CHAPTER 4 Evidence about effects of interventions

After reading this chapter, you should be able to:

• Understand more about study designs appropriate for answering questions about effects of interventions

• Generate a structured clinical question about intervention for a clinical scenario

• Appraise the validity of randomised controlled trials

• Understand how to interpret the results from randomised controlled trials and calculate additional results (such as confidence intervals) where possible

• Describe how evidence about the effects of intervention can be used to inform practice

This chapter focusses on research that can inform us about the effects of intervention. Let us consider a clinical scenario that will be useful for illustrating the concepts that are the focus of this chapter.

Clinical scenario

You are working in a community health centre and, during a regular team meeting, the general practitioner notes that there are a large number of older people attending the clinic who have had multiple falls. He questions whether there is a need for the delivery of a preventative program for this group. A number of staff have similar concerns and decide to form a small group to look for research regarding the effectiveness of falls prevention programs. In your experience working with people who have a history of falling, you are aware that many of them have low confidence in their ability (this is also known as self-efficacy) to prevent themselves from falling. You are therefore particularly interested in finding evidence about the effectiveness of falls prevention programs that have looked at improving participants’ self-efficacy as well as reducing the number of falls that they experience.

This clinical scenario raises several questions about the interventions that might be effective for reducing falls in people who are at risk of falling. Is balance and strength training effective in reducing the risk of falls? Does providing advice about how to modify a person’s home to make it safer prevent falls in people who are at risk of falling? Which of these interventions is most effective or are both combined more effective than one intervention alone? How cost-effective are multifactorial falls prevention education programs? These are questions that health professionals might ask when making decisions about which interventions will be most effective and optimise outcomes for their clients.

As we saw in Chapter 1, clinical decisions are made by integrating information from the best available research evidence with information from our clients, the practice context and our clinical experience. Given that one of the most common information needs in clinical practice relates to questions about the effects of interventions, this chapter will begin by reviewing the role of the study design that is used to test intervention effects before moving on to explaining the process of finding and appraising research evidence about the effects of interventions.

Study designs that can be used for answering questions about the effects of interventions

There are many different study designs that can provide information about the effects of interventions. Some are more convincing than others in terms of the degree of bias that might be in play given the methods used in the study. From Chapter 2, you will recall that bias is any systematic error in collecting and interpreting data. In Chapter 2, we also introduced the concept of hierarchies of evidence. The higher up the hierarchy that a study design is positioned, in the ideal world, the more likely it is that the study design can minimise the impact of bias on the results of the study. That is why randomised controlled trials (sitting second from the top of the hierarchy of evidence for questions about the effects of interventions) are so commonly recommended as the study design that best controls for bias when testing the effectiveness of interventions. Systematic reviews of randomised controlled trials are located above them (at the top of the hierarchy) because they can combine the results of multiple randomised controlled trials. This can potentially provide an even clearer picture about the effectiveness of interventions. Systematic reviews are explained in more detail in Chapter 12.

One of the best methods for limiting bias in studies that test the effects of interventions is to have a control group.¹ A control group is a group of participants in the study who should be as similar in as many ways as possible to the intervention group except that they do not receive the intervention being studied. Let us first have a look at studies that do not use control groups and identify some of the problems that can occur.

Studies that do not use control groups

Uncontrolled studies are studies where the researchers describe what happens when participants are provided an intervention, but the intervention is not compared with other interventions. Examples of uncontrolled study designs are case reports, case series and before and after studies. These study designs were explained in Chapter 3. The big problem with uncontrolled studies is that when participants are given an intervention and simply followed for a period of time with no comparison against another group it is impossible to tell how much (if any) of the observed change is due to the effect of the intervention itself. There are some obvious reasons this might occur and these problems need to be kept in mind if you use an uncontrolled study to guide your clinical decision making. Some of the forms of bias that commonly occur in uncontrolled studies are described below.

• Volunteer bias. People who volunteer to participate in a study are usually systematically different from those who do not volunteer. They tend to be more motivated and concerned about their health. If this is not controlled for, it is possible that the results can make the intervention appear more favourable (that is, more effective) than it really is. This type of bias can be controlled for by randomly allocating participants as we shall see later in this chapter.

