The Hyponatremia of Exercise, Part 3

ByProf. Timothy NoakesMarch 19, 2019

The heatstroke paper by my South African colleagues, Professors Cyril Wyndham and Nic Strydom, became one of the most influential in the history of the sports sciences, as previously discussed in the second post in this series (1). Wyndman and Strydom’s conclusions became what we call “foundation beliefs.” They also provided the basis for the Position Stands, produced by the American College of Sports Medicine (ACSM) in 1987 (2) and 1996 (3), which introduced entirely novel drinking guidelines to the athletic world.

For the first time in human history, these Position Stands mandated specific goals for how much athletes should drink during exercise—all based on the idea that humans are not designed to become dehydrated during exercise. Until this point, athletes usually drank when they felt like it; that is, in response to the unconscious biological controls that determine our thirst.

Unwittingly, the Wyndham and Strydom study also created two new and untested concepts as human biological “truths”: first, that humans have no capacity to resist the biological effects of dehydration; and second, that humans cannot rely on their thirst mechanisms to dictate how much they should drink during exercise, and perhaps by extension, also when they are not exercising.

These concepts were introduced by stealth. Neither Wyndham nor Strydom likely would have argued for these interpretations. But the reality is that this is exactly what happened.

These novel ideas also would decisively assist the global marketing of a novel product, the sports drink that had been “invented” by Dr. Robert Cade at the University of Florida less than four years earlier.

This introduces another great lesson: When we accept new evidence that radically changes what we have done in the past, we need to be sure the evidence actually supports the conclusion and be cautious when the evidence appears to introduce a new interpretation of how human biology works. In other words, we should be skeptical when the new idea conflicts with what is well-established about our human biology. In the end, biology always wins out. As British physician and author John Le Fanu says, “[B]iology does not readjust to accommodate the false theories of scientists” (4).

In the words of Thomas Sowell, “Much of the social history of the Western world, over the past three decades, has been a history of replacing what worked with what sounded good” (5).

Wyndham and Strydom’s study produced just such a moment in the sports sciences. With the adoption of the two “truths” interpreted from their study, we replaced what had worked for generations with something that, at the time, just sounded really, really good. As I will show, seldom has such a good idea produced such a bad outcome.

How, then, do we begin to distinguish the “science” we should believe from that which just sounds like a really good idea at the time? The goal of this column is to address that question.

The Different Levels of Scientific Evidence

Perhaps the most important function of science is to answer the simple question: Are two phenomena causally related? That is, does factor A directly cause the observed phenomenon B (Figure 1, top image). Or is it possible that both are dependent on a third factor that influences both A and B (Figure 1, bottom image)?

Figure 1 — Top image: It is often assumed that two events (A and B) that occur at the same time or in close proximity must be causally linked. But it is always possible that this relationship is spurious and could be explained by a third factor C that determines both A and B (bottom image). In this case, the causal relationship is between C and A and C and B, not between A and B.

To distinguish between these possibilities, scientists (usually) grade the quality of the scientific evidence they must evaluate according to an established scale (Table 1). The more rigorous the experimental design, the more credence we give to its findings since better designed studies are more likely to detect truly causal relationships. In contrast, experimental designs that receive a lower grading are more likely to identify relationships that could be explained either by chance or because they are spurious and due to a third factor that is unrecognized and hence not controlled in that study (Figure 1, bottom image).

Table 1: A scale to grade the relative validity of different experimental designs

