Blinding, concealing which participants receive the experimental intervention in a trial, is one of the central tenants of intervention trial design (Kaptchuk 1998, Moher 2001, Shultz 2002). The double blind randomized control trial is the gold standard for evaluating new interventions. In practical terms, blinding facilitates true randomization throughout the trial. Randomization allows the testable hypothesis that the differences between trial groups are due to chance alone. By maintaining randomization, blinding allows us to protect against multiple types of influences that could bias our estimate of these differences.
Masking participants during experiments has been a part of Western medicine since the 18th Century (Kaptchuk 1998). First used to debunk or prove non-traditional therapies, blindfolds, curtains, and sham therapies were used to keep participants from knowing if they received a therapy allowing others to assess a “true” response. In one of the earliest recorded uses of a placebo, Armand Trousseau used bread pills to demonstrate that homeopathic therapy was no better than “the spontaneous course of most natural diseases" (Kaptchuk 1998). In the 19th Century, non-traditional healers used these techniques to demonstrate the effectiveness of their therapies. Similarly, orthodox physicians who believed many current medical therapies were not any better than allowing nature to take its course used concealment to support their theories.
By the turn of the 20th Century, European practitioners recognized the powerful influence of suggestion on patients. Lead by the Germans, they began to integrate placebos and blinding into experiments to mitigate the effect of suggestion (Kaptchuk 1998). A little later, clinicians in the US and England began to appreciate the importance of comparison groups in demonstrating the effectiveness of therapies (Kaptchuk 1998). They realized that blinding was necessary to retain comparison group members and to keep them from seeking therapy from other sources.
After World War II, blinding became an essential element of the randomized study design advocated by RA Fisher (Kaptchuk 1998). After some convincing, physicians accepted that overenthusiastic advocates of a treatment could adversely affect research results. Knowledge of treatment allocation by the patient or the researcher could contaminate findings. Purposeful ignorance was the best way to ensure that physicians and researchers know what is best for patients. “Double blind,” meaning that both the participant and the clinician/researcher remain ignorant to which intervention participants receive, became a necessary component of the best randomized comparison trials.
A full history of the use of blind assessment in Western medicine is beyond this review. Ted Kaptchuk provides a thorough review of the subject in the Bulletin of the History of Medicine which can be found at the following link.
http://muse.jhu.edu/journals/bulletin_of_the_history_of_medicine/v072/72.3kaptchuk.html
What does “double blind” mean?
In the simplest form, the researcher/clinician and the participant compose the research dyad. If both are unaware of treatment allocation, then “double blind” conditions have been achieved. This simple definition belies the multiple tasks that interventional trials require. Researchers recruit and randomize participants, provide clinical care, assess participant outcomes, monitor for adverse events, analyze data, and write up research findings. Often these different tasks are accomplished by different or multiple members of research teams.
Knowledge of participant group allocation creates different types of biases depending on the researcher’s task or role. Due to these many possible roles, “double blind” has developed multiple meanings. A 2001 survey asked 91 internists at three Canadian academic medical centers the definition of “double blind.” The survey listed six roles in intervention trials and asked which roles are blinded in a “double blind” study. Survey respondents provided 17 different interpretations of what “double blind” means. (Deveareaux 2001). The same investigators found nine different definitions of “double blind” in textbooks. A review of 83 “double blinded” studies published in five “high impact” journals found eight different combinations of blinded groups reported by the authors (Montori 2002).
A similar study in 2006 surveyed the authors of 200 published trials (Haahr 2006). One hundred and fifty-six of these trials were reported as “double blinded.” Authors that responded to the survey stated that participants were blinded in 97% of their studies, health care providers were blinded in 89%, and data collectors were blinded in 90%. Respondents provided 15 different definitions of “double blind.”
Due to this confusion, the CONSORT statement, a guideline created by an expert group of researchers, methodologists, and journal editors, recommends that trial reports explicitly state “whether or not participants, those administering the interventions, and those assessing the outcomes were blinded to group assignment” (Moher 2001). First published in 1996, the CONSORT statement recommended this delineation should replace or accompany any reference to single, double, or triple blinding.