• Maturation. A participant may change between the time of pre-test (that is, before the intervention is given) and post-test (after the intervention has finished) as a result of maturation. For example, consider that you wanted to measure the improvement in fine motor skills that children in grade 2 of school experienced as a result of a fine-motor skill intervention program. If you test them again in grade 3, you will not know if the improvements that occurred in fine motor skills happened because of natural development (maturation) or because of the intervention.

• Natural progression. Many diseases and health conditions will naturally improve over time. Improvements that occur in participants may or may not be due to the intervention that was being studied. The participants may have improved on their own with time, not because of the intervention.

• Regression to the mean. This is a statistical trend that occurs in repeated non-random experiments, where participants’ results tend to move progressively towards the mean of the behaviour/outcome that is being measured. This does not occur due to maturation or improvement over time, but due to the statistical likelihood of someone with high scores not doing as well when a test is repeated or of someone with low scores being statistically likely to do better when the test is repeated. Suppose, for example, that you assessed 200 children who had attention deficit hyperactivity disorder with a behavioural test and scored their risk of having poor academic outcomes and that you provided the 30 children who had the poorest scores with an intensive behavioural regimen and medication. Even if the interventions were not effective, you would still expect to observe some improvement in the children’s scores on the behavioural test when it is next given due to regression to the mean. When outliers are repeatedly measured, subsequent values are less likely to be outliers (that is, they are expected to be closer to the mean value of the whole group). This always happens and health professionals who do not expect this to occur often attribute any improvement that is observed to the intervention. The best way to deal with the problem of regression to the mean is to randomly allocate participants to either an experimental group or a control group. The regression to the mean effect can only be accounted for by using a control group (which will have the same regression to the mean if the randomisation succeeded and the two groups are similar). How to determine this is explained later in this chapter.

• Placebo effect. This is a well-known type of bias where an improvement in the participants’ condition occurs because they expect or believe that the intervention they are receiving will cause an improvement (even though, in reality, the intervention may not be effective at all).

• Hawthorne effect. This is a type of bias that can occur when participants experience improvements, not because of the intervention that is being studied, but because of the attention that participants are receiving from being a part of the research process.

• Rosenthal effect. This occurs when participants perform better because they are expected to and, in a sense, this expectation has a similar sort of effect as a self-fulfilling prophecy.

Controlled studies

By now, it should be clear that having a control group which can be compared to the intervention group in a study is the best way of making sure that bias and extraneous factors that can influence the results of a study are limited. However, it is not so simple as just having a control group as part of the study. The way in which the control group is created can make an enormous difference to how well the study design actually controls for bias.

Non-randomised controlled studies

You will recall from the hierarchy of evidence about the effects of interventions (in Chapter 3) that case-control and cohort studies are located above uncontrolled study designs. This is because they make use of control groups. Cohort studies follow a cohort that have been exposed to a situation or intervention and have a comparison group of people who have not been exposed to the situation of interest (for example, they have not received any intervention). However, because cohort studies are observational studies, the allocation of participants to the intervention and control groups is not under the control of the researcher. It is not possible to tell if the participants in the intervention and control groups are similar in terms of all the important factors and, therefore, it is unclear to what extent the exposure (that is, the intervention) might be the reason for the outcome rather than some other factor.

We saw in Chapter 2 that a case-control study is one in which participants with a given disease (or health condition) in a given population (or a representative sample) are identified and are compared to a control group of participants who do not have that disease (or health condition). When a case-control study has been used to answer a question about the effect of an intervention, the ‘cases’ are participants who have been exposed to an intervention and the ‘controls’ are participants who have not. As with cohort studies, because this is an observational study design, the researcher cannot control the assembly of the groups under study (that is, which participants go into which group). Although the controls that are assembled may be similar in many ways to the ‘cases’, it is unlikely that they will be similar with respect to both known and unknown confounders. Chapter 2 explained that confounders are factors that can become confused with the factor of interest (in this case, the intervention that is being studied) and obscure the true results.

