Sunday, October 8, 2017

Can taking vitamin D help women burn more fat?

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Sorry I've been AWOL these last six months. Life, as you well know, gets busy and things get in the way. Blogging is a hobby for me, though. I have no aspirations to monetize or grow this practice, per se. Frankly, I'll be surprised if you're still reading. Props for your patience, though, if you are.

Of course, despite life's business, I have been keeping up with various bits and pieces of the scientific literature. As much as is possible, anyway, what with school and work and my recent engagement - I asked, he said yes! In any event, allow me to pander to something other than my rather uninteresting personal life, like... fat loss from a pill? One could only hope.

Salehpour, et al. (2012) purports to show that, after 12 weeks of vitamin D supplementation, 39 "healthy" overweight, non-pregnant/non-lactating females lost more body fat than did a parallel cohort of 38 representatively similar overweight females taking a placebo.

First, everything was free-living and self-reported, but what else is new in diet-related research? So, naturally, all the same standard limitations apply, here. Second, although this was a supplement trial, they collected food-frequency questionnaires (FFQ) and 24-hour dietary records to try to ensure standardization across the board, so that nobody was getting away with significantly lower food intakes, skewing the statistics in favor of one arm or another, for instance. (They also tried to standardize physical activity, as well.) Per usual, these techniques are quite poor, however "validated" nutrition scientists claim they are. If you don't already understand why this is, Schoeller, et al. (2013) provide a good explanation. Luckily, we don't need them to be great for this particular study, and I'm glad they tried to do something to standardize the groups - sometimes, a little something is better than nothing. And they did claim to have counted how many of the pills each participant, in both the intervention and placebo arms, had consumed at weeks 4 and 8, and adherence was estimated to be roughly 87%. You might be tempted to complain that this number isn't higher, but it might as well be 90%, and a score of 9/10 (essentially an A-) is pretty darn good. What little added benefit one might have achieved, hypothetically, with one extra dose which was accidentally skipped when rushing out the door in the morning for work, is probably small enough for our purposes as to not be worth considering. Asking people to give A+ effort at all times simply doesn't happen in the general populous. We are interested in real life, after all. But there are other reasons to be skeptical of their resultant data, which I will cover momentarily.

Participants were randomly allocated from an 85-person list to receive either 25 mcg/day of cholecalciferol (vitamin D3) from seal oil or 25 mcg/day of lactose (placebo), although they do not mention how this randomization was performed (e.g. whether it was done by random number generation or some other such thing). This is a minor bellyache, but I still prefer to see all the data, and since the Nutrition Journal is open access and there are no page number limitations that I am aware of, there's really no excuse to publish papers without the full sequence of methods, laid out plainly for all to see and validate or even replicate independently if they'd choose.

The study went on for 90 days, or 12 weeks time. Subjects' food frequency questionnaires were reviewed once per month (the authors never mention coaching participants on their 24-h diet record to improve adherence there), so presumably three times throughout the course of the study, which means only the first two really mattered much for the purposes of keeping them on course, assuming it does so at all.

At baseline, the data from all randomized participants were normally distributed across all measures, with the exception of serum calcium and fat free mass (2.2 mmol/L vs 2.3 mmol/L, and 44 kg vs 46 kg, respectively). These figures are even enough such that I'm not sure it matters. One rather important measurement these authors did not get was resting metabolic rate (RMR), which they admit in the discussion.

Over the life of this study, eight participants dropped out for various reasons, which brought the sample down from 85 to 77 persons. No big deal. But, then, instead of having to cope with these drop outs, the noise in the system as it were, by following through with their originally proposed intention-to-treat analyses, the authors decided to supplant this with a per-protocol analysis instead, which means they only incorporated and analyzed data from those who actually completed the intervention and adhered to the protocol as was asked of them. Ranganathan, Pramesh, & Aggarwal (2016) do a good job of explaining why this approach can be problematic, but, essentially, doing only the per-protocol analysis introduces bias both in the randomization and in subsequent interpretations of the data.

Common though it is, unfortunately, the authors did not report much in terms of their statistical analyses, but merely posited an alpha (statistical significance) of p < 0.05, utilized analyses of covariance (ANCOVA) for biochemical variables**, and then performed Pearson correlation coefficients to try to show some kind of a relationship between 25(OH)D/iPTH and body fat mass. I'd like to have known explicitly what their 1 - B (statistical power) was, but I can only assume it was set at 0.8 (80%), as most of these trials tend to be. Working off of this assumption, an alpha of 0.05 and 1 - B of 0.8 would make the Cohen's d (effect size) approximately 0.32, which translates to a Pearson correlation coefficient (r) of 0.16, a very small linear relationship, at best. (For those interested, a d of 0.32 and an r of 0.16 would equal a number needed to treat (NNT) of approximately 11, meaning 11 people would have to be treated with this supplement in order for 1 person to glean whatever benefits there might be, assuming there are any.)

**I must say, I am happy to see that the authors knew the importance of quantifying biochemical variables in the serum (vitamin D, PTH, etc.) and correlated them back to the outcome measures of interest. It seems self-evident that this ought to be done, but you might be surprised at how many studies purport to show that a supplement, drug or substance does or does not produce some benefit or harm, when the authors never actually measured its concentrations in the serum, and so we actually have no idea what they're "measuring" at all.

So what were their results?

Serum 25(OH)D levels increased in the intervention arm, as would be expected, since 25 mcg/day is about 1,000 IU, which brought their serum values from roughly 15 ng/mL at baseline to approximately 30 ng/mL at the end of the study. 1,000 IU isn't an awfully large amount by common standards, but was probably a reasonable dose. It also strikes me that the subjects initial values were very low (< 20 ng/mL). Should we really be looking at two separate trials, here? One to demonstrate the efficacy of this kind of intervention in people with normal 25(OH)D levels, and another to demonstrate whether it is efficacious in those with abnormally low levels of 25(OH)D, such as the participants in this trial? Something to ponder, anyway.

Whereas serum iPTH values decreased slightly in the intervention arm (-0.26 pmol/L), they increased slightly in the placebo arm (0.27 pmol/L), p < 0.001.

Body weight change was minuscule and non-significantly different between groups, where the intervention arm lost -0.3 kg (or 0.7 lb.) and the placebo arm lost -0.1 (or 0.2 lb.).

They seemed to be suggesting that waist circumference was somehow meaningfully different between groups, where the intervention arm lost 0.3 cm around the waist, while the placebo arm gained 0.4 cm, but this was a non-significant change with a p < 0.38. Besides, even if this was statistically meaningful - and it's not - after 12 weeks of fairly religious pill popping, we're talking about a difference of less than one centimeter, here!

Hip circumference decreased in both groups, although non-significantly (-0.39 cm vs. -0.9 cm for intervention and placebo arms, respectively; p < 0.36).

Body fat mass supposedly decreased in both groups, where the vitamin D group (intervention arm) supposedly lost 2.7 kg (~6 lb.), and the placebo arm supposedly lost 0.4 kg (~1 lb.). So, let me get this straight: there's an 0.5 lb. difference in body weight between arms, but a 5.0 lb. difference in fat mass between arms? How on earth is that possible? Did the average subject in the intervention arm both lose 6 lb. of fat and gain 5+ lb. of muscle in 12 weeks? Give me a break. How much of this purported change could easily be explained away by the fact that the researchers used bioelectrical impedance to estimate body fat percentage in order to calculate these fat mass values? That would be my primary contention. So, no. I don't buy it. Perhaps if their body weights were also at least somewhat reflective of this kind of change. (But, no cigar.)

They claim to have demonstrated statistically significant inverse Pearson correlation coefficients (r) between the changes in 25(OH)D in serum and body fat mass (r = -0.319) from baseline - which was only significant in that it achieved a p < 0.005, in my view - and changes in iPTH in serum and body fat mass (r = -0.318) from baseline - which also achieved a p < 0.005. On the flip side, they also claim to have demonstrated a positive r between the changes in serum iPTH concentrations and body fat mass from baseline (r = 0.32, p < 0.004). However, that these values were statistically significant, doesn't change the fact that the correlation coefficients were small, as can be seen in the scatter plots provided below.

Lastly, they say they've shown that changes in these values correlate linearly with the outcomes posited above, yet their last statement in the results section states:

How in the world could it be that changes in 25(OH)D and iPTH were linearly correlated with fat mass, while serum 25(OH)D and iPTH concentrations were simultaneously not correlated with fat mass?

It took me a while to realize that, although there was apparently some kind of a linear relationship between the serum changes (from baseline) of these values to the outcomes they've posited above, the actual serum concentrations of 25(OH)D and iPTH at any given moment were not linearly correlated to these same outcomes. (And notice how they didn't give a value for r or an alpha for this last measure. Bit sneaky, if you ask me.)

