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Science, Pseudoscience, Nutritional Epidemiology, and Meat

March 14, 2012 377 Comments

 

I’m writing this post with a little more haste than is my wont. I’ve received dozens of e-mails asking me to comment on the recent news — ala the the New York Times — that meat-eating apparently causes premature death and disease. So this post is likely to contain more than my usual number of typos, egregious spelling mistakes, grammatical errors, etc. Bear with me. Rather than spend a week rewriting and editing, as I usually do, I’m going to do my best to get this up and out in a few hours.

Back in 2007 when I first published Good Calories, Bad Calories I also wrote a cover story in the New York Times Magazine on the problems with observational epidemiology. The article was called “Do We Really Know What Makes Us Healthy?” and I made the argument that even the better epidemiologists in the world consider this stuff closer to a pseudoscience than a real science. I used as a case study the researchers from the Harvard School of Public Health, led by Walter Willett, who runs the Nurses’ Health Study. In doing so, I wanted to point out one of the main reasons why nutritionists and public health authorities have gone off the rails in their advice about what constitutes a healthy diet. The article itself pointed out that every time in the past that these researchers had claimed that an association observed in their observational trials was a causal relationship, and that causal relationship had then been tested in experiment, the experiment had failed to confirm the causal interpretation — i.e., the folks from Harvard got it wrong. Not most times, but every time. No exception. Their batting average circa 2007, at least, was .000.

Now it’s these very same Harvard researchers — Walter Willett and his colleagues — who have authored this new article claiming that red meat and processed meat consumption is deadly; that eating it regularly raises our risk of dying prematurely and contracting a host of chronic diseases. Zoe Harcombe has done a wonderful job dissecting the paper at her site. I want to talk about the bigger picture (in a less concise way).

This is an issue about science itself and the quality of research done in nutrition. Those of you who have read Good Calories, Bad Calories (The Diet Delusion in the UK) know that in the epilogue I make a point to say that I never used the word scientist to describe the people doing nutrition and obesity research, except in very rare and specific cases. Simply put, I don’t believe these people do science as it needs to be done; it would not be recognized as science by scientists in any functioning discipline.

Science is ultimately about establishing cause and effect. It’s not about guessing. You come up with a hypothesis — force x causes observation y — and then you do your best to prove that it’s wrong. If you can’t, you tentatively accept the possibility that your hypothesis was right. Peter Medawar, the Nobel Laureate immunologist, described this proving-it’s-wrong step as the  ”the critical or rectifying episode in scientific reasoning.” Here’s Karl Popper saying the same thing: “The method of science is the method of bold conjectures and ingenious and severe attempts to refute them.” The bold conjectures, the hypotheses, making the observations that lead to your conjectures… that’s the easy part. The critical or rectifying episode, which is to say, the ingenious and severe attempts to refute your conjectures, is the hard part. Anyone can make a bold conjecture. (Here’s one: space aliens cause heart disease.) Making the observations and crafting them into a hypothesis is easy. Testing them ingeniously and severely to see if they’re right is the rest of the job — say 99 percent of the job of doing science, of being a scientist.

The problem with observational studies like those run by Willett and his colleagues is that they do none of this. That’s why it’s so frustrating. The hard part of science is left out  and they skip straight to the endpoint, insisting that their interpretation of the association is the correct one and we should all change our diets accordingly.

In these observational studies, the epidemiologists establish a cohort of subjects to follow (tens of thousands of nurses and physicians, in this case) and then ask them about what they eat. The fact that they use questionnaires that are notoriously fallible is almost irrelevant here because the rest of the science is so flawed. Then they follow the subjects for decades — 28 years in this case. Now they have a database of diseases, deaths and foods consumed, and they can draw associations between what these people were eating and the diseases and deaths.

The end result is an association. In the latest report, eating a lot of red meat and processed meat is associated with premature death and increased risk of chronic disease. That’s what they observed in the cohorts — the observation.  The subjects who ate the most meat (the top quintile) had a 20 percent greater risk of dying over the course of the study than the subjects who ate the least meat (the bottom quintile). This association then generates a hypothesis, which is why these associations used to be known as “hypothesis-generating data” (before Willett and his colleagues and others like them decided they got tired of their hypotheses being shot down by experiments and they’d skip this step). Because of the association that we’ve observed, so this thinking goes, we now hypothesize that eating red meat and particularly processed meat is bad for our health and we will live longer and prosper more if we don’t do it. We hypothesize that the cause of the association we’ve observed is that red and processed meat is unhealthy stuff.

Terrific. We have our bold conjecture. What should we do next?

Well, because this is supposed to be a science, we ask the question whether we can imagine other less newsworthy explanations for the association we’ve observed. What else might cause it? An association by itself contains no causal information. There are an infinite number of associations that are not causally related for every association that is, so the fact of the association itself doesn’t tell us much.

Moreover, this meat-eating association with disease is a tiny association. Tiny. It’s not the 20-fold increased risk of lung cancer that pack-a-day smokers have compared to non-smokers. It’s a 0.2-fold increased risk — 1/100th the size. So with lung cancer we could buy as a society the observation that cigarettes cause lung cancer because it was and remains virtually impossible to imagine what other factor could explain an association so huge and dramatic. Experiments didn’t need to be done to test the hypothesis because, well, the signal was just so big that the epidemiologists of the time could safely believe it was real. And then experiments were, in effect, done anyway. People quit smoking and lung cancer rates came down, or at least I assume they did. (If not, we’re in trouble here.) When I first wrote about the pseudoscience of epidemiology in Science back in 1995,  “Epidemiology Faces It’s Limits”, I noted that very few epidemiologists would ever take seriously an association smaller than a 3- or 4-fold increase in risk. These Harvard people are discussing, and getting an extraordinary amount of media attention, over a 0.2-fold increased risk. (Horn-blowing alert: my Science article has since been cited by over 400 articles in the peer-reviewed medical literature, according to Thomson Reuter’s Web of Knowledge.)

So how can we explain this tiny association between the risk of eating a lot of red and processed meat — the 1/100th-the-size-of-the-lung-cancer-cigarette effect–compared to eating virtually none? Again, we have an observation — or an association, two or more things happening in concert; let’s think of all the possible reasons that might explain why these two variables, meat-eating and disease, associate together in our cohorts of nurses and physicians.  Here’s how the great German pathologist Rudolph Virchow phrased this in 1849: How, he said, can we “with certainty decide which of two coexistent phenomena is the cause and which the effect, whether one of them is the cause at all instead of both being effects of a third cause, or even whether both are effects of two entirely unrelated causes”? This is the hard part.

The answer ultimately is that we do experiments, which is what Virchow went on to discuss. But we’ll get back to this in a minute. Before we get around to doing the experiments, we must rack our brains to figure out if there are other causal explanations for this association beside the the meat-eating one. Another way to think of this is that we’re looking for all the myriad possible ways our methodology and equipment might have fooled us.  The first principle of good science, as Richard Feynman liked to say, is that you must not fool yourself because you’re the easiest person to fool. And so before we go public and commit ourselves to believing this association is meaningful and causal, let’s think of all the ways we might be fooled. Once we’ve thought up every possible, reasonable alternative hypotheses (space aliens are out on this account), we can then go about testing them to see which ones survive the tests: our preferred hypothesis (meat-eating causes disease, in this case) or one of the many others we’ve considered.

So let’s think of reasonable ways in which people who eat a lot of meat might be different from people who don’t, looking specifically for differences that might also explain some or all of the association we observed between meat-eating, disease and premature death. What else can explain this association, which might have nothing to do with whatever happens when we consume meat or processed meat?

Zoe Harcombe made this point beautifully using the Harvard data. The obvious clue is that as we move from the bottom quintile of meat-eaters (those who are effectively vegetarians) to the top quintile of meat-eaters we see an increase in virtually every accepted unhealthy behavior — smoking goes up, drinking goes up, sedentary behavior (or lack of physical activity) goes up — and we also see an increase in markers for unhealthy behaviors — BMI goes up, blood pressure, etc. So what could be happening here?

If you go back and read my New York Times Magazine article on this research, you’ll see that I discussed a whole host of effects, known technically as confounders  — they confound the interpretation of the association — that could explain associations between two variables but have nothing to do biologically with the variables themselves. One of these confounders is called the compliance or adherer effect. Heres’ what I said about it in the article:

The Bias of Compliance

A still more subtle component of healthy-user bias has to be confronted. This is the compliance or adherer effect. Quite simply, people who comply with their doctors’ orders when given a prescription are different and healthier than people who don’t. This difference may be ultimately unquantifiable. The compliance effect is another plausible explanation for many of the beneficial associations that epidemiologists commonly report, which means this alone is a reason to wonder if much of what we hear about what constitutes a healthful diet and lifestyle is misconceived.

The lesson comes from an ambitious clinical trial called the Coronary Drug Project that set out in the 1970s to test whether any of five different drugs might prevent heart attacks. The subjects were some 8,500 middle-aged men with established heart problems. Two-thirds of them were randomly assigned to take one of the five drugs and the other third a placebo. Because one of the drugs, clofibrate, lowered cholesterol levels, the researchers had high hopes that it would ward off heart disease. But when the results were tabulated after five years, clofibrate showed no beneficial effect. The researchers then considered the possibility that clofibrate appeared to fail only because the subjects failed to faithfully take their prescriptions.

As it turned out, those men who said they took more than 80 percent of the pills prescribed fared substantially better than those who didn’t. Only 15 percent of these faithful “adherers” died, compared with almost 25 percent of what the project researchers called “poor adherers.” This might have been taken as reason to believe that clofibrate actually did cut heart-disease deaths almost by half, but then the researchers looked at those men who faithfully took their placebos. And those men, too, seemed to benefit from adhering closely to their prescription: only 15 percent of them died compared with 28 percent who were less conscientious. “So faithfully taking the placebo cuts the death rate by a factor of two,” says David Freedman, a professor of statistics at the University of California, Berkeley [who passed away, regrettably, in 2008]. “How can this be? Well, people who take their placebo regularly are just different than the others. The rest is a little speculative. Maybe they take better care of themselves in general. But this compliance effect is quite a big effect.”

The moral of the story, says Freedman, is that whenever epidemiologists compare people who faithfully engage in some activity with those who don’t — whether taking prescription pills or vitamins or exercising regularly or eating what they consider a healthful diet — the researchers need to account for this compliance effect or they will most likely infer the wrong answer. They’ll conclude that this behavior, whatever it is, prevents disease and saves lives, when all they’re really doing is comparing two different types of people who are, in effect, incomparable.

