Effects of a low carbohydrate diet on energy expenditure during weight loss maintenance: randomized trialBMJ 2018; 363 doi: https://doi.org/10.1136/bmj.k4583 (Published 14 November 2018) Cite this as: BMJ 2018;363:k4583
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In Table 3, the heading of the third column with pre-randomization data should read “Mean (SE)" not Mean (SD).
Competing interests: As described in the manuscript
The substance of Professor Polychronakos' criticisms have been addressed in our manuscript, but we will take this opportunity to clarify a few points.
Non-adherence is a methodological limitation in any outpatient feeding study, and to some degree inpatient studies, too (if any participant is ever out of sight or allowed visitors). We considered this issue in depth in our Discussion section. We provide detailed sensitivity analyses that show the robustness of our primary outcome to substantial non-adherence, even with unfavorable assumptions (eTables 6 and 7).
We disagree that the low carbohydrate diet would be inherently most unpalatable. Process measures indicated high levels of acceptability of all test diets in our study. Indeed, drop-out rates from the low carbohydrate group were nominally lower than for the high carbohydrate group.
Polychronakos has reversed the strength of the findings between the Intention-to-Treat and Per Protocol analyses. The diet effect was stronger among the latter – including those who had objective evidence of better adherence. As Polychronakos recognizes, the opposite would be expected if non-adherence played a substantive role in the primary outcome. While baseline insulin secretion status could theoretically be a marker for selective non-adherence, a more plausible explanation is offered by the Carbohydrate-Insulin Model (that individuals with the highest insulin secretion on a high carbohydrate diet experience the most adverse metabolic consequences) .
Our preliminary assessment of energy intake was consistent with the primary outcome, but not statistically significant in the full Per Protocol group. We discussed reasons for the major imprecision in this measure in our manuscript. Interestingly, and as related to the point above, the difference in energy intake among the high insulin secretors was significant by diet, arguing against non-adherence as a material explanation. A variety of secondary outcomes of relevance to this discussion are the subject of ongoing analyses by our group.
The biological mechanisms relating nutrition to metabolism and body weight regulation are inherently complex. Every study addressing a major scientific debate in this field will likely have methodological and interpretive limitations. But cautious interpretation is warranted not only for our study, but also for the small, short-term feeding studies that dominant the literature (see our Introduction section for the special limitations of such studies).
We strongly disagree that “the only credible studies on nutritional intervention on humans are the ones performed on hospitalised subjects.” In the modern era, few volunteers would be willing to spend more than a few weeks in a hospital research unit. Even if volunteers could be found, the costs for a long-term, large-scale study would be prohibitive. Conservatively assuming $1000 per hospital day in the U.S., the food and residential costs alone for our study would exceed $40 million. A further concern with inpatient studies is the artificial environment and physical confinement, which would inevitably confound energy expenditure and other metabolic variables. Rather, high quality research with a variety of designs – ward studies, outpatient feeding trials, behavioral trials and prospective observational studies – will be needed to answer questions that have bedeviled the field of obesity for more than a century.
1. Ludwig DS, Ebbeling CB. The Carbohydrate-Insulin Model of Obesity: Beyond "Calories In, Calories Out". JAMA Intern Med. 2018;178(8):1098-1103
Competing interests: As disclosed in the manuscript
It has been said that the only credible studies on nutritional intervention on humans are the ones performed on hospitalised subjects. This paper is a good illustration of how, beyond loss of statistical power, difficulties with adherence of ambulatory subjects to nutritional prescription can introduce strong systematic bias.
