CLARK, VIRGINIA R.; HOPKINS, WILLIAM G.; HAWLEY, JOHN A.; BURKE, LOUISE M.
The placebo effect is a favorable outcome arising purely from belief that one has received a beneficial treatment. In clinical settings the placebo effect is known to produce substantial reductions in pain or suffering (for review see (22)). Indeed, several authors have argued that placebo treatments should be a recognized component of clinical practice (4,17).
Placebos may also have important effects on physical performance. The unsolicited testimonials for nutritional products and training aids cited by manufacturers are consistent with placebo effects, especially when some of these products and aids have no reasonable underlying mechanism for enhancing performance. The capacity for the mind to affect the body is also evident in nearly a score of reports of substantial effects of expectation, hypnosis, mental preparation, motivation, music, and self-efficacy on strength or short-term endurance (11,15,23,24) (for earlier references see (3)). These reports represent indirect evidence that belief in the efficacy of a treatment could enhance physical performance, but we could find only one full report of a study providing direct evidence. The study appeared in this journal more than 25 yr ago (1). The researchers reported that subjects in a training study who believed mistakenly that they were receiving oral anabolic steroids showed a greater increase in strength than subjects in a control group who performed the same training program without the placebo. An important implication is that treatment groups in studies where blinding is not possible may show enhanced performance purely because of the placebo effect.
It is clear that more research is needed to explore the placebo effect with various treatments and various kinds of exercise. We therefore undertook the present study to investigate the acute effect of a placebo treatment on endurance performance. We decided to combine the study of the placebo effect with an investigation of a treatment that was potentially, but not unquestionably, ergogenic. In this way our subjects would have an attitude toward the treatment similar to that of subjects in other studies of potentially ergogenic treatments. The treatment we chose was carbohydrate supplementation during a time trial lasting ∼1 h.
It is now well accepted that ingesting carbohydrate at a rate of ∼1 g·min−1 produces a substantial enhancement of performance in simulated time trials lasting more than 1.5 h (for review see (5)). The enhancement has been attributed to the maintenance of normal blood-glucose concentration (euglycemia, 4–5 mmol·L−1) and high rates of blood-glucose oxidation late in exercise, when muscle glycogen stores are low. Recently, several groups of researchers have shown that carbohydrate ingestion may also improve cycling performance lasting ∼1 h (2,6,10,13). Some researchers are skeptical of these findings, because in other studies carbohydrate availability does not appear to be a limiting factor for intense exercise lasting an hour. Indeed, carbohydrate loading has little observed effect on such exercise (7). Furthermore, carbohydrate supplementation does not appear to affect blood glucose concentration or spare muscle glycogen during constant-load cycling (5). We therefore thought that another study of the effect of carbohydrate supplementation on ∼1-h endurance performance was justified in a research design that would allow us also to study the placebo effect.
We used a balanced repeated-measures design to determine the magnitude of the placebo and real effects of carbohydrate supplementation during a simulated 40-km time trial. After preliminary testing subjects performed a baseline time trial, during which they drank water. Approximately 1 wk later, subjects performed an experimental time trial, during which they consumed a flavored drink containing a noncaloric sweetener with or without carbohydrate. For the experimental trial, subjects were randomized to one of three main treatment groups according to what they were told was in the drink. The first group was told the drink contained carbohydrate. The second group was told the drink contained a noncaloric placebo sweetener. The subjects did not know that half of the first group was randomized to receive the placebo, and half of the second group was randomized to receive the carbohydrate. Cyclists in the third group were told truthfully there was a 50:50 chance their drink would contain carbohydrate, but individuals in this group were not told what their drink contained. Thus, there were six treatment groups in total: two subgroups (given carbohydrate, given placebo) for each of three main groups (told carbohydrate, told placebo, not told).
Because we were examining the placebo effect of a suspected ergogenic aid, we had to make sure through verbal persuasion that each subject had the appropriate expectation from the carbohydrate drink. Each cyclist was advised before s/he was allocated into a group that those who received the carbohydrate drink would probably show an improvement in performance compared with those who received the noncaloric drink.