This phenomenon is a particularly compelling explanation for why the Nurses’ Health Study and other cohort studies saw a benefit of H.R.T. [hormone replacement therapy, one subject of the article] in current users of the drugs, but not necessarily in past users. By distinguishing among women who never used H.R.T., those who used it but then stopped and current users (who were the only ones for which a consistent benefit appeared), these observational studies may have inadvertently focused their attention specifically on, as Jerry Avorn says, the “Girl Scouts in the group, the compliant ongoing users, who are probably doing a lot of other preventive things as well.”

 

It’s this compliance effect that makes these observational studies the equivalent of conventional wisdom-confirmation machines. Our public health authorities were doling out pretty much the same dietary advice  in the 1970s and 1980s, when these observational studies were starting up, as they are now. The conventional health-conscious wisdom of the era had it that we should eat less fat and saturated fat, and so less red meat, which also was supposed to cause colon cancer, less processed meat (those damn nitrates) and more fruits and vegetables and whole grains, etc. And so the people who are studied in the cohorts could be divided into two groups: those who complied with this advice — the Girl Scouts, as Avorn put it — and those who didn’t.

Now when we’re looking at the subjects who avoided red meat and processed meat and comparing them to the subjects who ate them in quantity, we can think of it as  effectively comparing the Girl Scouts to the non-Girl Scouts, the compliers to the conventional wisdom to the non-compliers. And the compliance effect tells us right there that we should see an association — that the Girl Scouts should appear to be healthier. Significantly healthier. Actually they should be even healthier than Willet et al. are now reporting, which suggests that there’s something else working against them (not eating enough red meat?). In other words, the people who avoided red meat and processed meats were the ones who fundamentally cared about their health and had the energy (and maybe the health) to act on it. And the people who ate a lot of red meat and processed meat in the 1980s and 1990s were the ones who didn’t.

Here’s another way to look at it: let’s say we wanted to identify markers of people who were too poor or too ignorant to behave in a health conscious manner in the 1980s and 1990s or just didn’t, if you’ll pardon the scatological terminology, give a sh*t. Well, we might look at people who continued to eat a lot of bacon and red meat after Time magazine ran this cover image in 1984 — “Cholesterol, and now the bad news”. I’m going to use myself as an example here, realizing it’s always dangerous and I’m probably an extreme case. But I lived in LA in the 1990s where health conscious behavior was and is the norm, and I’d bet that I didn’t have more than half a dozen servings of bacon or more than two steaks a year through the 1990s. It was all skinless chicken breasts and fish and way too much pasta and cereal (oatmeal or some other non-fat grain) and thousands upon thousands of egg whites without the yolks. Because that’s what I thought was healthy.

So when we compare people who ate a lot of meat and processed meat in this period to those who were effectively vegetarians, we’re comparing people who are inherently incomparable. We’re comparing health conscious compliers to non-compliers; people who cared about their health and had the income and energy to do something about it and people who didn’t.  And the compliers will almost always appear to be healthier in these cohorts because of the compliance effect if nothing else. No amount of “correcting” for BMI and blood pressure, smoking status, etc. can correct for this compliance effect, which is the product of all these health conscious behaviors that can’t be measured, or just haven’t been measured. And we know this because they’re even present in randomized controlled trials. When the Harvard people insist they can “correct” for this, or that it’s not a factor, they’re fooling themselves. And we know they’re fooling themselves because the experimental trials keep confirming that.

That was the message of my 2007 article. As one friend put it years ago to me (and I wish I could remember who so I could credit him or her properly), when these cohort studies compare mostly health advice compliers to non-compliers,  they might as well be comparing Berkeley vegetarians who eat at Alice Water’s famous Chez Panisse restaurant once a week after their yoga practice to redneck truck drivers from West Virginia whose idea of a night on the town is chicken-fried steak (and potatoes and beer and who knows what else) at the local truck stop. The researchers can imply, as Willett and his colleagues do, that the most likely reason these people have different levels of morbidity and mortality is the amount of meat they eat; but that’s only because that’s what Willett and his colleagues have to believe to justify the decades of work and tens, if not hundreds, of millions of dollars that have been spent on these trials. Not because it’s the most likely explanation. It’s far more likely that the difference is caused by all the behaviors that associate with meat-eating or effective vegetarianism — whether you are, in effect, a Girl Scout or not.

This is why the best epidemiologists — the one’s I quote in the NYT Magazine article — think this nutritional epidemiology business is a pseudoscience at best. Observational studies like the Nurses’ Health Study can come up with the right hypothesis of causality about as often as a stopped clock gives you the right time. It’s bound to happen on occasion, but there’s no way to tell when that is without doing experiments to test all your competing hypotheses. And what makes this all so frustrating is that the Harvard people don’t see the need to look for alternative explanations of the data — for all the possible confounders — and to test them rigorously, which means they don’t actually see the need to do real science.

As I said, it’s a sad state of affairs.

Now we’re back to doing experiments — i.e., how we ultimately settle this difference of opinion. This is science.  Do the experiments.  We have alternative causal explanations for the tiny association between meat-eating and morbidity and mortality. One is that it’s the meat itself. The other is that it’s the behaviors that associate with meat-eating. So do an experiment to see which is right. How do we do it? Well you can do it with an N of 1. Switch your diet, see what happens. Or we can get more meaningful information by starting with your cohort of subjects and assigning them at random either to a diet rich red meat and processed meat, or to a diet that’s not — a mostly vegetarian diet. By assigning subjects at random to one of these two interventions, we mostly get rid of the behavioral (and socio-economic and educational…) factors that might associate with choosing of your own free will whether to be a vegetarian (or a mostly-vegetarian) or a meat-eater.

So we do a randomized-controlled trial. Take as many people as we can afford, randomize them into two groups — one that eats a lot of red meat and bacon, one that eats a lot of vegetables and whole grains and pulses-and very little red meat and bacon — and see what happens. These experiments have effectively been done. They’re the trials that compare Atkins-like diets to other more conventional weight loss diets — AHA Step 1 diets, Mediterranean diets, Zone diets, Ornish diets, etc. These conventional weight loss diets tend to restrict meat consumption to different extents because they restrict fat and/or saturated fat consumption and meat has a lot of fat and saturated fat in it. Ornish’s diet is the extreme example. And when these experiments have been done, the meat-rich, bacon-rich Atkins diet almost invariably comes out ahead, not just in weight loss but also in heart disease and diabetes risk factors. I discuss this in detail in chapter 18 of Why We Get Fat, ”The Nature of a Healthy Diet.” The Stanford A TO Z Study is a good example of these experiments. Over the course of the experiment — two years in this case — the subjects randomized to the Atkins-like meat- and bacon-heavy diet were healthier. That’s what we want to know.

Now Willett and his colleagues at Harvard would challenge this by saying somewhere along the line, as we go from two years out to decades, this health benefit must turn into a health detriment. How else can they explain why their associations are the opposite of what the experimental trials conclude? And if they don’t explain this away somehow, they might have to acknowledge that they’ve been doing pseudoscience for their entire careers. And maybe they’re right, but I certainly wouldn’t bet my life on it.

Ultimately we’re left with a decision about what we’re going to believe: the observations, or the experiments designed to test those observations. Good scientists will always tell you to believe the experiments. That’s why they do them.

 

 

Egregious (and embarrassing) error correction: In an early version of the post, I suggested that if you read the chapter on nutritional epidemiology in the textbook Modern Epidemiology, you’d see that the best epidemiologists agree that this pursuit is pathological. A reader from my institution — a UC Berkeley grad student — pointed out that the chapter on nutritional epi in the textbook was actually written by Walter Willett and that, not surprisingly, it does not agree with this position. Here’s how Willett ends that chapter:

The last two decades have seen enormous progress in the development of nutritional epidemiology methods. Work by many investigators has provided clear support for the essential underpinnings of this field. Substantial between-person variation in consumption of most dietary factors in populations has been demonstrated, methods to measure diet applicable to epidemiologic studies have been developed, and their validity has been documented. Based on this evidence, many large prospective cohort studies have been established that are providing a wealth of data on many outcomes that will be reported during the next decade. In addition, methods to account for errors in measurement of dietary intake have been developed and are beginning to be applied in reporting findings from studies of diet and disease.

Nutritional epidemiology has contributed importantly to understanding the etiology of many diseases. Low intake of fruits and vegetables has been shown to be related to increased risk of cardiovascular disease. Also, a substantial amount of epidemiologic evidence has accumulated indicating that replacing saturated and trans fats with unsaturated fats can play an important role in the prevention of coronary heart disease and type 2 diabetes. Many diseases—as diverse as cataracts, neural-tube defects, and macular degeneration—that were not thought to be nutritionally related have been found to have important dietary determinants. Nonetheless, much more needs to be learned regarding other diet and disease relations, and the dimensions of time and ranges of dietary intakes need to be expanded further. Furthermore, new products are constantly being introduced into the food supply, which will require continued epidemiologic vigilance.

The development and evaluation of additional methods to measure dietary factors, particularly those using biochemical methods to assess long-term intake, can contribute substantially to improvements in the capacity to assess diet and disease relations. Also, the capacity to identify those persons at genetically increased risk of disease will allow the study of gene–nutrient interactions that are almost sure to exist. The challenges posed by the complexities of nutritional exposures are likely to spur methodologic developments. Such developments have already occurred with respect to measurement error. The insights gained will have benefits throughout the field of epidemiology.

Now the reason I made this mistake is because I was rushing (no excuse, despite the warning up front) and so working from memory about a chapter that the UCLA epidemiologist Sander Greenland, one of the editor/authors of Modern Epidemiology, sent me when I was writing the New York Times Magazine article in 2007. The chapter Greenland was discussing and that he had sent me at the time was one he had authored, chapter 19 — “Bias Analysis” — and it was discussing observational epidemiology in general.

Here’s Greenland on the problem with all these studies — nutritional epi included — and how they’re interpreted:

Conventional methods assume all errors are random and that any modeling assumptions (such as homogeneity) are correct. With these assumptions, all uncertainty about the impact of errors on estimates is subsumed within conventional standard deviations for the estimates (standard errors), such as those given in earlier chapters (which assume no measurement error), and any discrepancy between an observed association and the target effect may be attributed to chance alone. When the assumptions are incorrect, however, the logical foundation for conventional statistical methods is absent, and those methods may yield highly misleading inferences. Epidemiologists recognize the possibility of incorrect assumptions in conventional analyses when they talk of residual confounding (from nonrandom exposure assignment), selection bias (from nonrandom subject selection), and information bias (from imperfect measurement). These biases rarely receive quantitative analysis, a situation that is understandable given that the analysis requires specifying values (such as amount of selection bias) for which little or no data may be available. An unfortunate consequence of this lack of quantification is the switch in focus to those aspects of error that are more readily quantified, namely the random components.