In spite of this recommendation, many published studies do not include this information. Montori et al. found that of the 83 reviewed “double blind” trials, 41 (49%) did not report which groups were blinded. The Haahr et al. review revealed that 41 (26%) of 156 “double blind” trial articles provided no other information on who was masked to group allocation.
How does knowledge of treatment allocation introduce bias?
The goal of randomization is to keep both the treatment and control groups as similar as possible with respect to all factors except for the intervention being tested. As an extension, the goal of blinding is to inhibit differential effects between the treatment and control groups that may be introduced by the study itself. It has been noted that open, non-blinded trials exaggerate treatment effects by 14% compared to blinded trials (Rees 2005).
Knowledge of treatment group may introduce different types of biases depending on the role of the person in a study. There are many different potential biases introduced in a study if a participant knows whether they are receiving the intervention or not. Simply receiving an intervention can create a positive or negative effect on the measured outcome. Therefore, it is important that both the treatment and control groups believe they are receiving an intervention. Commonly referred to as the placebo effect, we know that simply receiving an intervention can lead to real psychological and physical responses (Schulz 2002b). In addition, participants may introduce bias by differentially seeking additional treatments or interventions, complying with trial regimens, or leaving the trial early (Schulz 2002b). All of these activities may be influenced by a participant’s belief that he or she is receiving an active treatment.
Health care providers often have hypotheses about the effect of the intervention that can lead to biased estimates. Blinding health care providers helps to prevent differential transference of these hypotheses to their patients. If a provider believes that an experimental treatment will work, he can overtly or subtly share this positive perspective with his patients. For example, he might be prone to focus more on positive clinical data with patients he believes to be receiving the treatment and not the placebo. Providers can also directly influence results by differential administration of additional interventions, differential adjustment of drug doses, and differential withdrawal of patients from studies (Schulz 2002b).
The biggest risk for data collectors and judicial assessors of outcomes is ascertainment bias, bias created due to differential assessment of outcomes (Schulz 2002b). Data collectors may be separate trial personnel, but they also can be health care providers. Furthermore, participants who provide subjective reports of symptoms are a key part of the data collection team. Blinded data collectors are less likely to differentially define or search for outcomes. Ascertainment bias is less of a concern when primary outcomes are objective like biological measures (Schulz 2002b).
Data analyst and writers may introduce error when deciding how to analyze and summarize data. Since studies with new and positive findings are more likely to be published, these groups might present data in ways that are more likely to produce positive results. This trend is referred to as publication bias. Blinding of these two groups of study personnel is much rarer than blinding of other members of the study team (Haahr 2006, Schulz 2002b).
Mechanisms of Blinding
Allocation concealment
For maximum effectiveness, successful blinding follows successful randomization. Allocation concealment, the process used to protect the allocation sequence, is an essential part of ensuring randomization. Allocation concealment prevents selection bias by ensuring that participant recruitment and enrollment is not determined by factors that might influence outcomes ( Schulz 2002a).
Successful allocation concealment ensures study personnel cannot predict group assignment prior to enrolling a participant in the study. For this reason, quasi-randomization techniques that use parts of medical record numbers, birth dates, days of the week, or social security numbers fail to achieve allocation concealment (Schulz 2002a). Successful techniques for allocation concealment include: maintaining group assignment in sequentially numbered, opaque, sealed envelopes; distributing the intervention through a pharmacy; keeping intervention drugs in numbered or coded containers; controlling randomization from a centralized location; and using secure computer-assisted methods (Schulz 2002a). Allocation concealment involves purposeful ignorance, but it is not a form of blinding. It proceeds blinding. While some study designs and interventions do not allow for blinding, allocation concealment can always be achieved and should be reported (Moher 2001, Schulz 2002a).
