Recover faster

An umbrella review inherits the primary trials' limitations and cannot fix them, and moderate certainty still means the true effect may differ substantially from the estimate. No pooled effect sizes appear, only the gradings, so nothing here says how big the reduction is. Searches ran only to May 2022.

The pooled training ran about 12.6 weeks on average, so nothing here shows whether the gains hold over a year. The pool of qualifying trials is small, and the authors ask for more work in this age group before the functional gains are treated as durable.

These trials were built to test performance rather than to hunt for harm, so anything rare or slow enough to slip past them would have slipped past. The adverse-event reports are filed voluntarily, which distorts the count in both directions. Average intake across the pooled trials was about 12.5g of creatine a day.

An average 3.6 percent of body mass is more dehydration than most recreational exercisers ever reach, and the performance tests averaged 22 minutes. The dehydration was deliberately induced, usually by heat or fluid restriction, which brings its own fatigue on top of the water deficit. The confidence interval on the headline runs from 0.8 to 4.0 percent. Nothing here compares an electrolyte drink with water.

The people tested were mostly older adults with night-time leg cramps, not athletes cramping mid-race, so this settles the mineral rather than the sport. The pregnancy trials in the same review could not be pooled at all because their outcomes were reported inconsistently, and a separate Cochrane review graded those same trials as far less biased than this one did. Nothing here tests magnesium during exercise.

Children with gastroenteritis, which is nobody in a gym. The trials were graded poor to moderate quality and mostly unblinded, since a drink cannot be disguised as a drip. Each route carries its own complication: vein inflammation with the drip, a stalled gut with drinking, roughly one in 50 and one in 33. The death counts, six against two across four trials, are far too small to read anything into.

Hospitalised children with acute diarrhoea, compared against another rehydration solution rather than against water, so nothing here reaches a well person drinking one. This is the 2002 version of a review since updated, cited for the finding that changed the formulation. The trials were mostly unblinded and largely in low- and middle-income hospital settings. Low blood sodium was looked for in only six trials with events in three, so that reassurance rests on thin data.

The best diclofenac figure rests on two studies, and some of the ketoprofen data come from 1980s trials with loosely defined outcomes. Around 5,900 participants' worth of registered but never fully reported efficacy data was identified and could not be obtained, which is the direction publication bias usually runs. Only 220 people across all 61 trials were given a tablet for comparison, so the comparison with swallowing one is thin.

Ten trials is a small base, and the review reports no pooled effect size at all. Soreness is self-reported. The dose ceiling is where the evidence stops, not where a harm begins, and the review is explicit that it cannot speak to anything above it.

An overview of reviews inherits every weakness of the trials underneath it, and the same small primary studies are counted inside several of the eleven. The authors grade those reviews and report the recurring flaws: no justification for excluding studies, and no funding disclosure for the primary trials.

With 17 men on coffee, the trial was sized to catch a difference of 220 ml of urine or more, so a smaller loss could have gone unseen. Larger doses were not tested, and the researchers note a measurable effect on urine is likely once a single dose passes about 300 mg of caffeine. The men were fully hydrated and had fasted overnight. The litre went down in half an hour, not as cups spread across a day.

A position stand is expert consensus with no stated search and no risk-of-bias grading, and panels in this field have included researchers with sports-drink funding. It was written before the 2015 consensus on exercise-related low blood sodium and before the field studies that found sodium supplements did not prevent it. Advising people to individualise because sweat varies is not evidence that individualising improves any outcome, which is the step the personalised-hydration industry takes.

These are general-population reference values, not sport nutrition, and they describe what a healthy adult is thought to need over a day rather than what anyone should drink during exercise. The salt equivalent is arithmetic from the sodium figure, not a separately measured value. The report's own opening observation is that what you eat does not usually move your blood electrolyte levels, because the kidneys and hormones hold them steady.

One real exception sits inside the largest of these studies: among American footballers alone, sweat measurements did carry a weak signal, and in the other ten sports none did. Beyond that, cramping was self-reported throughout, and serum electrolytes were sampled before and after a race rather than inside the muscle at the moment a cramp struck, which is where the theory actually locates the problem. Forty-three crampers is enough to rule out a dominant effect, not a small one.

Twenty crampers is a small group, and the finish-line enzyme gap is borderline at p = 0.034 with spreads wide enough to swallow it. The blood was drawn after the cramp, so muscle damage could as easily follow a cramp as cause one. Crampers and non-crampers only diverged in pace from 25 kilometres onward, which points back at effort. The paper's own abstract calls 20 of 88 a rate of 24 percent; it is 22.7 percent.