Sample sizes have to be as large as practicable in studies on athletic performance (8). We opted for a sample size of 60, which was as many as we could accommodate for testing with the available time and resources. We had difficulty recruiting subjects of uniformly high caliber, and we finished with 54 moderately to well trained male and female endurance cyclists (49 male and 5 female). To participate a cyclist had to have completed a local 105-km cycle tour (the Argus) in less than 3.5 h, and had to have been training regularly for the past year, riding at least 200 km·wk−1. The subjects signed consent forms in accordance with the guidelines outlined by the Research and Ethics Committee of the Faculty of Medicine of the University of Cape Town. We subsequently restricted our main analyses and conclusions to the 43 fastest cyclists (2 female, 41 male) in the first time trial.
The base for the carbohydrate and placebo drinks was a commercially available noncaloric drink concentrate sweetened with cyclamate and saccharine. We chose a novel flavor (orange-mango) to reduce any sensory cues the subjects might use to guess which drink they received. We prepared the carbohydrate drink by mixing one part of the concentrate with four parts of water. (The manufacturer’s recommendation of three parts of water produced a drink that we thought would be too sweet for consumption during a high-intensity time trial.) We then added glucose polymer (hydrolyzed from corn starch) at the rate of 7.6 g·100 mL−1. In subsequent taste testing with volunteers, we found that that we needed to mix the placebo drink into a slightly more concentrated solution (3.5 parts of water) to compensate for the slight mouth feel resulting from the glucose polymer in the carbohydrate drink. Volunteers were then unable to distinguish between the carbohydrate and placebo drinks.
On their first visit to the laboratory, subjects performed a standard incremental test to maximum effort for the determination of peak power and peak oxygen uptake. For this test, the subject’s bike was attached to an air-braked ergometer (Kingcycle Ltd., High Wycombe, UK), which was then calibrated as previously described (16). The subject then warmed up at a self-selected intensity for 10–15 min. At the end of the warm-up, the workload was adjusted to on average 150 W and continuously increased by 20 W·min−1 until the subject could no longer maintain the required power output. The subject’s peak power output was the highest average power during any 60 s period of the exercise test. Peak oxygen uptake (in L·min−1) was estimated from peak power using the following formula (12): 0.435 + 0.0114·(peak power in W). After a rest of 15–30 min, subjects performed a 15-min trial on the Kingcycle at an intensity they thought they could maintain for 40 km, as a familiarization for the 40-km performance trials.
Baseline and experimental trials.
Subjects returned to the laboratory between 0700 and 2000 at least 3 d later to perform the baseline time trial. After at least another 3 d, they returned to perform the experimental trial. Each subject performed the second time trial at approximately the same time of day as the first.
During the 30 min before the start of a time trial, subjects drank a volume of the given fluid (water in the first trial, carbohydrate or placebo in the second trial) equivalent to 8 mL·kg−1 of body mass. Fifteen minutes before the start of the time trial, the Kingcycle was calibrated and the subject warmed up in a self-selected manner. Two minutes before the start the subject drank another 2 mL·kg−1 of the fluid. Thereafter, the subject ingested the same amount of fluid after 10, 20, and 30 km of the time trial, for a total of 16 mL·kg−1. We instructed the subjects to cover the assigned distance in the shortest time possible. During the performance rides, the only feedback they received was the elapsed distance as a percentage of total distance. We recorded time to complete the time trial and mean power output.
The six treatments were arranged into a random sequence. As subjects volunteered, they were allocated to the next treatment in the sequence. When selecting a subgroup of faster subjects for subsequent analysis, we found there were substantially fewer subjects in two of the groups than in the other four groups. We therefore recruited more subjects and allocated them randomly to these two groups.
We asked subjects to maintain their usual training and diets during the study, and for the 24 h before each time trial, they were asked to eat what they would normally eat in the lead-up to a race. They were also asked to refrain from heavy training for the 24 h before each time trial. Each subject kept a dietary and training diary for the 2 days before the first time trial, but they did not record the exact time of day they consumed meals, ate snacks, and trained. The diary was copied and returned to the subject so it could be followed before the second 40-km time trial. We collected the second diary after the second time trial and examined both diaries to ensure there were no major changes in training and diet, but we did not analyze the diaries.