In a non-randomised experimental study, the researchers can control the assembly of both experimental and control groups, but the groups are not assembled using random allocation. In non-randomised studies, participants may choose which group they want to be in, or they may be assigned to a group by the researchers. For example, in a non-randomised experimental study that is evaluating the effectiveness of a particular public health intervention (such as an intervention that encourages walking to work) in a community setting, a researcher may assign one town to the experimental condition and another town to the control condition. The difficulty with this approach is that the people in these towns may be systematically different to each other and so confounding factors, rather than the intervention that is being trialled, may be the reason for any difference that is found between the groups at the end of the study.

So not only are control groups essential, but in order to make valid comparisons between groups, they must be as similar as possible at the beginning of a study. This is so we can say with some certainty that any differences that are found between groups at the end of the study are likely to be due to the factor under study (that is, the intervention), rather than because of bias or confounding. To maximise the similarity between groups at the start of a study, researchers need to control for both known and unknown variables that might influence the results. The best way to achieve this is through randomisation.Non-randomised studies are inherently biased in favour of the intervention that is being studied, which can lead researchers to reach the wrong conclusion about the effectiveness of the intervention.²

Randomised controlled trials

The key feature of randomised controlled trials is that the participants are randomly allocated to either an intervention (experimental) group or a control group. The outcome of interest is measured in participants in both groups before (known as pre-test) and then again after the intervention (known as post-test) is provided. Therefore, any changes that appear in the intervention group pre-test to post-test, but not in the control group, can be reasonably attributed to the intervention. Figure 4.1 shows the basic design of a randomised controlled trial.

FIGURE 4.1 Basic design of a randomised controlled trial

You may notice that we keep referring to how randomised controlled trials can be used to evaluate the effectiveness of an intervention. It is worth noting that they can also be used to evaluate the efficacy of an intervention. Efficacy refers to interventions that are tested in ideal circumstances, such as where intervention protocols are very carefully supervised and participant selection is very particular. Effectiveness is an evaluation of an intervention in circumstances that are more like real life, such as where there is a broader range of participants included and a typical clinical level of intervention protocol supervision. In this sense, effectiveness trials are more pragmatic in nature (that is, they are accommodating of typical practices) than efficacy trials.

There are a number of variations on the basic randomised controlled trial design, which partly depend on the type or combination of control groups used. There are many variations on what the participants in a control group in a randomised controlled trial actually receive. For example, participants may receive no intervention of any kind (a ‘no intervention’ control), or they may receive a placebo, some form of social control or a comparison intervention. In some randomised controlled trials, there are more than two groups. For example, in one study there might be two intervention groups and one control group or, in another study, there might be an intervention group, a placebo group and a ‘no intervention’ group. Randomised crossover studies are a type of randomised controlled trial in which all participants take part in both intervention and control groups but in random order. For example, in a randomised crossover trial of transdermal fentanyl (a pain medication) and sustained-release oral morphine (another pain medication) for treating chronic non-cancer pain, participants were assigned to one of two intervention groups.³ One group was randomised to four weeks of treatment with sustained release oral morphine followed by transdermal fentanyl for four weeks. The second group received the same treatments but in reverse order. A difficulty with crossover trials is that there needs to be a credible wash-out period. That is, the effects of the intervention provided in the first phase must no longer be evident prior to commencing the second phase. In the example we used here, the effect of oral morphine must be cleared prior to the fentanyl being provided.

As we have seen, the advantage of a randomised controlled trial is that any differences that are found between groups at the end of the study are likely to be due to the intervention rather than extraneous factors. But the extent to which these differences can be attributed to the intervention is also dependent on some of the specific design features that were used in the trial, and these deserve close attention. The rest of this chapter will look at randomised controlled trials in more depth within the context of the clinical scenario that was presented at the beginning of this chapter. In this scenario you are a health professional who is working in a small group at a community health centre and you are looking for research regarding the effectiveness of falls prevention programs. To locate relevant research, you start by focusing on what it is that you specifically want to know about.

How to structure a question about the effect of intervention

In Chapter 2, you learnt how to structure clinical questions using the PICO format: Patient/Problem/Population, Intervention/Issue, Comparison (if relevant) and Outcomes.

