (Zonta et al., 2002), there is no evidence that either COX1 or 2 are present in astrocytes in situ (Hoozemans et al., 2001). However, there are alternative pathways by which the astrocytic endfeet can influence the arterioles and the cyclooxygenase may be located elsewhere with the astrocytic influence being indirect, to explain the findings of Zonta et al. (2002).
In general, evidence is very weak or perhaps even misleading when it only derives from astrocyte cultures. Differences in activities and protein profiles have been shown for primary astrocyte cultures as compared with freshly isolated GFAP(+) astrocytes (Kimelberg et al., 1997), or for Muller cells with increasing time in culture (Hauck et al., 2003). Thus it is a major weakness when both the original ASLNH hypothesis and the recent detailed rebuttal (Chih and Roberts, 2003) both use data for astrocytic and neuronal cultures to support and refute. The expression of the genome is plastic and influenced to a major degree by changes in the cellular environments via surface receptors (Peng et al., 1998). The latter follows logically from modern understanding of the biology of gene expression.
Hypothetically, one reason why astrocytes may be developmentally retained to modulate arteriole diameter and therefore blood flow to respond to the varying energy needs of changes in brain activity is illustrated in Fig. 1. One should acknowledge, however, that this is only one possible hypothesis among many that can be proposed. Astrocytes are known to have a variety of receptors in situ as well as in vitro (Kimelberg, 1988, 1995;Porter and McCarthy, 1997) that can then integrate messages from neurons in the form of released transmitters so that the results of a wide range of different brain activities can be integrated and relayed to the blood vessels. In terms of the restraint, I propose that this is a good example of a reasonable hypothesis that one would have trouble supporting meaningfully. The existence of several receptors subtypes on freshly isolated astrocytes (Zhu and Kimelberg, 2004) is clearly consistent but not in any meaningful way because there could be numerous reasons for this coexistence. One possible approach that comes to mind is to determine whether the perivascular astrocytes are a specific subtype that can be specifically manipulated to see if it affects blood flow response to brain activity. This assumes the conclusion, as do all hypotheses, that there are vascular specific types, and this should be a doable task. After this is achieved, then one could talk about specific manipulation. It is not clear if all astrocytes have processes that surround blood vessels, although there is current evidence for the functional heterogeneity of astrocytes (Nedergaard et al., 2003;Zhou and Kimelberg, 2001). Note, though, that the demonstration of a specific perivascular astrocyte would have important implications for the ANLSH, as well as a host of other possible hypotheses. So, again, why can't we state that our objective is to look for this cell? Then, the discussion would be only about whether proposed methods are likely to be successful, which is less a matter of opinion than the worth of some hypothesis.
Models comparing the hypothetical control of arteriolar diameter directly by individual neurons (A), with integration of inputs from different neurons through the perivascular astrocytic end feet (B). (A) The integration would be at the level of the arteriole or more strictly the smooth muscle cell, which would then have to integrate the different direct neuronal inputs. (B) The astrocyte acts as the integrator that translates the neuronal inputs for its receptors into an appropriate transmitter output for contraction or relaxation (black arrow). There is no obvious structure additional to the smooth muscle within the blood vessel that can serve this integrator role.
Direct evidence in situ is lacking for the ASNLH. The 1:1 relation between glucose uptake and glutamate turnover (Sibson et al., 1998) is consistent with a number of possible models and therefore is not definitive because other scenarios can be proposed to explain this relationship (Chih and Roberts, 2003). However, definitive tests of hypotheses regarding processes in organisms need to be obtained in vivo and that is why genetic knockouts are increasingly used. Such manipulations will need to be astrocyte-specific and possibly astrocytic subtype-specific, such as for the putative perivascular astrocyte just discussed. Thus the relation shown in Fig. 1 may only apply to a subgroup of astrocytes. Knockout experiments could be designed to see if 1) the elimination of the perivascular astrocytic glucose transporter essentially starves neurons, and 2) if, after knockout of astrocytic COX enzymes, the brain loses blood flow regulation. It will needed to be assessed if the knockouts are specific enough and then to see if the results are amenable of a clear interpretation. As always, it is better to conduct some pilot experiments, but, because of their complexity and the time needed to generate the animals, knockouts are not traditional pilot experiments.