And, ultimately, what do you think these scatter plots and correlation coefficients would look like, if the authors had kept their analyses true to the original intention-to-treat?

I'll say it, again: I don't buy it. Do you? Until next time.

~ ~ ~ ~ ~ ~ ~ ~ ~ ~ ~ ~ ~ ~ ~


Ranganathan, Pramesh, & Aggarwal. (2016). Common pitfalls in statistical analysis: Intention-to-treat versus per-protocol analysis. Perspectives in clinical research. 7(3), 144-146.
Salehpour, et al. (2012). A 12-week double-blind randomized clinical trial of vitamin D3 supplementation on body fat mass in healthy overweight and obese women. Nutrition Journal, 11, 78.
Schoeller, et al. (2013). Self-report–based estimates of energy intake offer an inadequate basis for scientific conclusions. The American journal of clinical nutrition. 97(6), 1413-1415.

Sunday, April 16, 2017

Does eating too much, too often increase liver fat?

Possibly, but this trial doesn't give us the answer....

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It has been postulated that a major proximate cause of non-alcoholic fatty liver disease (NAFLD) - ignoring hepatitis C infection and things of that sort - is obesity itself (Yilmaz & Younossi, 2014). Since we're told obesity is "caused by an imbalance in energy intake versus expenditure," it must be that NAFLD is caused by a sustained increase in intrahepatic triglycerides (IHTG), due to a general overconsumption of Calories.

Fair enough. But, for now, I'm not interested in getting into whether or not a specific nutrient, or lack thereof, is on the hook for contributing to fatty liver disease per se, or whether or not an overconsumption of calories in itself is sufficient to cause it. What I am interested in, however, is the question posed in an article by Koopman et al. (2014) inquiring into whether or not hypercaloric between-meal snacking might lead to more IHTG accumulation, independent of the Caloric or macronutrient content of the diet, which is in fact what they ended up concluding in their Discussion section.

It's a bold claim, that between meal snacking independently predisposes to NAFLD - which, if you follow their line of reasoning to it's logical conclusion, is effectively the underlying implication of this idea. I want to discuss this trial in particular, because it purports to be the first of its kind. A human intervention study showing that snacking increases IHTG and intra-abdominal fat mass had never been reported, before it. Yet, that's what these authors claim to have done, here. So, let's see what they did.

Most of my concerns and comments will be those typed in red, below.


Two important things, right out of the gate:

First, this study purports to be a randomized controlled trial, testing the effect of various dietary interventions against a control group. I will come back to this, but I don't consider this study properly randomized or adequately controlled. It is, in my estimation, a glorified observational study, whose conclusions are meager at best, and, at worst, totally unwarranted.

Secondly, since this was not a metabolic ward experiment, but a free-living study, the results must be interpreted with caution, since there is little opportunity for anyone to validate whether or not the participants adhered in any meaningful way to their respective interventions (or lack thereof).

  • 37 lean (mean BMI: 22.5), otherwise healthy (no NIDDM) young men (mean age: 22 years)
All studies have limitations, and this one is no different. It will contain its fair share, and that's fine. Depending on what it is, a limitation needn't necessarily be a trial-ruiner. That said, it's important to recognize the first, which is that, should these results wring true in the end, these data may not be extrapolated and applied to women, geriatric or pediatric populations, persons of other ethnicities, and possibly individuals with acute or chronic disease; the mechanisms alluded to may have radically different molecular implications for obese or ill individuals. Therefore, although they could be interesting to a young, healthy, 20-something year old male, the generalizability of these data outside of that cohort are already of a "low-to-no" sort.

Exclusion Criteria:
  • Eating disorders, psychiatric disorders, type II diabetes, an "unhealthy ad libitum diet," (according to Dutch guidelines), and exercising > 3 hours/week
It may be worth considering that the Dutch guidelines have asked people to consume a largely plant-based diet. The notion that a more carnivorous or meat-based diet may lead to more IHTG or NAFLD has, as far as I am aware, never been demonstrated, thus making this exclusion criteria somewhat strange in my view. Then again, as with anything, there are some good things about their guidelines, and I suspect they wanted some kind of a baseline to iron out any significant fluctuations in intergroup diet variability.

The idea that these young, healthy guys were told to remain sedentary and refrain from vigorous physical activity for more than 3 hours per week is a little funny, although I get why they asked it of them. But do we believe that each of these 37 subjects complied with this 3 hour per week exercise maximum? They were all lean and prone to spontaneous activity, and might have easily forgotten about, misunderstood, underestimated or even just not cared much about the importance of this aspect of the study - and it is important. Yet, since this is a free-living study, there's no way to know for sure that they weren't doing more. Even if everything were perfect, and these results held true, who's to say that it isn't simply the case that a more frequent overconsumption of Calories contributes to increased IHTG only in the absence of concomitant exercise, or if one is sedentary? Then, the implication would be less relevant to diet and geared more toward a recommendation to increase physical activity. Of course, this question would require a separate trial altogether to answer, however, I still think it's worth considering.

Study Design:
  • 37 subjects were split into 5 groups:
    • control group consumed their usual, baseline diet
    • one intervention group consumed their usual diet plus a high fat, high sugar supplement, which they were was asked to consume with their meals, ensuring (at least hypothetically) that they were not snacking between meals. This arm was labeled: high fat, high sugar-SIZE (HFHS-S)
    • a second intervention group consumed the same aforementioned supplement, but were asked to consume them as snacks, 2-3 hours after their daily meals, instead of with them. This arm was labeled: high fat, high sugar-FREQUENT (HFHS-F)
    • a third intervention group consumed their normal meals, plus a high sugar supplement (devoid of Calories from protein or fat), which they were asked to consume with their daily meals. This arm was labeled: high sugar-SIZE (HS-S)
    • a fourth intervention group consumed their normal meals, plus the same aforementioned high sugar supplement, but, as with group two, were required to consume these as snacks, 2-3 hours after each meal. This arm was labeled: high sugar-FREQUENT (HS-F)
  • Subjects were asked to consume three meals per day and three supplement drinks per day
  • In theory, following these requests should have led to a 40% increase in Calories (1.4 x REE)
    • The HS-S and HS-F drink (x3/day) was essentially just = 3,000 mL of any one of a variety of nutritionally comparable sugar-sweetened sodas. (e.g. Coca Cola, Pepsi, etc.)
      • HS-S and HS-F drinks contained:
        • 43.3 kcal/100 mL x 10 x 3 servings/day = 1,299 kcal/day
        • 10.3 g sucrose/100 mL x 10 x 3 servings/day = 309 g sugar/day
    • The HFHS-S and HFHS-F drink (x3/day) contained:
      • 240 kcal/100 mL x 3 servings/day = 720 kcal/day
      • 9.6 g casein protein x 3 servings / day = 28.8 g protein/day
      • 9.3 g fat x 3 servings/day = 27.9 g fat/day
      • 29.4 g carbohydrate x 3 servings/day = 88.2 g carbohydrate/day
  • This study was undertaken for six weeks
    • Anthropometric measurements, laboratory testing and intensive counseling were said to have been implemented weekly to attempt to account for any inconsistencies in subjects' compliance with the protocol

Note that all four intervention diets are high sugar. There are no purely high fat intervention arms, thus precluding any conclusions about high fat intake under hypercaloric conditions contributing to IHTG one might want to make.

It may be worth mentioning that, considering the sugar-sweetened beverages in the HS-S/F groups were comprised of added sucrose, the subjects' fructose consumption should have been approximately 154.5 g/day. This is significant, given the impact we think the chronic overconsumption of fructose might have on hepatocytes (Ouyang et al., 2008). Therefore, it might have been wise to study this in such a way that only glucose or only fructose was being manipulated. This seems to add another confounder to the mix.

Perhaps my biggest problem with this aspect of the methodology is that they've presented the intervention groups as all being in a hypercaloric phase of 1.4 X REE, or 140% of their normal diet in terms of Calories, and that each group would be isocaloric. Yet, given the figures presented above, the HS-S/F arms should have been consuming a mean 579 kcal/day more than the HFHS-S/F arms. By the end of the trial (42 days), this would have amounted to about 24,318 kcal, between groups, assuming 100% dietary compliance. Assuming stable BMR for all subjects, this should come out to be roughly 7 lb. of fat gained over and above the HFHS-S/F intervention arms, given ~3,500 Calories per pound of fat. But what was the actual difference in weight gained? None; or, rather, no statistically significant difference was detected. Something doesn't add up. Shall we simply assume subjects were noncompliant with the protocol?