Systematic errors can be and often are larger than random errors, and failure to appreciate their impact is potentially disastrous. The problem is magnified in large studies and pooling projects, for in those studies the large size reduces the amount of random error, and as a result the random error may be but a small component of total error. In such studies, a focus on “statistical significance” or even on confidence limits may amount to nothing more than a decision to focus on artifacts of systematic error as if they reflected a real causal effect.

 

 

Filed Under: Bad Science, General

Catching up on lost time – the Ancestral Health Symposium, food reward, palatability, insulin signaling and carbohydrates… Part II(d)

November 23, 2011 46 Comments

 

When last I left off, the subject of discussion was the critical question about the food reward/palatability hypothesis of obesity: Can palatability and reward value of foods be disassociated from the metabolic and hormonal effects of the individual nutrients being consumed and, in particular, the sugar and refined grains that “hyper-rewarding” foods seem to invariably contain?

Let’s start with the experiment in humans that Dr. Stephan Guyenet of wholehealthsource.org finds such compelling support of the food reward hypothesis. This was work done by Ted Van Itallie and Sami Hashim back in the 1960s. (For an idea of the simplistic notions held by Dr. Hashim about obesity and its cause and prevention, I highly recommend this video here. I discuss Dr. Van Itallie’s critical role in shaping the current thinking about obesity — i.e., the mess we’re in today — in chapter 23 of Good Calories, Bad Calories.)

In his “Case for the Food Reward Hypothesis of Obesity, Part II” post, Dr. Guyenet argues that this experiment is important because it demonstrates what he considers one of several critical requirements for the validity of the food reward hypothesis: “Decreasing the reward/palatability of the diet should cause fat loss in animals and humans that carry excess fat.” Here’s what he says:

One of the most striking weight loss studies I’ve seen was conducted in 1965 and involved feeding a bland liquid diet through a dispensing straw (12).  Lean and obese volunteers were instructed to eat as much of the liquid food as they wanted, but they were permitted no other food.  While lean volunteers ate a normal amount of calories and maintained weight, obese volunteers dramatically reduced their spontaneous calorie intake and lost fat rapidly, with one man losing 200 lbs in 255 days without hunger.  This is exactly what one would expect if unpalatable/unrewarding food lowered the biologically “defended” level of fat mass.  Interestingly, the diet was high in sugar but was otherwise very low in palatability/reward value.

This was Dr. Guyenet’s second discussion of the tube-feeding paper. As he explained in an earlier post on this experiment, the total number of subjects was four: two lean and two obese. The two lean were kept on the feeding machine for 16 and 9 days. They didn’t bother to decrease caloric intake, and so their experiment ended then. The two obese subjects, however, curtailed intake dramatically, to 275 calories per day for the male volunteer and 144 for the female). The man stayed with the feeding machine for another 70 days and was then sent home with the formula and the instruction to drink only 400 calories a day. He kept this up for another half year until he had lost the 200 pounds. Says Dr.  Guyenet (in “Food Reward: a Dominant Factor in Obesity, Part II”, his earlier post):

 This machine-feeding regimen was nearly as close as one can get to a diet with no rewarding properties whatsoever. Although it contained carbohydrate and fat, it did not contain any flavor or texture to associate them with, and thus the reward value of the diet was minimized. As one would expect if food reward influences the body fat setpoint, lean volunteers maintained starting weight and a normal calorie intake, while their obese counterparts rapidly lost a massive amount of fat and reduced calorie intake dramatically without hunger. This suggests that obesity is not entirely due to a “broken” metabolism (although that may still contribute), but also at least in part to a heightened sensitivity to food reward in susceptible people. [The italics are mine.]

So immediately we have a problem, and it strikes me as near-fatal for the food reward hypothesis of obesity. In Dr. Guyenet’s first post on the experiment (the one immediately above), he says that the regimen “was nearly as close as one can get to a diet with no rewarding properties whatsoever…. It did not contain any flavor or texture to associate them with, and thus the reward value of the diet was minimized.” In his second post (the first of the two I quote, just to make life confusing), he notes that the diet was “high in sugar” although he tries to hold onto the food reward hypothesis by stating that it “was otherwise very low in palatability/reward value.”

This is why I asked Dr. Guyenet at the AHS whether the formula diet had sugar in it. If it did, then how could it be bland? And how could it have a low food reward value, which is, more or less, the whole point? It might have a lower food value than what the two obese subjects were eating prior to the experiment, but low?

As Hashim and Van Italie noted in a footnote in their 1965 paper, and as Dr. Guyenet notes in his blog, the formula used was Nutrament. This was a liquid diet formula that went on sale in 1960 (according to Wikipedia), and if the composition then was anything like the composition now, a significant portion of the carbohydrate calories came from sugar.

So was it non-rewarding? Hashim and Van Italie refer to it as “bland” and Guyenet assumes it was as well, hence his description of it as “otherwise very low in palatabily/reward value.” But it had to be sweet if it had significant sugar in it; and indeed in the modern incarnation of Nutrament, which may or may not be the same as the original, there are 47 grams in every 12-ounce serving. This happens to be more sugar than you’d find in a 12-ounce can of Coke.

Frankly, the stuff sounds awful, but low in reward value? Well, only if a Coke is, too, and certainly not if Dr. Guyenet includes “liquid calories, particularly sweetened beverages” among the low-hanging fruit of the food reward hypothesis, which he does.

In fact, the point of a diet formula like Nutrament is not just that it contains enough protein and other nutrients that people can thrive on, say, 400 or 800 calories-a-day of the stuff. But it also has to taste good, so that consumers will continue to buy it and drink it day in and day out, even after they’ve moved into the weight maintenance phase of their lives — i.e., for the rest of their lives. It’s an example from the 1960s of what Dr. Guyenet describes as “the goal of processed food manufacturers… to create a product that maximally reinforces purchase and consumption behaviors—food reward!”

We can try to get around this problem by suggesting that bland and sweet is just not high in food reward value, as Dr. Guyenet tries to do, but we’re going to resort to this kind of, well, blatant contradiction only because we want to salvage this experiment as support for the hypothesis. So this formula must have a low-food reward value because an obese subject consumed less of it and lost weight and because we believe that foods with high reward value cause people to gain weight. Now we’re back to circular-definition land, a place I would prefer to never visit.

Now, how about the idea that a “cafeteria” or “junk food” diet makes humans and animals fat, a concept that was pioneered by Anthony Sclafani. The assumption is that such a diet is fattening because there’s something about eating a variety of foods, mostly junk foods, that is so rewarding or at least so less bland than a plain chow diet that both humans and animals get fat eating it. Here’s how Dr. Guyenet describes it:

In this model, animals are allowed free access to standard chow and water while concurrently offered highly palatable, energy dense, unhealthy human foods ad libitum.

In other words, they’re given an unlimited amount of human junk food in addition to their whole food-based “standard chow.” In this particular paper, the junk foods included Froot Loops, Cocoa Puffs, peanut butter cookies, Reese’s Pieces, Hostess Blueberry MiniMuffins, Cheez-its, nacho cheese Doritos, hot dogs, cheese, wedding cake, pork rinds, pepperoni slices and other industrial delicacies. Rats exposed to this food almost completely ignored their healthier, more nutritious and less palatable chow, instead gorging on junk food and rapidly attaining an obese state.

Aside from Dr. Guyenet’s description of standard rat chow as “whole-food based,” my major problem with this (which is the same problem Ramirez et al had 20-odd years ago with the existing research then) is that this is an experiment that changes an unholy host of variables, and the results are evoked to make a point about one: food reward value.

One advantage I have in this nutrition business as an arguably ignorant journalist is that I actually get to interview the researchers who do the work. (Technically anyone could do this, but the researchers are certainly more likely to give their time to a journalist, ignorant or not, than to what one of my acquaintances in academia refers to as “just a person.”) I interviewed Sclafani back on January 30, 2003 for GC,BC, and the interview revealed the obvious problem with this interpretation. As Sclafani told me, they started their cafeteria diet (which he was calling the “supermarket” diet at the time) with a variety of different foods (not quite as wide a variety as Dr. Guyenet is discussing above, but wide nonetheless): chocolate chip cookies, salami, cheese, bananas, marshmallows, milk chocolate, peanut butter and sweetened condensed milk, and then they later simplified it to four foods because the rats didn’t eat all the foods they gave them.

Which foods did they ignore? Sclafani said they never did a systematic study, nor had anyone else, as far as he knew (as of January 2003), but cheese, salami and peanut butter—the foods highest in fat and lowest in refined grains and sugar—seemed to be the foods they avoided in favor of the sweeter, starchy options. So the obvious question: are refined grains and/or sugar necessary to impart not just reward value, but reward value that leads to people and animals getting fat?

In fact, Sclafani told me that they had based their selection of foods on a hunch about what rats preferentially like, and so that’s why they included cheese in the list. It seemed like an obvious choice. After all, don’t you stick cheese in mouse traps when you want to rid your house of mice? And yet, cheese was not among the foods the Sclafani’s rats preferentially ate when given all these other refined carbs and sugary foods to eat instead. Maybe because the cheese was unrewarding. Or maybe because it was relatively if not completely refined-carb and sugar free, as were the salami and peanut butter.

This inability to differentiate food reward and/or palatability from the presence of refined carbs and sugars haunts virtually every example of the studies cited to document food reward and/or palatability.

Another example, not one used by Dr. Guyenet, is Kelly Brownell’s Yale Food Addiction Scale . This scale attempts to identify  people who suffer from addiction to certain foods. The scale is based on a survey that gives a series of statements about eating habits. Subjects must say how true each statement is, on a scale from “never” to “four or more times or daily.” This goes along with a list of foods of which food addicted subjects might have “difficulty controlling their intake.” Here are the first four statements to give you an idea of what Brownell is getting at:

  1. I find that when I start eating certain foods, I end up eating much more than planned.
  2. I find myself continuing to consume certain foods even though I am no longer hungry.
  3. I eat to the point where I feel physically ill.
  4. Not eating certain types of food or cutting down on certain type of food is something I worry about.

So let’s assume, for the sake of argument at least, that the “certain foods” that illicit addictive behavior is very similar to the list of hyper-rewarding foods, the ones most likely to cause obesity. Here’s Brownell’s list of the foods that are most likely to be addictive:

-       Sweets like ice cream, chocolate, doughnuts, cookies, cake, candy, ice cream [yes, ice cream is listed twice.]