A hypothesis is only the first step in a laborious scientific investigation. Thus, as Newton wrote, hypotheses are a guide for experiments, but perhaps to be consistent with the scientific method we need only the publication of hypotheses supported by data. However, supporting data for the ANSLH are almost exclusively experiments with primary GFAP(+) astrocyte cultures. Because these cells have active glutamate transporters and, of course, the ubiquitous Na pump, the cells will naturally take up glutamate with Na, the intracellular accumulation of which then conventionally activates the pump. There will then be an increased uptake of glucose and, being adapted to a limited supply of oxygen, relative to consumption, through unstirred layers, the monolayer cultures are likely to mainly metabolize the glucose glycolytically with lactate production. The question is whether this occurs under the conditions that normally pertain in vivo. The ANLSH seems prima facie a reasonable hypothesis because it gives reasons for the persistence of astrocyte processes around all the blood vessels—the key finding—as well as other features. On one hand, we have a role for astrocytes in integrating signals from a diversity of neurons via receptors to balance blood flow to activity (Fig. 1), and, on the other hand, we set forth that a signal of increased activity, namely glutamate, can signal the astrocyte to increase uptake of glucose from the blood and convert this to substrate for the neurons in the form of lactate in a simple servo-feedback type mechanism. However, the evidence for this is inconsistent, if not in opposition, and the data fit other scenarios as has recently been put forward in considerable detail (Chih and Roberts, 2003).
The need for a hypothesis is that thinking about why we are doing particular measurements in terms of how they advance understanding is the most important aspect. Here is where the need for a hypothesis is advanced as necessary: to avoid indiscriminate collection of data with no end in mind, to force the scientist to have an end, and clarify for others what that end is. However, I hope I have pointed out that hypotheses only illustrate what one is driving toward. They do not determine that one is on the right track, and insisting upon them as a prerequisite to any proposed scientific investigation means that areas in which there is insufficient information to propose any sensible hypothesis will not be investigated or only investigated clandestinely. Looking at history, we see that it is not only not how major discoveries in the biological science have been made, but the proposal of hypotheses depends upon data in the inductive scientific method pioneered by Isaac Newton and which is the same method as we use today (Feynman, 1965). What if the existent data seems insufficient to an individual investigator to propose a sensible hypothesis? It then becomes a matter of opinion, which will be decided first by one's peers and then by history. A not entirely satisfactory system but perhaps, like democracy, better than any others one can think of.
It would be useful for the modern experimental biological sciences if this intellectual straight-jacket was recognized for what it is: simply a useful but easily disposed of intellectual technique. Then we would not get into these unending either/or arguments. The question of what mechanisms are subserved by the astrocytic processes that persist around the CNS blood vessels, and also the astrocytic processes that surround synapses (Araque et al., 1999), are critical ones that beg for answers. After sufficient data have been obtained to suggest a plausible mechanism, which as discussed above is a matter of opinion, the essence of the scientific method is that we test the implications of these mechanisms to see if they correspond with reality (Feynman, 1965). These tests have to be specific in that no reasonable alternative mechanism should lead to the same phenomena. One must test the actual hypothesis directly: if one is talking about how astrocytes behave in the brain, the tests must be performed in the brain. Reductionism in the sense of using simpler and more experimentally tractable systems can only be suggestive and are in the final analysis not compelling. Thus after Kuffler et al. (1966) usefully used the simple leech nervous system and then the amphibian optic nerve to show that glial cells were actually high K+ cells and their membranes showed selective K+ currents, rather than high Na cells that functioned as the extracellular space of the brain (Grossman, 1972), a number of studies addressed themselves to whether the same properties translated to mammalian glia and specifically astroglia (Somjen, 1975). These investigations are still ongoing because the ion channels of astrocyte membranes are more complex than indicated in the earlier electrophysiologic experiments (Barres et al., 1990;Sontheimer, 1995;Verkhratsky and Steinhauser, 2000).