- Randomized controlled trial
A randomized controlled trial (RCT) is a type of scientific experiment - a form of clinical trial - most commonly used in testing the safety (or more specifically, information about adverse drug reactions and adverse effects of other treatments) and efficacy or effectiveness of healthcare services (such as medicine or nursing) or health technologies (such as pharmaceuticals, medical devices or surgery). The key distinguishing feature of the usual RCT is that study subjects, after assessment of eligibility and recruitment, but before the intervention to be studied begins, are randomly allocated to receive one or other of the alternative treatments under study. Random allocation in real trials is complex, but conceptually, the process is like tossing a coin. After randomization, the two (or more) groups of subjects are followed up in exactly the same way, and the only differences between the care they receive, for example, in terms of procedures, tests, outpatient visits, follow-up calls etc. should be those intrinsic to the treatments being compared. The most important advantage of proper randomization is that it minimises allocation bias, balancing both known and unknown prognostic factors, in the assignment of treatments."
The terms "RCT" and randomized trial are often used synonymously, but some authors distinguish between "RCTs" which compare treatment groups with control groups not receiving treatment (as in a placebo-controlled study), and "randomized trials" which can compare multiple treatment groups with each other. RCTs are sometimes known as randomized control trials. RCTs are also called randomized clinical trials or randomized controlled clinical trials when they concern clinical research; however, RCTs are also employed in other research areas such as criminology, education, social work and international development.
Randomized experiments first appeared in psychology, where they were introduced by Charles Sanders Peirce, and in education. Later, randomized experiments appeared in agriculture, due to Jerzy Neyman and Ronald A. Fisher. Fisher's experimental research and his writings popularized randomized experiments.
The first published RCT appeared in the 1948 paper entitled "Streptomycin treatment of pulmonary tuberculosis", which described a Medical Research Council investigation. One of the authors of that paper was Austin Bradford Hill, who is credited as having conceived the modern RCT.
By the late 20th century, RCTs were recognized as the standard method for "rational therapeutics" in medicine. As of 2004, more than 150,000 RCTs were in the Cochrane Library. To improve the reporting of RCTs in the medical literature, an international group of scientists and editors published Consolidated Standards of Reporting Trials (CONSORT) Statements in 1996, 2001, and 2010 which have become widely accepted.
Although the principle of clinical equipoise ("genuine uncertainty within the expert medical community... about the preferred treatment") common to clinical trials has been applied to RCTs, the ethics of RCTs have special considerations. For one, it has been argued that equipoise itself is insufficient to justify RCTs. For another, "collective equipoise" can conflict with a lack of personal equipoise (e.g., a personal belief that an intervention is effective). Finally, Zelen's design, which has been used for some RCTs, randomizes subjects before they provide informed consent, which may be ethical for RCTs of screening and selected therapies, but is likely unethical "for most therapeutic trials."
Classifications of RCTs
By study design
- Parallel-group – each participant is randomly assigned to a group, and all the participants in the group receive (or do not receive) an intervention.
- Crossover – over time, each participant receives (or does not receive) an intervention in a random sequence.
- Split-body – separate parts of the body of each participant (e.g., the left and right sides of the face) are randomized to receive (or not receive) an intervention.
- Cluster – pre-existing groups of participants (e.g., villages, schools) are randomly selected to receive (or not receive) an intervention.
- Factorial – each participant is randomly assigned to a group that receives a particular combination of interventions or non-interventions (e.g., group 1 receives vitamin X and vitamin Y, group 2 receives vitamin X and placebo Y, group 3 receives placebo X and vitamin Y, and group 4 receives placebo X and placebo Y).
By outcome of interest (efficacy vs. effectiveness)
RCTs can be classified as "explanatory" or "pragmatic." Explanatory RCTs test efficacy in a research setting with highly selected participants and under highly controlled conditions. In contrast, pragmatic RCTs test effectiveness in everyday practice with relatively unselected participants and under flexible conditions; in this way, pragmatic RCTs can "inform decisions about practice."
By hypothesis (superiority vs. noninferiority vs. equivalence)
Another classification of RCTs categorizes them as "superiority trials," "noninferiority trials," and "equivalence trials," which differ in methodology and reporting. Most RCTs are superiority trials, in which one intervention is hypothesized to be superior to another in a statistically significant way. Some RCTs are noninferiority trials "to determine whether a new treatment is no worse than a reference treatment." Other RCTs are equivalence trials in which the hypothesis is that two interventions are indistinguishable from each other.
