Introduction

In the two previous chapters in this book, we introduced the process of evidence-based dentistry¹ and explained how to search for evidence to inform clinical practice.² In this chapter, we explain how to use a research report to inform clinical decisions pertaining to questions of therapy. We will introduce and describe the basic concepts for understanding randomized controlled trials (RCTs), and we explain how to critically appraise such studies. In subsequent chapters in this book, we describe how to use other types of study designs.

Clinical Questions of Therapy

Dental practitioners spend most of their time administering treatments to their patients. A therapy or treatment can be defined as “any intervention, which may include prescribing drugs, performing surgery, or counseling, that is intended to improve the course of disease once it is established.”³ Many of the clinical questions that arise in clinical practice have to do with the effectiveness of treatments or interventions.

As described by the authors of Chapter 2 of this book, therapy questions can be stated using the population, intervention, comparison, outcomes (PICO) framework.⁴ The population is the patients who are to receive the intervention, the intervention is the treatment of interest, the comparison is the reference to which we are comparing the intervention, and the outcomes are the health consequences that depend on the intervention. The comparison can be a different treatment or no treatment at all. Table 3.1 shows two examples of therapy questions and their corresponding questions in the PICO framework: one of them has no treatment as the comparison and the other has an alternative treatment.

Table 3.1. Examples of Therapy Questions and the PICO* Framework

* PICO = population, intervention, comparison, outcomes.

What Study Design Best Addresses Questions of Therapy?

At the level of primary studies, RCTs represent the optimal study design to address questions of therapy. An RCT is an experiment assessing a medical treatment in patients.⁵ In an RCT, participants are allocated randomly into two or more groups that are treated equally except for the intervention the participants receive. After the intervention is applied, investigators follow patients over a specified time and measure outcomes, ideally those that are important to patients. If the study has been well designed and implemented, we can attribute differences that arise to the treatment under investigation (Figure 3.1).³

Figure 3.1. Randomized Clinical Trial

One RCT in dentistry, conducted by Hita-Iglesias and colleagues,⁶ addressed whether chlorhexidine gel or chlorhexidine rinse was more effective in preventing alveolar osteitis following third-molar extraction. After the surgery was performed, the investigators randomly allocated patients to receive either the gel or the rinse for one week, and evaluated patients on the third and seventh days postextraction to determine the presence of alveolar osteitis.

RCTs are the best type of study design to determine the effectiveness of an intervention because they minimize bias—a systematic deviation from the underlying truth⁷—by ensuring that patients in the intervention and control groups are similar with respect to factors that determine whether the outcome of interest will occur. If well designed, RCTs also control events that occur after randomization and most aspects of the course of events, such as how the outcomes are measured.⁸ Therefore, clinicians should aim to inform their clinical decisions regarding therapy using individual RCTs or, even better, systematic reviews of RCTs. In this chapter, we will focus on how to use stand-alone RCTs, and in subsequent chapters in this book, we will describe how to use systematic reviews.

Critically Appraising an RCT to Inform Clinical Decisions

The process of using an article from the dental literature to inform clinical decisions involves assessing the risk of bias, the results, and the applicability of the results.⁹ Below, we describe each of these three steps.

How Serious Is the Risk of Bias?

The extent to which a study’s results are likely to be correct for the sample of patients enrolled¹⁰ depends on how well the study was designed and conducted. Investigators of RCTs strive to ensure that determinants of the outcome of interest (factors such as age, sex, and disease severity, which we call prognostic factors) other than the treatment under investigation are similar between the groups being compared at the start of the study, and that these determinants remain similar throughout the study.⁸ Only if investigators achieve and maintain prognostic balance can we be sure that any differences in outcomes are owing to the intervention (and not to bias introduced by the prognostic factors). Table 3.2^11–16 presents the aspects to consider when assessing the risk of bias of an RCT addressing a question of therapy.

Table 3.2. Critically Appraising the Risk of Bias in an Article About Therapy*

* Sources: Luchesi and colleagues,¹¹ Higgins and colleagues,¹² Christidis and colleagues,¹³ Santos and colleagues,¹⁴ Neuhaus and colleagues,¹⁵ and Kelleher and colleagues.¹⁶

† DM = diabetes mellitus.

‡ TMJ = temporomandibular joint.

Did the intervention and control groups start with the same prognosis?

One key aspect of a study that can help answer a question regarding therapy is whether the groups were balanced with regard to prognostic factors at the beginning of the study. Investigators can achieve this balance through their control of how the patients are allocated to the intervention and control groups.

Randomization assigns patients to the intervention or control groups by chance.⁸ The goal is to ensure that both known and unknown prognostic factors are distributed similarly in the intervention and control groups and, thus, avoid bias.^{9, 17} This is why, when therapy questions are to be answered, the use of RCTs is superior to the use of observational studies: when the decision of what treatment to provide to a given patient is left to the dentist (as is done in observational studies), it is likely that patient characteristics may influence the choice of therapy. For instance, because of its ease of use, dentists may prefer to use chlorhexidine mouth rinse rather than gel in older patients who have a greater risk of experiencing subsequent infection, and to use the chlorhexidine gel in younger patients who have a lower risk of experiencing subsequent infection.

