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Open-Label vs Placebo-Controlled Trials: Why Blinding Changes the Result

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· 10 min read

A summary of published research, with citations. It states no amount, schedule or route, and makes no claim about what this compound does in a person. Supplied for laboratory research use only.

On this page · 9 sections
  1. What do the terms actually mean?
  2. What is the placebo effect, really?
  3. And the nocebo effect?
  4. How much does missing blinding inflate results?
  5. Why do open-label extensions inflate effects?
  6. What about the Russian Semax studies?
  7. When is an open-label design reasonable?
  8. Questions to ask of any trial
  9. Frequently asked questions

In an open-label trial, participants and investigators know who is receiving the study drug. In a placebo-controlled trial, a comparison group receives an inactive look-alike, and in a double-blind version neither participants nor investigators know who has which. The difference matters most for outcomes that involve judgement or effort, such as symptom scores, fatigue, pain or walking tests. There, unblinded trials report larger effects. Open-label extensions, where everyone receives the drug after a blinded phase, are the most common way this inflation reaches a reader.

Two identical sealed envelopes, one with a teal dot and one with a navy dot, beside a clipboard
Illustration: concealed allocation keeps a study's arms indistinguishable.

What do the terms actually mean?

Placebo-controlled means one group receives an inactive preparation made to be indistinguishable from the drug. Active-controlled means the comparison is another treatment. SURPASS-CVOT compared tirzepatide with dulaglutide double-blind, for example. Uncontrolled or single-arm means there is no concurrent comparison group at all.

Blinding, or masking, is about who knows the allocation. Registries list it by role: participant, care provider, investigator and outcomes assessor. "Double-blind" usually means participants and investigators; "quadruple" means all four. Open-label means nobody is masked. A trial can be randomised and open-label. Randomisation decides who gets what; blinding decides who knows.

DesignWho knows the allocationWhat it protects againstExample
Double-blind, placebo-controlledNobody, until unblindingExpectation, biased assessment, natural course, regression to the meanMMPOWER-3; TRIUMPH-1
Double-blind, active-controlledNobodyThe same, but measures the drug against another drugSURPASS-CVOT
Randomised, open-labelEveryoneSelection bias onlyMany pragmatic and long-term trials
Open-label extensionEveryone; all on drugAlmost nothing about efficacy; useful for long-term tolerabilityTAZPOWER part 2
Uncontrolled case seriesEveryoneNothingMost human BPC-157 reports

What is the placebo effect, really?

Less than people assume. Hróbjartsson and Gøtzsche reviewed 130 trials that randomised patients to placebo or to no treatment at all, which is the only way to isolate a placebo effect. For binary outcomes, placebo had no significant effect: the pooled relative risk was 0.95, with a confidence interval of 0.88 to 1.02. For continuous outcomes there was a small benefit, concentrated in subjective outcomes. In pain trials it amounted to 6.5 mm on a 100-mm scale. The effect also shrank as trials got larger, which hints at small-study bias.

Much of what looks like a placebo effect in a trial's placebo arm has other causes: illness fluctuating on its own, regression to the mean, and the extra attention of being in a trial. A placebo arm does not need to know which of these is at work. It absorbs all of them, so that whatever is left over in the drug arm can be attributed to the drug. Without one, every one of them is counted as drug effect.

And the nocebo effect?

Expectation also produces side effects, and the clearest demonstration is the SAMSON trial (NCT02668016). People who had stopped statins because of side effects were given a year of monthly bottles in random order: some containing a statin, some placebo and some empty. Of 60 randomised, 49 completed. The mean symptom score was 8.0 in months with no tablets, 16.3 in statin months and 15.4 in placebo months, with no significant difference between statin and placebo. The authors calculated that 90% of the symptom burden of taking the statin was also produced by taking a placebo.

The lesson runs both ways. An open-label study can overstate benefit, and it can also misattribute harm. Only a blinded comparison separates what the drug does from what taking a drug does. How adverse events are recorded in blinded trials is illustrated in tirzepatide side effects.

How much does missing blinding inflate results?

It depends on the outcome. Wood and colleagues pooled 146 meta-analyses containing 1,346 trials. For subjective outcomes, trials without blinding exaggerated treatment effects, with a ratio of odds ratios of 0.75. Trials with inadequate allocation concealment did the same, at 0.69. For objective outcomes, the bias was negligible, at 1.01 for lack of blinding.