Preliminary analyses revealed that the slower a cyclist performed in the first time trial, the greater was his or her gain in performance in the second time trial, irrespective of the treatment group. We therefore included speed in the first time trial as a linear covariate in the analysis, to reduce the effect of this source of variation. The standard approaches to repeated-measures analysis using least-squares estimation (analysis of variance) or restricted maximum-likelihood estimation (mixed modeling) do not permit inclusion of one of the test values of the dependent variable as a covariate, so we opted for a nonrepeated measures analysis of change scores (experimental minus baseline). This method is no less powerful than repeated measures when there are only two tests per subject.
We used Proc Mixed in the Statistical Analysis System (version 6.12, SAS Institute, Cary, NC) to perform mixed modeling. The dependent variables in the analyses were change in mean power and change in time in the time trial. Three sources of variation were modeled: what the subjects were told was in the drink (a nominal variable with three levels: carbohydrate, placebo, not told); what was actually in the drink (a nominal variable with two levels: carbohydrate, placebo); and the subjects’ speed in the first time trial (a linear covariate). The analysis also included different estimates of residual variances for each of the three told groups. Analyses were performed on the natural logarithm of duration and mean power, because variations in human performance are better modeled as percentages of a subject’s true performance rather than as absolute values (8). The variations in performance (δ) derived from the analyses of the log-transformed variables were converted to percents via the transformation 100(eδ − 1) ≈ 100δ (20). To compare the reliability of the performance test under the conditions of the experimental trial with published reliability, we converted the standard deviation of the change scores to coefficients of variation by dividing them by √2.
We have used means and standard deviations to represent the average and typical spread of values of variables. We have shown the precision of our estimates of outcome statistics as 95% confidence limits, which define the 95% likely range of the true value in the population from which we drew our sample.
Figure 1 shows performance times in the two 40-km time trials. It is apparent from the scatter of points in this figure that slower cyclists in the first time trial showed a greater variability in performance between the tests. We therefore analyzed the 43 subjects who had a performance time of less than 65 min in the first time trial. We chose this performance time to exclude a subject who showed an improvement in power of 39% on retest. This strategy also eliminated two subjects who had improvements of 28% and 44%. The biggest change in performance in the subjects included in the final analysis was an increase in mean power of 17%. In the full analysis, this group of 43 faster cyclists had a smaller overall standard deviation for change in power output between the time trials (6.5%; likely range 5.3–8.5%) than that of the full sample (9.0%; 7.5–11%).
The scatter of points about the line of identity in Figure 1 also reveals a tendency for slower subjects in the first time trial to show a greater reduction in performance time in the second time trial. In the full mixed-model analysis of the data for the subset of faster subjects, this tendency amounted to an enhancement of power of 1.2% (0.5–1.8, P = 0.001) for every 1 km·h−1 slower they cycled in the first time trial. This trend did not differ substantially between the groups (data not shown).
Characteristics of the subset of faster cyclists in each experimental group are shown in Table 1. Differences between means of some groups were substantial (more than 0.2 of a standard deviation) for every measure. Time for the first time trial showed the least differences between the six groups.
Figure 2 shows the raw mean and standard deviation for percent changes in mean power of the faster subjects within each of the experimental groups. The subjects who were told they received carbohydrate in their drink showed an improvement in performance on the second time trial, particularly those who were given the placebo. Subjects who were not told what was in the drink showed little change in performance in comparison with those who were told the drink was a placebo, irrespective of what was actually in the drink. The standard-deviation bars in Figure 2 show that the variation in performance in the two not-told groups was substantially greater than in the told-placebo and told-carbohydrate groups.
Full analysis of the changes in power output in the three told groups (taking into account the effect of speed in the first time trial and the different variances in change in performance in the three groups) produced the following outcomes: told carbohydrate, 4.3 ± 4.8%; told placebo, 0.5 ± 5.8%; and not told, −1.1 ± 8.5%. The change for the told-carbohydrate group minus the change for the told-placebo group (what might be called the full placebo effect) was 3.8% (7.9 to −0.2%, P = 0.06); the corresponding effect on simulated speed was 1.6%. The real effect of carbohydrate on output power (the change in power for those who were given carbohydrate minus the change in power for those who were given placebo) was a slight reduction in power (0.3%, 4.4 to −3.8%, P = 0.87), equivalent to a reduction in simulated speed of 0.2%.