Statistical Methods:
  • The authors of this paper had published a previous report - one I have not yet read through - from which they determined their prior; an effect size of 0.46, predicated on previous data demonstrating that a hypercaloric diet increased HOMA-IR by 0.46 +/- 0.17. (Brands et al., 2013)
  • From this predetermined effect size, they reasoned that they would need 7 subjects per group to maintain a statistical power of 0.8 (80%) for an alpha level or significance set at p < 0.05, in order to detect statistically meaningful differences in insulin sensitivity between groups
Already violating the 7-person-per-group rule, the Control group only had 5 subjects. Then again, as will be discussed shortly, the controls were never compared to the intervention arms in the final analysis....
  • Subjects were "randomly allocated" to five groups via simple, non-stratified lot drawing. The randomization process was not blinded.
  • To determine normal distribution curves, they did normality testing, prior to paired Student t tests. Otherwise, they used Wilcoxon matched pairs. Between-group differences were analyzed with two way ANOVA and then post-hoc Bonferroni.
It is true that with an effect size (Cohen's d) of 0.46, a Power (1 - B) of 0.8 (or 80%) is right on the money, but only if the n = 37, in the final analysis. However, if you look at what they did after random allocation, they dropped three participants from the trial. Two, for "uncertain diet compliance," and one for alcohol abuse. Fine, but then they added two subjects, after that. They just added a couple folk, and that's all they say about it, anywhere. Not only were subjects not blindly allocated to intervention groups, which itself is problematic (Dettori, 2010), the run in and diet protocol phases of the study were complete before they just plopped two new guys in the analysis. Not okay. All trials lose people, that's why you shoot for a larger n, from the start, to account for this loss to follow up. But, you don't get to just add new guys to the mix, after the fact, because you feel like it.

Suppose we now calculate a new Power, for Cohen's d of 0.46, knowing that we've lost three and then gained two subjects. This obviously leaves us with a total of 36 participants, rather than 37. If you do the calculations, this brings the study's Power down from 0.8 to 0.79 (79%). That's not terrible, although the estimated type II error rate is approximately 21%. This is somewhat typical, but then if you notice that they didn't actually analyze the control group in the final analyses, or compare their results to those of the four intervention arms by the end, we must conclude that the true n is really 32. Your n is only your analyzed n. This makes the study significantly more underpowered, bringing the original (1 - B) of 0.8 down to (1 - B) = 0.74 (74%). It also increases the type II error rate to ~26%.

Furthermore, the overall Power is even further reduced, in the end, due to the repeated Bonferroni corrections (Nakagawa, 2004). I liked that they thought to do this, in that Bonferroni corrections attempt to account for multiple comparisons. The problem, as described by Nakagawa (2004), is that the more of these one completes, the lower (1 - B) tends to become. And (1 - B) in the Koopman et al. (2014) trial was low to begin with.


  • BMI remained stable for all six weeks of the trial
  • "Caloric intake and intake of specific macronutrients were stable during the observational period (data not shown)"
Of course they're not shown, these data are assumed.
  • IHTG content, abdominal fat, insulin-mediated suppression of EGP, and peripheral rate of disappearance of glucose (Rd) were not statistically different after the observational period
  • "Control subjects were included to show reproducibility of the measurements only and are therefore not further analyzed"
In other words, these five subjects were not analyzed alongside the other 32, thus bringing (1 - B) down, as I've described above. This is the only pertinent information we are given about the control group. What I would like to have seen, and what I think would have constituted a true control arm, is to compare these data with results from the intervention groups. I cannot help but wonder why they chose not to?

Food Intake:
  • Caloric intake between intervention groups was considered equivalent
This is incorrect. Take a few moments to work through the math:

If the HFHS arms are consuming their Nutridrink Compact supplement x 3/day, at 240 kcal a pop, this equates to 720 kcal per day. On the other hand, if the HS arms are consuming their soda in 1,000 mL units, at 433 kcal x 3 drinks/day, this equates to a total of 1,299 kcal. As I said before, this is a difference of 579 kcal. In what world is that equivalent? And yet, inter-arm participants equaled out to roughly the same weight, BMI and fatness, in the final analysis? I am left wondering whether the authors made an error in the report, the subjects were noncompliant with their protocols, or something similar.

Even if, in the end, it was demonstrated that consuming one of the HS diets led to greater increases in IHTG, we wouldn't be able to tell whether or not this was a product of the diet composition, meal frequency, or merely by virtue of the sheer difference in Calories they were consuming above the other interventions.

BMI and Resting Energy Expenditure (REE):
  • Subjects gained a mean 2.5 kg (5.5 lb.) over the course of the 6 weeks
If the subjects were consuming their diets precisely as described, the HS groups should have gained more fat than the HFHS groups over the same six weeks. Again, this points to noncompliance (or some other error in reporting).
  • All subjects' BMI increased, and there were no differences between them
  • REE did not change in any of the intervention groups, throughout the 6 weeks
Intra-Hepatic Triglyceride (IHTG):
  • "IHTG significantly increased in the HFHS-F and the HS-F groups"
  • "The increase in IHTG tended to be higher in the HS-frequency group"
I take issue with "tended to be higher." Statistically significant figures are only significant if they've actually reached significance! Trending toward significance is just a sneaky way to imply that an alpha level wasn't reached, but came close. Sorry, no cigar. That's not how this stuff works. The result of a significance test is either significant or it isn't. A non-significant finding is just that. (In this case, the purported "increase in IHTG... in the HS-F group" was p < 0.07.)

0.07 =/= 0.05

It's true that the result of a significance test could be statistically non-significant, yet still be practically significant. Unfortunately, this was not the case for these data. These results were meager, and may have actually been meaningless. Therefore, not only were their results statistically non-significant, they were also practically insignificant.
  • "In the two groups with increased meal size, IHTG did not change"
Abdominal Fat:
  • Total abdominal fat increased in the HFHS-F group
By a mere 0.1 kg or 0.22 lb. How clinically meaningful are we supposed to believe this is, assuming it's not just a statistical error?
  • Total abdominal fat tended to increase in the HS-F group
No. It was non-significant.
0.051 =/= 0.05
  • In the HFHS-S and HS-S groups, abdominal fat did not change
  • The increase in abdominal fat was not different between the two frequency groups
  • The increase in total abdominal fat was mainly caused by an increase in subcutaneous fat in both frequency groups
By a mere 0.035 kg (0.077 lb.). Of what practical significance is that?
  • (In the HFHS-F arm) visceral fat tended to increase, but was unchanged in all other groups
No. It was non-significant.
0.074 =/= 0.05

Glucose Metabolism:
  • Fasting glucose and EGP did not change
  • Fasting insulin levels slightly but significantly increased in the HS-S group only
By 12 pmol/L, going from 36 to 48 pmol/L
(A fasting insulin level < 174 pmol/L is generally considered to be within normal limits (WNL))
  • Hepatic insulin sensitivity (expressed as percent insulin-mediated suppression of baseline EGP) tended to decrease in the HFHS-F group only
No. It was non-significant.
0.083 =/= 0.05
  • Peripheral insulin sensitivity did not change in any of the diet groups
  • In the HFHS-F group insulin-mediated suppression of FFA significantly decreased
Only by 4.6%, and only in Step 1 of a two-Step analysis.

Glucoregulatory Hormones, Leptin and Plasma Lipids:
  • Plasma leptin concentrations increased in all diet intervention groups
All with the exception of HS-F, which was non-significant, at 0.075. (0.075 =/= 0.05) Fasting leptin increased a mean 1.25 ng/mL in all but the HS-F groups.

Fasting leptin levels are considered to be WNL when they are found to be < 15 ng/mL. It makes sense that leptin increased a little, given a few lb. of fat gain over the 6 weeks, but none of the intervention arms ever got over 5 ng/mL, and considering a well articulated argument by Askari, Tykodi, Liu & Dagogo-Jack (2010), fasting hyperleptinemia may act as an appropriate surrogate endpoint for identifying impaired insulin action. Thus, since Koopman et al. (2014) have claimed not only that hypercaloric feeding with more frequency induces more IHTG, but also that it induces insulin resistance, their own fasting leptin data seem to further combat this latter claim.
  • Glucoregulatory hormones did not change
  • Fasting triglycerides increased in the HFHS-F diet only
By a mere 0.28 mmol/L (a TAG level of < 1.7 mmol/L is considered desirable)

None of the participants ever got above 0.85 mmol/L, and thus were never hypertriacylglycerolemic.