Per calorie expended, carbohydrate (CH2O) produces more CO2 than fat does. As a consequence, the method used to estimate TEE is very sensitive to how accurately the proportions of macronutrients metabolized are known. In this study, the respiratory quotient (RQ) was not measured but estimated based “on food”. I presume that this refers to the food delivered to the subject’s household. The assumption that this was what was actually ingested, in its entirety and to the exclusion of any other intake, without fail over 20 weeks, requires a considerable degree of faith in human self-discipline. Both the high and (especially) the low CH2O diets are unpalatable and much harder to sustain in the long run than balanced caloric restriction. Given that the RQ of CH2O (1.0) exceeds the RQ of fat (0.7) by 43%, a modest degree of non-adherence, maintaining statistical distinction among the groups and not detectable by the 1,5-anhydroglucitol measurements, may introduce serious systematic bias. Consuming slightly more CH2O and less fat would overestimate TEE in the low-CH2O group, while the reverse would underestimate it in the high-CH2O group. The larger effect size upon inclusion of subjects who failed to maintain weight loss (i.e. the least adherent), is consistent with this interpretation and against the paper’s main premise. Thus, there is a real possibility that the findings of this study are spurious. The insulin effect could also result from pre-loss insulin level being a quite plausible marker for the subjects least likely to adhere to a low-CH2O regime.
An orthogonal confirmation of the reported differences in TEE would have been a detection of the expected differences (209/day) in caloric adjustments needed to avoid weight changes that would have resulted in an almost 3 kg difference over 140 days. These were not statistically significant, and neither were the weight changes among groups (of the latter, only the p values are shown). Therefore, I would urge extreme caution in interpreting the results of this study, especially given the high profile, in the lay media, of irrational dietary recommendations presenting carbohydrate as only slightly better than poison.
Competing interests: No competing interests
In the previous response, Mr. Moulthrop claims that he has identified a serious error in Dr. Hall's analysis. He suggests that because Dr. Ludwig's study "gives a highly significant result" and because it was the primary outcome … "random chance is very unlikely" and that Hall's reasoning for the result being random chance is not as compelling as Ludwig's interpretation.
There are several misconceptions here regarding P-values and hypothesis testing. The P-value is the probability of getting a test statistic at least as extreme as what was observed if every model assumption is correct . Some key assumptions include:
- Randomization (sampling, assignment)
- No uncontrolled sources of systematic error in the results
- That the test model (often a null model) is correct
When we make these assumptions (that are often not correct) we are engaging in a thought experiment, so that all results that deviate from what we expect under the model are thought to be a result of pure random error. These are assumptions, not truths. Again, by this logic, all results under these assumptions are via random error.
A highly significant result indicates a few things.
- A dimensional violation specified by the test hypothesis has been detected by the test.
- The data are not very compatible with the test model and test hypothesis.
- In a Neyman-Pearson framework, we are allowed to reject the test hypothesis based on a prespecified alpha.
What a highly significant result does not indicate:
- That the results are meaningful
- That random chance is unlikely
- That the test hypothesis is most likely to be false (significance can indicate a violation of assumptions, it doesn't tell us *which* assumption has been violated)
Furthermore, an inflated familywise error rate (which is important in a Neyman-Pearson framework) does not simply occur as a result of multiple comparisons and is not solved by specifying the primary endpoint in advance. There are several other factors that can inflate this error rate, where it is far more likely in the long run to produce a significant result that is a false positive [2,3].
Rather than fixate only on P-values and whether or not they are "highly significant", we can interpret observed p (the realization of the random variable P), as a continuous measure of compatibility and look to the width of the compatibility (confidence) interval to see what effects are compatible with the test model and its assumptions. Producing a likelihood function  and a P-value function [6,7] where every compatibility interval is graphed, will foster a much more nuanced interpretation of the data.
Trying to produce explanations as to why results gave "highly significant results" is highly misguided. Statistical significance and hypothesis testing have utility in certain areas where one is trying to automate decisions and control errors in the long run . This may be useful in areas where replication is feasible, such as psychology . In nutrition, where experiments similar to this are not always feasible, it may not hold as much utility.
The fixation on trying to explain highly significant results from a test of the null hypothesis truly is reflective of “cargo-cult statistics” .
