Philosophical realism—usually not treated as a position of its own but as a stance towards other subject matters—is the view that a certain kind of thing (ranging widely from abstract objects like numbers to moral statements to the physical world itself) has mind-independent existence, i.e. that it exists even in the absence of any mind perceiving it or that its existence is not just a mere appearance in the eye of the beholder. This includes a number of positions within epistemology and metaphysics which express that a given thing instead exists independently of knowledge, thought, or understanding. This can apply to items such as the physical world, the past and future, other minds, and the self, though may also apply less directly to things such as universals, mathematical truths, moral truths, and thought itself. However, realism may also include various positions which instead reject metaphysical treatments of reality altogether.
Realism can also be a view about the properties of reality in general, holding that reality exists independent of the mind, as opposed to non-realist views (like some forms of skepticism and solipsism) which question the certainty of anything beyond one's own mind. Philosophers who profess realism often claim that truth consists in a correspondence between cognitive representations and reality.
Realists tend to believe that whatever we believe now is
only an approximation of reality but that the accuracy and fullness of
understanding can be improved. In some contexts, realism is contrasted with idealism. Today it is more often contrasted with anti-realism, for example in the philosophy of science.
The oldest use of the term "realism" appeared in medievalscholastic interpretations and adaptations of ancient Greek philosophy. The position was also held among many ancient Indian philosophies.
Etymology
The term comes from Late Latinrealis "real" and was first used in the abstract metaphysical sense by Immanuel Kant in 1781 (CPR A 369).
Metaphysical realism maintains that
"whatever exists does so, and has the properties and relations it does,
independently of deriving its existence or nature from being thought of
or experienced." In other words, an objective reality exists (not merely one or more subjective realities).
Perceptual realism is the common sense view that tables, chairs and
cups of coffee exist independently of perceivers. Direct realists also
claim that it is with such objects that we directly engage. The objects
of perception include such familiar items as paper clips, suns and olive
oil tins. It is these things themselves that we see, smell, touch,
taste and listen to. There are, however, two versions of direct realism:
naïve direct realism and scientific direct realism. They differ in the
properties they claim the objects of perception possess when they are
not being perceived. Naïve realism claims that such objects continue to
have all the properties that we usually perceive them to have,
properties such as yellowness, warmth, and mass. Scientific realism,
however, claims that some of the properties an object is perceived as
having are dependent on the perceiver, and that unperceived objects
should not be conceived as retaining them. Such a stance has a long
history:
By convention sweet and by convention bitter, by convention hot, by
convention cold, by convention colour; in reality atoms and void.
[Democritus, c. 460-370 BCE, quoted by Sextus Empiricus in Barnes, 1987,
pp. 252-253.
In contrast, some forms of idealism assert that no world exists apart from mind-dependent ideas and some forms of skepticism say we cannot trust our senses. The naive realist view is that objects have properties, such as texture, smell, taste and colour, that are usually perceived absolutely correctly. We perceive them as they really are.
Immanent realism is the ontological understanding which holds that universals are immanently real within particulars themselves, not in a separate realm, and not mere names. Most often associated with Aristotle and the Aristotelian tradition.
Scientific realism
is, at the most general level, the view that the world described by
science is the real world, as it is, independent of what we might take
it to be. Within philosophy of science,
it is often framed as an answer to the question "how is the success of
science to be explained?" The debate over what the success of science
involves centers primarily on the status of unobservable entities apparently talked about by scientific theories.
Generally, those who are scientific realists assert that one can make
reliable claims about unobservables (viz., that they have the same ontological status) as observables. Analytic philosophers
generally have a commitment to scientific realism, in the sense of
regarding the scientific method as a reliable guide to the nature of
reality. The main alternative to scientific realism is instrumentalism.
Scientific realism in physics
Realism in physics (especially quantum mechanics)
is the claim that the world is in some sense mind-independent: that
even if the results of a possible measurement do not pre-exist the act
of measurement, that does not require that they are the creation of the
observer (contrary to the "consciousness causes collapse" interpretation of quantum mechanics). That interpretation of quantum mechanics, on the other hand, states that the wave function
is already the full description of reality. The different possible
realities described by the wave function are equally true. The observer
collapses the wave function into their own reality. One's reality can be
mind-dependent under this interpretation of quantum mechanics.
