Un ensayo controlado aleatorio (o ensayo de control aleatorio ; [2] ECA ) es un tipo de experimento científico (por ejemplo, un ensayo clínico ) o estudio de intervención (en oposición al estudio observacional ) que tiene como objetivo reducir ciertas fuentes de sesgo al probar la efectividad de nuevos tratamientos; esto se logra asignando sujetos al azar a dos o más grupos, tratándolos de manera diferente y luego comparándolos con respecto a una respuesta medida. Un grupo, el grupo experimental, recibe la intervención que se está evaluando, mientras que el otro, generalmente llamado grupo de control, recibe un tratamiento alternativo, como unplacebo o ninguna intervención. Los grupos se controlan en las condiciones del diseño del ensayo para determinar la eficacia de la intervención experimental y se evalúa la eficacia en comparación con el control. [3] Puede haber más de un grupo de tratamiento o más de un grupo de control .
El ensayo puede ser cegado , lo que significa que la información que puede influir en los participantes se retiene hasta que se completa el experimento. Se puede imponer un ciego a cualquier participante de un experimento, incluidos sujetos, investigadores, técnicos, analistas de datos y evaluadores. El cegamiento efectivo puede reducir o eliminar algunas fuentes de sesgo experimental .
La aleatoriedad en la asignación de sujetos a grupos reduce el sesgo de selección y el sesgo de asignación, equilibrando factores pronósticos conocidos y desconocidos, en la asignación de tratamientos. [4] El cegamiento reduce otras formas de sesgos del experimentador y del sujeto .
Un ECA bien ciego a menudo se considera el estándar de oro para los ensayos clínicos . Los ECA cegados se utilizan comúnmente para probar la eficacia de las intervenciones médicas y, además, pueden proporcionar información sobre los efectos adversos, como las reacciones a los medicamentos . Un ensayo controlado aleatorio puede proporcionar pruebas convincentes de que el tratamiento del estudio tiene un efecto sobre la salud humana. [5]
Los términos "ECA" y " ensayo aleatorizado " a veces se usan como sinónimos, pero el último término omite la mención de los controles y, por lo tanto, puede describir estudios que comparan múltiples grupos de tratamiento entre sí en ausencia de un grupo de control. [6] De manera similar, el inicialismo a veces se expande como " ensayo clínico aleatorio " o " ensayo comparativo aleatorio ", lo que genera ambigüedad en la literatura científica . [7] [8] No todos los ensayos clínicos aleatorios son ensayos controlados aleatorios (y algunos de ellos nunca podrían serlo, como en los casos en que los controles no serían prácticos o no serían éticos de instituir). El término ensayo clínico controlado aleatorio es un término alternativo utilizado en la investigación clínica ; [9] sin embargo, los ECA también se emplean en otras áreas de investigación, incluidas muchas de las ciencias sociales .
Historia
El primer ensayo clínico informado fue realizado por James Lind en 1747 para identificar el tratamiento del escorbuto . [10] Los experimentos aleatorios aparecieron en psicología , donde fueron introducidos por Charles Sanders Peirce y Joseph Jastrow en la década de 1880, [11] y en educación . [12] [13] [14] Más tarde, a principios del siglo XX, aparecieron experimentos aleatorios en la agricultura, gracias a Jerzy Neyman [15] y Ronald A. Fisher . La investigación experimental de Fisher y sus escritos popularizaron los experimentos aleatorios. [dieciséis]
El primer ECA publicado en medicina apareció en el artículo de 1948 titulado " Tratamiento con estreptomicina de la tuberculosis pulmonar ", que describía una investigación del Medical Research Council . [17] [18] [19] Uno de los autores de ese artículo fue Austin Bradford Hill , a quien se le atribuye haber concebido el ECA moderno. [20]
El diseño de los ensayos también se vio influenciado por los ensayos de ISIS a gran escala sobre tratamientos para ataques cardíacos que se realizaron en la década de 1980. [21]
A finales del siglo XX, los ECA fueron reconocidos como el método estándar para la "terapéutica racional" en la medicina. [22] En 2004, más de 150 000 ECA se encontraban en la Biblioteca Cochrane . [20] Para mejorar la presentación de informes de ECA en la literatura médica, un grupo internacional de científicos y editores publicó Declaraciones Consolidated Standards of Reporting Trials (CONSORT) en 1996, 2001 y 2010, que han sido ampliamente aceptadas. [1] [4] La aleatorización es el proceso de asignar sujetos de prueba a grupos de tratamiento o de control utilizando un elemento de azar para determinar las asignaciones con el fin de reducir el sesgo.