1. Greenland S, Senn SJ, Rothman KJ, et al. Statistical tests, P values, confidence intervals, and power: a guide to misinterpretations. Eur J Epidemiol 2016;31:337–50. doi:10.1007/s10654-016-0149-3
2. Simmons JP, Nelson LD, Simonsohn U. False-positive psychology: undisclosed flexibility in data collection and analysis allows presenting anything as significant. Psychol Sci 2011;22:1359–66. doi:10.1177/0956797611417632
3. Wicherts JM, Veldkamp CLS, Augusteijn HEM, et al. Degrees of Freedom in Planning, Running, Analyzing, and Reporting Psychological Studies: A Checklist to Avoid p-Hacking. Front Psychol 2016;7:1832. doi:10.3389/fpsyg.2016.01832
4. Greenland S. Valid P-values behave exactly as they should: Some misleading criticisms of P-values and their resolution with S-values. Am Stat 2018;18.
5. Royall R. Statistical evidence: a likelihood paradigm. Routledge 2017. https://www.taylorfrancis.com/books/9781351414562
6. Poole C. Beyond the confidence interval. Am J Public Health 1987;77:195–9.https://www.ncbi.nlm.nih.gov/pubmed/3799860
7. Rothman KJ, Greenland S, Lash TL, et al. Modern epidemiology. Published Online First: 2008.https://www.annemergmed.com/article/S0196-0644(08)01394-2/abstract
8. Lehmann EL, Romano JP. Testing Statistical Hypotheses. Springer Science & Business Media 2006. https://market.android.com/details?id=book-K6t5qn-SEp8C
9. Lakens D, Adolfi FG, Albers CJ, et al. Justify your alpha. Nature Human Behaviour 2018;2:168–71. doi:10.1038/s41562-018-0311-x
10. Stark PB, Saltelli A. Cargo-cult statistics and scientific crisis. Significance 2018;15:40–3. doi:10.1111/j.1740-9713.2018.01174.x
Competing interests: No competing interests
Re: Effects of a low carbohydrate diet on energy expenditure during weight loss maintenance: randomized trial
I have read the responses of Hall et al. and the replies of Ludwig et al. Admittedly I have no special expertise in these subjects, but I believe I have identified a serious flaw in Dr. Hall’s arguments.
He says that his analysis is correct, while Dr. Ludwig’s is incorrect. But Ludwig’s analysis gives a highly significant result. Dr. Hall, if he is right, should be able to explain why Ludwig’s analysis gives a highly significant result. The only explanation implied by Hall’s arguments is that it is random chance. We know “p-hacking” can occur if there are many possible analyses. Then one can choose the analysis that gives a significant result by random chance. This is clearly not the situation here, since this is the primary endpoint, and there only a small number of possible analyses.
Hence, since random chance is very unlikely, there should be a reason that Dr. Ludwig’s analysis gives a significant result. Dr. Ludwig has a compelling explanation for this. Dr. Hall, if he is to be convincing, should give an explanation for the significant result. The non-significant result of Hall is explained plausibly by both Hall and Ludwig, so that result does not distinguish who is correct. The significant result is explained much more plausibly by Dr. Ludwig, so it is compelling evidence that Ludwig is correct and Hall is wrong.
Competing interests: No competing interests
We would like to clarify procedures related to data acquisition and maintenance of the study group assignment masking (blind).
The final analysis plan, with a change in specification of the baseline for total energy expenditure (TEE, the primary outcome) was approved by the institutional review board and posted in September 2017, prior to unmasking diet group assignment, as stated in the main manuscript.
At that time, the final outcome data for the third and main cohort (comprising 50% of participants) had not yet been received by the Boston investigators. However, data for the prior cohorts had been received.
Therefore, the relevant sentence in the online Supplement (page 16) would more accurately include the word “complete” as follows (1): “Submitted Final Data Analysis Plan (version 2017.06.14) to IRB and obtained approval prior to receiving the complete primary outcome data and breaking the randomization blind."