Five desert stage races, which is what extreme heat does across six days, not what a hot afternoon does. Only 174 of the 266 runners enrolled gave a post-race sample. The link between hot races and low blood sodium is not statistically reliable, its interval running from 0.9 to 25.9; the link with high blood sodium is much firmer. And the 4.7 kilogram average carries a standard deviation twice its own size.

Both are narrative reviews with no stated search and no risk-of-bias grading, so which literature they cite is at the authors' discretion. The lead author of one chaired the consensus conferences on this condition, which makes the summary authoritative and not independent of the position it summarises. 'Conclusively identified' is their own confidence wording, not a graded rating.

One race, one temperate day in 2002, and a blood sample at the finish line rather than an experiment. Only 488 of the 766 runners who signed up gave a usable sample, so the 13 percent could sit either side of the truth. What people drank was reconstructed from a questionnaire they filled in after four hours of running.

These are the cases somebody wrote up. Severe and unusual presentations get published and mild ones do not, so this describes the case record rather than everyone it happened to. The search was a manual sweep of two databases, not a registered protocol. Women appear more often as a share of participants, not in greater numbers, a distinction the review itself insists on.

This concerns water, not electrolyte products, which were not tested here, so it undercuts the theory the hangover sachets rest on rather than testing the sachets themselves. It is a narrative review with no protocol or stated search, by a group that has argued this position for years. Much of the underlying evidence is people recalling their own drinking and their own hangovers. The authors do report that dehydration after alcohol is real, just mild and short-lived.

Fully hydrated, fasted men, all 72 of them male, drinking a litre in half an hour. Retention was measured as urine volume over four hours, not as anything a person would notice. And milk brings protein, fat and lactose along with its sodium and potassium, so what did the holding is not separated out here.

This is a reference-intake document for the general population, not exercise guidance, and it says nothing about what to drink during a race. The 2,300 milligram figure is a chronic-disease risk-reduction value introduced in the same 2019 report, not a toxicity threshold, and the child and adolescent versions were extrapolated from the adult one rather than measured. Anyone whose kidneys or medication affect how they handle potassium sits outside all of it.

This is transport physiology rather than a trial, and the two-to-one ratio is standard textbook mechanism restated by the review, not a new finding of it. The review was written to argue for developing drugs that improve on rehydration therapy, which frames how generously that therapy is described. Its own authors note the treatment reverses dehydration without shortening the illness or reducing stool output.

A survey of what runners believe; nothing in it tests whether the capsules work. Participants opted into a longitudinal tracking study, so they are more engaged with the sport than average, which makes the belief's persistence more striking rather than less. One country dominates the sample, one sport, 2018 data. The authors' verdict that the evidence is settled rests partly on their own earlier studies.

A chemical identity record, not a study: it says what these compounds weigh and nothing about what they do in a body. Both percentages were calculated from the retrieved molecular weights rather than read off the record, so they carry that rounding.

The men were fully hydrated and fasted when they drank, which is nobody's state when they reach for one of these, and retention behaves differently in someone already short of fluid. All 72 were male. The outcome is urine volume over four hours, a stand-in for retention rather than for feeling or performing better. The drinks were not matched for sodium, so this ranks these particular products, not electrolytes as an idea.

The analysis came out of a sports-drink manufacturer's own sweat-testing database, which cuts against the simplest commercial reading but travels with the finding either way. The people tested had chosen to come for sweat testing, so they skew athletic. Two of the three models used forearm patches, an indirect estimate; the whole-body method covered 48 tests. Unexplained variance includes measurement error, so this shows these variables do not predict sweat sodium, not that nothing could.

This is a second analysis of the same 31 participants, not an independent replication, so it inherits that trial's size and design unchanged. A null result across the markers measured narrows the candidates rather than showing that no mechanism exists. Muscle fibre size specifically was unaffected, which sits awkwardly next to the whole-muscle scan difference the earlier report described, and the authors do not reconcile the two.

The review's verdict that lion's mane is the most promising of the four is a ranking inside eleven papers, partly earned by having the most of them and by being safer than fly agaric. Several of those five come from one research group, so they are less independent than the count suggests.

Opioids showed a similar association, at 1.69, with no proposed bone-healing mechanism at all, which points at more painful or more severe fractures attracting stronger prescriptions rather than at the drugs themselves. Prescriptions filled stand in for drugs actually swallowed, and anything bought over the counter is invisible, which weakens the non-selective comparison specifically. Nonunion was rare, following 0.9% of episodes, so these odds sit on small absolute numbers.

Only the immediate before-versus-after contrast has been tested this way; nobody has randomised protein eaten hours from training. The direct-comparison review had five studies to work with, and in it lower-body strength did favour eating beforehand at p = 0.048, before the subgroup test declined to confirm it. The ten-week trial had 21 men, too few to prove equivalence. The author group behind two of these is publicly associated with the position they support.