Placebos
Placebos are agents given to participants allocated to the control group in trials of pharmaceuticals. The central tools in blinding, placebos are designed to mimic the treatment in size, shape, color, texture, smell, and taste (Schulz 2002b). Placebos are traditionally inert, but active placebos that mimic the most prominent known side effects of experimental treatments can help to maintain blinding. One has to be careful that the ingredients in an active placebo do not impact the measured outcome (Schulz 2002b).
In trials for conditions for which no efficacious treatment exists, the comparison of a new treatment to a placebo is warranted. In modern medicine, that situation is increasingly rare and effective treatments usually already exist. This raises both practical and ethical issues with comparing a new treatment to a placebo. Comparison with a placebo allows determination of the absolute effectiveness of the new treatment, but leaves the ethical problem of denying people known available treatment. On the other hand, comparison to the standard of care only gives information on relative effectiveness. In addition, if the two treatments are dissimilar in appearance, then blinding will not be achieved.
A double dummy placebo can blind a study with multiple treatment arms (Schulz 2002b). In this type of study, placebos are developed for both interventions. Consider a hypothetical study in which treatment A, the current standard, is a green liquid taken twice a day, and the experimental treatment is a blue pill taken once a day. In study arm one, all participants would take treatment A twice a day and a blue placebo sugar pill once a day. In study arm two, participants would take a green inert liquid twice a day and the experimental pill once a day. This study with two placebos ensures that both study arms are blinded. A double dummy design is particularly helpful in situations when the interventions are administered by different methods, like when one is a pill and the other is an injection.
While they are a wonderful tool, placebos can not be used in all intervention trials. In some cases, treatments have too many idiosyncratic traits to make an effective placebo. In other cases, cost limitations may make it difficult to create a quality placebo. Finally, treatment effects may be so large or side effects so severe that participants can easily determine group assignment (Rees 2005).
Non-pharmaceutical Trials
Non-pharmaceutical trials that study surgery, behavioral interventions, rehabilitation, devices, or psychotherapy often make blinding of certain groups impossible. For example, during an RCT of the effect of male circumcision on HIV rates in South Africa, it was impossible to have participants and their surgeons unaware of circumcision status (Auvert 2005). In a study comparing pharmaceutical to non-pharmaceutical trials, researcher reviewed 110 trials evaluating interventions for knee and hip osteoarthritis. They concluded that per the description of the methods described in the manuscripts, blinding of participants, providers, and outcome assessors was infeasible much more frequently in the non-pharmaceutical trials (Boultron 2004).
In spite of these limitations, there are techniques that can be used to minimize bias in these types of studies (Boutron 2007). First, sham procedures, alternative attention activities, and mock devices are often used to approximate placebos. In some cases, these activities can be as effective as a true placebo. In device studies, non-functional devices that look and sound like the intervention can make it hard for participants to know if their device is real or not (Boutron 2007, Rees 2005). Similarly, sham acupuncture has been used to approximate acupuncture in studies either by placing needles in the incorrect position or using needle-like devices that do not pierce the skin (Boutron 2007).
Alternative action activities are often used in behavioral, therapy, or rehabilitation studies (Boutron 2007). For example, if students participate in a 4-hour health education curriculum, a control group of students might participate in a 4-hour art curriculum. While students will be aware that they participated in the group, this alternative activity at least controls for the difference that might exist simply because of the attention given to the group receiving the health education intervention.
A second strategy used in non-pharmaceutical studies is to blind participants, health care providers, and/or outcome assessors to the hypothesis in question (Boutron 2007). If people do not know why the intervention is being tested, hopefully there will be fewer differences in the effect of participation across the intervention and control groups. In the circumcision trial, researchers informed participants that, at the time of the study, “the impact of male circumcision on the acquisition of sexually transmitted infections (STIs), including HIV, is not known” (Auvert 2005).