-       Starches like white bread, rolls, pasta, and rice

-       Salty snacks like chips, pretzels, and crackers

-       Fatty foods like steak, bacon, hamburgers, cheeseburgers, pizza, and French fries

-       Sugary drinks like soda pop

With the exception of steak and bacon, all of these foods are high in carbohydrates — refined or otherwise (the French Fries) — and/or sugars, even the foods defined as “fatty” with the aforesaid exceptions.  If these foods are addictive and if they cause obesity, is it because they’re addictive or is it because of the metabolic and hormonal effects of consuming them — their effects on insulin signalling? There’s no way to tell without an exceedingly well-controlled and well-conceived experiment, but you can guess where my vote lies.

What about the steak and bacon, then? Well, if you ate nothing but those—steak and bacon every day, plus, say, the hamburgers or cheeseburgers without the refined grains attached, i.e., the buns—you’d be eating a weight loss diet (a ketogenic diet) and would almost assuredly lose weight doing it. So whether or not you consider steak and bacon addictive, it’s unlikely that they could be defined as foods high in reward value because they would tend to refute the hypothesis that high food reward value causes obesity. And now we’d be back to this problem of having to differentiate between hyper-rewarding foods or at least addictive foods that come with refined/easily digestible carbohydrates and sugars and cause fat accumulation and hyper-rewarding foods that don’t, and well, don’t.

Of the examples I could find in Dr. Guyenet’s discussions of the food reward/palatability hypothesis that held the promise of differentiating food reward value from underlying metabolic effects of the foods themselves (and the presence of refined or easily-digestible carbs and sugars), none of them actually came through with meaningful evidence.

The studies most likely to offer such a differentiation were those mentioned by Dr. Guyenet  in his post, “The Case for the Food Reward Hypothesis of Obesity, Part II.” These were the studies evoked as evidence for the hypothesis because they demonstrate that “Individual sensitivity to food reward should predict future fat gain.” About this evidence he says:

I’m aware of three studies that have investigated this question.  In the first, researchers found that the reinforcing value of food relative to a non-food stimulus predicted fat gain over the next year in 7-10 year old children (19).  In the second, the responsiveness of reward-related brain regions to imagining palatable vs. unpalatable foods (as assessed using fMRI) predicted body mass index (BMI) gains in adolescent girls, and this effect was modified by gene polymorphisms in dopamine receptor genes (20).  The third study also used fMRI to demonstrate that greater activation in reward-related brain regions during exposure to appetizing food cues predicted greater BMI gains over time in adolescent girls (21).

But of those three studies, none of them define what the high reward foods were, which foods were considered palatable and which were unpalatable. For all we know, the palatable foods were the ones rich with refined grains and sugars and the reason reward-related regions of our brain light up when we eat them (or at least when obese people do) is because our brains are responding to what these foods do to our bodies.

Reference 19 doesn’t specify at all which foods are actually high in reward value, nor do references 20 and 21, which are both by the same authors. They do, however, include a “cheeseburger” as an example of a processed food, demonstrating a certain bias against cheeseburgers that may be misplaced.

And reference 21 says that while BMI may have been related to the extent of activation in reward-related brain regions, as Dr. Guyenet points out, this was true regardless of whether the food being imagined was rewarding or palatable or not. Or the authors put it, “BMI [body mass index] was positively correlated with behavioral response to both appetizing and unappetizing food images, implying that food cues in general trigger greater attention in overweight vs. lean individuals.”

One obvious interpretation is that overweight individuals are hungrier than lean individuals, and so they have a greater response to any food in their reward centers. And, in fact, one point Dr. Guyenet’s mentor, Michael Schwartz, made of interest in his 2006 review in Nature “Central nervous system control of food intake and body weight” was that “food deprivation strongly augments the reward value… reduced food availability seems to exert a global, stimulatory effect on reward perception.” And so maybe the greater the BMI, the more likely the subjects were hungry or food deprived—a phenomenon I discuss at length in GC,BC— a state that could be due to increased insulin secretion and chronic hyperinsulinemia. And maybe refined grains and sugars augment reward value because they cause us to secrete more insulin and store calories away as fat and glycogen and make us hungry.

In GC,BC I quote Mark Friedman commenting on this potential carbs-insulin-hunger connection regarding just the cephalic phase of insulin secretion, the one that comes just by thinking about a particular food:

This cephalic release of insulin also serves to clear the circulation of “essentially anything an animal or a person can use for fuel. Not just blood sugar, but fatty acids, as well. All those nutrients just go away.” Hence, the thought of eating makes us hungry, because the insulin secreted in response depletes the bloodstream of the fuel that the peripheral tissues and organs need to survive.

And if this happens more in individuals who are insulin resistant,  as most obese individuals are, we’re now back at a hypothesis that maybe the insulin signaling in the body is running the brain’s response, not vice versa. Yes, it’s the brain that’s stimulating the insulin secretion when we think about food, but what makes us hungry and makes the food then seem so rewarding is the effect of the insulin secreted in the body.

Filed Under: Bad Science, Calories-in-Calories-out, Diets, food reward/palatability hypothesis, General, Glycemic Index, Obesity and weight regulation, Weightloss Diets

Catching up on lost time – the Ancestral Health Symposium, food reward, palatability, insulin signaling and carbohydrates… Part II(c)

November 18, 2011 148 Comments

 

We’ve been discussing the food reward/palatability hypothesis of obesity and whether this idea adds anything meaningful to our understanding of obesity.  Is the evidence for it sufficiently compelling that we should cease to pay attention to the fact that insulin, as Yalow and Berson noted in 1965, is “the principal regulator of fat metabolism?”

One point I’ve been making in my posts and in my books is that it’s possible to find evidence in favor of virtually any idea – including the Flying Spaghetti Monster as the ruling force in the universe. More important to the validation of an idea or a hypothesis is the strength of the evidence that seems to refute it. Can the hypothesis survive more or less intact our best attempts to refute it?

This is one of the points I was trying to get across at the Ancestral Health Symposium: that the foods we eat today during our current obesity epidemic might have a high reward value, and that diets consumed by lean populations in faraway locales might not, isn’t particularly interesting. Yes, it supports the hypothesis, but how do we explain epidemics of obesity in populations that  eat diets that don’t appear to have a high reward value? Do we need an entirely different hypothesis for them? That would be unfortunate.

“Here’s the fundamental concept that I think explains a lot of obesity in industrialized nations,” writes Dr. Stephen Guyenet of wholehealthsource.org .

We live in a more or less Darwinian economic framework (capitalism). Food manufacturers are in constant competition, and any food that sells poorly will rapidly disappear from stores. How do you get people to buy your product? You produce something that causes them to come back and buy it again. In other words, the goal of processed food manufacturers is to create a product that maximally reinforces purchase and consumption behaviors – food reward! If the product is not extremely rewarding, it won’t sell because it’s competing against other products that are extremely rewarding. Only the most rewarding products survive.

This certainly sounds reasonable, but don’t we also want a hypothesis of obesity that explains obesity rates in populations that lack such highly evolved food industries – obesity in non-industrialized nations? This would be a hypothesis that explains obesity-ridden populations in which the local industry isn’t quite so diligent in increasing food reward, if there are food manufacturers to speak of at all?

This is the question I asked in chapter one of Why We Get Fat. It’s why I listed a host of populations in which levels of obesity were reported, in some cases, approaching or exceeding those in the U.S. today, and yet with none of this Darwinian competition between food manufacturers, none of this extremely rewarding food (or at least not extremely-rewarding as we would define it today).

These populations included the Pima in 1902, the Sioux on the Crow Creek Reservation in 1928, the citizens of Naples in the years of extreme poverty following the Second World War and African-Americans in Charleston South Carolina in 1959. They included Zulu in Durban South Africa in 1960, and the citizens of Nauru in the South Pacific in 1961 — “By European standards,” a local physician wrote, “everyone past puberty is grossly overweight.” They included Trinidadians in the early 1960s and Chilean factory workers. They included urban Bantu pensioners “the most indigent of elderly Bantu,” in Johannesburg, South Africa in 1965, and so on.

What these populations had in common was varying degrees of poverty — from very poor to unimaginably poor — and the absence of a Darwinian food industry as Dr. Guyenet and others would describe it. They did have sugar and refined grains, but don’t we want a hypothesis of food reward that can make a claim more meaningful than “rewarding (or hyper-rewarding) foods are foods with sugar and/or refined grains in them?” (And if this ultimately is our definition, as I’ll discuss shortly, then we should be able to establish whether the reason they’re rewarding is or is not due to the peripheral effects of these foods, rather than their ability to influence brain chemistry, set point, etc.)

We also want a concept (or at least I do) that explains how we can have populations in which obesity and malnutrition and under-nutrition co-exist — for example, obese mothers with starving children, a common observation now in the literature.

Take Jamaica, for instance, where the British-trained diabetologist Rolf Richards, as I have quoted in Why We Get Fat and in my lectures, discussed the situation in 1973:

It is difficult to explain the high frequency of obesity seen in a relatively impecunious [very poor] society such as exists in the West Indies, when compared to the standard of living enjoyed in the more developed countries. Malnutrition and subnutrition are common disorders in the first two years of life in these areas, and account for almost 25 per cent of all admissions to pediatric wards in Jamaica.  Subnutrition continues in early childhood to the early teens.  Obesity begins to manifest itself in the female population from the 25th year of life and reaches enormous proportions from 30 onwards.

Now if we blame the mother’s obesity on the hyper-rewarding nature of the food she’s eating, we have to ask why these foods are rewarding only to the women and not to their children. The children aren’t fat, after all (not yet, anyway). In fact they’re starving. They’re under-nourished. We also have to explain why these foods only become rewarding from “the 25th year of life” onward? And, perhaps most important, we have to explain why these women don’t fight the hyper-rewarding nature of these foods and remain lean.

After all, the food reward/palatability hypothesis of obesity, as we discussed in the first post on the subject, dictates that these foods cause neurochemical changes in the brain, which then raises the adiposity set point, thus making us eat more and get fat.  Put simply, raising the set point in the brain makes us hungry or at least hungrier. Okay, so if this is right, then we can assume that the reward value of the food eaten in Jamaica made these women hungrier; they ate more, they got fatter. But why couldn’t they control their impulses and remain lean? Why couldn’t they experience the semi-starvation—or at least the perception of not having enough to eat—rather than their children who are indeed semi-starved?