(Overall) Meal Size vs. Meal Frequency:
  • BMI significantly increased in both groups
By a mere 0.7 kg/m^2... and none of the participants came close to approaching an overweight BMI of > 25 kg/m^2. 
  • Only increasing meal frequency significantly increased IHTG and total abdominal fat
By a mere 0.96%. According to Ress & Kaser (2016), if < 5% of hepatocytes are afflicted with an over-accumulation of IHTG, this is considered a Grade 0 on a 0-3 Grade scale. So, whether statistically significant or not, here, I would venture to guess that an increase of < 1% (and thus a Grade 0 on the aforementioned scale) isn't especially meaningful.
  • Only increasing meal frequency reduced insulin-mediated suppression of FFA
Sure, but only at Step 1 of a two-Step analysis, and only by 2.9%. Does that matter?


Finally, the first thing in this paper I agree with, 100%.

~ ~ ~ ~ ~ ~ ~ ~ ~ ~

My TL;DR Takeaway

Given the limitations in this paper - errors in random allocation, the addition of two random subjects with no additional information, the low statistical power and small sample size, a lack of individual participant data points, the fact that the control group wasn't compared to the intervention groups, mathematical errors in intervention arms, etc. - and the meager effects reported in the Results section, that even if you are a young, healthy 20-something year old male, you shouldn't concern yourself (based on these data alone) with reducing hypercaloric meal frequency, versus meal size, for the sake of preventing the accumulation of intrahepatic triglycerides.

A more straightforward and elegantly-designed trial with a larger n, better reliability, concealed randomization, and actually comparing intervention arms to controls, would be necessary in order to fully elucidate the answer to the initial question posed by Koopman et al. (2014). These hypothetical data would further need to be replicated and their results reproduced by an independent research group, before we could then decide that, indeed, disturbances in meal frequency such as those described above would be expected to increase liver fat stores, and potentially predispose to non-alcoholic fatty liver disease.


Askari, H., Tykodi, G., Liu, J., & Dagogo-Jack, S. (2010). Fasting plasma leptin level is a surrogate measure of insulin sensitivity. The Journal of Clinical Endocrinology & Metabolism, 95(8), 3836-3843.
Brands, M., Swat, M., Lammers, N. M., Sauerwein, H. P., Endert, E., Ackermans, M. T., ... & Serlie, M. J. (2013). Effects of a hypercaloric diet on β‐cell responsivity in lean healthy men. Clinical endocrinology, 78(2), 217-225.
Dettori, J. (2010). The random allocation process: two things you need to know. Evidence-based spine-care journal, 1(03), 7-9.
Koopman, K. E., Caan, M. W., Nederveen, A. J., Pels, A., Ackermans, M. T., Fliers, E., ... & Serlie, M. J. (2014). Hypercaloric diets with increased meal frequency, but not meal size, increase intrahepatic triglycerides: a randomized controlled trial. Hepatology60(2), 545-553.
Nakagawa, S. (2004). A farewell to Bonferroni: the problems of low statistical power and publication bias. Behavioral Ecology, 15(6), 1044-1045.
Ouyang, X., Cirillo, P., Sautin, Y., McCall, S., Bruchette, J. L., Diehl, A. M., ... & Abdelmalek, M. F. (2008). Fructose consumption as a risk factor for non-alcoholic fatty liver disease. Journal of hepatology, 48(6), 993-999.
Ress, C., & Kaser, S. (2016). Mechanisms of intrahepatic triglyceride accumulation. World journal of gastroenterology, 22(4), 1664.
Yilmaz, Y., & Younossi, Z. M. (2014). Obesity-associated nonalcoholic fatty liver disease. Clinics in liver disease, 18(1), 19-31.

Thursday, April 14, 2016

The benefits of exercise exist on a U-curve

Few would dispute the idea that intense exercise, as a hormetic stressor, is beneficial for improving human health. From reducing blood pressure and cardiovascular disease mortality rates, to aiding in the prevention of body fat accumulation after or during diet-induced weight loss, and more, exercise has innumerable, virtually unquestionable benefits. However, the type, volume and intensity of said exercise matters a great deal.

Many people begin with the supposition that there are "cardio" based exercises, like running and swimming, and "strength" based exercises, such as resistance training, as in a gym, lifting weights, or partaking in Crossfit, which is all-the-rage now. Sticking with this concept, endurance exercises, such as running, biking and swimming, can be classified neatly in the "cardio" category, and have been quite popular since about the 1970s. In the last few decades, one of the most common themes I have seen in individuals who proactively decide to go from living a traditional American lifestyle, to engaging in healthy lifestyle behavior changes, has been that of deciding to "run the marathon."

As I have not yet spent much time overseas, I do not know whether this is strictly a Western phenomenon, but it seems to me that if someone in our neck of the woods learns that something is beneficial, well, by golly, a whole lot more of it must be that much better. Implicit in this notion is that if running is good for my heart, then participating in an ultra-endurance activity like the Boston marathon should make me IronGirl.

Sorry, no cigar. The benefits of [endurance] exercise exist on a U-curve.*

*This is not to suggest that the benefits of resistance exercise do not also exist on their own U-curve. They very well might. I have just not seen any corroborating data, with respect to that question.

Just because something is healthy at one level of intensity, or by a certain volume, does not mean that if you ramp it up a few notches, it will confer the same benefit, let alone even more. Now, we could sift through an endless array of decently well-controlled studies that exist in the peer-reviewed literature touting the benefits of exercise, many of which have looked exclusively or predominantly at endurance training. But I should like, instead, to take a gander at some of the fascinating data demonstrating what might happen if we intentionally ramp up the intensity and volume of endurance exercise in both humans and experimental animals, and look at a few n=1 case reports of people who have voluntarily done the same thing, under the presupposition that because running is healthy, running a lot must be even healthier.

A few years ago, I randomly stumbled across this experiment, by Benito, et al, conducted in Barcelona, and published in Circulation,[1] where they took male Wistar rats and exposed a group of them to intensive 4, 8 or 16 week exercise regimes, while a Sedentary group got to essentially kick back and relax, and then compared the effects of the intervention on the rats' hearts.

Significant functional and morphologic changes occurred in the hearts of those rats in the Exercise group, after 8 weeks of intense training, such that, upon close postmortem inspection, they had marked increases in interventricular septum and left ventricular wall thickness. Statistically significant increases in overall cardiac hypertrophy was noted in the Ex group. Evidence of both left ventricular systolic and diastolic dysfunction occurred by week 8 and 16, respectively, based on echocardiographic results. (RV diastolic dysfunction was claimed evident, but was apparently not statistically significant, and so did not make much of an appearance in the paper, from what I could tell.) In contrast, of course, the Sed group of rats did not show any signs of these significant pathological changes, throughout the duration of the 16 week experiment.

Perhaps the most interesting thing, to me, since hypertrophy of the myocardium as a result of intense and chronic over-exertion is an anticipated, or at least relatively expected, outcome, was when the researchers then looked at the effects of this exercise regimen on "chamber-specific ultrastructural remodeling." A.k.a. The development of myocardial fibrosis.

Here is what they found:

"There is widespread interstitial collagen deposition with disarray of myocardial architecture." Aside from being a clever way to say, "These rat hearts are fucked, and this kind of training is probably not a good idea," (at least for Wistar rats) these results suggest that the formation of these fibrotic lesions may present a substantially increased risk of potentially fatal dysrhythmia -- this could be one possible explanation for the all-too-common ultra-endurance athlete who drops dead at 35 from sudden cardiac related death. So, naturally, that's precisely what their team looked for next.

According to figure 6, researchers were able to induce polymorphic ventricular tachyarrhythmias via ventricular stimulation in the Ex rats:

Luckily -- again, if you are an unreasonably trained Wistar rat -- there is an upside to all this. A period of "de-training" post-intervention could reduce the cardiac remodeling seen in this experiment, which may indeed mitigate the detrimental effects of the overtraining seen, here. There are some pretty big questions implicit in this, however. Such as, will this detraining benefit continue to exist, if the intervention period is stretched further? At what point will the negative effects of the intervention persist? What are the mechanisms involved in producing these effects? As the authors state in their discussion: 

The biggest question of all, as many of you reading this will have already been screaming at me for the last ten minutes, assuming you've made it this far, is... Will it translate to humans?

Here is where things get really interesting.

In 2011, Wilson and colleagues published a paper in the Journal of Applied Physiology[2] examining 12 veteran endurance athletes, many of whom had either completed 100 marathons or spent over ten years continuously training at an olympic level. This is about as close as I can imagine coming to an ecological replication of the Benito experiment, if ever I've seen one.