The standard deviations in the change scores in each of the three told groups are equivalent to the following within-subject coefficients of variation: told carbohydrate, 3.4%; told placebo, 4.1%, not told, 6.0%. The coefficient of variation of the subjects in the not-told group was 1.6 times larger (likely range 1.0–2.6, P = 0.05) than the combined coefficients of variation of the subjects who were told what was in the drink.
Outcomes of the full analysis for the full set of 54 subjects were similar to those for the reduced set of faster, more reliable subjects, but the confidence intervals were wider. For example, the full placebo effect on power was 4.3% (9.2 to −0.7%, P = 0.09), and the true effect of carbohydrate was a reduction in power of 0.5% (5.3 to −4.3%, P = 0.83).
Cyclists in the not-told groups were asked, after completing the second time trial, whether they could tell which drink they had been given. All subjects reported that they could not tell whether they had been given carbohydrate or placebo.
Placebo effect of carbohydrate.
The main finding in this study is that the placebo effect of carbohydrate in a drink consumed during a time trial lasting about an hour is approximately a 4% enhancement of mean power for competitive cyclists of overall moderate ability. This enhancement is equivalent to an increase in speed of around 1.5%, on the reasonable assumption that the speed simulated by the Kingcycle is valid for road cycling. For such an enhancement to be worthwhile, it needs to be about half the typical variation in a top cyclist’s performance between competitions (8). As yet, there are no published data on the variability of competitive performance for cyclists, but for elite triathletes the variability of time for the 40-km cycle stage is 2.3% (W. G. Hopkins and C. D. Paton, unpublished observations). The variability of road cycling races is probably of similar magnitude, or even less if the effect of the preceding swim and the prospect of a following half marathon decreases the reliability of cycling 40 km in the triathlon. The variability of performance in cycling time trials, in which performance is not affected by the drafting strategies in massed-start events, is almost certainly less than the 2.3% of the cycle stage in a triathlon. The enhancement of 1.5% we observed for time to complete the time trial would therefore be worthwhile for competitive endurance cyclists. The estimate is not particularly precise, because the likely range of the true enhancement extends from a much stronger effect (about twice the observed enhancement) down to a trivial negative effect.
In an attempt to increase the precision of the estimate, we restricted the analysis to a subgroup consisting of faster, more reliable cyclists. Even so, the coefficients of variation of power in the conditions of the experiment (3.4, 4.1, and 6.0%) were substantially greater than the coefficient of variation of the same test in a reliability study (16) (∼2.5% when expressed as the reliability of power output (8)). We attribute the overall lower reliability to three factors. First, there is evidence that reliability of performance of self-paced endurance tests improves after a familiarization trial (for example (18,19)). Our subjects, especially those who were slower and presumably less familiar with 40-km time trials and road races, would almost certainly have been more reliable if they had performed a full 40-km familiarization trial. Second, our subjects performed the time trial in 58 min in the first time trial, which is a little slower than the 56 min of the subjects in the previous reliability study (16). As we have seen in the present study, slower subjects are less reliable. Finally, in the published reliability study, subjects were tested and retested without an experimental treatment, whereas we calculated the reliability of the performance test from data involving one of several treatments. Although a change in mean performance in response to a treatment does not directly affect the estimate of reliability, individual differences in the response to the treatment manifest themselves as a decrease in reliability (9) (an increase in within-subject variation). The extent of individual differences in the placebo effect (the effect of being told what was in the drink) was probably small, inasmuch as the first two factors contribute to at least part of the difference between the published reliability of 2.5% and our observed reliability of 3.4% and 4.1% with these two treatments. But not being told what was in the drink resulted in a substantially larger within-subject variation in performance (6.0%), and the confidence interval for this variation relative to that of the other two treatment groups indicates that the effect is almost certainly substantial in reality. Uncertainty about the treatment must have caused some subjects to make a greater effort than in the first time trial, whereas others resigned themselves to poorer performance.