So the question to ask is not only "was it blinded?" but "could knowing have changed the measurement?" Death is hard to influence by expectation. A six-minute walk test, a fatigue questionnaire, a pain score or a clinician's global impression are not.

Why do open-label extensions inflate effects?

An open-label extension follows a randomised phase: everyone who wants to continue receives the drug, unblinded, often for years. Extensions are useful for long-term tolerability, and TAZPOWER's, for one, listed safety and tolerability as its primary endpoints. As efficacy evidence they have five built-in problems:

  • Expectation. Everyone knows they are on drug, and effort-dependent tests respond to motivation.
  • Selection. The people who continue are the ones who tolerated the drug and believed it helped. Those who dropped out are missing from the later averages.
  • No concurrent comparison. Changes are measured from a baseline, so natural fluctuation, regression to the mean and practice on a repeated test are all counted as effect.
  • A moving baseline. Results are often reported "from extension baseline", which resets the clock after the blinded phase.
  • Shrinking numbers. Late timepoints rest on whoever is left.

TAZPOWER is the example on this site. In the blinded crossover part, 12 people with Barth syndrome received elamipretide and placebo in random order, and neither primary endpoint was met. Ten continued into the open-label extension and eight reached 36 weeks, by which point the six-minute walk distance had improved by 95.9 metres. In the long-term report, eight of the ten reached week 168, with a cumulative 96.1-metre improvement from extension baseline. A later analysis compared the eight treated patients with 19 untreated patients from a natural-history cohort, matched by propensity score, and reported a 79.7-metre difference at week 64. An external control is better than none, but historical patients were not randomised, blinded or measured in the same programme.

Compare the same walk test measured blind at scale in a different mitochondrial disease. In MMPOWER-3, 218 adults with primary mitochondrial myopathy were randomised to elamipretide or placebo for 24 weeks. The difference in walk distance was −3.2 metres. These are different diseases, so the comparison proves nothing about Barth syndrome. It shows how far apart blinded and unblinded estimates of the same kind of measure can be.

Elamipretide received US accelerated approval for Barth syndrome in September 2025, and the randomised, quadruple-masked, placebo-controlled confirmatory trial, 4TAZPower (NCT07531251), is now recruiting. That trial is the design that can answer the question the extension could not. The wider record is in what is SS-31 (elamipretide), and the regulatory pathway in clinical trial phases explained.

What about the Russian Semax studies?

Semax is registered as a medicine in Russia on the strength of clinical research published largely in Russian. It is not approved by Health Canada, the FDA or the EMA. Two of the indexed stroke studies show why that literature is hard to weigh from outside.

In a 1997 study, Gusev and colleagues gave Semax to 30 patients in the acute period of ischaemic stroke. They compared them with 80 patients on conventional therapy, described as having strokes of similar severity and location, using clinical rating scales and electrophysiology. The abstract describes no randomisation and no placebo. A 2018 study by the same lead author followed 110 patients after stroke in early and late rehabilitation groups, each subdivided by whether they received Semax. It measured plasma BDNF, motor scores and the Barthel index. Again, the abstract describes no randomisation, placebo or blinding.

Rating scales and functional indices are exactly the outcomes Wood and colleagues found most susceptible to unblinded assessment. These studies may well have been carefully run, and the full texts may say more than the abstracts. As indexed, though, they cannot separate the compound's effect from expectation, selection and recovery over time. Semax and cerebral ischaemia covers the preclinical work, and Semax neuroprotection: known and untested covers what remains untested.

When is an open-label design reasonable?

When the outcome is objective and measured by someone who does not know the allocation; when blinding is impossible, as with surgery versus a drug; when the question is long-term tolerability; or when a disease is so rare that a placebo arm is not feasible. In each case the limitation should be stated, and claims about subjective benefit should be held more loosely.

Questions to ask of any trial

  • Was there a concurrent control group, and was allocation randomised?
  • Who was masked: participants, clinicians, outcome assessors?
  • Is the outcome objective, or does it depend on effort, report or judgement?
  • If results come from an extension, how many entered, how many remained, and what did the blinded phase show?
  • Are adverse events compared against a placebo rate, or reported in isolation?