- "It eliminates bias in treatment assignment," specifically selection bias and confounding.
- "It facilitates blinding (masking) of the identity of treatments from investigators, participants, and assessors."
- "It permits the use of probability theory to express the likelihood that any difference in outcome between treatment groups merely indicates chance."
There are two processes involved in randomizing patients to different interventions. First is choosing a randomization procedure to generate an unpredictable sequence of allocations; this may be a simple random assignment of patients to any of the groups at equal probabilities, may be "restricted," or may be "adaptive." A second and more practical issue is allocation concealment, which refers to the stringent precautions taken to ensure that the group assignment of patients are not revealed prior to definitively allocating them to their respective groups. Non-random "systematic" methods of group assignment, such as alternating subjects between one group and the other, can cause "limitless contamination possibilities" and can cause a breach of allocation concealment.
An ideal randomization procedure would achieve the following goals:
- Equal group sizes for adequate statistical power, especially in subgroup analyses.
- Low selection bias. That is, the procedure should not allow an investigator to predict the next subject's group assignment by examining which group has been assigned the fewest subjects up to that point.
- Low probability of confounding (i.e., a low probability of "accidental bias"), which implies a balance in covariates across groups. If the randomization procedure causes an imbalance in covariates related to the outcome across groups, estimates of effect may be biased if not adjusted for the covariates (which may be unmeasured and therefore impossible to adjust for).
However, no single randomization procedure meets those goals in every circumstance, so researchers must select a procedure for a given study based on its advantages and disadvantages.
This is a commonly used and intuitive procedure, similar to "repeated fair coin-tossing." Also known as "complete" or "unrestricted" randomization, it is robust against both selection and accidental biases. However, its main drawback is the possibility of imbalanced group sizes in small RCTs. It is therefore recommended only for RCTs with over 200 subjects.
- Permuted-block randomization or blocked randomization: a "block size" and "allocation ratio" (number of subjects in one group versus the other group) are specified, and subjects are allocated randomly within each block. For example, a block size of 6 and an allocation ratio of 2:1 would lead to random assignment of 4 subjects to one group and 2 to the other. This type of randomization can be combined with "stratified randomization", for example by center in a multicenter trial, to "ensure good balance of participant characteristics in each group." A special case of permuted-block randomization is random allocation, in which the entire sample is treated as one block. The major disadvantage of permuted-block randomization is that even if the block sizes are large and randomly varied, the procedure can lead to selection bias. Another disadvantage is that "proper" analysis of data from permuted-block-randomized RCTs requires stratification by blocks.
- Adaptive biased-coin randomization methods (of which urn randomization is the most widely-known type): In these relatively uncommon methods, the probability of being assigned to a group decreases if the group is over-represented and increases if the group is under-represented. The methods are thought to be less affected by selection bias than permuted-block randomization.
At least two types of "adaptive" randomization procedures have been used in RCTs, but much less frequently than simple or restricted randomization:
- Covariate-adaptive randomization, of which one type is minimization: The probability of being assigned to a group varies in order to minimize "covariate imbalance." Minimization is reported to have "supporters and detractors"; because only the first subject's group assignment is truly chosen at random, the method does not necessarily eliminate bias on unknown factors.
- Response-adaptive randomization, also known as outcome-adaptive randomization: The probability of being assigned to a group increases if the responses of the prior patients in the group were favorable. Although arguments have been made that this approach is more ethical than other types of randomization when the probability that a treatment is effective or ineffective increases during the course of an RCT, ethicists have not yet studied the approach in detail.
"Allocation concealment" (defined as "the procedure for protecting the randomisation process so that the treatment to be allocated is not known before the patient is entered into the study") is considered desirable in RCTs. In practice, in taking care of individual patients, clinical investigators in RCTs often find it difficult to maintain impartiality. Stories abound of investigators holding up sealed envelopes to lights or ransacking offices to determine group assignments in order to dictate the assignment of their next patient. Such practices introduce selection bias and confounders (both of which should be minimized by randomization), thereby possibly distorting the results of the study. Adequate allocation concealment should defeat patients and investigators from discovering treatment allocation once a study is underway and after the study has concluded. Treatment related side-effects or adverse events may be specific enough to reveal allocation to investigators or patients thereby introducing bias or influencing any subjective parameters collected by investigators or requested from subjects.