Plato (left) and Aristotle (right), a detail of The School of Athens, a fresco by Raphael. In Plato's metaphysics, ever-unchanging Forms, or Ideas, exist apart from particular physical things, and are related to them as their prototype or exemplar. Aristotle's philosophy of reality also aims at the universal. Aristotle finds the universal, which he calls essence, in the commonalities of particular things.
Platonic realism is a radical form of realism regarding the existence of abstract objects, including universals,
which are often translated from Plato's works as "Forms". Since Plato
frames Forms as ideas that are literally real (existing even outside of
human minds), this stance is also called Platonic idealism. This should not be confused with "idealistic" in the ordinary sense of "optimistic" or with other types of philosophical idealism, as presented by philosophers such as George Berkeley. As Platonic abstractions
are not spatial, temporal, or subjectively mental, they are arguably
not compatible with the emphasis of Berkeley's idealism grounded in
mental existence. Plato's Forms include numbers and geometrical figures,
making his theory also include mathematical realism; they also include the Form of the Good, making it additionally include ethical realism.
In Aristotle's more modest view, the existence of
universals (like "blueness") is dependent on the particulars that
exemplify them (like a particular "blue bird", "blue piece of paper",
"blue robe", etc.), and those particulars exist independent of any
minds: classic metaphysical realism.
Ancient Indian philosophy
There were many ancient Indian realist schools, such as the
Mimamsa, Vishishtadvaita, Dvaita, Nyaya, Yoga, Samkhya, Sauntrantika,
Jain, Vaisesika, and others. They argued for their realist positions,
and heavily criticized idealism, like that of the Yogachara and Advaita Vedanta, and composed refutations of the Yogacara position.
Medieval philosophy
Medieval realism developed out of debates over the problem of universals. Universals are terms or properties that can be applied to many things,
such as "red", "beauty", "five", or "dog". Realism (also known as exaggerated realism) in this context, contrasted with conceptualism and nominalism, holds that such universals really exist, independently and somehow prior to the world. Moderate realism holds that they exist, but only insofar as they are instantiated in specific things; they do not exist separately
from the specific thing. Conceptualism holds that they exist, but only
in the mind, while nominalism holds that universals do not "exist" at
all but are no more than words (flatus vocis) that describe specific objects.
In early modern philosophy, Scottish Common Sense Realism was a school of philosophy which sought to defend naive realism against philosophical paradox and scepticism, arguing that matters of common sense
are within the reach of common understanding and that common-sense
beliefs even govern the lives and thoughts of those who hold
non-commonsensical beliefs. It originated in the ideas of the most
prominent members of the Scottish School of Common Sense, Thomas Reid, Adam Ferguson and Dugald Stewart, during the 18th century Scottish Enlightenment and flourished in the late 18th and early 19th centuries in Scotland and America.
The roots of Scottish Common Sense Realism can be found in responses to such philosophers as John Locke, George Berkeley, and David Hume. The approach was a response to the "ideal system" that began with Descartes' concept of the limitations of sense experience
and led Locke and Hume to a skepticism that called religion and the
evidence of the senses equally into question. The common sense realists
found skepticism to be absurd and so contrary to common experience that
it had to be rejected. They taught that ordinary experiences provide
intuitively certain assurance of the existence of the self, of real
objects that could be seen and felt and of certain "first principles"
upon which sound morality and religious beliefs could be established.
Its basic principle was enunciated by its founder and greatest figure,
Thomas Reid:
If there are certain principles, as I
think there are, which the constitution of our nature leads us to
believe, and which we are under a necessity to take for granted in the
common concerns of life, without being able to give a reason for
them—these are what we call the principles of common sense; and what is
manifestly contrary to them, is what we call absurd.