The companion pages on how to read a peptide study and how to read a PubMed abstract cover the rest of the methods section. Nothing here is medical, dosing, or therapeutic guidance.

Frequently asked questions

Is a randomised open-label trial still a randomised controlled trial? Yes. Randomisation removes selection bias in who gets which treatment, and that survives without blinding. What is lost is protection against expectation and biased assessment, so open-label RCTs are most trustworthy when outcomes are objective or assessed by someone masked to allocation.

Why do open-label extensions exist if they inflate efficacy? Because they answer a different question well: whether a drug remains tolerable over years, and what rare adverse events emerge. They also let trial participants keep receiving an investigational drug. TAZPOWER's extension listed safety and tolerability as its primary endpoints. The problem arises when their efficacy figures are quoted as if they came from the blinded phase.

Can a placebo-controlled trial be unblinded by side effects? Yes. If a drug causes noticeable effects, such as nausea, participants and investigators may guess the allocation, and expectation partly returns. Good trials sometimes ask participants to guess their group at the end. Objective outcomes and masked outcome assessors limit the damage.

What is a nocebo effect? Symptoms caused by the expectation of harm rather than by the drug. In the SAMSON trial, participants who had previously abandoned statins reported nearly as many symptoms in placebo months as in statin months. Nocebo effects inflate apparent side effects in open-label settings, just as expectation inflates apparent benefit.

Selected Research References

  1. Hróbjartsson A, Gøtzsche PC. Is the placebo powerless? An analysis of clinical trials comparing placebo with no treatment. New England Journal of Medicine. 2001;344(21):1594-1602. pubmed.ncbi.nlm.nih.gov/11372012
  2. Howard JP, Wood FA, Finegold JA, et al. Side Effect Patterns in a Crossover Trial of Statin, Placebo, and No Treatment. Journal of the American College of Cardiology. 2021;78(12):1210-1222. pubmed.ncbi.nlm.nih.gov/34531021
  3. Wood L, Egger M, Gluud LL, et al. Empirical evidence of bias in treatment effect estimates in controlled trials with different interventions and outcomes: meta-epidemiological study. BMJ. 2008;336(7644):601-605. pubmed.ncbi.nlm.nih.gov/18316340
  4. Reid Thompson W, Hornby B, Manuel R, et al. A phase 2/3 randomized clinical trial followed by an open-label extension to evaluate the effectiveness of elamipretide in Barth syndrome, a genetic disorder of mitochondrial cardiolipin metabolism. Genetics in Medicine. 2021;23(3):471-478. pubmed.ncbi.nlm.nih.gov/33077895
  5. Thompson WR, Manuel R, Abbruscato A, et al. Long-term efficacy and safety of elamipretide in patients with Barth syndrome: 168-week open-label extension results of TAZPOWER. Genetics in Medicine. 2024;26(7):101138. pubmed.ncbi.nlm.nih.gov/38602181
  6. Hornby B, Thompson WR, Almuqbil M, et al. Natural history comparison study to assess the efficacy of elamipretide in patients with Barth syndrome. Orphanet Journal of Rare Diseases. 2022;17(1):336. pubmed.ncbi.nlm.nih.gov/36056411
  7. Karaa A, Bertini E, Carelli V, et al. Efficacy and Safety of Elamipretide in Individuals With Primary Mitochondrial Myopathy: The MMPOWER-3 Randomized Clinical Trial. Neurology. 2023;101(3):e238-e252. pubmed.ncbi.nlm.nih.gov/37268435
  8. Gusev EI, Skvortsova VI, Miasoedov NF, et al. Effectiveness of semax in acute period of hemispheric ischemic stroke (a clinical and electrophysiological study). Zhurnal Nevrologii i Psikhiatrii imeni S.S. Korsakova. 1997;97(6):26-34. pubmed.ncbi.nlm.nih.gov/11517472
  9. Gusev EI, Martynov MY, Kostenko EV, et al. The efficacy of semax in the treatment of patients at different stages of ischemic stroke. Zhurnal Nevrologii i Psikhiatrii imeni S.S. Korsakova. 2018;118(3 Vyp 2):61-68. pubmed.ncbi.nlm.nih.gov/29798983

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