Some standard methods of ensuring allocation concealment include sequentially-numbered, opaque, sealed envelopes (SNOSE); sequentially-numbered containers; pharmacy controlled randomization; and central randomization. It is recommended that allocation concealment methods be included in an RCT's protocol, and that the allocation concealment methods should be reported in detail in a publication of an RCT's results; however, 2005 study determined that most RCTs have unclear allocation concealment in their protocols, in their publications, or both. On the other hand, a 2008 study of 146 meta-analyses concluded that the results of RCTs with inadequate or unclear allocation concealment tended to be biased toward beneficial effects only if the RCTs' outcomes were subjective as opposed to objective.
An RCT may be Blinded, (also called "masked") by "procedures that prevent study participants, caregivers, or outcome assessors from knowing which intervention was received." Unlike allocation concealment, blinding is sometimes inappropriate or impossible to perform in an RCT; for example, if an RCT involves a treatment in which active participation of the patient is necessary (e.g., physical therapy), participants cannot be blinded to the intervention.
Traditionally, blinded RCTs have been classified as "single-blind," "double-blind," or "triple-blind"; however, in 2001 and 2006 two studies showed that these terms have different meanings for different people. The 2010 CONSORT Statement specifies that authors and editors should not use the terms "single-blind," "double-blind," and "triple-blind"; instead, reports of blinded RCT should discuss "If done, who was blinded after assignment to interventions (for example, participants, care providers, those assessing outcomes) and how."
RCTs without blinding are referred to as "unblinded", "open", or (if the intervention is a medication) "open-label". In 2008 a study concluded that the results of unblinded RCTs tended to be biased toward beneficial effects only if the RCTs' outcomes were subjective as opposed to objective; for example, in an RCT of treatments for multiple sclerosis, unblinded neurologists (but not blinded neurologists) felt that the treatments were beneficial. In pragmatic RCTs, although the participants and providers are often unblinded, it is "still desirable and often possible to blind the assessor or obtain an objective source of data for evaluation of outcomes."
Analysis of data from RCTs
The types of statistical methods used in RCTs depend on the characteristics of the data and include:
- For dichotomous (binary) outcome data, logistic regression (e.g., to predict sustained virological response after receipt of peginterferon alfa-2a for hepatitis C) and other methods can be used.
- For continuous outcome data, analysis of covariance (e.g., for changes in blood lipid levels after receipt of atorvastatin after acute coronary syndrome) tests the effects of predictor variables.
- For time-to-event outcome data that may be censored, survival analysis (e.g., Kaplan–Meier estimators and Cox proportional hazards models for time to coronary heart disease after receipt of hormone replacement therapy in menopause) is appropriate.
Regardless of the statistical methods used, important considerations in the analysis of RCT data include:
- Whether a RCT should be stopped early due to interim results. For example, RCTs may be stopped early if an intervention produces "larger than expected benefit or harm," or if "investigators find evidence of no important difference between experimental and control interventions."
- The extent to which the groups can be analyzed exactly as they existed upon randomization (i.e., whether a so-called "intention-to-treat analysis" is used). A "pure" intention-to-treat analysis is "possible only when complete outcome data are available" for all randomized subjects; when some outcome data are missing, options include analyzing only cases with known outcomes and using imputed data. Nevertheless, the more that analyses can include all participants in the groups to which they were randomized, the less bias that an RCT will be subject to.
- Whether subgroup analysis should be performed. These are "often discouraged" because multiple comparisons may produce false positive findings that cannot be confirmed by other studies.
Reporting of RCT results
The CONSORT 2010 Statement is "an evidence-based, minimum set of recommendations for reporting RCTs." The CONSORT 2010 checklist contains 25 items (many with sub-items) focusing on "individually randomised, two group, parallel trials" which are the most common type of RCT. For other RCT study designs, "CONSORT extensions" have been published.
RCTs are considered by most to be the most reliable form of scientific evidence in the hierarchy of evidence that influences healthcare policy and practice because RCTs reduce spurious causality and bias. Results of RCTs may be combined in systematic reviews which are increasingly being used in the conduct of evidence-based medicine. Some examples of scientific organizations' considering RCTs or systematic reviews of RCTs to be the highest-quality evidence available are:
- As of 1998, the National Health and Medical Research Council of Australia designated "Level I" evidence as that "obtained from a systematic review of all relevant randomised controlled trials" and "Level II" evidence as that "obtained from at least one properly designed randomised controlled trial."
- Since at least 2001, in making clinical practice guideline recommendations the United States Preventive Services Task Force has considered both a study's design and its internal validity as indicators of its quality. It has recognized "evidence obtained from at least one properly randomized controlled trial" with good internal validity (i.e., a rating of "I-good") as the highest quality evidence available to it.