Although there are a few inherent limitations in its use, such as it "relies on the signal intensity difference between fibrotic and normal myocardial tissue, and hence a region of 'normal' nulled myocardium is needed as a reference to detect abnormalities,"[3] Wilson, et al, used late gadolinium enhancement imaging (LGE) to detect patterns of myocardial fibrosis in the study participants. 50% of them had diffuse patterns of myocardial fibrosis. These are people who are supposed to be healthier than all of us, especially due in large part to their exceptional athleticism. In spite of it, they actually appear to be worse off, at least with respect to the health of their heart muscle! (Age is a factor for some of the athletes studied in this trial, but age-matched controls were examined, and the age-confounder was set aside as an important contributor.)

The study was of course a small one, and so generalizability may be a factor of consideration. But think about it, though. This is not supposed to be representative of the population at large, but of a small subset of elite athletes. Therefore, the sample may in fact be sufficient to generalize, at least to other extreme endurance athletes. And remember, all 12 of these individuals were "otherwise healthy" at the outset of the study. None of them were smokers, as far as they were willing to admit to on the inclusion data. (Though, being that they were all males, translating these data to females may prove challenging. Gosh, we could really use some more data on female athletes...)

Although I found this study fascinating because it was almost like a real-life corroboration of Benito and colleagues animal study, this is not the end of the line for similar research in human beings. Oh, no. There's actually quite a bit more, following this same line of logic:

In 2012, Dr. James O'Keefe, et al, published a review in Mayo Clinic Proceedings[4] suggesting that, although the hypothesis warrants further research for substantiation, there is good human and animal data to suggest, at least on a preliminary basis, that excessive endurance exercise (EEE) may predispose susceptible individuals to adverse cardiovascular events, including arrhythmia and extensive myocardial fibrosis.

In a 2011 issue of the European Heart Journal[5], La Gerche, et al, describe their study of 40 endurance athletes, after the completion of a marathon, and suggest that "although short-term recovery appears complete, chronic structural changes and reduced right ventricular function are evident in some of the most practiced athletes..."

In 2010, Wilson, et al, published a study in the European Journal of Applied Physiology[6] demonstrating that long-term, high intensity endurance activity is strongly associated with maladaptive changes in cardiac morphology and electrical conductivity, among other physiologic and pathophysiologic alterations, even connecting it to implications with respect to brain function.

In 2013, Doutreleau, et al[7] showed that such chronic and excessive endurance training could have negative consequences on the conduction pathways in the heart, presumably through this remodeling and fibrotic changes in the myocardium. In their study, they report two cases of type II second-degree atrioventricular block in well-trained, otherwise healthy, middle-aged adult athletes.

Although merely a case report, and not a study, per se, in 2012, in the Journal of Athletic Training[8], Poussem, et al, describe a highly-trained, 30 year old cyclist with "nonsustained ventricular tachycardia originating from the left ventricle on a stress test associated with myocardial fibrosis of the left ventricle as shown with magnetic resonance imaging." The unique thing about this case report was that most often these findings are seen after sudden cardiac death (SCD), on autopsy. Presumably, the diagnosis in this instance is being relegated to an effect of intense, unrelenting endurance exercise, but, there are probably too many confounding variables in this particular instance to be able to say one way or another. It is particularly interesting, however, that it happens to line up quite nicely with the rest of the data, thus far. (Was the cyclist in this case a recreational drug user? Could that have caused or contributed to the pathology seen, here?) Still...

In 2008, published in the British Journal of Sports Medicine,[9] professor Whyte and colleagues ask the question whether exercise may or may not have been the cause of the idiopathic left ventricular hypertrophy and idiopathic interstitial myocardial fibrosis found during the autopsy of an "experienced, highly trained" marathon runner, who died suddenly while running.

Published in the British Journal of Sports Medicine back in 2007[10], Mitchell M. Lindsay and Francis G. Dunn conducted the first experiment, to my knowledge, demonstrating that, in veteran endurance athletes with left ventricular hypertrophy, there is "biochemical evidence of disruption of the collagen equilibrium favoring fibrosis... suggest[ing] that fibrosis occurs as part of the hypertrophic process in veteran athletes."

In 2011, La Gerche published another trial[11], this time with 39 endurance athletes and 14 controls, looking for evidence that intense exercise might be putting an exorbitant load on the right ventricle of the heart. Despite some inherent limitations, which they carefully outline in the paper, the following is what they found after careful analysis of the data:

On top of all the myocardial fibrosis business, there are other potential risks that have been outlined in the literature, since Benito and others' work. For instance, just this year, M Sanz de la Garza, et al, published a study in the Scandinavian Journal of Medicine and Science in Sports[12] looking to examine the potential impact of intense endurance training on multiple thrombotic risk factors, and claim that excessive endurance exercise may actually increase the chances of pulmonary embolism, through the development of deep vein thromboses (DVT), or clots in the legs. Unlike the mechanisms that may be involved in the development of cardiac morphologic changes via collagen recruitment in cardiomyocytes, etc., these are likely to be due to extraneous complications from overexercising; including dehydration, inflammation and, as they put it in the abstract of the paper, "hemoconcentration."

So, ultimately, what does this mean? Does this mean that I think cardio is uniformly "bad" and that you should stop partaking entirely? Do I think any and all forms of endurance training are unhealthy?

Uh... No. Wait, that wasn't good enough. Can I get a hell no, instead?

Look at the one consistency in all these data. Everyone studied (including the rodents!) were pushed -- or, rather, pushed themselves, in the vast majority of cases -- to the breaking point. There is an unimaginable difference between running a weak 2 miles per day and running 11 miles per day, at 80% of your purported maximum heart rate.

Will some regular, light endurance training destroy your heart? No! Will training at intensities similar to ultra-endurance triathletes destroy your heart? It's a little too soon to tell, but, it appears quite possible... so, again, what's "the answer?"

My recommendation would be to avoid participating in multiple marathons. Otherwise, I would be equally as concerned about the health of your heart muscle, if you remain seated on your love seat like a lazy slob eating Sun Chips all day, delicious though they are.

As I have said twice now, there is an undoubted U-curve associated with the benefits of [endurance] exercise. Too little is not good; way too much is also bad. My final recommendation? Adopt the Goldilocks principle of "just right" and you'll be good to go. But, whatever you do, please choose to move, rather than be a slug. "Eat less, move more" doesn't have to be "right" for me to know that exercise in appropriate amounts is incredibly beneficial and health promoting. The lesson in this post is more about what happens if you push it to an extreme on the spectrum -- and to suggest that, as with most things, there may be a sweet spot, somewhere in the middle, where a balanced approach confers the best results.

(Me? I'll stick with picking up heavy things and putting them back down, and the occasional sprint or HIIT session, here and there... but my rationale for that will have to wait. I've already kept you plenty long enough.)


1. Benito, B., Gay-Jordi, G., Serrano-Mollar, A., Guasch, E., Shi, Y., Tardif, J. C., ... & Mont, L. (2011). Cardiac arrhythmogenic remodeling in a rat model of long-term intensive exercise training. Circulation, 123(1), 13-22.
2.Wilson, M., O'Hanlon, R., Prasad, S., Deighan, A., MacMillan, P., Oxborough, D., ... & George, K. (2011). Diverse patterns of myocardial fibrosis in lifelong, veteran endurance athletes. Journal of Applied Physiology, 110(6), 1622-1626.
3. Karamitsos, T. D., & Neubauer, S. (2013). Detecting diffuse myocardial fibrosis with CMR: the future has only just begun. JACC: Cardiovascular Imaging, 6(6), 684-686.
4. O'Keefe, J. H., Patil, H. R., Lavie, C. J., Magalski, A., Vogel, R. A., & McCullough, P. A. (2012, June). Potential adverse cardiovascular effects from excessive endurance exercise. In Mayo Clinic Proceedings (Vol. 87, No. 6, pp. 587-595). Elsevier.
5. La Gerche, A., Burns, A. T., Mooney, D. J., Inder, W. J., Taylor, A. J., Bogaert, J., ... & Prior, D. L. (2011). Exercise-induced right ventricular dysfunction and structural remodelling in endurance athletes. European heart journal, ehr397.
6. Wilson, M., O’hanlon, R., Basavarajaiah, S., George, K., Green, D., Ainslie, P., ... & Nevill, A. (2010). Cardiovascular function and the veteran athlete. European journal of applied physiology, 110(3), 459-478.
7. Doutreleau, S., Pistea, C., Lonsdorfer, E., & Charloux, A. (2013). Exercise-induced second-degree atrioventricular block in endurance athletes. Medicine and science in sports and exercise, 45(3), 411-414.
8. Poussel, M., Djaballah, K., Laroppe, J., Brembilla-Perrot, B., Marie, P. Y., & Chenuel, B. (2012). Left ventricle fibrosis associated with nonsustained ventricular tachycardia in an elite athlete: is exercise responsible? a case report. Journal of athletic training, 47(2), 224.
9. Whyte, G., Sheppard, M., George, K., Shave, R., Wilson, M., Prasad, S., ... & Sharma, S. (2008). Post-mortem evidence of idiopathic left ventricular hypertrophy and idiopathic interstitial myocardial fibrosis: is exercise the cause?. British journal of sports medicine, 42(4), 304-305.
10. Lindsay, M. M., & Dunn, F. G. (2007). Biochemical evidence of myocardial fibrosis in veteran endurance athletes. British journal of sports medicine, 41(7), 447-452.
11. La Gerche, A., Heidbuchel, H., Burns, A. T., Mooney, D. J., Taylor, A. J., Pfluger, H. B., ... & Prior, D. L. (2011). Disproportionate exercise load and remodeling of the athlete’s right ventricle. Med Sci Sports Exerc, 43(6), 974-981.
12. Sanz de la Garza, M., Lopez, A., & Sitges, M. (2016). Multiple pulmonary embolisms in a male marathon athlete: Is intense endurance exercise a real thrombogenic risk?. Scandinavian Journal of Medicine & Science in Sports.