Ética
Aunque el principio de equilibrio clínico ("incertidumbre genuina dentro de la comunidad médica experta ... sobre el tratamiento preferido") común a los ensayos clínicos [23] se ha aplicado a los ECA, la ética de los ECA tiene consideraciones especiales. Por un lado, se ha argumentado que el equilibrio en sí mismo es insuficiente para justificar los ECA. [24] Por otro lado, el "equilibrio colectivo" puede entrar en conflicto con la falta de equilibrio personal (por ejemplo, la creencia personal de que una intervención es eficaz). [25] Finalmente, el diseño de Zelen , que se ha utilizado para algunos ECA, aleatoriza a los sujetos antes de que brinden el consentimiento informado, lo que puede ser ético para los ECA de detección y terapias seleccionadas, pero probablemente no sea ético "para la mayoría de los ensayos terapéuticos". [26] [27]
Aunque los sujetos casi siempre dan su consentimiento informado para su participación en un ECA, los estudios desde 1982 han documentado que los sujetos del ECA pueden creer que seguramente recibirán el mejor tratamiento para ellos personalmente; es decir, no comprenden la diferencia entre investigación y tratamiento. [28] [29] Se necesitan más investigaciones para determinar la prevalencia y las formas de abordar este " concepto terapéutico erróneo ". [29]
Las variaciones del método RCT también pueden crear efectos culturales que no se han entendido bien. [30] Por ejemplo, los pacientes con enfermedades terminales pueden participar en los ensayos con la esperanza de curarse, incluso cuando es poco probable que los tratamientos tengan éxito.
Registro de prueba
En 2004, el Comité Internacional de Editores de Revistas Médicas (ICMJE) anunció que todos los ensayos que se inscribieran después del 1 de julio de 2005 deben registrarse antes de ser considerados para su publicación en una de las 12 revistas miembros del comité. [31] Sin embargo, el registro de la prueba puede ocurrir tarde o no. [32] [33] Las revistas médicas han tardado en adaptar las políticas que requieren el registro obligatorio de ensayos clínicos como requisito previo para la publicación. [34]
Clasificaciones
Por diseño de estudio
Una forma de clasificar los ECA es mediante el diseño del estudio . De la más a la menos común en la literatura sobre atención médica, las categorías principales de diseños de estudios de ECA son: [35]
- Grupo paralelo : cada participante se asigna aleatoriamente a un grupo y todos los participantes del grupo reciben (o no reciben) una intervención. [36] [37]
- Cruce : con el tiempo, cada participante recibe (o no recibe) una intervención en una secuencia aleatoria. [38] [39]
- Clúster : grupos preexistentes de participantes (por ejemplo, pueblos, escuelas) se seleccionan al azar para recibir (o no recibir) una intervención. [40] [41]
- Factorial : cada participante es asignado al azar a un grupo que recibe una combinación particular de intervenciones o no intervenciones (p. Ej., El grupo 1 recibe vitamina X y vitamina Y, el grupo 2 recibe vitamina X y placebo Y, el grupo 3 recibe placebo X y vitamina Y , y el grupo 4 recibe placebo X y placebo Y).