Dr. William Wong in Houston sent raw isotopic data periodically in batches to Boston during the study. Data cleaning and modeling (i.e., curve fitting to allow for calculation of the primary outcome) were performed in late 2017 after posting the final analysis plan. The statistician broke the blind and delivered the initial results to the principal investigators in January 2018. The statistician maintained the only depository for the primary outcome until posting the full database with publication of the manuscript in November 2018.
1. Supplemental Information (online): https://www.bmj.com/content/bmj/suppl/2018/11/13/bmj.k4583.DC1/ebbc04619...
Competing interests: As detailed in manuscript
Hall and Guo posted a reanalysis of our study using the pre-weight loss rather than the post-weight loss measure of total energy expenditure, finding a non-significant effect (1). They propose that the pre-weight loss baseline is more “correct” and raise concern about the timing of our change to the clinical trials registry.
This alternative analysis is not new. We performed this calculation during manuscript revision, as publicly available in the Peer Review material (2). The BMJ editors and statistician had full access to these data and we deferred to them regarding whether to include this analysis in the manuscript. We did not “refuse” to do so.
The reasons for using the post-weight loss baseline were extensively discussed in the Peer Review material and in the manuscript. (For reader convenience, we include the Peer Review response at bottom.) We were transparent about this a priori change, and included a detailed timeline in the Supplemental materials (3).
We further addressed this issue in a prior Rapid Response (4), showing that Hall’s previously stated concerns about changing body weight (5) were unfounded, and that statistical models including pre-weight loss baseline did not materially change the result.
There is a straightforward explanation for why the registry was corrected as the “7[th] of 8 versions of the protocol.” We planned to post a final analysis plan, with comprehensive detail of our statistical methods, prior to receiving the final data from our collaborator in Houston and breaking the blind. In preparing that plan under guidance of our statistician, we identified the misspecification – an inadvertent holdover from a prior cross-over study (our present study is parallel design, in which the weight-loss phase would introduce inter-individual variability) (6). Earlier protocol revisions addressed logistical and other issues in study conduct; we had no reason to review the analysis plan and identify the misspecification prior to that time. We are puzzled as to the relevance and implication of this point about protocol revision number.
Finally, we note that our study went through a highly rigorous review, involving 6 independent experts, including more than 120 points of criticism and discussion. We exceeded professional standards of transparency, by making the full database publicly available immediately upon publication – perhaps for the first time for a nutrition study of this magnitude and complexity.
1. Hall KD, Guo J. 28 November 2018. No significant effect of dietary carbohydrate versus fat on the reduction in total energy expenditure during Maintenance of lost weight. https://www.bmj.com/content/363/bmj.k4583/rr-16
2. Peer Review, Author Response, 18 September 2018, Point #1 pages 2-4: https://www.bmj.com/sites/default/files/attachments/bmj-article/pre-pub-...
3. Supplemental information, page 16: https://www.bmj.com/content/bmj/suppl/2018/11/13/bmj.k4583.DC1/ebbc04619...
4. Ludwig DS, Ebbeling, CB, Feldman HA. 20 November 2018. Choice of baseline for primary endpoint. https://www.bmj.com/content/363/bmj.k4583/rr-11
5. Belluz J, Vox, updated November 21, 2018. Does cutting carbs really help keep weight off? The big new diet study, explained. https://www.vox.com/science-and-health/2018/11/16/18096633/keto-low-carb...
6. Ebbeling CB, Swain JF, Feldman HA, Wong WW, Hachey DL, Garcia-Lago E, Ludwig DS. Effects of dietary composition on energy expenditure during weight-loss maintenance. JAMA. 2012, 307:2627-34 https://www.ncbi.nlm.nih.gov/pmc/articles/PMC3564212/
POINT #1 FROM PEER REVIEW, 18 SEPTEMBER 2018:
We closely adhered to the a priori clinical trials and protocol plans, also as detailed in our methods paper and Open Science Framework registry (https://osf.io/rvbuy/).