This strategy has two major limitations. First, not providing the study hypothesis may limit the ability of participants to provide truly informed consent. In addition, although the study staff does not share the study hypothesis, this does not mean that participants do not create their own beliefs about the effects of the intervention. These beliefs can be derived from many sources and still lead to biased results.
Using objective outcomes and maintaining the blinding of outcome assessors also can help to limit bias in non-pharmaceutical studies (Boutron 2007). The primary outcome in the circumcision trial was HIV infection. While providers and participants could not be blinded, this hard outcome mitigated the potential ascertainment bias of data collectors. In a hypothetical study of a behavioral intervention for children with learning disabilities, psychological test used as outcome measures can be administered by team members who are unaware of which children participated in the intervention.
Judging the effectiveness of your blinding
We have demonstrated that not all “double blind” trials are equal, but even trials that clearly define blinding can be unsuccessful in blinding efforts. Cases in which maintenance of blinding has been unsuccessful should be reported. Rees argues that successful blinding does not depend on participants’ ability to correctly identify their allocation. Blinding fails if participants in the allocation groups have significantly different beliefs about which treatment they received. These differential beliefs become a problem when they affect the measured outcome (Rees 2004).
Rees et al. recommend the following steps in assessing the success of blinding and reporting any potential blinding failures.
- Assess participants’ beliefs, not the correctness of beliefs
- Measure these beliefs for two time points at a minimum (beginning and end of study)
- Make participants who initially answer “don’t know” guess their allocation.
- Analyze the main measure of effect and/or other reasons for participants’ beliefs, stratified by belief patterns
- Describe potential reasons for participants’ beliefs to elucidate the possible role of beliefs in the causal pathway (Rees 2004).
Conclusion
Blinding is an integral part of the conduct of intervention trials. Ensuring proper blinding of all key constituencies strengthens our use of the scientific method, bringing our estimate closer to real world phenomenon. Since the use of bread pills to disprove homeopathy, Western medicine has refined our use of purposeful ignorance to improve our understanding of the world.
References
Auvert et al. Randomized, Controlled Intervention Trial of Male Circumcision for Reduction of HIV Infection Risk: The ANRS 1265 Trial. Plos Medicine 2005; 2(11):1113-1122.
Boutron I et al. Blinding was judged more difficult to achieve and maintain in nonpharmacologic than pharmacologic trials. Journal of Clinical Epidemiology 2004; 57: 543–550.
Boutron I et al. Reporting Methods of Blinding in Randomized Trials Assessing Nonpharmacological Treatments. Plos Medicine 2007; 4( 2): 370-380.
Devereaux PJ et al. Physician Interpretations and Textbook Definitions of Blinding Terminology in Randomized Controlled Trials. JAMA 2001; 285(15):2000-2003.
Devereaux PJ et al. An observational study found that authors of randomized controlledtrials frequently use concealment of randomization and blinding, despite the failure to report these methods. Journal of Clinical Epidemiology 2004; 57: 1232–1236.
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Kaptchuk TJ. Intentional Ignorance: A History of Blind Assessment and Placebo Controls in Medicine. Bulletin of the History of Medicine 1998; 72(3): 389-433.
Moher D, Schulz KF, Altman D. The CONSORT statement: revised recommendations for improving the quality of reports of parallel-group randomized trials. JAMA 2001; 285(15):1987-1991.
Montori VM et al. In the dark: The reporting of blinding status in randomized controlled trials. Journal of Clinical Epidemiology 2002; 55: 787–790.
Rees JR et al. Changes in beliefs identify unblinding in randomized controlledtrials: a method to meet CONSORT guidelines. Contemporary Clinical Trials 2005; 26: 25–37.
Schulz KF. Grimes DA. Allocation concealment in randomised trials: defending against deciphering. Lancet 2002; 359: 614–18.
Schulz KF. Grimes DA. Blinding in randomised trials: hiding who got what. Lancet 2002; 359: 696–700.
Schulz KF. Grimes DA. Generation of allocation sequences in randomised trials: chance, not choice. Lancet 2002; 359: 515–19.
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