In our falls clinical scenario, the population that we are interested in is elderly people who fall. We know from our clinical experience that people who have had falls in the past are at risk of falling again, so it makes sense to target our search for interventions aimed at people who are either ‘at risk’ of falling and/or have a history of falling. The intervention that we are interested in is a falls prevention program. Are we interested in a comparison intervention? While we could compare the effectiveness of one type of intervention with another, for this scenario it is probably more useful to start by firstly thinking about whether the intervention is effective. To do this we would need to compare the intervention to either a placebo (a concept we will discuss later) or to usual care. There are a number of outcomes that we could consider important for people who fall. The most obvious outcome of interest is a reduction in the number of falls. However, we could also look for interventions that consider the factors that contribute to falls such as balance problems or, in this scenario, a person’s confidence (or self-efficacy) to undertake actions that will prevent them from falling.

Clinical scenario (continued): The question

While there are a number of questions about interventions that can be drawn from the scenario that was presented at the beginning of this chapter, you decide to form the following clinical question: In community-dwelling older people with a history of falling, are falls prevention programs effective in reducing falls and increasing self-efficacy compared to usual care?

How to find evidence to answer questions about the effects of intervention

Our clinical scenario question is a question about the effectiveness of an intervention to prevent falls and to improve self-efficacy. You can use the hierarchy of evidence for this type of question as your guide to know which type of study you are looking for and where to start searching. In this case, you are looking for a systematic review of randomised controlled trials. If there is no relevant systematic review, you should next look for a randomised controlled trial. If no relevant randomised controlled trials are available, you would then need to look for the next best available type of research, as indicated by the hierarchy of evidence for this question type that is shown in Chapter 2.

As we saw in Chapter 3, the best source of systematic reviews of randomised controlled trials is the Cochrane Database of Systematic Reviews, so this would be the logical place to start searching. The Cochrane Library also contains the Cochrane Central Register of Controlled Trials which includes a large collection of citations of randomised controlled trials. If you are looking for randomised controlled trials specifically in the rehabilitation field, two other databases that you could consider searching for this topic are PEDro (www.pedro.org.au/) or OTseeker (www.otseeker.com). These databases were explained in Chapter 3. One of their advantages is that they have already evaluated the risk of bias that might be of issue in the randomised controlled trials that they index.

Now that you have found a research article that you are interested in, it is important to critically appraise it. That is, you need to examine the research closely to determine whether and how it might inform your clinical practice. As we saw in Chapter 1, to critically appraise research, there are three main aspects to consider: 1) its internal validity (in particular, the risk of bias); 2) its impact (the size and importance of any

Clinical scenario (continued): Finding evidence to answer your question

You search the Cochrane Database of Systematic Reviews and there are two reviews concerning falls prevention. One of these reviews evaluated the effect of interventions that were designed to reduce the incidence of falls in the elderly, but not just those who are community-living—it also included those in institutional care and hospital care. The other review focussed on population-level interventions. As neither of these reviews is what you are after, you next search OTseeker and find six articles that are possibly relevant. You are specifically interested in interventions aimed at community-dwelling older people and the title of one of these articles matches this. After reading the abstract, you know that this article describes a randomised controlled trial that has investigated the effectiveness of a program (called the ‘Stepping On’ program) for reducing the incidence of falls in the community-living elderly.4 As you found this article indexed in OTseeker, it has been evaluated with respect to risk of bias; however, in order to evaluate whether it also measured self-efficacy as an outcome and to specifically examine the results of the trial and determine whether the findings may be applicable to your clinical scenario, you obtain the full text of the article. You find that it does measure self-efficacy, so you proceed to critically appraise the article. (As most of the trials in OTseeker are pre-appraised, you would normally not need to appraise the risk of bias in the article for yourself. However, as the purpose of this clinical scenario exercise is to demonstrate how to appraise a randomised controlled trial, we will proceed to appraise this article even though it was located in OTseeker.)

Clinical scenario (continued): Structured abstract of our chosen article (the ‘stepping on’ trial)

Citation: Clemson L, Cumming R, Kendig H et al. The effectiveness of a community-based program for reducing the incidence of falls in the elderly: a randomised trial. Journal of the American Geriatrics Society 2004; 52:1487–1494.