Un análisis de los 616 ECA indexados en PubMed durante diciembre de 2006 encontró que el 78% eran ensayos de grupos paralelos, el 16% eran cruzados, el 2% eran de cuerpo dividido, el 2% eran grupos y el 2% eran factoriales. [35]
Por resultado de interés (eficacia frente a efectividad)
Los ECA se pueden clasificar como "explicativos" o "pragmáticos". [42] Los ECA explicativos prueban la eficacia en un entorno de investigación con participantes muy seleccionados y en condiciones muy controladas. [42] En contraste, los ECA pragmáticos (pRCT) prueban la efectividad en la práctica diaria con participantes relativamente no seleccionados y bajo condiciones flexibles; de esta manera, los ECA pragmáticos pueden "informar las decisiones sobre la práctica". [42]
Por hipótesis (superioridad frente a no inferioridad frente a equivalencia)
Otra clasificación de los ECA los clasifica como "ensayos de superioridad", "ensayos de no inferioridad" y "ensayos de equivalencia", que difieren en metodología e informes. [43] La mayoría de los ECA son ensayos de superioridad, en los que se supone que una intervención es superior a otra de una manera estadísticamente significativa . [43] Algunos ECA son ensayos de no inferioridad "para determinar si un nuevo tratamiento no es peor que un tratamiento de referencia". [43] Otros ECA son ensayos de equivalencia en los que la hipótesis es que dos intervenciones son indistinguibles entre sí. [43]
Aleatorización
Las ventajas de una asignación al azar adecuada en los ECA incluyen: [44]
- "Elimina el sesgo en la asignación del tratamiento", específicamente el sesgo de selección y los factores de confusión .
- "Facilita el cegamiento (enmascaramiento) de la identidad de los tratamientos de los investigadores, participantes y evaluadores".
- "Permite el uso de la teoría de la probabilidad para expresar la probabilidad de que cualquier diferencia en el resultado entre los grupos de tratamiento simplemente indique el azar".
Hay dos procesos involucrados en la asignación aleatoria de pacientes a diferentes intervenciones. Primero es elegir un procedimiento de aleatorización para generar una secuencia impredecible de asignaciones; esto puede ser una simple asignación aleatoria de pacientes a cualquiera de los grupos con probabilidades iguales, puede ser "restringida" o puede ser "adaptativa". Una segunda cuestión más práctica es la ocultación de la asignación , que se refiere a las estrictas precauciones que se toman para garantizar que la asignación grupal de pacientes no se revele antes de asignarlos definitivamente a sus respectivos grupos. Los métodos "sistemáticos" no aleatorios de asignación de grupos, como la alternancia de sujetos entre un grupo y otro, pueden causar "posibilidades ilimitadas de contaminación" y pueden causar una violación del ocultamiento de la asignación. [45]
Sin embargo, la evidencia empírica de que la asignación al azar adecuada cambia los resultados en relación con la asignación al azar inadecuada ha sido difícil de detectar. [46]
Procedimientos
La asignación al tratamiento es la proporción deseada de pacientes en cada grupo de tratamiento.
Un procedimiento de aleatorización ideal lograría los siguientes objetivos: [47]
- Maximizar el poder estadístico , especialmente en análisis de subgrupos . Generalmente, los tamaños de grupo iguales maximizan el poder estadístico, sin embargo, los tamaños de grupos desiguales pueden ser más poderosos para algunos análisis (p. Ej., Comparaciones múltiples de placebo versus varias dosis usando el procedimiento de Dunnett [48] ), y algunas veces se desean por razones no analíticas (p. Ej. , los pacientes pueden estar más motivados para inscribirse si existe una mayor probabilidad de recibir el tratamiento de prueba, o las agencias reguladoras pueden requerir un número mínimo de pacientes expuestos al tratamiento). [49]
- Minimice el sesgo de selección . Esto puede ocurrir si los investigadores pueden, consciente o inconscientemente, inscribir preferentemente a pacientes entre los grupos de tratamiento. Un buen procedimiento de aleatorización será impredecible de modo que los investigadores no puedan adivinar la asignación de grupo del siguiente sujeto en función de asignaciones de tratamiento anteriores. El riesgo de sesgo de selección es mayor cuando se conocen las asignaciones de tratamientos anteriores (como en los estudios no cegados) o se pueden adivinar (tal vez si un fármaco tiene efectos secundarios distintivos).