Grade	Type of Experiment	Description
1	Anecdote	An opinion. The perceived validity of the anecdote usually relates to the perceived status of the person expressing the opinion. Thus, an anecdote told by a professor has greater validity than one expressed by a student.
2	Case report	Describes the characteristics present in a single individual. There is no control group.
3	Case series	Describes the characteristics of a group of subjects or patients with a common condition. There is no control group, although the characteristics of the group may be compared to those of other groups described in the literature.
4	Cross-sectional study / Descriptive laboratory study	Observations of a defined population at a single point in time. The presumption is that the outcome is determined only by the variables of interest that are measured. There is no control group.
5	Case control study	Comparison of the characteristics of one group of patients or subjects who have a particular condition of interest with another group of individuals who do not have that specific condition. The presumption is that the unique characteristics present in either group and not present in the other group may explain the cause of the condition of interest.
6	Cohort study	Involves the treatment of only one of two groups of patients or subjects. Both groups are followed to determine the outcome of the treatment in the treated group. Since the groups may not be the same at the start of the experiment, it cannot be determined that any difference in outcome is purely the result of the treatment.
7	Controlled laboratory study	The responses of one group receiving an experimental intervention under tightly controlled laboratory conditions are compared to those of a control group that undergoes the identical experiment but without receiving the specific experimental intervention of interest. As is the case with a cohort study, the groups may not be the same at the start of the experiment. Thus, any difference in outcome may be influenced by the nature of the inherent differences that were present between the groups at the start of the experiment.
8	Crossover study design	A group of subjects or patients is randomized (divided) into an experimental group and a control group so that at the start of the experiment, all characteristics of the two groups are essentially identical; that is, the groups are matched for all personal and other characteristics considered important by the researchers. Only the experimental group is exposed to the experimental intervention. The measurements of interest are continued in both groups as they are followed for varying time periods.
9	Randomized controlled prospective clinical trial	A group of subjects or patients is randomized (divided) into an experimental group and a control group so that at the start of the experiment, all characteristics of the two groups are essentially identical; that is, the groups are matched for all personal and other characteristics considered important by the researchers. Only the experimental group is exposed to the experimental intervention. The measurements of interest are continued in both groups as they are followed for varying time periods.
10	Systematic review	A review of all the published material on a clearly defined subject, conducted in a systematic way.
11	Meta-analysis	A quantitative analysis of all review studies previously published on a particular topic. It seeks to provide a numerical measure to a particular question: for example, the efficacy of a treatment or procedure, or the strength of an association between two variables.

Based in part on the study types identified by Bruce Reider (6).

Anecdotes: Their Power and Limitations

As presented above, the simplest form of evidence is known as an anecdote, wherein an individual expresses his or her opinion of what is the “truth.” A typical example might be a statement such as: “The reason why I ran so well was because I drank so much (or because I did not drink at all) during today’s marathon.”

Of course, either proposition might be correct, but one person’s opinion that this is the case is not sufficient evidence that this opinion is in fact a “truth” that can be generalized to all other humans in all possible circumstances.

However, each person’s experience or “truth” is intensely powerful and will determine how each interprets and responds to the world. In a real sense, we are each an “experiment of one.”

Thus, the athlete who believes that drinking during exercise improves her performance will perform better when she drinks and less well if she is denied access to fluids during exercise. This will happen regardless of whether the value of drinking has been established beyond doubt in properly controlled scientific studies that fulfill all the criteria listed in Table 1.

The key to the response is that the outcome usually will be that which the athlete believes it will be — the classic placebo effect (7).

This placebo effect is immensely powerful, even if it remains poorly understood. I would say it is so powerful that if one does not “believe” in an outcome then it becomes increasingly unlikely that that outcome ever will eventualize. I was privileged to present a lecture on belief and sporting outcomes at the 2017 CrossFit Games Scientific Symposium in Madison, Wisconsin (8).

Much of scientific inquiry begins with an anecdote. My personal interest in the possible dangers of over-drinking during exercise — and thus the origins of my book Waterlogged (9) and these columns — stemmed from the letter I received in June 1981 (10), which described the world’s first case (11) of what would become known as Exercise-Associated Hyponatremic Encephalopathy (EAHE).

This form of anecdote is known as a case report. A series of anecdotes can form a case series (11). A case series can produce a powerful indication of what might be the truth, but it cannot establish “truth,” as each case is merely an untested anecdotal observation. To begin the journey toward truth, a superior experimental design is needed to test any hypotheses (theories) the case series suggests.

Claude Bernard, known as the father of the modern experimental physiology, described the phenomenon thus: “To reason experimentally, we must first have an idea and afterwards induce or produce facts, i.e., observations to control our preconceived idea” (12).

When faced with an anecdote, the true scientist asks: What hypothesis does this anecdote suggest, and is there any published scientific evidence that tests that hypothesis? If there is none, the scientist can design an appropriate experiment of the appropriate grading that will begin the scientific process.