Design: Randomised controlled trial.

Setting: Community venues and follow-up home visits in New South Wales, Australia.

Participants: 310 community-living people aged over 70 years and older (mean age 78.4 years, 74% female) with a history of falling in the past year or who were concerned about falling.

Intervention: A community-based small-group education program that aimed to help older people reduce falls and enhance their self-efficacy in fall-risk situations. Key content that was covered by the program included: lower limb balance and strength exercises, coping with visual impairment, medication management and home and community safety. One session also involved community mobility practice. A cognitive-behavioural approach was used, with practice and application of behaviours encouraged during and after groups. The program consisted of 2-hour group sessions (held weekly for 7 weeks), an individual home visit (held within 6 weeks of the last group session) and a 3-month group booster session. All intervention was provided by an experienced occupational therapist. Participants in the control group received one or two social home visits from a student.

Outcomes: The primary outcome measure was the occurrence of falls (for which a specific definition was used). There was also a range of secondary outcome measures used. Of particular interest to this clinical scenario, there were two self-efficacy outcome measures that were used. One was the Modified Falls Efficacy Scale, which assesses how confident a person is in their ability to avoid falls when performing basic activities of daily living. The other was the Mobility Efficacy Scale, which assesses how confident a person is in their ability to avoid falls when performing functional tasks that require a greater degree of postural challenge than the tasks assessed by the Modified Falls Efficacy Scale.

Follow-up period: Approximately 14 months (median 420 days).

Main results: The intervention group experienced a 31% reduction in falls relative to the control group.

Conclusion: Cognitive-behavioural learning in a small group environment can reduce falls and the Stepping On program is an option for effective falls prevention.

effect found); and 3) whether or how the evidence might be applicable to your client or clinical practice.

Is this evidence likely to be biased?

In this chapter we will discuss six criteria that are commonly used for appraising the potential risk of bias in a randomised controlled trial. These six criteria are summarised in Box 4.1 and can be found in the Users Guide to the Literature⁵ and in many appraisal checklists such as the Critical Appraisal Skills Program (CASP) checklist and the PEDro scale.⁶ A number of studies have demonstrated that estimates of treatment effects may be distorted in trials that do not adequately address these issues.^7,⁸ As you work through each of these criteria when appraising an article, it is important to consider the direction of the bias (that is, is it in favour of the intervention or control group?) as well as its magnitude. As we pointed out in Chapter 1, all research has flaws, but we do not just want to know what the flaws might be, but whether and how they might influence the results of a study.

Was the assignment of participants to groups randomised?

Randomised controlled trials, by definition, randomise participants to either the experimental or control condition. The basic principle of randomisation is that each participant has an equal chance of being assigned to any group, such that any difference between the groups at the beginning of the trial can be assumed to be due to chance. The main benefit of randomisation is related to the idea that this way, both known and unknown participant characteristics should be evenly distributed between the intervention and control groups. Therefore, any differences between groups that are found at the end of the study are likely because of the intervention.⁹

Random allocation is best done by a random numbers table which can be computer-generated. Sometimes it is done by tossing a coin or ‘pulling a number out of a hat’. Additionally, there are different randomisation designs that can be used and you should be aware of them. Researchers may choose to use some form of restriction, such as blocking or stratification, when allocating participants to groups in order to create a greater balance between the groups at baseline in known characteristics.¹⁰ Different randomisation designs are summarised below:

• Simple randomisation: involves randomisation of individuals to the experimental or control condition.

• Cluster randomisation: involves random allocation of intact clusters of individuals rather than individuals (for example, randomisation of schools, towns, clinics or general practices).

• Stratified randomisation: in this design, participants are matched and randomly allocated to groups. This method ensures that potentially confounding factors such as age, gender or disease severity are balanced between groups. For example, in a trial that involves people who have had a stroke, participants might be stratified according to their initial stroke severity as belonging to either a ‘mild’, ‘moderate’ or ‘severe’ stratum. This way when randomisation to study groups occurs, researchers can ensure that, within each stratum, there are equal numbers of participants in the intervention and control groups.