Monday, January 11, 2016

Are dietary carbohydrates required for building muscle?

The question I am concerned with asking is not so much "Is it possible to build muscle while eating very low carb," but more like, "Can I build an appreciable amount of muscle, without adding extra carbohydrates into my ketogenic diet?"

The important question is not necessarily "Is it optimal?" or "Is it the easiest way?" or "Is it the best way?" It is definitely possible, at the very least; I know this from first-hand experience, anecdotal though that is. It may or may not be optimal, I don't know. Nor, for the time being, does it matter much. Let us concern ourselves with one question at a time.

We want to know whether it is reasonable to expect, coupled with resistance exercise, a ketogenic diet to be appreciably anabolic, without additional carbohydrates. Can one accrue significant muscle mass with this approach, or do we require supplemental carbohydrates to make this happen?

If you are not immersed in today's exercise science dogma, you might find yourself wondering why supplemental carbs should be necessary for muscle building, at all. The hypothesis essentially goes as follows:

Carbohydrates stimulate the secretion of insulin; insulin is a highly anabolic hormone (one of its essential functions is to regulate tissue hypertrophy); therefore, driving insulin by eating carbohydrates around your workouts will accelerate muscle protein synthesis (MPS) and accretion on a greater scale than would have been possible without them.

Or, stated a different way:

Because carbohydrates stimulate insulin, and insulin is one of the body's most anabolic hormones, it is reasonable to think that, without the additional insulin secretion caused by the consumption and absorption of these carbs, muscle protein accretion on a very low carbohydrate diet will be minimal, blunted, or otherwise unlikely.

(AKA: Without supplemental carbs, and, therefore, bursts of hyperinsulinemia, building muscle mass while on a very low carbohydrate diet is unlikely to occur. That's the presumption, anyway.)

This latter proposition is, in a roundabout sort of way, how I've seen the argument formed, more times than not. In my opinion, there are a few important caveats to consider, with regard to this particular argument, before moving on.

a.) We are not just considering the potential effects of consuming a ketogenic diet, alone, on muscle protein synthetic rates, but as coupled with weight training (or some other form of resistance exercise), designed for skeletal muscle hypertrophy. Assuming dietary protein, and, therefore, the plasma free amino acid pool, is appropriately topped off, and exercise intensity sufficient to promote tissue growth and remodeling is present, is it reasonable to think that the amount of dietary carbohydrate matters all that much?*

*Remember, we are thinking specifically of intracellular (myofibrillar) hypertrophy, at the moment, not of myocyte bioenergetics and energy utilization to fuel specific workouts, per se. Let's not confuse fuels that may or may not be required to sustain certain types of contractions with fuels that may or may not maximize hypertrophy. As far as we can tell, right now, the exercise science literature seems to show, rather consistently, that carbohydrates are quite useful for sports performance purposes, and have their place, depending on the context and the activities in question. However, this may not be reflective of what metabolic fuels best suit muscular hypertrophy. (e.x. Elite long-distance runners and other high-volume endurance athletes typically consume large quantities of carbohydrates, yet remain quite... frail, for lack of a better term.* No offense intended, of course.)

*Just a random consideration, but, something to ponder: These ultra-endurance athletes are quite emaciated, despite large quantities of dietary carbohydrate and, thus, big bursts of hyperinsulinemia.... Hence my perspective that this popular conception of "more insulin = bigger anabolic response" is too simplistic.

b.) Oftentimes, for the sake of simplicity, we like to talk about "The" Ketogenic Diet, as though it is a single, uniform approach to nutrition. For the most part, this seems to be sufficient for the purposes of discussing very low carbohydrate diets versus diets higher in carbohydrate, in general. Naturally, however, distinctions must be made, when certain points of discussion or contention are brought up. In this situation, to say The ketogenic diet is not necessarily appropriate, because there is not just one approach to ketogenic dieting. There is the traditional, pediatric, anti-epileptic approach to ketogenic dieting that was low in protein, virtually zero carbohydrate, and even restricted water intake (for whatever reason). We are not talking about that. Nor are we talking about the kind of ketogenic diet that is used as a neuropsychiatric therapy, today, to keep glucose and glutamate low and insulin at bay, for neuronal health. Because I tend to occam's razor most things, where possible, I think we could simplify this into ketogenic diets that restrict protein as well as carbohydrates, and ketogenic diets that contain ample dietary protein.

In most circumstances, for healthy persons, it is my personal and professional opinion that it is unreasonable to suggest one should be asked to restrict dietary protein -- even for the purposes of keeping glucose and insulin at its absolute floor. (It is highly unlikely that you will experience souring plasma glucose excursions by eating 10 oz of chicken, instead of 3.5 oz of 80:20 ground beef.) Therefore, "the ketogenic diet" I am considering, here, with special regard to the aforementioned question(s) regarding muscular hypertrophy, include not only concomitant and consistent resistance exercise, but also an appropriate amount of protein to maximize hyperaminoacidemia.

c.) Lastly, I used the word "significant," earlier in the post, re: building muscle on keto. How much muscle are we talking about, here? Massive, Lee Priest-like, bodybuilding muscles are never built by anyone without (1) a genetic propensity, and a vast, inborn number of myocytes for it, or are (2) taking exogenous anabolic steroid hormones. Will the ketogenic diet help me in my unlikely pursuit to look like Ronnie Coleman? Not a chance. Then again, neither will a high carbohydrate, high protein, traditional bodybuilding-style diet, so...

I don't intend for that to come across as snarky so much as to say that it is imperative that for this discussion to have any meaning, we must first define our terms. What level of bulk are we considering "built," here? (I may have my own view on what constitutes built, and your view may differ significantly from that, maybe by a few orders of magnitude. For the sake of this argument, I'd like to use a pictorial example of what, in competitive bodybuilding circles, is considered a "physique" build. Below is a picture of a friend of mine. Although he is not a bodybuilder in the traditional sense, in that he isn't ridiculously massive, he is quite muscular and symmetrical, even after cutting down to a low body fat percentage. This is what I would consider sufficiently muscular to make this discussion worth having:

This is probably how I would distinguish muscular, in this context, because anything less can be construed as simply "lean" or "toned," and anything more might be taken to be "unachievable muscularity" for most normal people. You might disagree, and that's fine, but I'm simply putting this here as a point from which to argue from, for the sake of logic. It can't just be some up-in-the-air, random target post, on which none of us agree, or have even attempted to nail down. At least not if we can hope to achieve anything meaningful in having this discussion. Perhaps important to note is that Ari was not using a low carbohydrate diet to bulk, as far as I know. That is beside the point, however. The picture is meant to serve as a reference point, not evidence on behalf of my position.

From my perspective, most significant muscle building seems to occur, predominantly, as a result of two things: Amino acid availability, and consistent strength training, intense enough to maximally stimulate the muscle fibers and fatigue the motor units. Bing, bang, boom. Little to no evidence, from what I have seen, demonstrates a further need for carbohydrate to augment the process of muscle protein accretion.*

*I am not denying the anabolic effect of insulin. That would be silly. In fact, I am suggesting that perhaps the post-prandial insulinemia achieved by obtaining a nice big bolus of protein, post-workout, should be sufficient to induce this process.[1] (For the record, that wasn't really meant to be a sly reference to the "anabolic window," which is sort of a bunk concept.) Unless you are a type I diabetic producing so little insulin that if you don't inject it you will wither away and die, it is unlikely, in my opinion, that hyperinsulinemia to the degree that is presumed to be necessary from the aforementioned pro-high-carb camp is, in any way, a requirement for substantial skeletal muscle hypertrophy.