- Minimizar el sesgo de asignación (o confusión ). Esto puede ocurrir cuando las covariables que afectan el resultado no se distribuyen por igual entre los grupos de tratamiento y el efecto del tratamiento se confunde con el efecto de las covariables (es decir, un "sesgo accidental" [44] [50] ). Si el procedimiento de asignación al azar causa un desequilibrio en las covariables relacionadas con el resultado entre los grupos, las estimaciones del efecto pueden estar sesgadas si no se ajustan por las covariables (que pueden no medirse y, por lo tanto, es imposible ajustarlas).
Sin embargo, ningún procedimiento de aleatorización cumple esos objetivos en todas las circunstancias, por lo que los investigadores deben seleccionar un procedimiento para un estudio determinado en función de sus ventajas y desventajas.
Sencillo
Este es un procedimiento intuitivo y de uso común, similar al "lanzamiento de una moneda al aire en forma repetida". [44] También conocida como aleatorización "completa" o "sin restricciones", es robusta contra los sesgos de selección y accidentales. Sin embargo, su principal inconveniente es la posibilidad de tamaños de grupo desequilibrados en ECA pequeños. Por lo tanto, se recomienda solo para ECA con más de 200 sujetos. [51]
Restringido
Para equilibrar el tamaño de los grupos en ECA más pequeños, se recomienda alguna forma de aleatorización "restringida" . [51] Los principales tipos de aleatorización restringida que se utilizan en los ECA son:
- Aleatorización permutado-bloque o aleatorización bloqueado : un "tamaño de bloque" y "relación de asignación" (número de sujetos en un grupo en comparación con el otro grupo) se especifican, y los sujetos se asignan aleatoriamente dentro de cada bloque. [45] Por ejemplo, un tamaño de bloque de 6 y una proporción de asignación de 2: 1 llevaría a la asignación aleatoria de 4 sujetos a un grupo y 2 al otro. Este tipo de aleatorización se puede combinar con la " aleatorización estratificada ", por ejemplo, por centro en un ensayo multicéntrico , para "asegurar un buen equilibrio de las características de los participantes en cada grupo". [4] Un caso especial de aleatorización de bloques permutados es la asignación aleatoria , en la que toda la muestra se trata como un bloque. [45] La principal desventaja de la aleatorización de bloques permutados es que incluso si los tamaños de los bloques son grandes y variados al azar, el procedimiento puede conducir a sesgos de selección. [47] Otra desventaja es que el análisis "adecuado" de los datos de los ECA aleatorizados en bloques permutados requiere estratificación por bloques. [51]
- 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.[45] The methods are thought to be less affected by selection bias than permuted-block randomization.[51]
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."[51] Minimization is reported to have "supporters and detractors"[45] because only the first subject's group assignment is truly chosen at random, the method does not necessarily eliminate bias on unknown factors.[4]
- 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.[51] 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.[52]
Allocation concealment
"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.[53] 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.[45] Such practices introduce selection bias and confounders (both of which should be minimized by randomization), possibly distorting the results of the study.[45] 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.[45] 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.[54] 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.[55]
Sample size
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.[56]
Cegador
An RCT may be blinded, (also called "masked") by "procedures that prevent study participants, caregivers, or outcome assessors from knowing which intervention was received."[55] 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.[57][58] 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."[4]
RCTs without blinding are referred to as "unblinded",[59] "open",[60] or (if the intervention is a medication) "open-label".[61] 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;[55] for example, in an RCT of treatments for multiple sclerosis, unblinded neurologists (but not the blinded neurologists) felt that the treatments were beneficial.[62] 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."[42]
Análisis de los datos
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[63]) 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[64]) 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[65]) is appropriate.