- The GRADE Working Group concluded in 2008 that "randomised trials without important limitations constitute high quality evidence."
- For issues involving "Therapy/Prevention, Aetiology/Harm," the Oxford Centre for Evidence-based Medicine]] as of 2009 defined "Level 1a" evidence as a systematic review of RCTs that are consistent with each other, and "Level 1b" evidence as an "individual RCT (with narrow Confidence Interval)."
Notable RCTs with unexpected results that contributed to changes in clinical practice include:
- After Food and Drug Administration approval, the antiarrhythmic agents flecainide and encainide came to market in 1986 and 1987 respectively. The non-randomized studies concerning the drugs were characterized as "glowing", and their sales increased to a combined total of approximately 165,000 prescriptions per month in early 1989. In that year, however, a preliminary report of a RCT concluded that the two drugs increased mortality. Sales of the drugs then decreased.
- Prior to 2002, based on observational studies, it was routine for physicians to prescribe hormone replacement therapy for post-menopausal women to prevent myocardial infarction. In 2002 and 2004, however, published RCTs from the Women's Health Initiative claimed that women taking hormone replacement therapy with estrogen plus progestin had a higher rate of myocardial infarctions than women on a placebo, and that estrogen-only hormone replacement therapy caused no reduction in the incidence of coronary heart disease. Possible explanations for the discrepancy between the observational studies and the RCTs involved differences in methodology, in the hormone regimens used, and in the populations studied. The use of hormone replacement therapy decreased after publication of the RCTs.
Limitations of external validity
- Where the RCT was performed (e.g., what works in one country may not work in another)
- Characteristics of the patients (e.g., an RCT may include patients whose prognosis is better than average, or may exclude "women, children, the elderly, and those with common medical conditions")
- Study procedures (e.g., in an RCT patients may receive intensive diagnostic procedures and follow-up care difficult to achieve in the "real world")
- Outcome measures (e.g., RCTs may use composite measures infrequently used in clinical practice)
- Incomplete reporting of adverse effects of interventions
RCTs can be expensive; one study found 28 Phase III RCTs funded by the National Institute of Neurological Disorders and Stroke prior to 2000 with a total cost of US$335 million, for a mean cost of US$12 million per RCT. Nevertheless, the return on investment of RCTs may be high, in that the same study projected that the 28 RCTs produced a "net benefit to society at 10-years" of 46 times the cost of the trials program, based on evaluating a quality-adjusted life year as equal to the prevailing mean per capita gross domestic product.
The conduction of a RCT takes several years until being published, thus data is restricted from the medical community for long years and may be of less relevance at time of publication.
Relative importance of RCTs and observational studies
Two studies published in The New England Journal of Medicine in 2000 found that observational studies and RCTs overall produced similar results. The authors of the 2000 findings cast doubt on the ideas that "observational studies should not be used for defining evidence-based medical care" and that RCTs' results are "evidence of the highest grade." However, a 2001 study published in Journal of the American Medical Association concluded that "discrepancies beyond chance do occur and differences in estimated magnitude of treatment effect are very common" between observational studies and RCTs.
Two other lines of reasoning question RCTs' contribution to scientific knowledge beyond other types of studies:
- If study designs are ranked by their potential for new discoveries, then anecdotal evidence would be at the top of the list, followed by observational studies, followed by RCTs.
- RCTs may be unnecessary for treatments that have dramatic and rapid effects relative to the expected stable or progressively worse natural course of the condition treated. One example is combination chemotherapy including cisplatin for metastatic testicular cancer, which increased the cure rate from 5% to 60% in a 1977 non-randomized study.
Difficulty in studying rare events
Interventions to prevent events that occur only infrequently (e.g., sudden infant death syndrome) and uncommon adverse outcomes (e.g., a rare side effect of a drug) would require RCTs with extremely large sample sizes and may therefore best be assessed by observational studies.
Difficulty in studying outcomes in distant future
Pro-industry findings in industry-funded RCTs
Some RCTs are fully or partly funded by the health care industry (e.g., the pharmaceutical industry) as opposed to government, nonprofit, or other sources. A systematic review published in 2003 found four 1986-2002 articles comparing industry-sponsored and nonindustry-sponsored RCTs, and in all the articles there was a correlation of industry sponsorship and positive study outcome. A 2004 study of 1999-2001 RCTs published in leading medical and surgical journals determined that industry-funded RCTs "are more likely to be associated with statistically significant pro-industry findings." One possible reason for the pro-industry results in industry-funded published RCTs is publication bias.