Rather than giving in to the urge, consuming the superfluous calories themselves, and getting fat, why didn’t these mothers fight the urge and give those excess calories to their starving kids? If one of them has to go hungry or at least feel hungry, evolution, it seems, would always favor the mother doing it rather than the child.

We can try to rescue  the food reward/palatability hypothesis of obesity in a case like this by simply making the claim that if these people are fat, then obviously something about their food must have been hyper-rewarding. (Something other than the refined carbs and sugars, as we’ll discuss in the next post.) But now our definition is becoming circular: The women get fat because of the hyper-rewarding nature of the food they’re eating, and we know that the food is hyper-rewarding because they’re fat. We just have to find or identify the particular foods in their diet that are the hyper-rewarding ones, and, as I said, it would be nice if they weren’t just sugar and refined carbs.

In his blogs, Dr. Guyenet suggests that home cooked food has a lower food reward value than processed, restaurant-produced fast food. This is one reason why, he suggests, populations like the Ache of Paraguay, the !Kung San, Polynesians and Melanesians (not counting those on Nauru and other islands that were obese) were lean: They “cooked their food in earth ovens and used no flavorings or salt .“

That we don’t cook our foods by these simple, spice-free, salt-free methods is offered as another explanation for the current obesity epidemic — “the shift from simpler home-cooked food to professionally engineered/processed food designed to maximize palatability and reward.” And this is also an explanation often offered for why carbohydrate restriction and paleo diets (not necessarily two different things) are weight loss diets. It’s not that they’re simply absent refined grains and sugars, as they are, but that the meats, fish, fowl, vegetables, and maybe tubers consumed are home cooked and/or so relatively bland that somehow they are low in food reward value.

But we can be confident that these extremely poor populations with high levels of obesity were also getting by on simple home-cooked food. Without having had the opportunity to visit Trinidad in the early 1960s or the South Dakota Crow Creek Reservation in 1928, I’m going to assume with confidence that a large proportion of the population, if not all, were not frequenting fast food joints and buying hyper-rewarding candy bars and soft drinks. So why were they fat? Certainly the presence or absence of flavorless home cooking is not enough to explain it. Nor can we explain it by claiming that only the affluent were obese, as Dr. Guyenet suggests, because these populations were anything but affluent.

So why were they fat? A familiar question.

Well, maybe it’s the low-hanging fruit of food reward—the refined grains and sugars? Populations that got fat ate significant quantities—particularly, the sugar—and populations that didn’t, well, didn’t. And when obesity suddenly blossomed in populations, it was because sugar and refined grains were new additions to their diets. And so diets that work for weight loss and weight maintenance are those that restrict refined grains and sugars (and maybe easily digestible starchy vegetables, as well, or maybe not) and diets that don’t, well, don’t.

This is what I argued in my books, although I’m arguing that the problem is caused by the metabolic hormonal effects of these foods in the periphery, their effect primarily on insulin signaling and, ultimately, fat accumulation. And the reason we find these foods rewarding and palatable is because of these metabolic hormonal effects.

As I’ve suggested in prior posts, the kinds of observations that are meaningful in situations like this—two competing hypotheses/paradigms—are only those that can differentiate between the two competitors. Evidence or observations that can be explained equally well by either hypothesis might have rhetorical value—good in an argument, in the spur of the moment—but they don’t add much to the scientific question at hand: Which hypothesis/paradigm is the right one?

This is why the observation that the Ache, the !Kung San, the Polynesians and Kitavans and Masai are lean or were lean, for instance, doesn’t tell us anything of significance about which hypothesis is right: Their lack of excess adiposity might be a result of their bland, unrewarding diets or it might be because their diets lack or lacked any significant amount of refined grains and/or sugars.

And even if the foods or diets that are consumed by obese populations and individuals today in the U.S. and elsewhere do seem indisputably rewarding and palatable, we’re still left having to demonstrate that this palatability, this high food reward value, is not due to the nutritional composition of the diet and the peripheral effects of the nutrients—the metabolic and hormonal effects in the body.

This was a point made back in 1989 by Israel Ramirez, Michael Tordoff and Mark Friedman of the Monell Chemical Senses Center in Philadelphia in an article entitled “Dietary Hyperphagia and Obesity: What causes them?”(Friedman is one of the scientists whose thoughts on obesity and over-eating significantly shaped my own. I owe him a debt of gratitude. For those who want to read what I think may be the single most thoughtful article written on obesity and hunger in the post-WW2 era, I’d recommend Friedman’s article with Edward Stricker, The Physiological Psychology of Hunger: A Physiological Perspective.)

The Monell researchers were discussing only the concept of palatability, not the food reward value of a particular food. (The idea that food reward and palatability could be differentiated — that they weren’t precisely the same thing — hadn’t gotten much if any play up until then.) So the question was whether or not palatability (whether a food tastes good) could be legitimately disassociated from nutrient composition and peripheral effects of the food. As Ramirez et al said repeatedly in this article, researchers almost invariably assumed that a food could be defined as palatable if the animals (or humans) ate more of that food than some other food, but this was an inference and nothing more.

It was well known at the time (although it may have been forgotten since then), as I discussed in Good Calories, Bad Calories, that animals can be made to like one food more than another, and so eat more of the one than the other, by interventions that influenced their underlying physiologic/metabolic/hormonal states. Here’s how I illustrated this in GC,BC:

Throughout the first half of the twentieth century, a series of experimental observations, many of them from [Curt] Richter’s laboratory [at Johns Hopkins University], raised questions about what is meant by the concepts of hunger, thirst and palatability, and how they might reflect metabolic and physiological needs. For example, rats in which the adrenal glands are removed cannot retain salt and will die within two weeks on their usual diet from the consequences of salt depletion. If given a supply of salt in their cages, however, or given the choice of drinking salt water or pure water, they will chose to either eat or drink the salt and, by doing so, keep themselves alive indefinitely. These rats will develop a “taste” for salt that did not exist prior to the removal of their adrenal glands. Rats that have had their parathyroid glands removed will die within days of tetany, a disorder of calcium deficiency. If given the opportunity, however, they will drink a solution of calcium lactate rather than water—not the case with healthy rats—and will stay alive because of that choice. They will appear to like the calcium lactate more than water. And rats rendered diabetic voluntarily choose diets devoid of carbohydrates, consuming only protein and fat. “As a result,” Richter said, “they lost their symptoms of diabetes, i.e., their blood sugar fell to its normal level, they gained weight, ate less food and drank only normal amounts of water.

In short, change underlying physiologic/hormonal conditions and it will affect what an animal chooses to eat and so seems to like or find rewarding. The animal’s behavior and perceptions will change in response to a change in homeostasis – in the hormonal milieu of the cells in the body.

It’s quite possible that all those foods we seem to like, or even the ones we find rewarding but don’t particularly like, as Dr. Guyenet argues, and that subsequently cause obesity (not necessarily the same thing) are those foods that somehow satisfy an underlying metabolic and physiological demand. This in turn might induce our brains to register them as more palatable or rewarding, but the initial cause would be the effect in the periphery.  The nutrient composition of the food, in this case, would be the key—what it’s doing in the body, not necessarily the brain.

Here’s how Ramirez, Tordoff and Friedman phrased this issue back in 1989:

In order to demonstrate that diet palatability per se causes hyperphagia [overeating or a voracious appetite], it must be shown that obesity-inducing foods are more palatable than control foods, this greater palatability is not merely a reflection of the postingestive [after entering the digestive tract] consequences of the foods, and altering palatability without altering nutritional composition can cause obesity. This has not been done.… Although various experiments have been cited as supporting the palatability hypothesis, they are not decisive because, in every case, palatability was confounded with changes in nutritional composition.

That an experiment is “not decisive” unless this is done is the critical point. If an experiment that ostensibly changes food reward makes an animal eat more of a particular food and/or get fatter, and it does so by changing nutritional composition—say, the foods that are defined as more rewarding have more sugar in them, or are more refined, or have a greater water or fat content—then the researchers have to demonstrate that it’s not the change in nutritional composition and post-ingestive effects of that change that is causing the overeating and obesity. An observation that one diet produces obesity compared to another because it’s ostensibly more rewarding or palatable has to do the same. Otherwise either hypothesis could be true, and we haven’t learned anything.

Take the idea, as Dr. Guyenet suggests, that people will eat more at a sitting if foods are palatable than if they’re not, which seems kind of obvious. The better a food tastes, the more likely we are to eat more of it. But then Dr. Guyenet adds that this is true even of foods with “little or no nutritional quality.” This is how he phrases it in a recent post:

Many human studies have shown that people eat more food at a sitting if the food is higher palatability than if it is lower palatability (11).  This is true even if palatability is manipulated using substances that have little or no impact on the nutritional quality of the food, including saccharin (sweet), monosodium glutamate (savory) and herbs/spices.

The reference is a review article that actually makes the point that the evidence is ambiguous on the eating more issue when the foods have little or no nutritional quality. “Several studies showed no effect of sweet taste on either hunger ratings or food intake,” the authors write, “when the sweetener was provided in the form of gelatine, corn flakes or fromage blanc or as aspartame- or saccharin-sweetened drinks.” In fact, the authors then go on to suggest this is true of all “sweet taste” whether from caloric sweeteners or non-caloric, which doesn’t seem to do my hypothesis any favors either.

But what I’m arguing is that the key isn’t whether people eat more, but whether the foods stimulate fat accumulation. And if they do make us fatter, how?

The food reward hypothesis suggests that it happens because of the effect of the sweet taste in the brain, not in the body. If the former, then sugar and saccharine might be expected to be equally fattening, so long as we consider sugar and saccharine-sweetened beverages to have equal reward value or to be considered equally palatable by humans.

If the reward value is not the critical factor, then it’s a reasonable assumption that sugar-sweetened beverages will be more fattening than saccharine or aspartame-sweetened beverages. And we could do a clinical trial and see which turns out to be true, although we can also guess what we think such a trial (randomized, well-controlled) would find. Not surprisingly, I’d vote for the sugar-sweetened beverages being more fattening.

This doesn’t mean, by the way, that artificially-sweetened beverages could be absolved of having any fattening properties because we might still secrete insulin in response to these beverages. They may fool us into thinking that they have carbohydrate or sugar calories in them. And this insulin secretion could be cephalic — a kind of Pavlovian response — which would mean that the brain is telling the pancreas to secrete insulin (via the vagus nerve). But it would now be doing so not because the food is rewarding necessarily, but because the body has come to associate sweet taste with the presence of carbohydrates and feedback loops in the brain are working to get the body ready by secreting insulin.