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."[4]
- 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;[66] when some outcome data are missing, options include analyzing only cases with known outcomes and using imputed data.[4] 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.[4]
- 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.[4]
Informe de resultados
The CONSORT 2010 Statement is "an evidence-based, minimum set of recommendations for reporting RCTs."[67] 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.[1]
For other RCT study designs, "CONSORT extensions" have been published, some examples are:
- Consort 2010 Statement: Extension to Cluster Randomised Trials[68]
- Consort 2010 Statement: Non-Pharmacologic Treatment Interventions[69][70]
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.[71][72] 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."[71][72] 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.[73]
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.[74]
- 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.[75][76] 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.[76][77]
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.[78] 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,[79] by 2005-2006 a sizeable proportion of RCTs still had inaccurate or incompletely reported sample size calculations.[80]
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 over-generalizing 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.[81]
Ventajas
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."[82]
- 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.[83] 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.[83]
- The GRADE Working Group concluded in 2008 that "randomised trials without important limitations constitute high quality evidence."[84]
- 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)."[85]
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.[86] The non-randomized studies concerning the drugs were characterized as "glowing",[87] and their sales increased to a combined total of approximately 165,000 prescriptions per month in early 1989.[86] In that year, however, a preliminary report of an RCT concluded that the two drugs increased mortality.[88] Sales of the drugs then decreased.[86]
- 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.[87] 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.[65][89] 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.[90][91] The use of hormone replacement therapy decreased after publication of the RCTs.[92]
Desventajas
Many papers discuss the disadvantages of RCTs.[75][93][94] Among the most frequently cited drawbacks are:
Time and costs
RCTs can be expensive;[94] 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,[95] 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.[95]
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.[96]
It is costly to maintain RCTs for the years or decades that would be ideal for evaluating some interventions.[75][94]
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.[75]
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).[96]
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."[97]
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.[98] 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."[99] 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.[100] One possible reason for the pro-industry results in industry-funded published RCTs is publication bias.[99] 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.[101]
Ethics
If a disruptive innovation in medical technology is developed, it may be difficult to test this ethically in an RCT if it becomes "obvious" that the control subjects have poorer outcomes—either due to other foregoing testing, or within the initial phase of the RCT itself. Ethically it may be necessary to abort the RCT prematurely, and getting ethics approval (and patient agreement) to withhold the innovation from the control group in future RCT's may not be feasible.
Historical control trials (HCT) exploit the data of previous RCTs to reduce the sample size; however, these approaches are controversial in the scientific community and must be handled with care.[102]
En ciencias sociales
Due to the recent emergence of RCTs in social science, the use of RCTs in social sciences is a contested issue. 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.
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.[103] Graham-Rowe and colleagues[104] 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[105] 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.[106] The authors classified the studies they found into five categories: "policing", "prevention", "corrections", "court", and "community".[106] 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.[107]
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.[108] 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.[109] 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.[110]
Crítica
A 2017 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".[111]
Ver también
- Drug development
- Hypothesis testing
- Impact evaluation
- Jadad scale
- Statistical inference
- The Royal Commission on Animal Magnetism
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enlaces externos
- Bland M. Directory of randomisation software and services. University of York, 2008 March 19.
- Evans I, Thornton H, Chalmers I. Testing treatments: better research for better health care. London: Pinter & Martin, 2010. ISBN 978-1-905177-35-6.
- Gelband H. The impact of randomized clinical trials on health policy and medical practice: background paper. Washington, DC: U.S. Congress, Office of Technology Assessment, 1983. (Report OTA-BP-H-22.)
- REFLECT (Reporting guidElines For randomized controLled trials for livEstoCk and food safeTy) Statement
- Wathen JK, Cook JD. Power and bias in adaptively randomized clinical trials. M. D. Anderson Cancer Center, University of Texas, 2006 July 12.