Flowchart
of four phases (enrollment, allocation, intervention, follow-up, and
data analysis) of a parallel randomized trial of two groups (in a
controlled trial, one of the interventions serves as the control),
modified from the CONSORT (Consolidated Standards of Reporting Trials)
2010 Statement
A randomized controlled trial (RCT) is a type of statistical experiment
designed to evaluate the efficacy or safety of an intervention by
minimizing bias through the random allocation of participants to one or
more comparison groups.
In this approach, at least one group receives the intervention or process under study (such as a drug, surgical procedure, medical device or diet), while the other groups receive an alternative treatment, a placebo, or standard care.
RCTs are a fundamental methodology in modern clinical trials and have been widely considered one of the highest-quality sources of evidence in evidence-based medicine,
due to their ability to reduce selection bias and the influence of
confounding factors. However, they have also been criticized for failing
to reduce bias in some cases.
Participants who enroll in RCTs differ from one another in
known and unknown ways that can influence study outcomes, and yet cannot
be directly controlled. By randomly allocating participants among compared treatments, an RCT enables statistical control
over these influences. Provided it is designed well, conducted
properly, and enrolls enough participants, an RCT may achieve sufficient
control over these confounding factors to deliver a useful comparison of the treatments studied.
Definition and examples
An RCT in clinical research typically compares a proposed new treatment against an existing standard of care;
these are then termed the 'experimental' and 'control' treatments,
respectively. When no such generally accepted treatment is available, a placebo may be used in the control group so that participants are blinded,
or not given information, about their treatment allocations. This
blinding principle is ideally also extended as much as possible to other
parties including researchers, technicians, data analysts, and
evaluators. Effective blinding experimentally isolates the physiological
effects of treatments from various psychological sources of bias.
The randomness in the assignment of participants to treatments reduces selection bias and allocation bias, balancing both known and unknown prognostic factors, in the assignment of treatments. Blinding reduces other forms of experimenter and subject biases.
A well-blinded RCT is considered the gold standard for clinical trials. Blinded RCTs are commonly used to test the efficacy of medical interventions and may additionally provide information about adverse effects, such as drug reactions. A randomized controlled trial can provide compelling evidence that the study treatment causes an effect on human health.
The terms "RCT" and "randomized trial" are sometimes used
synonymously, but the latter term omits mention of controls and can
therefore describe studies that compare multiple treatment groups with
each other in the absence of a control group. Similarly, the initialism is sometimes expanded as "randomized clinical trial" or "randomized comparative trial", leading to ambiguity in the scientific literature. Not all RCTs are randomized controlled
trials (and some of them could never be, as in cases where controls
would be impractical or unethical to use). The term randomized
controlled clinical trial is an alternative term used in clinical
research; however, RCTs are also employed in other research areas, including many of the social sciences.
History
In the posthumously published Ortus Medicinae (1648), Jan Baptist van Helmont made the first proposal of a RCT, to test two treatment regimes of fever. One treatment would be conducted by practitioners of Galenic medicine
involving bloodletting and purging, and the other would be conducted by
van Helmont. It is likely that he never conducted the trial, and merely
proposed it as an experiment that could be conducted.
The first reported clinical trial was conducted by James Lind in 1747 to identify a treatment for scurvy, and principles for conducting controlled trials were further elaborated by the Irish physician James Henry in 1843. The first blind experiment was conducted by the French Royal Commission on Animal Magnetism in 1784 to investigate the claims of mesmerism. An early essay advocating the blinding of researchers came from Claude Bernard in the latter half of the 19th century. Bernard recommended that the observer of an experiment should not have
knowledge of the hypothesis being tested. This suggestion contrasted
starkly with the prevalent Enlightenment-era attitude that scientific observation can only be objectively valid when undertaken by a well-educated, informed scientist. The first study recorded to have a blinded researcher was published in 1907 by W. H. R. Rivers and H. N. Webber to investigate the effects of caffeine.
In the early 20th century, 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 Randomized Controlled Trial in medicine 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.
Trial design was further influenced by the large-scale ISIS trials on heart attack treatments that were conducted in the 1980s.
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, and these have become widely accepted.
Ethics
Although subjects almost always provide informed consent
for their participation in an RCT, studies since 1982 have documented
that RCT subjects may 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. Determining the amount of information required to ensure informed consent can be difficult, and further research is necessary to determine the prevalence of and ways to address therapeutic misconception.