As you may have already noticed, this experiment looked at a 50 g bolus of protein, from chicken, as compared to a 50 gram bolus of glucose, and then a 50 g bolus of each, coupled together. As you can see, 50 grams of protein rather substantially increases serum insulin concentrations; quite similarly to dietary glucose alone. Recall, however, that, under the circumstances of most therapeutic ketogenic diets, people do not tend to consume 50 g boluses of protein in single meals. Hence, insulin levels may not go nearly that high. But, again, we are considering a very low-carb diet with more protein than is typical.

We know from metabolic ward overfeeding experiments -- even in sedentary people (or, more specifically "untrained individuals") -- that lean body mass (LBM) can increase concomitantly (though not necessarily proportionally) with adipose tissue growth, even in spite of lower protein intakes sometimes. Therefore, I contend that perhaps we are putting far too much stake on "what should I eat for growth?" Importantly, muscle building is about more than just diet. Arguably, more than anything else, it is about lifting; or otherwise maximally fatiguing the muscle tissue with resistance training. Are you sleeping like shit, always stressed out and constantly over-trained? Prepare for more muscle protein degradation, due to chronically elevated cortisol levels and a dysregulated circadian rhythm, even if your diet is considered well-formulated by some standard or other. A well-formulated diet is imperative for success in this area, of course, but, it is not the only component involved.

It has been hypothesized that poor sleep quality and sleep deprivation could both decrease the muscle protein synthetic response to exercise and protein ingestion and increase muscle protein degradation.[7] Speaking of lifestyle factors other than nutrition that impact muscle mass, cigarette smoking can impair muscle protein synthesis and may increase the expression of myostatin, a powerful muscle growth-inhibitor.[8]

Up until this point, much of the discussion has centered around anecdotes. In fairness, that's probably because there is little to no substantive and controlled data on muscular hypertrophy in the context of ketogenic dieting. In fact, I only know of one research group actively studying this specific area, right now. Whatever answer one chooses to accept must, if we are being honest, inevitably come from a piecing together of various data points from random, and sometimes seemingly arbitrary, trials, and then a commonsense summation of all the data.

Now, let's take a look at some relevant data.

Throughout my career in the fitness industry, nothing else has been claimed or cited as the gospel truth with more vehemency than the notion that there is an anabolic window that ends about 45-60 minutes post-exercise. That if you don't get all the protein and sugar in the world into your system within that period of time, the fucking moon will explode and Jupiter will shit molten meteorites that will fall into your grandmother's living room and kill her and your favorite childhood cat in one fell swoop. Basically, 30 minutes post-workout, you had better pound that protein shake, or else all your hard work will have gone to Hell in a handbag.

In reality, there is very little reason to believe this concept. At least nothing that has really been substantiated by the scientific literature. In fact, if there is an anabolic window, per se, it likely spans the course of several hours after an intense workout, not one. An interesting bit of evidence in favor of this idea is the fact that GLUT4 translocation occurs in skeletal muscle cells after a workout, irrespective and totally independent of insulin secretion,[2-3] which allows for amino acids to be taken up into the myocytes and initiates the physiological process of exercise-induced muscle protein synthesis -- and also for glucose to be oxidized, which is one of the reasons exercise is prescribed for hyperglycemic diabetic patients. This GLUT4 transmembrane receptor translocation alone is maintained for a few hours after the workout is over, meaning a good percentage of the subsequent glucose and amino acids you absorb will likely be shuttled preferentially to fuel the muscle tissue.

Also, intense muscular contractions (acute resistance exercise) cause a complicated intracellular biomolecular cascade called mammalian target of rapamycin complex 1 (mTORC1), which is a powerful regulator of protein synthesis. Although you can augment this process with supplemental leucine, as would be found in a BCAA drink or whey protein shake, or by consuming more protein in general, intense exercise, by itself, is sufficient to initiate the mTOR redox signal and lead to an impressive increase in rates of muscle protein synthesis.[4-6] Albeit an extremely complicated process, as you can see from the chart below, this signaling cascade does not appear to be reliant on post-workout carbohydrate consumption for activation. (That's not to suggest insulin does not play its own interesting role in regulating mTORC1. Merely that it is more complicated than this, and does not rely exclusively or necessarily upon either carbohydrates or insulin for activation.)

From Hulmi, et al. (2009). [ref 6]...

So why were people so adamant that this refueling immediately post-workout was a downright necessity for optimal recovery and hypertrophic muscular adaptations to exercise? I think, to a large extent, it had something to do with the hypothesis that tapping off muscle glycogen levels as quickly as possible is an essential component to post-workout recuperation.

I'm not sure I believe there is any good published literature that substantiates the claim that we must replenish intramuscular glycogen stores immediately after an intense bout of exercise for recovery or performance -- unless one is an elite athlete, or overreaching. Or, indeed, that these energy storage sites would not appropriately refill themselves, as the day goes on and you eat your normal diet. Frankly, with rare exceptions for elite ultra-endurance athletes and the like, virtually no one is totally wiping out their glycogen stores in a single workout.

That said, Camera, et al, in 2012, showed that low intramuscular glycogen levels do not appear to have any suppressive effect with respect to the anabolic impact of resistance exercise on muscle growth.[9] When I first read the conclusions of that paper, I thought to myself, Well, even if the hypertrophic response to low intramuscular glycogen isn't impaired, perhaps athletic performance is a different beast.... It turns out that Symons, et al, studied this back in 1989 and found that there is no such performance declination as a result of training with low intramuscular glycogen, either.[10]

Over the last few years, there have been some rather fascinating studies in the exercise physiology literature that have set out to examine whether or not increasing carbohydrates along with an athletes post-workout protein might aid in building more muscle than with the protein, alone. If the answer to these questions clearly favors the hypothetically anabolic role of supplemental carbohydrate, in this context, it would mean, of course, that more carbohydrate would be better for building muscle, while a diet lower in carbohydrate, like the ketogenic diet, might be decidedly less effective in promoting the same level of muscle growth. If, on the other hand, the answer is negative, we cannot necessarily suggest, then, that a very low carbohydrate diet is better or even equal to a high-carbohydrate diet for muscle protein accretion; just that supplemental carbohydrates, post-workout, are not a necessary requirement for additional hypertrophy beyond consuming protein alone. A standard training diet, already high in carbohydrates, without extra post-workout carbs =/= a ketogenic diet without post-workout carbs.

There are three specific studies I would like to touch on, quickly, each of which I believe did a fantastic job at covering this particular topic:

~ [11] Figueiredo, et al (2013).
~ [12] Koopman, et al. (2007).
~ [13] Staples, et al. (2011).

Overall, I think the JISSN review is a good one. The authors asked some very interesting questions, not the least of which was Does leucine require insulin to stimulate protein synthesis? The answer they arrived at, by the way, was no. Not necessarily.

In the end, as anticipated, Figueiredo and Cameron-Smith concluded, after a well thought out and provocative article, that there is currently (circa 2013) insufficient evidence to suggest that supplemental carbohydrates should be expected to provide any muscle building effects beyond protein alone; but that, as always, further investigations are warranted.

The Koopman study was a randomized-controlled crossover trial of 10 healthy, physically fit men, designed to answer the same basic question: Do supplemental carbohydrates contribute to further muscle protein synthesis, above and beyond the consumption of protein, alone?

Even though the sample population seems small, it was statistically powered to detect an effect, and this population is sufficiently representative of that which we are interested in extrapolating to. Their answer was another resounding No, seen clearly in their title: "Co-ingestion of carbohydrate with protein does not further augment post-exercise muscle protein synthesis."

Figure 1 shows the between group insulin levels, which were significantly greater in the PRO + HCHO group, yet, despite this difference, as the results demonstrate, there was no difference in muscle protein synthesis. This seems to lend further credence to my hypothesis that adequate protein and exercise intensity are the two most important factors for muscular hypertrophy.

Lastly, we have the Staples study. This is easily one of my all-time favorite papers. I thought the authors did a fantastic job writing up this experiment and connecting all the dots. Here are some important highlights, relevant to the same study question as before:

"Muscle protein synthesis increased by approximately 54% after exercise, compared with the values in the non-exercised leg, but there were no differences between the protein and protein + carbohydrate trials in the non-exercised or the exercised legs."

"Muscle protein breakdown was increased by approximately 37% after exercise compared with values from the non-exercised leg, but there were no differences between the protein and protein + carbohydrate trials in the non-exercised leg or after exercise."

There was a statistically significant difference between the PRO vs PRO + CHO, in favor of the latter, with respect to Akt phosphorylation, as shown above. However, it clearly wasn't important enough to cause any discernible changes in muscle protein accretion between groups which would be necessary to show that the CHO supplemented group reaped additional benefit. (This alteration in Akt, favoring the PRO + CHO group is likely due, from what I understand of the mechanisms of this molecular signaling pathway, from the significantly higher insulin levels in the PRO + CHO group, as compared with PRO alone. As is clear, though, this was insufficient to contribute to an appreciable difference in MPS in favor of PRO + CHO over PRO alone.)