In my next post, I’ll discuss more of the evidence offered in support of the food reward/palatability hypothesis and ask the question that Ramirez et al did: are palatability and food reward confounded with changes in nutritional composition, and if so, what might that confounding be?

 

Filed Under: Bad Science, Calories-in-Calories-out, Diets, food reward/palatability hypothesis, General, Obesity and weight regulation, Weightloss Diets

Calories, fat or carbohydrates? Why diets work (when they do).

December 13, 2010 821 Comments

Last September, the Williams College psychologist Susan Engel had an opinion piece in the New York Times on the value of standardized testing as a means of assessing the quality of a child’s education.  Engel argued that there was scant evidence that these tests were of any value at all, and that they should be replaced by the many “promising techniques” that psychologists had already identified as valuable in assessing the learning of our children.

So what does this have to do with nutrition and weight control? Well, among the promising techniques, wrote Engel, was this one:

Researchers have also found that the way a student critiques a simple science experiment shows whether he understands the idea of controlling variables, a key component in all science work. To assess children’s scientific skills, an experiment could be described to them, in writing, and then they would explain how they would improve upon it.

So the value of controlling variables in a scientific experiment is something that a reasonably well-educated child supposedly understands. And what I want to know is why don’ t nutritionists understand it and those researchers out there doing diet trials and studying obesity and weight regulation. Because their failure to do so — and I would argue that it may be a willful failure — has led to what may be another of the great misconceptions in modern nutrition research. In particular, that carbohydrated-restricted diets are “valuable tools” in the arsenal against overweight and obesity, but they’re just one of the dietary tools.

This belief stems from the last decade of diet trials comparing carbohydrate-restricted diets (usually Atkins) to low-calorie, low-fat diets. Instead of thinking of low-carbohydrate diets like Atkins as deadly, which was formerly the case, nutritionists and dietitians (or at least most of them) now think of these diets as useful, just as other diets, low in calories or fats, are also useful. The idea now is that some people do well on carbohydrate-restricted diets and some people do well on low-fat diets, and maybe this is a result of whether they happen to be insulin sensitive or insulin resistant or maybe its just a product of their particular food tastes and preferences.

And this belief, of course, is based on the notion that we get fat for reasons other than the nutrient composition of the diet – probably because of some combination of our genes, our tendency to eat to much and our sedentary behavior – and so the diet that works best is the one that allows us to most comfortably restrict our intake of total calories.

This was the conclusion, for instance, of a 2008 article by Chris Gardner and his colleagues at Stanford, reporting on a subgroup analysis of their famous A to Z study.  (The trial is famous, at least, in the low-carb world, because the Atkins diet resulted in twice the weight loss of any of the three other diets tested, and it also did a better job of improving heart disease risk factors). In this follow-up study, Gardner and his colleagues reported that in each diet group — from the Atkins diet on the high end of the dietary fat to carbohydrate ratio to the Ornish diet on the low end — the subjects who actually adhered to the diet lost the most weight. Hence, their conclusion: maybe adherence to a diet is more important than the actual nutrient composition of the diet. Here’s the concluding paragraph:

The main findings of this weight loss study, presented in a previous report, indicated that while all three diet groups lost modest amounts of weight, the Atkins group at 12 months lost approximately twice the weight of the other groups. The findings presented here indicate that weight loss in the lowest tertile [third] of adherence was negligible in all three diet groups, and more pronounced in the highest tertile of adherence for each diet group. It appears that substantial differences in proportions of dietary macronutrients play only a modest role in weight loss success, and that success is possible on any of these diets provided there is adequate adherence. Getting individuals to adhere to whatever diet they choose to follow deserves more emphasis. It remains to be determined to what extent there is a need for dietary weight loss programs that are easier to adhere to vs identifying and addressing individual barriers to adherence, or both.

So the nutrient composition of the diet is less important than whether or not the subject can live with the diet and is willing to do so for as long as it takes — ideally, a life time.

This concept of low-carb diets being good for some people and low-fat for others  is invariably reinforced by the fact that most of us  know someone who has lost weight and kept it off on Weight Watchers or after reading Skinny Bitch or some other popular low-calorie diet book. As a result, we assume that dieting isn’t a one-sized fits all endeavor and that everyone is different – perhaps metabolically and hormonally, as well – and that what works for me won’t necessarily work for you, and vice verse.

So what does this have to do with controlling variables or even understanding the concept of controlling variables?

What researchers like Gardner and his colleagues do in these diet trials  (and it’s the same thing most of us do when we think about those people who succeed on conventional  diets or after reading diet books like Skinny Bitch) is make the assumption that a diet that is described as a “low-fat diet” is low in fat only and that’s why it works. And they also make the assumption that a diet that restricts total calories works (if it does) because it restricts total calories. Another way of saying this is that we all tend to assume — researchers and lay people alike — that when someone embarks on a low-fat diet, the only meaningful variable that changes in their diet is the fat-to-carbohydrate ratio. The ratio gets smaller. Fat consumption goes down and carbohydrate consumption goes up. And, by the same token, when someone tries to simply eat less, the only meaningful variable that’s changing is the total number of calories they’re consuming.

The most extreme or perhaps egregious example of this thinking was the recent publication by Gary Foster and his colleagues, comparing low-fat diets, as they described them, to low-carbohydrate diets. The title was “Weight and Metabolic Outcomes After 2 years on a Low-Carbohydrate Versus a Low-Fat Diet.” And here was the conclusion as stated in the abstract:

Successful weight loss can be achieved with either a low-fat or low-carbohydrate diet when coupled with behavioral treatment. A low-carbohydrate diet is associated with favorable changes in cardiovascular disease risk factors at 2 years.

So the way the media and the nutrition community treated this was as further evidence that nutrient composition of the diet makes little difference in weight loss — maybe low-carb works for some of us, but low-fat works for others — although,  in this case, maybe low-carb had some modest advantage when it came to heart disease risk factors.

But if you read this article carefully, you’d have noticed that there was another significance difference between the “low-fat” and low-carbohydrate diets. The low fat diet was a low-calorie diet also — “A low-fat diet consisted of limited energy intake (1200 to 1800kcal/d; less than or equal to 30 % calories from fat),” the authors explained. The low-carbohydrate diet was not calorie-restricted. And if Foster and his colleagues were being either intellectually honest or good scientists, they’d have defined the two diets to make this clear. Not  “low-fat” vs.  “low-carbohydrate”, but “low-fat, calorie-restricted” vs, “low-carbohydrate, calorie-unrestricted.”In other words they’d have acknowledged that there was at least one other variable that was different between the two experiments and had to be taken into account when interpreting the results — the amount of calories the subjects were instructed to consume. As we’ll see, there were also other variables that were changing, but this one — how much food can be consumed if desired — is a whopper.

It’s a whopper because it begs this question: is it the total calories consumed that is the variable determining weight loss? And, by the same token, is it the calories consumed (or expended) that determines how much weight we gain?

In this case, both diets resulted in roughly equal weight loss but those subjects randomized to the “low-fat” diet were instructed and counseled to semi-starve themselves (eat a maximum of 1500 calories for women, 1800 for men), while those counseled to eat low-carb were counseled and instructed not to worry about how much they ate and, one hopes, as this was an Atkins diet being prescribed, eat until they were full. So if weight loss is the same in both groups, doesn’t this suggest, at least, that weight loss can be independent of whether dieters semi-starve themselves or eat to satiety? And, if so, of course, wouldn’t you rather get to eat to satiety?

Had Foster and his colleagues understood what school children are supposed to understand, according to Engels,  “the idea of controlling variables, a key component in all science work,” they may have decided to control for calories and instructed both groups that they could eat as much as they want, rather than just the low-carbohydrate group. Or, had they had the money to spend, they might have cooked meals for both groups of subjects, say, 2700 calories a day – either low-fat or low-carb – and encouraged both groups to eat all the food prepared. Such an experiment would have gone a long way to “controlling” for calories consumed or for whether the subjects were allowed to eat to satiety or not. In doing so, it might have revealed something meaningful about whether the nutrient composition of the diet plays a role in weight loss or weight gain independent of calories, which is one of the critical questions here. I’d hazard a guess that it surely does, but I could be wrong. It would be an interesting experiment to do and I’ll write  considerably more on that in a later post.

As for the other mistake Foster, Gardner and their colleagues make when they assume that a low-fat, calorie-restricted diet (defining it correctly) is restricted only in fat, it’s the same mistake we make when we assume that someone who lost weight following Weight Watchers or after reading Skinny Bitch did it merely because something about these regimens got them to eat fewer calories and maybe fewer fat calories in particular. And this is the other mistake that suggests a lack of understanding of the idea of controlling variables.

Virtually any diet that significantly restricts the number of calories consumed, even a diet that is described as low-fat (because the subjects are instructed to reduce the proportion of fat calories they consume), will cut the total amount of carbohydrate calories consumed as well. This is just simple arithmetic. If we cut all the calories we consume by half, for instance, then we’re cutting the carbohydrates by half, too. And because these typically constitute the largest proportion of calories in our diet to begin with, these will see the greatest absolute reduction. If we preferentially try to cut fat calories, we’ll find it exceedingly difficult to cut more than 400 or 500 calories a day by reducing fat — depending on how much fat we were eating to begin with — and so we’ll have to eat fewer carbohydrates as well.

Put simply, low-fat diets that also cut significant calories will cut carbohydrates significantly as well, and often by more than they cut fat.

Here’s the math: Imagine we want to cut our daily calories from 2,500 to 1,500, hoping to lose two pounds of fat a week. And imagine that the nutrient content of our pre-diet meals is what the authorities consider ideal — 20 percent protein, 30 percent fat and 50 percent carbohydrates. That’s 500 calories of protein, 750 calories of fat and 1,250 of carbohydrates.

If we keep the same balance of nutrients but eat only 1,500 calories a day, we’ll be eating 300 calories of protein, 450 calories of fat and 750 calories of carbohydrates. We’ll be cutting protein calories by 200, fat calories by 300 and carbohydrate calories by 500.

Now let’s make this a “low-fat” diet and try to reduce our fat consumption from 30 percent of calories to, say, 25 percent of calories, which is significantly less than most of us will tolerate. We’ll now be eating 300 calories of protein, 375 calories of fat and 825 of carbohydrates. We’ll be cutting our fat calories by 375 a day, but we’re still cutting carbohydrates by 425. So even though the percentage of carbohydrates consumed on this “low-fat” diet goes up — from 50 to 55 percent — the absolute amount of carbohydrates consumed goes down, and goes down more so than does the calories from fat. And if we increase the amount of protein we eat, we’ll have to eat still fewer carbohydrates to compensate.