Even a well-prepared (typically, computer-generated) randomization schedule does not ensure random allocation. If those enrolling patients are aware of the treatment (intervention or control) to which the next patient will be allocated, they may make choices that undermine randomization.¹⁸ For example, if the next scheduled patient is an older person, and a member of the research staff who is responsible for allocation believes that the assigned treatment of gel is not optimal for the patient, the staff member may manipulate the allocation to ensure that the patient receives the mouth rinse.

To prevent this manipulation of the randomization schedule, those recruiting patients should not be informed about which group the next patient will be allocated to. This strategy is called “allocation concealment.”¹⁹ The authors of one study found that the investigators of trials in which allocation concealment was either inadequate or unclear reported treatment effects approximately 40% larger than those reported by studies with adequate allocation concealment.²⁰

Particularly if the sample size is small, even concealed randomization may fail to do its job of ensuring prognostic balance. It is important, therefore, to check whether the baseline characteristics of the patients in both groups are similar.⁹

In summary, concealed random allocation with evidence that patients in the intervention and control groups started with the same prognosis reassures us that we are likely to obtain unbiased estimates of treatment effect.

Was prognostic balance maintained as the study progressed?

Awareness on the part of dentists administering the intervention, patients who receive the care, or those measuring the outcomes in the study of whether patients are receiving intervention or control treatment can influence their behavior. For instance, the judgment of whether osteitis occurs involves some subjectivity, and it is possible that an outcome assessor who favors using gel over wash will be more likely to diagnose osteitis in those receiving the wash.²¹ Blinding (also known as masking) refers to investigators ensuring that patients, clinicians, and those collecting data and adjudicating whether an outcome has occurred are unaware of whether patients are receiving the intervention or the control.9

Typically, trials are described as double-blinded, which may mean that none of the patients, clinicians, data collectors, or outcome assessors are aware of what treatment the patient was receiving.²¹ The term “double-blind” does not leave us confident that all four groups are unaware of allocation, and optimal reporting will inform us whether this is the case.⁹

The method to achieve blinding in RCTs is the use of a placebo. A placebo is a treatment that resembles the intervention of interest but has no biological effect.⁸ Most placebos are pills and are administered in the same way as the real drug. Many of the treatments administered in dentistry, however, are procedures. In this case, although doing so is ethically arguable, investigators of the most rigorously designed trials could use a sham procedure to blind patients.²²

Many times, however, it is not possible to blind patients or clinicians. Fortunately, lack of blinding will not always result in bias. For instance, it may not be possible to blind the clinician because two materials with different appearance and techniques of use are being compared. If, however, patients and outcome assessors are blinded, and there are no other treatments that affect the outcome that the dentists may administer differentially to intervention and control patients (known as cointervention), not blinding the dentist may not affect the results. Therefore, when evaluating whether prognostic balance was maintained as the study progresses, not only do we have to assess whether the groups of interest were blinded, but also we must consider whether any lack of blinding may have caused any bias.²¹

Were the groups prognostically balanced at the completion of the study?

Strategies to maintain the prognostic balance as the study proceeds include following up on all patients, analyzing them in the group to which they were allocated, and completing the trial as planned.⁹

There are circumstances in which researchers are not able to follow up and measure the outcome for some patients (referred to as “lost to follow-up”). Patients lost to follow-up may well have different prognoses from those who remain until the end of the study,⁹ and hence, the similarity of prognosis in intervention and control groups may be compromised. Ideally researchers should know the outcomes of all participants in a trial (or at least know the reasons why some patients were lost to follow-up).

If the proportion of patients lost to follow-up is so small that including their results in the data analysis would not change the overall results even if all of them had the best or worst outcome, and if the reasons for losing those patients are reported in the trial and are not potentially related to the outcome (for example, a patient moved to another city and could not attend the follow-up visits), then the risk of bias does not increase materially.

Sometimes patients do not receive the intervention as intended because they do not adhere to instructions. Patients may even receive the treatment meant for the patients allocated to the other group. If nonadherence to a treatment is related to a prognostic factor, excluding these patients from the analysis and using data only from patients who adhered to the treatment (that is, doing a per-protocol analysis) will destroy the prognostic balance achieved and maintained through all the previous strategies. To avoid this, researchers use the “intention-to-treat” principle; that is, they analyze the data from each patient in the group to which the patient was allocated. In this way, they get an unbiased estimate of the effect of the intervention at the level of adherence observed in the trial.23

Randomization only can ensure prognostic balance when the sample size is large; when the sample size is small, chance can result in large prognostic imbalance. As a result, early in an RCT when sample sizes are small, results may not be indicators of the future overall results even if the RCT otherwise is designed meticulously.²⁴ Therefore, it can be misleading if investigators stop a trial early on the basis that they have seen a large effect.⁹ Both simulations and empirical data show that, on average, the results of trials that were stopped early because of a perceived benefit overestimate treatment effects, and the smaller the number of patients randomized as well as the number of outcome events observed at the time the trial is stopped, the larger the overestimate of effect.²⁵ Thus, a final criterion to determine whether the intervention and control groups were balanced prognostically at the end of the study is to assess whether the trial was stopped early.

In summary, prognostic balance is maintained up to the completion of the study if there are few participants who are lost to follow-up, if the authors performed an intention-to-treat analysis, and if the trial was completed as planned.

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