The only discrepancy involves a change from initial specification in the anchor used to calculate change in the primary outcome. In our original analysis plan of 2014, we had indicated the preweight loss (i.e., pre-Run-In, BSL in Figure 1) measurement as the anchor for determining the diet effect on total energy expenditure (TEE), but this was an error on our part. We corrected this error in the Clinical Trials registry and used an analysis for our manuscript with the post-weight loss (i.e., post-Run-In, PWL in Figure 1) measurement as the anchor. For the reasons explained below, we request an exception to your general rule of including both analyses in the Results section, and instead have provided further clarification of this issue in Methods.
1. The initial listing was clearly an error:
A) As a general rule, anchor data should be collected as close to randomization as possible, to decrease error introduced by time-varying covariates. The pre-Run-In measurement involves a 3- to 4-month delay prior to initiation of the Test diets.
B) In addition to this delay, the pre-Run-In measurement is strongly confounded by weight loss, whereas the specific aim of the study is to examine TEE during weight maintenance. (Indeed, the title of the study in the registry is: Dietary Composition and Energy Expenditure During Weight-Loss Maintenance.)
C) The expressed purpose of the Run-In was to produce 12% weight loss, changing biological state (i.e., creating a predisposition to weight regain) to test the study hypotheses. Thus, it would be inconsistent with study aims and methodologically inappropriate to use the pre-Run-In time point to establish a precise and accurate anchor for determining how the Test diets change TEE. Doing so would necessitate a substantially larger number of participants (and cost) to account for the additional imprecision, with no scientific benefit.
2. Study power (and thus participant number) was determined with use of post-Run-In measurement as the anchor.
A) Our a priori power calculations defined the primary outcome as “change in total energy expenditure at week 20 of the test phase compared to week 0 (post-weight loss).”
B) We did not take into account the variability between pre-Run-In and post-Run-In (Week 0) measurements, which in our case had r-values on the order of only 0.3 for the unadjusted model and 0.5 for the adjusted model.
C) Not surprisingly, doing the analysis with the pre-Run-In measurement as the anchor yielded a mean estimate in the same direction, but with substantial loss of precision and a statistically non-significant overall effect in the ITT. For example, TEE in the unadjusted model of Low vs High Carbohydrate diets was + 141 kcal/day (p=0.08, overall p=0.2).
3. The error was recognized and corrected a priori. We obtained IRB approval for our final analysis plan on 06 Sept 2017, before the blind was broken (and indeed, before measurement of the primary outcome had been completed by our collaborator Bill Wong in Houston). Similarly, we corrected the Clinical Trials registry prior to breaking the blind. We provide documentation of this timeline, and additional detail, in the Supplement Protocol section.
Although we agree with the general policy of including multiple analyses where discrepancies exist, we think an exception would be warranted in this situation. For reasons suggested above, we believe that we have fulfilled the letter and spirit of an a priori analysis plan. Furthermore, we are concerned that the additional analysis would provide no meaningful biological insights – that is, no useful information about the nature of the relationship between dietary composition and energy expenditure. Rather, inclusion of the additional analysis would tend to elevate and give undue attention to an error, and therefore potentially cause confusion.
To place our study in the context of other diet trials, I reviewed the Clinical Trials registry of diet and weight loss trials published in one of the JAMA journals since 2015 (to obtain a collection of cross-specialty examples). Of the 13 trials identified, 8 had significant changes in the primary outcome since initial posting. In several additional trials, the level of detail for the primary outcome was insufficient to exclude multiple statistical treatments [NB, see online Peer Review for references to these studies].
Regarding this last point, our pre-analysis plan provided a comparatively great level of detail. For contrast, the study by Hall et al of 2016 (cited in the Endocrine Society Scientific Statement as major evidence against the Carbohydrate-Insulin Model) included only a 1- paragraph statistical plan (https://osf.io/9q8cu/ beginning bottom of page 23), thus providing freedom to analyze outcomes in many different ways (e.g., post hoc exclusion of outliers).
My intent in providing this context isn’t to justify suboptimal practices, but rather to clarify that error or lack of specificity in an initial registry of major diet trials (vs industry-sponsored drug trials which have much larger budgets, infrastructural support and standardization) is more the rule than the exception. However, we believe that our overall rigor is comparatively very high, and the proposed course of action entails no risk to the integrity of the data analyses.