If we start off eating enough fat, as I said — say, 40 percent of our calories — we can actually cut fat calories more so than carbs, but carbs are still cut significantly. Imagine our 2500 calorie per day diet is 40 percent fat, 40 percent carbs and 20 percent protein. That’s 1000 calories of fat and carbs each, and 500 calories of protein. If we now cut that to a 1500 calorie diet that’s 30 percent fat and 50 percent carbohydrates, we’ll be eating 450 calories of fat, 750 calories of carbohydrates and 300 calories of protein. So fat calories will have dropped by 550 calories, but we’ll still have reduced carbohydrate calories by 250. Not an enormous amount but an amount that might still have an effect on the regulation of our fat tissue and so fat loss.

Here’s an example of how this plays out in a real dietary trial. Consider  an Israeli trial published in the New England Journal of Medicine in 2008 by Iris Shai and her colleagues.  This trial compared a low-fat, calorie-restricted diet to a Mediteranean, calorie-restricted diet to a low-carbohydrate Atkins diet, unrestricted in calories. And, you’ll notice here, too, having explained that the first two diets are calorie-restricted and the latter diet isn’t, Shai and company get lazy and shorten their labeling of the diets so that they leave out the critical variable of whether the dieters are instructed or not to semi-starve themselves.

In this study, Shai and her colleagues made an attempt to assess what their subjects were eating before the trial started, and then after 6, 12, and 24 months. Keeping in mind that the dietary records from these studies have to be taken with a grain of salt, here’s the relevant data:

Let’s concentrate on the low-fat, calorie-restricted diet and the low-carb, Atkins diet. The changes in dietary intake and nutrients for the “low-fat diet” are shown in the first column. As you can see after 24 months, the subjects eating the low-fat diet were supposedly restricting calories consumed on average by 572 calories. The reduction in carbohydrates consumed, though, was 330 calories (82.8 grams per day times 4 calories per gram), compared to only a 170-calorie (18.9 grams per day times 9 calories per gram) reduction from baseline in fat. So the “low-fat diet” reduced carbohydrates nearly twice as much as it reduced fat.

The low-carbohydrate diet, on the other hand (the third column), reduced carbohydrate calories by 520 calories per day (129.8 grams per day times 4 calories per gram) and fat calories by a mere 15 calories (1.7 grams/day times 9 calories per gram). So certainly the low-carb diet was correctly described as a low-carb diet, and the question we have to ask is maybe the weight loss seen in the low-fat diet was also due to the restriction in carbohydrates. It is quite possible that even low-fat, calorie-restricted diets work because they restrict carbohydrates and maybe the reason they don’t work as well as the low-carb diets is they don’t restrict them as much. Or maybe they don’t work as well, on average, because they also restrict fat calories when dietary fat has little or no effect on body fat accumulation. We don’t know if this is true or not, but it could be true, and until these researchers realize that another variable is changing significantly on these low-fat, calorie-restricted diets –  the amount of carbohydrates consumed — they’ll never bother to test it or take it into account in their interpretation of these clinical trials, and we’ll never know.

Now, here’s yet another variable that’s changing on these diets, and this one the researchers ignore entirely and make no attempts to quantify — the quality of carbohydrates consumed. Any subject in these diet trials and anyone who tries a serious weight loss program on their own (the twinkie diet, perhaps, not included) will make a few consistent changes to what they eat. And they’ll do this regardless of the instructions that they’re given or the diet to which they’re randomized in the trial.

Specifically, they’ll get rid of or cut way back on the high-glycemic index carbohydrates and the foods or drinks with the high sugar or HFCS content. They’ll do so  because these foods are the easiest to eliminate and the most obviously inappropriate for anyone trying to get in shape. (And because for a almost 200 years these foods have been considered uniquely fattening.) They’ll stop drinking beer, for instance, or at least drink less beer or drink light beer instead. They might think of this as cutting calories, but the calories they’ll be cutting will be carbohydrates and, more importantly, they’re liquid, refined carbohydrates that are exceedingly easy to digest and so, perhaps, exceedingly fattening.

They’ll stop drinking caloric sodas – Coca Cola, Pepsi, Dr. Pepper – and replace them either with water or diet sodas. In doing so, they’ll  be removing not just  liquid carbohydrates but specifically sugars — sucrose or HFCS. The same is true of fruit juices. An easy change in any diet is to replace fruit juices with water. Dieters will get rid of candy bars, desserts, donuts and cinnamon buns. Again, they may perceive this as calorie-cutting – and maybe even a way to cut fat, which it is – but they’ll also be cutting carbohydrates, and specifically sugars with their high fructose content. And if sugars with their high fructose content are uniquely fattening as significant evidence suggests, then this reduction in sugar content may be precisely why the diets work.  Starches like potatoes and rice, refined carbohydrates like bread and pasta, may also be replaced in these diets — even “low-fat” diets — by green vegetables and salads or at least whole grains, because for the past 30 years, we’ve been all told to eat more fiber and to eat foods that are less energy dense and less processed.

Even the very-low-fat diet made famous by Dean Ornish restricts all refined carbohydrates, including sugars, white rice and white flour. This alone could explain any benefits that result. Ornish’s rationale, as he described it in 1996 is a familiar one: “Simple carbohydrates are absorbed quickly and cause a rapid rise in serum glucose, thereby provoking an insulin response. Insulin also accelerates conversion of calories into triglycerides, [and] stimulates… cholesterol synthesis.”

Simply put, anyone who tries to diet by any of the more accepted methods (i.e., Weight Watchers), and anyone who decides to “eat healthy” as its currently defined, will remove the carbohydrates from the diet that may be — if the carbohydrate/insulin hypothesis is correct — the most fattening. And if they’re trying to cut calories, they’ll be removing some number of total carbohydrates as well. And if these people lose fat on these diets, this is a very likely reason why.

The same is likely to be true for those who swear they lost their excess pounds and kept them off by taking up regular exercise. Rare is the individual who begins  running or swimming or doing aerobics regularly with the goal of losing weight and then doesn’t make any concomitant changes in what he or she eats. Rather beer and soda consumption will be reduced; sweet consumption will be reduced, and easily digested starches and high-glycemic index carbs are likely to be replaced by green vegetables and carbohydrates with a lower glycemic index.

So here’s the lesson, the moral of this story: before we assume that low-carbohydrate diets are just one tool in the dietary arsenal against overweight and obesity, and before we assume that everyone is different and that some of us lose weight and keep it off because we eat less fat (and more carbohydrates) and some because we cut carbs (and so eat maybe more fat),  we should make an effort to understand the concept of controlling variables and look to see which variables are really changing and by how much. Because it’s quite possible that the only meaningful way to lose fat is to change the regulation of the fat tissue, and the science of fat metabolism strongly implies that the best way to do that, if not the only meaningful way, is by reducing the amount of carbohydrates consumed and/or improving the quality of those carbs we do consume.

Now, one note about comments that I should have made in my last (and first) blog. I appreciate everyone who comments, but time constraints (earning a living, participating in my family life, etc.) makes it necessary that I keep my responses to a minimum. So I am going to thank everyone in advance for their comments. I will be reading all of them (up to the point, at least, that they degenerate into arguments between two or three particularly vociferous and contentious individuals), but I will be responding only to those that raise particularly interesting questions or issues, or point out any bone-head mistakes I may have made that need to be fixed.

Filed Under: Bad Science, Diets, Obesity and weight regulation, Weightloss Diets

The Inanity of Overeating

December 4, 2010 777 Comments

My new book is coming out at the end of the month. It’s called Why We Get Fat and the subtitle is What To Do About it. The book concentrates more on the first because once you understand why we get fat, the what to do about it part is pretty obvious. And the problem is that the conventional wisdom on why we get fat is almost incomprehensibly naïve and wrong-headed.

My goals in writing the book, as I explain in an author’s letter, are to push the issue (I keep wanting to use the cliché, “throw down the gauntlet,” but as I get older I notice I keep wanting to use more and more clichés, and it’s a bad sign for a writer) on this nonsensical notion that we get fat because of overeating and sedentary behavior, and to distill down and extend some of the arguments from my previous book, Good Calories, Bad Calories, into a book that can easily be airplane reading on any flight covering more than one time zone.

In this blog, if it goes as planned, I hope to ask questions as much as provide answers. Over the past decade, as I’ve read more than a century’s worth of literature on obesity and nutrition and chronic disease, I’ve been consistently amazed at the ability of researchers, learned commentators (and the far greater ranks of unlearned commentators), physicians and public health authorities to accept some of the rote ideas about these excruciatingly important subjects without seemingly giving it any conscious thought whatsoever, or without wanting to ask the kinds of questions that a reasonably smart junior high school student should ask if given the opportunity. To this date, I don’t understand this failure of intellect, although I’ll almost assuredly be returning to it regularly in future blogs.

So what do I mean about overeating being a nonsensical explanations for why we get fat? I was just reading Jonah Lehrer’s latest column in the Wall Street Journal–“The Real Culprit in Overeating.”

Now Lehrer is one of the most talented science writers working today. I’m tempted to say one of the brightest young science writers, but that would be to do him a disservice. He’s as good as any of us at any age. But in this column he falls short, as he’s working outside his area of expertise. (A common problem with most science and health writers is that we often write about a different subject every week or month, so if we’re being fed nonsense by the local experts in any particular field we will typically pass that nonsense along to the readers because we don’t know enough not do otherwise.) The underlying assumption of Lehrer’s column is that we get obese because we overeat, and evidence of the fact that Americans eat too much is that a third of us are obese. Okay, so let’s take a look at this concept from a less than conventional perspective and see what questions we might naturally ask.

First, obese people tend to be weight stable for long periods of their life, just like lean people. So when they’re weight stable, the obese and overweight are obviously in energy balance. They’re not overeating during these periods of stable weight. They’re eating to match their expenditure, doing exactly what the lean do (and get copious credit for). So one obvious question is why the overweight and obese are only in energy balance when they’re carrying 10, 20, 30 or maybe 100 pounds of excess fat, and lean people are in energy balance without the excess? What’s the culprit for that? Because the problem isn’t that the obese overeat when they’re obese, it’s that they overeat when they’re lean and they continue to overeat until they become obese.