The next level of evidence comes from cross-sectional or observational studies. In this study design, a snapshot is taken at one moment of a particular phenomenon, and then associations are sought between some or all the data collected in the course of the experiment.

The Wyndham and Strydom study is a classic example of a cross-sectional, observational study in which no attempt was made to control any variable other than the distance the athletes ran.

As an example, these races were run in 1968 before the introduction of accurate measurement of running distances. Thus, one would predict that the race distance was not actually 21.5 miles as the authors reported but could have been any distance from 19 to 21 miles, for instance. If the three races were not run on exactly the same course, then it is highly improbable that both would have been the same distance.

In Wyndham and Strydom’s observational studies (not “experiments” since there was no control group), the runners ran a set distance at their own chosen paces in uncontrolled environmental conditions when drinking at their own freely chosen rates. The attraction of such observational studies (as I well know because I kicked off my scientific career doing such studies (13)) is that they are highly cost-effective. This is because the athletes are studied all at the same time whilst doing that which they would have done anyway, which provides a cheap, quick, and highly effective method to make observations from which an initial hypothesis can be developed. That hypothesis then can be tested by the much more robust experimental method: the randomized, controlled, prospective clinical trial (RCT).

Wyndham and Strydom’s error, shared by all who became rather slavish devotees of the particular “truth” they believed Wyndham and Strydom had discovered, was to miss a vital step on the road to scientific truth. They had allowed the establishment of a “truth” from an observational study. But observational studies can only ever generate hypotheses, not definitive truths. And because this hypothesis would prove to be wrong, what these researchers ultimately established was nothing more than a “foundation myth.”

The key weakness in Wyndham and Strydom’s study was that they failed to control for the third factor, metabolic rate, which determines both the rectal temperature and the sweat rate during exercise.

Thus, the most likely explanation for Wyndham and Strydom’s finding of a linear (assumed causal) relationship between the post-race rectal temperature and the runners’ levels of dehydration (discussed in the previous post in this series (14)) is simply that both were determined by how fast the athletes ran in the different races. Those who ran the fastest also sweated the most and hence lost the most weight. But because they ran the fastest, they also sustained the highest metabolic rates (rates of oxygen consumption, or VO2). And since VO2 determines the rectal temperature during exercise, the fastest, heaviest sweating runners who lost the most weight during the races also had the highest post-race rectal temperatures.

So, for Wyndham and Strydom (or anyone else) to establish their hypothesis as the “truth” requires that it be subjected to the scrutiny of an RCT. Indeed, it is the development of the RCT that differentiates the sciences from the arts and is the cornerstone of the modern medical sciences (even though RCTs are not without their own problems).

The goal of an RCT is to control all possible influences, including the psychological, with the sole exception of the single variable that the scientist believes determines the outcome measurement. That single variable is then allowed to vary in a controlled way in a series of experiments. In this way, the influence of many different factors can be evaluated one at a time in consecutive experiments in a systematic manner. In short, the focus of the scientific method is to undertake experiments in each of which only one variable is allowed to change in a controlled manner. The scientist then measures any effect that changes in that specific variable may have on the key outcome measurement.

Wyndham and Strydom sought to determine a relationship between the outcome measurement — the post-exercise rectal temperature and the risk of heat stroke — and the controlled variable, which was the extent to which the athletes ingested fluid during the 21.5-mile races. To answer this question in the population they chose, only the following experimental design would have been appropriate:

The environmental conditions would need to be identical during all races or the researchers would need to prove that any variation in environmental conditions was too small to have influenced their conclusions. Alternatively, they could have compared the effects of drinking different volumes of fluid in either hot or cold environments.
The physical state of the runners would need to be identical at the start of each race, especially their state of training before each race. In addition, none of the athletes should have shown any evidence of medical illnesses before any of the trials.
The runners would need to run each race at exactly the same pace. That is, their speeds over the different sections of the course and especially over the last 4 miles of the race would need to be identical under all experimental conditions. (This is because the post-race rectal temperature is determined by the running speed maintained over the last 4 miles of the race.)
The course over which the races were run would need to be identical.