To address your reasonable concerns on this point and to maintain maximum transparency, we have clarified this situation in the Methods (page 12, para 2) and provided additional detail in the Supplement Protocol section. Please also note that we have committed to post the complete data set on a publicly available server upon publication of the manuscript, so that anyone can perform additional exploratory analyses, including this one. Nevertheless, we will defer to you, and include the additional analysis, if you disagree with our proposed solution.
Competing interests: As detailed in the manuscript
No Significant Effect of Dietary Carbohydrate versus Fat on the Reduction in Total Energy Expenditure During Maintenance of Lost Weight
The question of whether the ratio of dietary carbohydrates to fat substantially impacts total energy expenditure (TEE) or body fat has been investigated for decades, with most studies pointing to no clinically meaningful effect 1. However, a recent study by Ebbeling et al. reported substantial differences in TEE between diets varying in their ratio of carbohydrate to fat 2.
The original pre-registered statistical analysis plan for the primary study outcome of Ebbeling et al. addressed the question of whether the reduction in TEE during weight loss maintenance compared to the pre-weight loss baseline depended on the dietary carbohydrate to fat ratio – a design similar to a previous study by many of the same authors 3. However, the final analysis plan was modified to make the diet comparisons with the TEE measurements collected in the immediate post-weight loss period rather than at the pre-weight loss baseline. As fully described in a manuscript available on the bioRxiv pre-print server (https://www.biorxiv.org/content/early/2018/11/28/476655), reanalyzing the data according to the original analysis plan of Ebbeling et al. found that the TEE differences were no longer statistically significant between the diet groups and the nominal diet differences of ~100 kcal/d were much smaller than the ~250 kcal/d differences reported in the final publication. In other words, when conducting the analysis originally planned by the authors we found that the significant increases in TEE with the low carbohydrate diet that were reported by Ebbeling et al. disappeared. Furthermore, the significant TEE effect modification by baseline insulin secretion also disappeared.
As justification for our reanalysis, we note that most of the history of the study (7 of 8 versions of the protocol spanning from 2014-2016) the planned primary outcome calculations used the pre-weight loss TEE baseline as the anchor point for the subsequent diet comparisons during weight loss maintenance. Prior to unmasking the randomization blind, but after all cohorts had completed the trial, the final protocol amendment in 2017 altered the previously planned statistical analysis to use the post-weight loss TEE measurement as the anchor point to make the subsequent diet comparisons.
The reasons for the change in the analysis plan were not provided in the protocol amendment or the final statistical analysis plan, but the Supplemental Materials in the final publication provided three reasons. First, the post-weight loss TEE measurement was chosen as the new anchor point because it occurred closer to the point of diet randomization. Second, the pre-weight loss TEE measurement would be “strongly confounded by weight loss”. How this might happen and why the post weight loss measure would not be similarly affected is difficult to imagine. Finally, Ebbeling et al. argued that the pre-weight loss baseline would have been inappropriate because the TEE measurements were insufficiently accurate or precise and therefore the study would be under-powered. However, the power calculations in the protocol were based on TEE data from a pilot study using the pre-weight loss TEE measurements as the basis for comparing how different diets affected the absolute reduction in TEE during weight loss maintenance 3. The pilot study did not measure TEE in the period immediately post-weight loss and therefore could not have been used to power the recent study in question.
Despite a request by the BMJ Editors to report the results of their original analysis plan, Ebbeling et al. refused because they were “concerned that the additional analysis would provide no meaningful biological insights – that is, no useful information about the nature of the relationship between dietary composition and energy expenditure. Rather, inclusion of the additional analysis would tend to elevate and give undue attention to an error, and therefore potentially cause confusion.”