Placebo-controlled trials have been deemed unethical in
instances where not receiving treatment may lead to harm for the
patient, such as an aggravation of symptoms or risk of death. Crossover trials,
active-controlled trials, and other approaches have been used to
mitigate this issue, though these options may not always be suitable for
study, and have received their own criticism.
Active-controlled trials in particular may raise ethical considerations regarding clinical equipoise.
Although the principle of equipoise ("genuine uncertainty within the
expert medical community... about the preferred treatment") is common to
clinical trials and has been applied to RCTs, equipoise may be
difficult to ascertain, and the ethics of RCTs have special considerations. It has been argued that equipoise itself is insufficient to justify RCTs. "Collective equipoise" may also conflict with a lack of personal
equipoise (i.e., a personal belief that an intervention is effective), including that of the patient. 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." While some randomisation approaches have been used to minimize the risk
that patients are exposed to less effective treatment, such as
randomising patients with unequal rates, or adapting the rates during
the trial's duration based on outcomes, these solutions have been
criticized for raising more ethical problems than they resolve.
Whilst the above issues have resulted in robust practice
guidelines around the conduct of RCTs, formulating balanced regulations
tends to be difficult. Strict protections may act in favor of indigenous
populations, but could fail on a globalised setting, as their
imposition urges the outsourcing of trials to countries with poorer
standards and more economically vulnerable populations. Frameworks which
place great emphasis on patient well-being have also been criticized by
some as paternalistic.
The RCT method variations may also create cultural effects that have not been well understood. For example, patients with terminal illness may join trials in the hope
of being cured, even when treatments are unlikely to be successful.
Medical trial registration
In 2004, the International Committee of Medical Journal Editors
(ICMJE) announced that all trials starting enrolment after July 1,
2005, must be registered prior to consideration for publication in one
of the 12 member journals of the committee. However, trial registration may still occur late or not at all. Medical journals have been slow in adapting policies requiring mandatory
clinical trial registration as a prerequisite for publication.
Classifications
By study design
One way to classify RCTs is by study design. From most to least common in the healthcare literature, the major categories of RCT study designs are:
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.
Stepped-wedge trial
- " involves random and sequential crossover of clusters (of subjects)
from control to intervention until all clusters are exposed." In the past, this design has been called a "waiting list designs" or "phased implementations."
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).
An analysis of the 616 RCTs indexed in PubMed
during December 2006 found that 78% were parallel-group trials, 16%
were crossover, 2% were split-body, 2% were cluster, and 2% were
factorial.
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 (pRCTs) 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.
Randomization
The advantages of proper randomization in RCTs include:
"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.
However empirical evidence that adequate randomization
changes outcomes relative to inadequate randomization has been difficult
to detect.
Procedures
The treatment allocation is the desired proportion of patients in each treatment arm.
An ideal randomization procedure would achieve the following goals:
Maximize statistical power, especially in subgroup analyses.
Generally, equal group sizes maximize statistical power, however,
unequal groups sizes may be more powerful for some analyses (e.g.,
multiple comparisons of placebo versus several doses using Dunnett's
procedure), and are sometimes desired for non-analytic reasons (e.g., patients
may be more motivated to enroll if there is a higher chance of getting
the test treatment, or regulatory agencies may require a minimum number
of patients exposed to treatment).
Minimize selection bias. This may occur if investigators
can consciously or unconsciously preferentially enroll patients between
treatment arms. A good randomization procedure will be unpredictable
so that investigators cannot guess the next subject's group assignment
based on prior treatment assignments. The risk of selection bias is
highest when previous treatment assignments are known (as in unblinded
studies) or can be guessed (perhaps if a drug has distinctive side
effects).
Minimize allocation bias (or confounding). This may occur when covariates
that affect the outcome are not equally distributed between treatment
groups, and the treatment effect is confounded with the effect of the
covariates (i.e., an "accidental bias").
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.
Simple
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.