Although subjects almost always provide informed consent for their participation in an RCT, studies since 1982 have documented that many RCT subjects believe that they are certain to receive treatment that is best for them personally; that is, they do not understand the difference between research and treatment. Further research is necessary to determine the prevalence of and ways to address this "therapeutic misconception".
Narrowing of the studied question
Randomized clinical trials are usually only inspect one variable or very few variables, rarely reflecting the full picture of a complicated medical situation; whereas the case report, for example, can detail many different aspects of the patient’s medical situation (e.g. patient history, physical examination, diagnosis, psychosocial aspects, follow up).
RCTs are subject to both type I ("false positive") and type II ("false negative") statistical errors. Regarding Type I errors, a typical RCT will use 0.05 (i.e., 1 in 20) as the probability that the RCT will falsely find two equally effective treatments significantly different. Regarding Type II errors, despite the publication of a 1978 paper noting that the sample sizes of many "negative" RCTs were too small to make definitive conclusions about the negative results, by 2005-2006 a sizeable proportion of RCTs still had inaccurate or incompletely-reported sample size calculations.
The RCT method creates cultural effects that have not been well understood. For example, patients with terminal illness may attempt to join trials as a last ditch attempt at treatment, even when treatments are unlikely to be successful.
Conflict of interest dangers
A 2011 study done to disclose possible conflicts of interests in underlying research studies used for medical meta-analyses reviewed 29 meta-analyses and found that conflicts of interests in the studies underlying the meta-analyses were rarely disclosed. The 29 meta-analyses included 11 from general medicine journals; 15 from specialty medicine journals, and 3 from the Cochrane Database of Systematic Reviews. The 29 meta-analyses reviewed an aggregate of 509 randomized controlled trials (RCTs). Of these, 318 RCTs reported funding sources with 219 (69%) industry funded. 132 of the 509 RCTs reported author conflict of interest disclosures, with 91 studies (69%) disclosing industry financial ties with one or more authors. The information was, however, seldom reflected in the meta-analyses. Only two (7%) reported RCT funding sources and none reported RCT author-industry ties. The authors concluded “without acknowledgment of COI due to industry funding or author industry financial ties from RCTs included in meta-analyses, readers’ understanding and appraisal of the evidence from the meta-analysis may be compromised.”
RCTs in criminology, education, and international development
A 2005 review found 83 randomized experiments in criminology published in 1982-2004, compared with only 35 published in 1957-1981. The authors classified the studies they found into five categories: "policing", "prevention", "corrections", "court", and "community". Focusing only on offending behavior programs, Hollin (2008) argued that RCTs may be difficult to implement (e.g., if an RCT required "passing sentences that would randomly assign offenders to programmes") and therefore that experiments with quasi-experimental design are still necessary.
RCTs have been used in evaluating a number of educational interventions. For example, a 2009 study randomized 260 elementary school teachers' classrooms to receive or not receive a program of behavioral screening, classroom intervention, and parent training, and then measured the behavioral and academic performance of their students. Another 2009 study randomized classrooms for 678 first-grade children to receive a classroom-centered intervention, a parent-centered intervention, or no intervention, and then followed their academic outcomes through age 19.
RCTs are currently being used by a number of international development experts to measure the impact of development interventions worldwide. Development economists at research organizations including Abdul Latif Jameel Poverty Action Lab and Innovations for Poverty Action have used RCTs to measure the effectiveness of poverty, health, and education programs in the developing world. While RCTs can be useful in policy evaluation, it is necessary to exercise care in interpreting the results in social science settings. For example, interventions can inadvertently induce socioeconomic and behavioral changes that can confound the relationships (Bhargava, 2008).
For some development economists, the main benefit to using RCTs compared to other research methods is that randomization guards against selection bias, a problem present in many current studies of development policy. In one notable example of a cluster RCT in the field of development economics, Olken (2007) randomized 608 villages in Indonesia in which roads were about to be built into six groups (no audit vs. audit, and no invitations to accountability meetings vs. invitations to accountability meetings vs. invitations to accountability meetings along with anonymous comment forms). After estimating "missing expenditures" (a measure of corruption), Olken concluded that government audits were more effective than "increasing grassroots participation in monitoring" in reducing corruption. However, similar conclusions can also be reached by suitable modeling of the data from longitudinal studies. Overall, it is important in social sciences to account for the intended as well as the unintended consequences of interventions for policy evaluations.
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