We believe that the revised analysis plan has caused confusion and that the original statistical analysis plan that used pre-weight loss TEE as the anchor point is preferable for several reasons. First, it specifically addresses the question of whether the typical reduction in TEE that accompanies maintenance of lost weight depends on the carbohydrate to fat ratio of the weight loss maintenance diet. Second, the revised plan is potentially confounded by the substantial adaptive thermogenesis that occurs immediately post-weight loss that typically becomes less severe after a period of energy balance and weight loss maintenance 4 5. Finally, the pre-weight loss baseline TEE measurements were obtained in the situation where the doubly labeled water method is routinely employed: free-living people maintaining their habitual weight. Ideally, a post-weight loss TEE measurement should have first stabilized subjects at the lower body weight for several weeks prior to dosing with doubly labeled water 6. In contrast, the post-weight loss TEE measurements conducted by Ebbeling et al. were obtained during the same 2-week weight stabilization period when diet calories were being progressively increased at a rate determined by each individual subject’s recent rate of weight loss. While the doubly labeled water method generally provides a robust and valid estimate of TEE, this situation of simultaneous refeeding immediately post-weight loss potentially introduces uncertainty into the conversion of CO2 production into TEE. For example, the daily respiratory quotient during this period was clearly not equal to the food quotient as was assumed by Ebbeling et al. While such an effect can be appropriately modeled 7, this was not done in their TEE calculations.
In conclusion, when analyzed using the original statistical plan that was not confounded by the immediate post-weight loss period, the data of Ebbeling et al. do not support the conclusion that the ratio of dietary carbohydrate to fat affects the reduction in TEE during weight loss maintenance. While there are many reasons people could benefit from consuming healthy low carbohydrate diets 8, such diets are unlikely to help offset the usual reduction in TEE during maintenance of lost weight.
1. Hall KD, Guo J. Obesity Energetics: Body Weight Regulation and the Effects of Diet Composition. Gastroenterology 2017;152(7):1718-27 e3. doi: 10.1053/j.gastro.2017.01.052 [published Online First: 2017/02/15]
2. Ebbeling CB, Feldman HA, Klein GL, et al. Effects of a low carbohydrate diet on energy expenditure during weight loss maintenance: randomized trial. Bmj 2018;363:k4583. doi: 10.1136/bmj.k4583 [published Online First: 2018/11/16]
3. Ebbeling CB, Swain JF, Feldman HA, et al. Effects of dietary composition on energy expenditure during weight-loss maintenance. Jama 2012;307(24):2627-34.
4. Hall KD. Computational Modeling of Energy Metabolism and Body Composition Dynamics. In: Krentz AW, Heinemann L, Hompesch M, eds. Translational Research Methods for Diabetes, Obesity and Cardiometabolic Drug Development. London: Springer-Verlag 2015:265-82.
5. Weinsier RL, Nagy TR, Hunter GR, et al. Do adaptive changes in metabolic rate favor weight regain in weight-reduced individuals? An examination of the set-point theory. Am J Clin Nutr 2000;72(5):1088-94.
6. Bhutani S, Racine N, Shriver T, et al. Special Considerations for Measuring Energy Expenditure with Doubly Labeled Water under Atypical Conditions. Journal of obesity & weight loss therapy 2015;5(Suppl 5) doi: 10.4172/2165-7904.S5-002 [published Online First: 2016/03/11]
7. Hall KD, Guo J, Chen KY, et al. Methodologic Issues in Doubly Labeled Water Measurements of Energy Expenditure During Very Low-Carbohydrate Diets. bioRxiv 2018 doi: 10.1101/403931
8. Hall KD, Chung ST. Low-carbohydrate diets for the treatment of obesity and type 2 diabetes. Curr Opin Clin Nutr Metab Care 2018;21(4):308-12. doi: 10.1097/mco.0000000000000470 [published Online First: 2018/04/21]
Competing interests: KDH has participated in a series of debates with Dr. David S. Ludwig, the senior author of the main study in question, regarding the merits and demerits of the carbohydrate-insulin model of obesity as well as the physiological response of the human body to isocaloric diets varying in the ratio of carbohydrates to fat.