Twelve men per group is not enough to rule out a modest real difference between the two proteins; the comparisons came out at p = 0.69 and p = 0.44. One night, no training outcome, no women. The exercise was endurance rather than resistance training, so the mitochondrial finding does not carry straight over to lifting. Both proteins were measured against a non-caloric placebo, so part of what is captured is protein against nothing.

Five small trials and 598 people between them, in settings almost nobody lives in: a subarctic military exercise, a 90 kilometre race, an Alpine ski camp. None of them tested ordinary gym-goers. The underlying trials date from the 1960s to the early 1990s and counted colds largely by asking people.

Eleven people took acetaminophen in this trial, out of 36 across three arms, and one muscle group was measured. Healthy older adults on a supervised programme are not a general population and not athletes. The dose was 4 g a day, the labelled maximum, which carries liver considerations this trial was neither designed nor powered to detect. The drug did nothing to the untrained hamstrings, so whatever is happening depends on the training rather than on the drug alone.

Soreness is self-reported on a visual scale, and it is a symptom rather than a measure of recovery or performance. The abstract reports no publication-bias check, no risk-of-bias grading and no funding disclosure for the trials pooled, in a field where manufacturers fund much of the primary work.

How much BCAAs ease soreness is unsettled. The largest estimate rests on the thinnest base, never checked for publication bias, while three more careful syntheses of the same question land smaller.

Weak discrimination is not a screening test, and the authors do not offer it as one. Cramp history was self-reported, and sweat was collected during ordinary training, never during a cramp. Forearm patches estimate whole-body sweat sodium indirectly and carry real measurement error. One other significant result among roughly fourteen comparisons, potassium content in women, is what chance produces at that many tests.

A label proves what a company was permitted to print, not that anything printed on it is true, and being listed on the US drug label database is not approval. This is one product, so it shows such a thing exists and is listed rather than that the category behaves this way. Its marketing text, including the three-bottles promise, sits inside the section reserved for safe-handling warnings, while the sections for indications, purpose, active ingredient and precautions are all empty.

Nobody was randomised: runners chose their own salt and their own drinking, so everything else they did differently comes along with the comparison. Intake was reconstructed from a questionnaire filled in after the race. Almost everyone supplemented, 94 in 100, which leaves barely any unsupplemented group at all, so this says more salt did not protect rather than that salt does nothing. Self-selected ultramarathon fields, single races.

Whether deliberately taking salt changes the risk of low blood sodium in endurance races is untested. Nobody has randomised runners to salt or none, because in these races almost everyone already takes it.

The finish-time result is a single p-value of 0.04 among eight reported outcomes, the shape of finding that most often fails to repeat. The abstract never says how many minutes faster, so the size of the advantage is not on the record anywhere. The trial's registry entry declared 40 participants against the 26 analysed, unexplained. Four to six hours of racing by trained triathletes says nothing about an hour in a gym.

One randomised trial found salt capsules got triathletes to the finish sooner, on a single borderline result in 26 people. Whether that holds up is open, because nobody has repeated it.

Thirty-one people in one trial and thirty-six in the other, one muscle group each. The comparators were not the same: the younger trial used low-dose aspirin rather than a true placebo, so it set a high dose against a low one rather than a drug against nothing. The training protocols and durations differed too, eight weeks against twelve. The older trial's authors state the direction was the opposite of what they expected.

Ibuprofen during strength training roughly halved muscle growth in young adults and added to it in older ones. Age, comparator, training and programme length all differed, so what flips the effect is unknown.

Eighty-nine runners, and the 18-point gap was not statistically significant, with an interval running from 4 points the other way to 41 points in favour. Kidney injury here means a creatinine rise measured at the finish line, a marker that often settles, not a clinical kidney outcome with follow-up. Runners who lost more weight during the race were independently more likely to be affected, so dehydration and the drug are tangled together in these numbers. Multi-day desert racing in heat is a deliberately stressed setting.

These measure a building rate across one night, not muscle retained across a training block. The forty-gram result in older men reached p = 0.02, and its supporting tracer analysis only p = 0.08. The founding study's clearly significant effects were whole-body, which includes gut and liver protein, not muscle specifically. Young men in two of the three trials, older men in the other, no women anywhere.

The trials for and against bedtime protein came from one laboratory, so dose likely explains the split: the effect appears somewhere between 30 and 40 g. Where exactly, and whether any muscle is kept, is untested.

Vitamin C and vitamin E were given together, so neither can be credited or blamed on its own. The marker changes carry enormous spread: the placebo group's rise averaged 59% with a standard deviation of 97%. Reviewers add that the blunting is inconsistent and rarely reached in ordinary training.