The fact that uncertainty about a treatment can reduce the reliability of an endurance performance test has an important implication for the design of blind controlled trials: researchers can expect more variability in endurance performance in such trials than in reliability studies, where subjects are not given treatments. Sample sizes will therefore need to be larger than otherwise predicted from a reliability study. A crossover design for the controlled trial might avoid this problem, because each subject receives the placebo and real treatments in a crossover, and if the subject is equally uncertain about both treatments, the effect of uncertainty on performance should be reproducible between the treatments and should disappear when the difference between the treatments is calculated.
The existence of a placebo effect with a sham treatment and the existence of individual differences with a blind treatment both imply that at least some subjects do not give an all-out effort in a performance test. If, as seems likely, these subjects make a greater effort in a competitive event, the effect of a treatment in the performance test may be different from the effect of the treatment in a competitive event. For example, a treatment might work on the margin available between submaximal and maximal effort in a performance test, but that margin may be reduced or absent in a competitive event. We therefore advise caution in extrapolating endurance-performance enhancements observed in the laboratory to a competitive event, particularly if the enhancements in power are around 4% or less.
We must emphasize that we observed the placebo effect in a laboratory setting with athletes who on average were subelite. It is quite possible that top athletes in an important competitive event will be so motivated to succeed that any placebo effect will be over-ridden. Nevertheless, our findings are important for researchers studying endurance performance of subelite athletes who are not blind to a treatment that is potentially ergogenic. These researchers should recognize that observed enhancements of around 4% in output power could be due entirely to a placebo effect.
Further research on placebo effects for other treatments in other modes and durations of maximal performance is clearly warranted. Anyone conducting such research should increase the precision of their estimate of the placebo effect by getting their subjects to perform at least one full familiarization trial and by using a crossover design for the different treatments. Including a blind treatment in the crossover or in a more complex Latin-squares design would give useful information about the potential for crossovers to reduce the effect that uncertainty has on precision of estimates in blind trials. Identifying the subject characteristics that account for any individual differences in the placebo effect and for the apparently large individual differences in the response to a blind treatment would also be worthwhile. The most obvious place to start is with personality factors: we found one study in which the authors reported that dominant, independent subjects are less susceptible to the placebo effect of a sedative (14), although a later reviewer claimed that a placebo-responder personality has yet to be identified (22).
Real effect of carbohydrate.
In contrast to previous researchers (2,6,10,13), we found a negligible effect of supplementation with carbohydrate on performance of a high-intensity endurance test lasting about an hour. Differences in food consumption before the time trial may explain part of this discrepancy. We do not know exactly when our subjects had their last meal or snack before reporting to the laboratory, but our instruction to eat in the same manner as before a road race probably ensured that most had a substantial snack in the preceding hour. Many tests were also scheduled soon after breakfast or lunch. In contrast, subjects in previous studies had fasted either overnight (2), for at least 3 h (6), for at least 1 h (10), or for exactly 1.5 h (13) before exercise. It would appear that carbohydrate ingestion immediately before and during a time trial lasting ∼1 h is more likely to enhance performance the longer the athlete has fasted before the time trial. Other factors likely to be important include the amount and type of carbohydrate, the mode and duration of exercise, and the training status of the subjects (21).
Another possible explanation for the discrepancy is that the true effect is indeed a small enhancement encompassed by the confidence interval of our estimate and by the confidence intervals of the other reported enhancements. A meta-analysis of all the publications might reveal whether this true effect is likely to be large enough to be worthwhile in competitive events, but more research on the effect of the nature and timing of the last feeding before the time trial should precede any attempt to quantitatively synthesize research in this area. In the meantime, our advice to athletes will be based on the hypothesis that a light carbohydrate-rich meal consumed an hour or two before an endurance event lasting an hour should be sufficient to offset the negative effect of competing in a fasted state. We will also tell them that a drink containing carbohydrate consumed during the race may enhance their performance by an extra few percent. Should we tell them that any enhancement they get will probably be due to a placebo effect?
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