Second, let’s say you’re carrying around 40 pounds of excess fat and you put on that 40 pounds over the course of 20 years, as many of us do. When you’re in your late 20s, say, you’re still lean, and then, lo and behold, you celebrate your fiftieth birthday and you’re obese and your doctor is lecturing you on eating less and getting to the gym regularly (and probably writing you a prescription for Lipitor, as well). Now, if you gain 40 pounds of fat over 20 years, that’s an average of two pounds of excess fat accumulation every year. Since a pound of fat is roughly equal to 3500 calories, this means you accumulate roughly 7000 calories worth of fat every year. Divide that 7000 by 365 and you get the number of calories of fat you stored each day and never burned – roughly 19 calories. Let’s round up to 20 calories, so we have a nice round number. (In the new book I discuss this issue in a chapter called “The Significance of Twenty Calories a Day.”)

So now the question: if all you have to do to become obese is store 20 extra calories each day on average in your fat tissue — 20 calories that you don’t mobilize and burn — what does overeating have to do with it? And why aren’t we all fat? Twenty calories, after all, is a bite or two of food, a swallow or two of soda or fruit juice or milk or beer. It is an absolutely trivial amount of overeating that the body then chooses, for reasons we’ll have to discuss at some point, not to expend, but to store as fat instead. Does anyone – even Jonah Lehrer or the neuroscientists he consults – think that the brain, perhaps in cohort with the gut, is making decisions about how much we should eat, on how long we stay hungry and when we get full, so that we don’t overshoot by 20 calories a day. That’s matching intake to expenditure with an accuracy of better than 1 percent. (We consume, on average, about 2700 calories a day, so matching energy in to energy out and not overshooting by 20 calories requires better than one percent accuracy.) And, of course, if we only overshoot by ten calories a day on average, we’re still going to put on 20 pounds of excess fat in 20 years. So really when we talk about being in energy balance – or practicing energy balance, as the experts now like to say – we actually have to be perfect in our matching of intake to expenditure or we’re going to get inexorably fatter (or leaner, if we err on the side of going hungry), or at least we have to average perfection over decades.

One way to get around this is to assume that we overeat by this trivial amount for a few years on end and then we realize we’ve put on five or ten pounds – maybe our clothes no longer fit well or we’ve had to let out the belt a notch or two – and then we decide to undereat every day for however long it takes to make up for it. So now we walk away from the table hungry until all is back to leanness. But then how do animals do it? They don’t have mirrors or clothes to tell them they’re getting fat, and the world is full of animals that have plenty of food available all year round, plenty of opportunity to overeat if they want to and do so long enough to get chubby. And yet the only animals that get chronically obese are those that get their food directly from humans – in the laboratory, in the home or the zoo, or at the dinner table, since humans happen to be animals, too.

Considering the fact that not getting fatter year in and year out means literally matching energy in to energy expended without error for years on end, do we really think that this job is done by the brain, by either conscious behavior, or some system that listens to signals from the body and then puts a halt on eating behavior when it decides enough food has come in that the amount so far expended or likely to be expended in the near future is about to be exceeded? Here’s the idea: your gut is sending signals to this monitoring system in the brain and that monitoring system is tallying up calories consumed until it finally senses that it’s near the limit of intake. Uh oh, it’s thinking, that last bite of that hamburger is not going to be expended, abort abort! Put down the fork! Walk away from the table!

If you were designing an organism that didn’t accumulate excess fat in the fat tissue (in other words, any organism that isn’t human or isn’t getting fed by humans, directly or indirectly) would you leave it up to a different organ entirely, an organ off-site so to speak (the brain), to assure that calories consumed matched calories expended, so that no excess energy managed to somehow sneak into the fat tissue, without the fat tissue having any say in the matter? Or would you give the regulation to the fat tissue itself and let it do the job?

The reason people believe we get fat because of overeating and sedentary behavior is because they believe the laws of thermodynamics somehow dictate this to be true. In particular the first law, which tells us that energy is conserved, so if a system takes in more energy than it expends, the energy contained in the system has to increase. If that system happens to be our fat tissue, than the fat tissue accumulates fat. That’s the logic. So if we eat more than we expend, we get fatter and the logic turns this around to say that we get fat because we eat more than we expend. And so, overeating and sedentary behavior are the causes. This is the logic that leads virtually every government health agency and independent health organization (the AHA, the AMA, you name it) to have some variation of this World Health Organization statement on its website or in its promotional material: “The fundamental cause of obesity and overweight is an energy imbalance between calories consumed on one hand, and calories expended on the other hand.”

But now imagine that instead of talking about why we get fat, we’re talking about a different system entirely. This kind of gedanken (thought) experiment is always a good way to examine the viability of your assumptions about any particular problem. Say instead of talking about why fat tissue accumulates too much energy, we want to know why a particular restaurant gets so crowded. Now the energy we’re talking about is contained in entire people rather than just the fat in their fat tissue. Ten people contain so much energy; eleven people contain more, etc.. So what we want to know is why this restaurant is crowded and so over-stuffed with energy (i.e., people) and maybe why some other restaurant down the block has remained relatively empty — lean.

If you asked me this question — why did this restaurant get crowded? — and I said, well, the restaurant got crowded (it got overstuffed with energy) because more people entered the restaurant than left it, you’d probably think I was being a wise guy or an idiot. (If I worked for the World Health Organization, I’d tell you that “the fundamental cause of the crowded restaurant is an energy imbalance between people entering on one hand, and people exiting on the other hand.”) Of course, more people entered than left, you’d say. That’s obvious. But why? And, in fact, saying that a restaurant gets crowded because more people are entering than leaving it is redundant –saying the same thing in two different ways – and so meaningless.

Now, borrowing the logic of the conventional wisdom of obesity, I want to clarify this point. So I say, listen, those restaurants that have more people enter them then leave them will become more crowded. There’s no getting around the laws of thermodynamics. You’d still say, yes, but so what? Or at least I hope you would, because I still haven’t given you any causal information. I’m just repeating the obvious.

This is what happens when the laws of physics (thermodynamics) are used to defend the belief that overeating makes us fat. Thermodynamics tells us that if we get fatter and heavier, more energy enters our body than leaves it. Overeating means we’re consuming more energy than we’re expending. It’s saying the same thing in a different way. (In 1954, the soon-to-be-famous — and often misguided, although not in this case — nutritionist Jean Mayer said that to explain obesity by overeating was about as meaningful as explaining alcoholism by overdrinking, and merely reaffirmed, quite unnecessarily, the fact that the person saying it believed in the laws of thermodynamics.) Neither happens to answer the question why. Why do we take in more energy than we expend? Why do we get fatter?

Answering the “why” question speaks to actual causes. In the restaurant analogy, okay, maybe this restaurant has particularly great food, or it’s happy hour; the drinks are cheap. Maybe it’s pouring outside so a lot of people ran into the restaurant to stay dry. Maybe every other restaurant in the neighborhood, including our lean restaurant down the block, was recently closed by the local health bureau and this is the only one that didn’t have cockroaches in the kitchen and so remained open. Maybe it’s in the theater district and the shows just got out and now every restaurant in the neighborhood is packed with the post-theater crowd. Maybe the word has spread that Brad Pitt and Angelina Jolie frequent this restaurant regularly, or Oprah, and this attracted a crowd hoping for a glimpse of celebrity.

All these would be valid answers to the question we asked. Some speak to the conditions inside the restaurant (the quality of the food, the price of the drinks, celebrity customers); some speak to conditions immediately outside (a rain storm, no competition, the theater schedule). They all provide the causal information we’re seeking. They answer the “why” question. That more people are entering than leaving doesn’t. It’s what logicians call “vacuously” true. It’s true, but meaningless. It tells us nothing. And the same is true of overeating as an explanation for why we get fat. If we got fat, we had to overeat. That’s always true; it’s obvious, and it tells us nothing about why we got fat, or why one person got fat and another didn’t.

Some obesity experts are intuitively aware of this problem, which is why they’ll say, as the National Institutes of Health does on its website, that “Obesity occurs when a person consumes more calories from food than he or she burns.” By using the word occurs, they’re not actually saying that overeating is the cause, only a necessary condition. (It’s like saying “a crowded restaurant occurs when more people enter than leave.”) They’re just saying that when one thing happened – obesity –the other thing also happened – consuming more calories from food than we expend. And now it’s up to us to say, okay, so what? Aren’t you going to tell us why obesity occurs? Rather than tell us what else happens when it does occur.

As for the great majority of experts who say (and apparently believe) that we get fat because we overeat or we get fat as a result of overeating, they’re the ones making the junior-high-school-science-class mistake: they’re taking a law of nature that says absolutely nothing about why we get fat and assuming it says all that needs to be said. This was a common error in the first half of the 20th century. It’s become ubiquitous since.

If the experts had ever been open to a little skeptical thinking from others or had they been appropriately skeptical themselves, this might never have happened. What’s been needed (and still is) was for someone (a reasonably smart 14-year-old would suffice) to ask the obvious questions and then insist on intelligent answers. Here’s how such a dialog might go:

The experts: Obesity is caused by over-eating, by consuming more calories than are expended. There’s no getting around the first law of thermodynamics.

Us: But all that law says is that if somebody gets fat, they have to consume more calories then they expend. So why do they do that?

The experts: Because they do.

Us: That’s not a good enough answer.

The experts: Well, maybe they can’t help themselves.

Us: Why can’t they help themselves?

The experts: Because they can’t.

Us: That’s not a good enough answer either.

The experts: Because the food industry makes them do it. There’s so much good food around and it’s so tasty, they can’t help but eat it.

Us: But obviously some of us can, because we don’t all get fat. Why is it only some people can’t help themselves?

The experts: Because they can’t.

Us: Try again.

The experts: Well, it’s complicated.

Us: What do you mean complicated? We thought it was easy. Just this eating-too-much, exercising-too-little, calories-in-calories-out, thermodynamics thing.

The experts: Okay, how about this? [Now quoting from an NIH report published in 2000.] “Obesity is a complex, multifactorial chronic disease that develops from an interaction of genotype and the environment. Our understanding of how and why obesity develops is incomplete, but involves the integration of social, behavioral, cultural, physiological, metabolic and genetic factors.”

Us: So what do all those have to do with eating too much and the laws of thermodynamics?

Experts: They contribute to making fat people overeat.

Us: How do they do that?

The experts: We don’t know. It’s complicated.

Us: Then maybe there’s another way to look at it. Maybe when we get fat it’s because those physiological, metabolic and genetic factors you mentioned are dysregulating our fat tissue, driving it to accumulate too much fat, and that’s why we eat so much and appear — to you anyway — to be kind of lazy. We’re compensating for the loss of calories into our fat.

The experts: Yeah, well, maybe. Your guess is as good as ours.

Filed Under: Bad Science, Calories-in-Calories-out, Obesity and weight regulation