Restricted
To balance group sizes in smaller RCTs, some form of "restricted" randomization is recommended. The major types of restricted randomization used in RCTs are:
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 overrepresented and increases if the group is
underrepresented. The methods are thought to be less affected by selection bias than permuted-block randomization.
Adaptive
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 randomization process so that the treatment to be
allocated is not known before the patient is entered into the study") is
important in RCTs. In practice, 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), 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, a 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.
The number of treatment units (subjects or groups of
subjects) assigned to control and treatment groups, affects an RCT's
reliability. If the effect of the treatment is small, the number of
treatment units in either group may be insufficient for rejecting the
null hypothesis in the respective statistical test. The failure to reject the null hypothesis
would imply that the treatment shows no statistically significant
effect on the treated in a given test. But as the sample size increases,
the same RCT may be able to demonstrate a significant effect of the
treatment, even if this effect is small.
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 the 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
The types of statistical methods used in RCTs depend on the characteristics of the data and include:
Regardless of the statistical methods used, important considerations in the analysis of RCT data include:
Whether an 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 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, some examples are:
Consort 2010 Statement: Extension to Cluster Randomised Trials
"Reporting of surrogate endpoints in randomised
controlled trial reports (CONSORT-Surrogate): extension checklist with
explanation and elaboration"
Relative importance 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 questioned the belief 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. According to a 2014 (updated in 2024) Cochrane review, there is little
evidence for significant effect differences between observational
studies and randomized controlled trials. To evaluate differences it is necessary to consider things other than
design, such as heterogeneity, population, intervention or comparator.
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 metastatictesticular cancer, which increased the cure rate from 5% to 60% in a 1977 non-randomized study.
Interpretation of statistical results
Like all statistical methods, 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.
Peer review
Peer review of results is an important part of the scientific method.
Reviewers examine the study results for potential problems with design
that could lead to unreliable results (for example by creating a systematic bias),
evaluate the study in the context of related studies and other
evidence, and evaluate whether the study can be reasonably considered to
have proven its conclusions. To underscore the need for peer review and
the danger of overgeneralizing conclusions, two Boston-area medical
researchers performed a randomized controlled trial in which they
randomly assigned either a parachute or an empty backpack to 23
volunteers who jumped from either a biplane or a helicopter. The study
was able to accurately report that parachutes fail to reduce injury
compared to empty backpacks. The key context that limited the general
applicability of this conclusion was that the aircraft were parked on
the ground, and participants had only jumped about two feet.
Advantages
RCTs are considered 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 practice.
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."
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 2011 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 agentsflecainide 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 an 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.
Disadvantages
Many papers discuss the disadvantages of RCTs. Among the most frequently cited drawbacks are:
The conduct of an 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.
It is costly to maintain RCTs for the years or decades that would be ideal for evaluating some interventions.
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.
Due to the costs of running RCTs, these 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 aspects of the patient's medical situation (e.g. patient history, physical examination, diagnosis, psychosocial aspects, follow up).
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."
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." These results have been mirrored in trials in surgery, where although
industry funding did not affect the rate of trial discontinuation it was
however associated with a lower odds of publication for completed
trials. One possible reason for the pro-industry results in industry-funded published RCTs is publication bias. Other authors have cited the differing goals of academic and industry
sponsored research as contributing to the difference. Commercial
sponsors may be more focused on performing trials of drugs that have
already shown promise in early stage trials, and on replicating previous
positive results to fulfill regulatory requirements for drug approval.
Ethics and feasibility
Whilst RCTs are considered the golden standard of research
in evidence-based medicine, they may be inappropriate for study in
certain contexts. For instance, RCTs may be improper for studying
medical interventions with "obvious" benefits to patients, as such practice would unethically deny the control group of effective treatment. Challenges may also arise in instances where a treatment requires the
active participation of participants, such as psychotherapy or
approaches based on community development.
Historically, it has been difficult to effectively utilize
RCTs for the study of surgical procedures. Unlike with the study of
medication, where blinding tends to be relatively easy through placebos,
blinding of the investigator-surgeon may be impossible within a
surgical trial, and the evident physiological impacts of surgery may compromise
blinding on the part of the subjects without the use of sham controls,
which are only considered possible for a narrow range of surgical
interventions.