In experiments in which these four factors were rigorously controlled, the authors then would need to alter the one controlled variable of their study (which in our proposed study would have been the rate at which the runners ingested fluid during the race). Since Wyndham and Strydom believed that only weight losses in excess of 3% were likely to be detrimental, they would need to design experiments in which different rates of fluid intake produced, for example, the following range of weight losses during their 21.5-mile races: 0%, -3%, -4.5%, and -6%.

To do this, they first would have needed all the athletes to run the race at their chosen (but predetermined) running paces in the chosen environmental conditions whilst they drank as they normally did. In effect, this was the study that Wyndham and Strydom reported.

Once they knew how much each athlete sweated when running at his chosen marathon pace in these environmental conditions, they then could calculate how much each would need to drink to finish the 21.5-mile races on the same course under identical environmental conditions with levels of weight loss of 0%, -3%, -4.5%, and -6%.

So, if their experiments had been designed properly, the study that Wyndham and Strydom actually reported would have been merely a preliminary study to provide essential information for the design of all the subsequent experiments.

Then, over the next few months, whilst the athletes maintained their same levels of fitness and general health, they would then complete those races according to a randomized design. This means that in each race there would be equal numbers of runners who were drinking according to a regimen that would produce water deficits of 0, -3%, -4.5%, and -6%. However, the allocation of exactly who drank at what rate during which race would have been decided by random allocation even before the first experimental trial was conducted.

Furthermore, the athletes would be informed of their drinking regimen for each race only immediately before they began that race. This would limit the psychological (placebo) effects that would occur when the athletes were told what they were to drink during the race.

Importantly, the authors would not be able to express any opinions of which drinking protocol(s) they believed were likely to be optimal since that also might influence the study outcomes.

Note that in our proposed study, the speeds at which the athletes ran would not be an outcome measure. In other words, the study was not designed to determine the effects of different drinking patterns on how fast athletes ran. Instead it was controlled to ensure that running speeds and hence metabolic rates (VO2) were controlled in each athlete in all experiments.

But had the speed at which the athletes finished the race been an outcome measure, then ideally the study could not be funded by any organization that had a commercial interest in that outcome — or already had expressed an opinion of what it expected that outcome to be.

Nor could the study be conducted by scientists who had expressed any opinions on what they expected the outcome of the study to be. For athletes who know what is expected of them during the experiment will do just that: They will do exactly what the researchers expect of them.

Finally, our RCT study would involve perhaps 64 runners since there are 64 possible combinations in which the four different drinking patterns could be arranged. This number also would increase the probability that any effects of fluid ingestion would be measurable.

In this way, the possible effects of some environmental factor about which we know nothing and which might affect the results of only one or perhaps two of the experimental races would still have an equivalent effect on all four drinking regimens, since all would be represented equally in each experimental trial.

The point, of course, is that Wyndham and Strydom did not schedule the five 21.5-mile races that would have been necessary to prove the “antipyretic” effect of water drinking during running.

As a result, they could not exclude that at least one other factor, in particular the rate of energy use or VO2, was the real reason why they uncovered a spurious relationship between body-weight loss during those races and the post-race rectal temperature.

To summarize: An alternate explanation for an apparently causal relationship between dehydration and hyperthermia is that the faster the runners ran in that study, the higher were their metabolic rates (VO2), and as a consequence, their body temperatures, sweat rates, and levels of dehydration. For the speed at which the fastest runners ran would have produced the highest VO2, which in turn would have generated the highest body temperatures and the highest sweat rates in those runners. Since all runners drank sparingly during those races, as was the custom at that time, those who ran the fastest and sweated the most whilst drinking little also would have lost the most weight and been the most “dehydrated” at the finish.

There is one final factor to consider. In the 1960s, only well-trained athletes with reasonable athletic ability competed in marathon races. Most of these runners would have been of quite similar weights, probably between 55 and 70 kg (121 and 154 pounds). Since the VO2 during running is determined by running speed and body mass, the relatively similar body weights of all these runners (compared to large differences in modern marathoners) would have meant the major determinant of differences in VO2 between the runners in these races would have been differences in their running speeds.