Update: please also check out this paper[18], by Glynn, et al., from 2013. This one in particular -- because of the way the experiment was designed -- coupled with the strength of the Staples paper, is, from my perspective, sufficient to conclude, once and for all, that supplemental carbohydrates are in no way required for building muscle.

As it stands, it seems that the answer to the question we have been asking is that supplemental post-workout carbohydrate ingestion is not needed to further augment the well-established benefits of protein alone. However, as was mentioned previously, this does not serve as sufficient evidence in favor of ketogenic diets for muscle building, in and of itself. Moving on...

What about some other biochemical changes that result from altering the macronutrient composition of the diet?

At the University of Connecticut, in 2002, Dr. Jeff Volek and his team conducted an experiment[14] where they examined various biochemical assays to assess the effects of a carbohydrate-restricted diet on different hormones, such as thyroid hormone, testosterone and others. Unfortunately, this particular trial did not look at the effects of the intervention on female hormonal status, so we cannot extrapolate from the 20 otherwise healthy men who were involved, here, to whether this would also apply equally to women. However, with respect to male physiology, the 12 men who were randomized to receive carbohydrate restriction as a therapy for 6 weeks saw some rather dramatic changes in their blood panels.

Even though the authors make no mention that I can see of having the participants of this trial exercise, the low carb arm lost a mean of 3.4 kg in body fat over the 6 weeks, while increasing their lean body mass by an average of over 1 kilogram. These changes were apparently the direct result of changing just the macronutrient composition of their diets, favoring fats and restricting carbohydrates.

Interesting changes occurred with many of the assays, it seems, but, of particular importance to the question we are interested in, here, both total and free testosterone increased significantly, while sex-hormone binding globulin decreased. Depending on how substantial this difference is, this should mean that the men who were lucky enough to be randomized to the intervention group would experience an increase in lean mass and a decrease in fat mass. And, as we have just learned, that is precisely what happened. (Some of the reduction in body fatness was probably also due to increases in total and free thyroxine, in the carbohydrate-restricted arm, as well, as compared with the controls, whose laboratory findings, as predicted, remained largely the same throughout the duration of the trial.)

Fascinating though I think Volek and colleagues findings are, the impact of higher fat, lower carbohydrate dietary modifications on sex and steroid hormones has been well-established for many years. In 1986, Reed, et al, conducted an experiment to see what would happen to sex-hormone binding globulin (SHBG), free testosterone and total cholesterol concentrations, should the macronutrient ratios be shifted in this manner.[15] They, too, came to conclusions similar to those Volek and his team eventually reached.*

*Many traditional bodybuilders are indoctrinated to believe they need to eat very low fat diets for fat loss during the cutting aspect of their training, and, while reducing total fat intake can, under the right circumstances, certainly aid in the loss of body fat, to reduce it too low is to risk reducing total and free testosterone, as demonstrated in the two studies mentioned above. For both fat mass reduction and the inhibition of muscle protein breakdown, it would seem this is a bad plan.

More recently, in 2014, Jeremy Silva put together a nice little study on the effects of a very low carb, high fat diet on lipid and anabolic hormone status.[16] Like Volek and Reed, Silva, et al, also found that increasing dietary fat and decreasing carbohydrate led to a significant increase in total testosterone, as compared with the control group on the standard western diet.

So far, it seems there are no apparent strikes against the ketogenic diet as it pertains to building muscle, yet, with specific regard to these last three trials, there may be some interesting strikes against high carbohydrate, low-fat diets for muscle building -- the implications of which, if there are any such implications worth noting, will have to be further elucidated elsewhere.

Lastly and perhaps most importantly of all, these bits and pieces of articles will mean nothing, if a good randomized-controlled trial comes along and proves that very low carbohydrate diets significantly impede muscle growth or drastically increase protein degradation and that carbohydrate supplementation is necessary to attenuate this process, or something like that. However, as it happens, there is only one published trial that has ever set out to research the effect of a ketogenic diet on skeletal muscle strength and hypertrophy in trained individuals. Dr. Jacob Wilson is another active voice in the online fitness community, and he is how I learned about this study, which he contributed to, along with esteemed Drs. Volek and D'Agostino.

Wilson's trial (Rauch, et al[17]) of 26 trained, college-aged men used ultrasonography of the quadriceps muscles to determine that the VLCKD group increased their lean body mass by an average of 4.3 kg, while the traditional western diet controls only increased their lean body mass by 2.2 kg, even though the two groups were matched equally with dietary protein and exercise.

To be honest, I am not so sure about the use of ultrasound to accurately and reliably determine subtle changes in muscle tissue with enough sensitivity to be reasonably precise. Then again, I don't know, because it's the first time I've seen it. They did, however, use DEXA to determine bone and fat mass, which we know is one of the most reliable tools we have for measuring body fatness in trials like these. Perhaps if the authors juxtaposed the results of both pieces of equipment...?

In any case, this particular trial -- first of its kind -- actually looked directly at the impact of a ketogenic diet on muscle protein synthesis and skeletal muscle hypertrophy and body composition, and the very low carbohydrate diet in this case was actually superior! Significantly so, it seems. (Then again, I think each group may have had these measurements taken after glycogen and water replenishment, at the end of the trial, so that figure might actually be a bit confounded. However, when considering the only experiment we have, so far, on this very particular outcome question, one cannot say that a ketogenic diet of the sort we mean, here, is less anabolic than one higher in carbohydrate. At the very least, when matched for dietary protein intake and exercise intensity, they are equivalent, and seem to lead to virtually identical outcomes.)

So, do we need carbs to build muscle?

Based on my experience, and all the #anecdata I am aware of, I would say absolutely not. Based on the state of the evidence, right now, I don't think we can appropriately answer that question, in the context we are inquiring about, without better and more exhaustive research. That said, I do think we have enough bits and pieces of data, as compiled above, to at least tentatively suggest that a ketogenic diet is not "less than" a carbohydrate-rich diet, for the purposes of building muscle. I am willing to stick my neck out a little and wager that the results of these future studies, if and when they hit the press, will probably conclude that it really doesn't matter much whether you eat high or low carb, if your primary outcome is to maximize hypertrophy. (Although, if I'm being honest, I have a sneaking suspicion that similar results to Volek, Wilson and D'Agostino paper might make a consistent appearance over time...)

What should we do in the meantime, if building a decent amount of muscle is the goal?

1. Don't be afraid to eat enough food.

2. Maximize the anabolic potential of your diet by consuming sufficient protein. (Right now, this seems to peak at ~2x the RDA.)

3. Exercise to muscular fatigue a few times per week.

* * * * * * * * * *


1. Given sufficient dietary protein to maximize plasma hyperaminoacidemia and the anabolic response to exercise, and consistent resistance training with the right level of intensity and appropriate recovery, supplemental carbohydrate does not seem to be a requirement for the average person to build an appreciable amount of muscle.

2. Exercise, itself, as a means of initiating the mTORC1 cascade and other cellular anabolic signaling pathways is likely the single most important stimulus for promoting skeletal muscle cell protein synthesis, independent of any other factor, including carbohydrate consumption and insulin secretion.

3. Genetics arguably plays the biggest role in determining whether or not your muscle tissue will grow substantially. If I have some significant number of myocytes less than you, from birth, and we train and eat and sleep and live in exactly the same way, for the same exact same length of time, no matter what I do, I will never be able to build more muscle than you; muscle cells do not divide. This is genetic. I'm sorry. We do our best with the hands we're dealt... (Someone could have taken Jay Cutler as a young man, pre-bodybuilding, fed him a strict, low protein vegan diet, and he would still be the biggest guy in the room as soon as he picked up something heavy and put it back down.) In other words, it is highly doubtful, in my opinion, that extra carbs will really be your edge. (Bear in mind: whether or not supplemental carbohydrates are healthy and/or useful for other things, in other contexts, is beyond the scope of this post.)

4. If there did happen to be some advantage of higher carbohydrate, hyperinsulinemic diets, over very low carbohydrate diets, with respect to building muscle mass, it is probably so small as to be negligible. (At least as predicated on the data I have available to me, at this time.)

5. Carbohydrate-restricted diets higher in fat may have other anabolic benefits, distinct from insulin, like increased total and free-testosterone, as shown in Volek's study. But again, whether this will turn out to hold true in further human clinical trials remains to be seen. (Who knows, someday there may be data suggesting that "training low" is ideal for building muscle mass. Only time, and good experiments, will tell.)


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