RCTs may also be considered infeasible or unethical for
studying the mental health impacts of interventions with obvious
physical effects, especially when those are highly sought out by
patients, such as with abortion and adolescent transgender healthcare. Other than compromising masking, it is likely that RCT study designs
for some of these interventions would also result in high likelihood of
withdrawal, non-adherence, and response bias in the control groups,
making RCTs potentially unreliable.
In social science
Due to the recent emergence of RCTs in social science,
their application in these fields remain a contested issue among
academics. Some writers from a medical or health background have argued
that existing research in a range of social science disciplines lacks
rigour, and should be improved by greater use of randomized control
trials. Similarly, many economists have found RCTs are the gold standard for ensuring outcomes represent causal inference and not just correlation. Overall, the adaptation of RCTs into social science has become significant in recent decades.
Economics
RCTs have become a staple of identifying causal inference among microeconomic studies, particularly in development economics. In 1994, Paul Glewwe, eventual Nobel Prize winner, Michael Kremer, and Sylvie Moulin started one of the earliest RCTs in an economic setting by conducting a long run intervention in a school in Kenya, publishing the results fifteen years later. Three years later in 1997, the largest field experiment in a developing context, the PROGRESA program in Mexico, was studied by a multitude of economic researchers.The impact of RCTs on the discipline has only grown, as economists have
found this method as a first-best approach to causal inference
identification. While not at the forefront, the use of RCTs has helped
to bolster the credibility revolution in empirical microeconomics, as well as becoming popularized as a result of the need for more rigorous identification.
Despite the shift towards using RCTs in research, there still remains division between economists on its use. John A. List, a proponent of field experiments, particularly RCTs, finds that this method differs significantly from lab experiments, and therefore provide more robust measures for identification. RCTs also offer the advantage of providing true observational data that can be used where the absence of data would make it difficult to build a causal model with.
The American Economic Association maintains a registry of all active and completed RCTs within the discipline. The registry is free to use and is designed to ensure researchers may
share information with regard to on-going field work, as well as
failures or limitations of study settings. Since its founding in 2013, the AEA has tracked over 7,400 field
experiments across 100 countries, with annual RCT registries growing
year over year.
Transport science
Researchers in transport science argue that public
spending on programmes such as school travel plans could not be
justified unless their efficacy is demonstrated by randomized controlled
trials. Graham-Rowe and colleagues reviewed 77 evaluations of transport interventions found in the
literature, categorising them into 5 "quality levels". They concluded
that most of the studies were of low quality and advocated the use of
randomized controlled trials wherever possible in future transport
research.
Dr. Steve Melia took issue with these conclusions, arguing that claims about the
advantages of RCTs, in establishing causality and avoiding bias, have
been exaggerated. He proposed the following eight criteria for the use
of RCTs in contexts where interventions must change human behaviour to
be effective:
The intervention:
Has not been applied to all members of a
unique group of people (e.g. the population of a whole country, all
employees of a unique organisation etc.)
Is applied in a context or setting similar to that which applies to the control group
Can be isolated from other activities—and the purpose of the study is to assess this isolated effect
Has a short timescale between its implementation and maturity of its effects
And the causal mechanisms:
Are either known to the researchers, or else all possible alternatives can be tested
Do not involve significant feedback mechanisms between the intervention group and external environments
Have a stable and predictable relationship to exogenous factors
Would act in the same way if the control group and intervention group were reversed
Criminology
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.
Education
RCTs have been used in evaluating a number of educational
interventions. Between 1980 and 2016, over 1,000 reports of RCTs have
been published. 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.
Criticism
A 2018 review of the 10 most cited randomised controlled
trials noted poor distribution of background traits, difficulties with
blinding, and discussed other assumptions and biases inherent in
randomised controlled trials. These include the "unique time period
assessment bias", the "background traits remain constant assumption",
the "average treatment effects limitation", the "simple treatment at the
individual level limitation", the "all preconditions are fully met
assumption", the "quantitative variable limitation" and the "placebo
only or conventional treatment only limitation".