Relevance to Nutrition Science

The scientific basis for most of what is taught in the modern nutrition sciences is cross-sectional observational studies, also known as epidemiological studies, which (like Wyndham and Strydom’s study) cannot prove causation except in certain very exceptional circumstances.

It is perhaps not a complete surprise to readers of this series that I have been involved in a 4½-year trial of my professional conduct for suggesting dietary advice that was not considered “conventional” or “evidence-based.” In the end, as described in Marika Sboros’ and my book, Lore of Nutrition (20), I was found innocent of all charges.

What I learned in the process is that most of the ideas that are taught in the nutrition sciences as indisputably true are in fact no better than “foundation myths” because they are based on observational studies that cannot prove causation. The greatest critic of the nutrition sciences is one of the most respected and reputable scientists of modern times, Dr. John Ioannidis, MD, Professor of Medicine at Stanford University (21-22). To say that his status in the profession is close to genius is not an overstatement.

In essence, his message is that as far as nutrition research is concerned, we need to begin all over again. Recently, in an interview with CBC News, Ioannidis said, “Nutritional epidemiology is a scandal. It should just go to the waste bin.” No doubt we will return to this topic frequently in the future.

A Final Word on Meta-Analyses

Table 1 lists meta-analysis as the highest form of evidence. But this clearly depends on the quality of the studies that make up any particular meta-analysis, as well as the independence of the persons conducting the meta-analysis.

Ioannidis notes that the production of meta-analysis has become a major growth industry in modern science: “Currently there is a massive production of unnecessary, misleading, and conflicted systematic reviews and meta-analyses. Instead of promoting evidence-based medicine and health care, these instruments often serve mostly as easily produced publishable units or marketing tools. Suboptimal systematic reviews and meta-analyses can be harmful” (23). He concludes that only 3% of all meta-analyses are clinically useful.

So, How Do You Judge Which Science Is Likely to Be True?

Consider the following principles:

Consider all the evidence. The evidence you either don’t know about or choose to ignore will come back to haunt you. We have a saying that everyone is entitled to his or her opinion. But no one is entitled to his or her own set of facts.
The most important evidence is not that which supports your biases. The most important evidence is that which disagrees with what you believe. A single credible study (done by reputable scientists who do not have an agenda) that refutes your ideas is more important information for you than hundreds of studies that apparently support your biases.
If a new idea conflicts with what is generally accepted as a biological truth, it is probably wrong unless it is presented together with a body of new and credible evidence that disproves those previously accepted biological “truths.” Biology always rules (See previously cited quote of John Le Fanu (4)).

Additional Reading

Noakes

Professor T.D. Noakes (OMS, MBChB, MD, D.Sc., Ph.D.[hc], FACSM, [hon] FFSEM UK, [hon] FFSEM Ire) studied at the University of Cape Town (UCT), obtaining a MBChB degree and an MD and DSc (Med) in Exercise Science. He is now an Emeritus Professor at UCT, following his retirement from the Research Unit of Exercise Science and Sports Medicine. In 1995, he was a co-founder of the now-prestigious Sports Science Institute of South Africa (SSISA). He has been rated an A1 scientist by the National Research Foundation of SA (NRF) for a second five-year term. In 2008, he received the Order of Mapungubwe, Silver, from the President of South Africa for his “excellent contribution in the field of sports and the science of physical exercise.”

Noakes has published more than 750 scientific books and articles. He has been cited more than 16,000 times in scientific literature and has an H-index of 71. He has won numerous awards over the years and made himself available on many editorial boards. He has authored many books, including Lore of Running (4th Edition), considered to be the “bible” for runners; his autobiography, Challenging Beliefs: Memoirs of a Career; Waterlogged: The Serious Problem of Overhydration in Endurance Sports (in 2012); and The Real Meal Revolution (in 2013).

Following the publication of the best-selling The Real Meal Revolution, he founded The Noakes Foundation, the focus of which is to support high quality research of the low-carbohydrate, high-fat diet, especially for those with insulin resistance.

He is highly acclaimed in his field and, at age 67, still is physically active, taking part in races up to 21 km as well as regular CrossFit training.

References

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Ioannidis JPA. Evidence-based medicine has been highjacked. A report to David Sackett. J. Clin. Epidemiol. 73(2016): 82-86.