Scientific debates in nutrition may sometimes proceed along predictable lines, seemingly influenced by personal ethical views. Advocates of vegan diets tend to emphasize studies showing the benefits of consuming carbohydrate over fat, perhaps because virtually all dietary carbohydrates come from plants. (In a previous post, we responded to criticism of our study by 2 individuals with leadership roles in Physicians Committee for Responsible Medicine, a group that discourages use of animals for food and medical research (1).)
Conversely, advocates of low-carbohydrate diets commonly highlight the advantages of animal products, perhaps because meat, eggs and dairy products were historically primary sources of dietary fat.
However, these implicit biases do not reflect the reality of the modern food environment. One can easily consume a low-fat, animal-based diet with foods such as chicken breast, lean beef, egg whites, and low-fat cheese.
Alternatively, a low-carbohydrate diet can be based on high-fat plant foods including nuts, seeds, olive oil, avocado, coconut oil and dark chocolate – as exemplified by several recent popular books and a large social media group (2) that recommend a vegan ketogenic diet.
To find common ground, we must carefully distinguish scientific from ethical considerations. But with the abundant choice of foods now available for most people in developed countries, all sides of the diet debates can take comfort that scientific truth and the pursuit of an ethical lifestyle need not be in conflict.
1. Authors' response to Kahleova, Katz and Barnard. https://www.bmj.com/content/363/bmj.k4583/rr-12
2. Facebook Group, Vegan Keto Made Simple. https://www.facebook.com/groups/320351758396552/
Competing interests: As detailed in the manuscript
The details of the diet given in the methods paper:
make it clear that while this study has stuck to the official guidelines and recommendations for nutrient composition, there is still a problem here that should be addressed by all researchers in this field. According to the article:
"Total fiber content was consistent with recommendations from the Institute of Medicine (1) and reflected a gradient across the 3 diets (17.5, 15, and 12.5 g/1000 kcal with the high-, moderate-, and low-carbohydrate diets)."
Now, the argument for a low-fat high carb diet has its roots in observational studies done on indigenous populations, e.g. (2), but the sorts of diets that people in such studies ate, are planted based whole food diets containing small amounts of meat and fish that are very low in refined oils. Such diets have a fiber content of a factor of 2 to 3 higher than the current recommendation. Also such diets will contain much more magnesium, which is an element that plays an important role in metabolism, also about a factor of 2 to 3 more than current guidelines.
We can easily verify this by considering the fiber and magnesium contents of a list of whole foods and computing the amounts of these nutrients per Kcal of energy. E.g. potatoes contain 2.9 *10^(-2) g/Kcal of fiber and 0.3 mg/Kcal of magnesium. Looking at a large list of many such energy rich whole foods reveals that a 2500 Kcal carb based whole food diet should contain at least 0.7 grams of magnesium and at least 70 grams of fiber. Here we note that sources of dietary fat cannot be refined oils but can be foods like walnuts, almonds, linseed etc. which are also high in magnesium and fiber. Also vegetables have a much higher fiber to energy ratio than then carb-rich foods.
One can formulate this in the opposite way by asking what kind of whole food diet of a 2500 kcal would actually yield the RDAs of 400 mg of magnesium and 40 grams of fiber. One then finds that this is not possible, unless one includes large amounts of olives which contain an atypically low amount of fiber and magnesium per unit energy.
Then given that the human body should be assumed to have adapted itself to a diet that based on unrefined foods that can be obtained from Nature, we should have some doubts about the healthfulness of the much lower official recommendations for fiber and magnesium compared to that of a diet based on whole foods.
1. Institute of Medicine Dietary Reference Intakes for energy, carbohydrate, fiber, fat, fatty acids, cholesterol, protein, and amino acids. Washington (DC): National Academies Press; 2002.
2. Shaper AG, Jones KW. Serum-cholesterol, diet, and coronary heart-disease in Africans and Asians in Uganda. The Lancet, 534–537 (1959).
Competing interests: No competing interests