• Block randomisation: In this design, participants who are similar are grouped into ‘blocks’ and then assigned to the experimental or control conditions within each block. Block randomisation often uses stratification An example of block randomisation can be seen in a randomised controlled study of a community-based parenting education intervention program designed to increase the use of preventive paediatric

Clinical scenario (continued): Was the assignment of participants to groups randomised?

In the Stepping On trial, it is explicitly stated that participants were randomised and that the randomisation was stratified in blocks of four, according to participants’ gender and number of falls in the previous 12 months.

healthcare services among low income, minority mothers.¹¹ Two hundred and eighty-six mother–infant dyads recruited from four different sites in Washington DC were assigned to either the standard social services (control) group or the intervention group. To ensure that there were comparable numbers within each group across the four sites, site-specific block randomisation was used. By using block randomisation, selection bias due to demographic differences across the four sites was avoided.

Was the allocation sequence concealed?

As we have seen, the big benefit of a randomised controlled trial over other study designs is the fact that participants are randomly allocated to the study groups. However, the benefits of randomisation can be undone if the allocation sequence is manipulated or interfered with in any way. As strange as this might seem, a health professional who wants their client to receive the intervention that is being evaluated may swap their client’s group assignment so that their client receives the intervention being studied. Similarly, if the person who recruits participants to a study knows which condition the participants are to be assigned to, this could influence their decision about whether or not to enrol them in the study. This is why assigning participants to study groups using alternation methods, such as every second person who comes into the clinic, or assigning participants by methods such as date of birth is problematic because the randomisation sequence is known to the people involved.⁹

Knowledge about which group a participant will be allocated to if they are recruited into a study can lead to the selective assignment of participants, and thus introduce bias into the trial. This knowledge can result in manipulation of either the sequence of groups that participants are to be allocated to or the sequence of participants to be enrolled. Either way, this is a problem. This problem can be dealt with by concealing the allocation sequence from the people who are responsible for enrolling clients into a trial or from those who assign participants to groups, until the moment of assignment.¹² Allocation can be concealed by having the randomisation sequence administered by someone who is ‘off-site’ or at a location away from where people are being enrolled into the study. Another way to conceal allocation is by having the group allocation placed in sealed opaque envelopes. Opaque envelopes are used so that the group allocation cannot be seen if the envelope is held up to the light! The envelope is not to be opened until the client has been enrolled into the trial (and is therefore now a participant in the study).

Hopefully, the article that you are appraising will clearly state that allocation was concealed, or that it was done by an independent or off-site person or that sealed opaque envelopes were used. Unfortunately though, many studies do not give any indication about whether allocation was concealed,^13,¹⁴ so you are often left wondering about this, which is frustrating when you are trying to appraise a study. It is possible that some of these studies did use concealed allocation, but you cannot tell this from reading the article.

Clinical scenario (continued): Concealed allocation

In the Stepping On trial, allocation was concealed. The article states that the randomisation was conducted by a researcher who was not involved in participant screening or assessment.

Were the groups similar at the baseline or start of the trial?

One of the principal aims of randomisation is to ensure that the groups are similar at the start of the trial in all respects, except for whether they received the experimental condition (that is, the intervention of interest) or not. However, the use of randomisation does not guarantee that the groups will have similar known baseline characteristics. This is particularly the case if there is a small sample size. Authors of a research article will usually provide data in the article about the baseline characteristics of both groups. This allows readers to make up their own minds as to whether the balance between important prognostic factors (variables that have the potential for influencing outcomes) is sufficient at the start of the trial. Consider, for example, a study about the effectiveness of acupuncture for reducing pain from migraines compared to sham acupuncture. If the participants who were allocated to the acupuncture group had less severe or less chronic pain at the start of the study than the participants who were allocated to the sham acupuncture group, any differences in pain levels that are seen at the end of the study might be the result of that initial difference and not the acupuncture that was provided.

Differences between the groups that are present at baseline after randomisation have occurred due to chance and, therefore, determining if these differences are statistically significant by using p values is not an appropriate way of assessing such differences.¹⁵ That is, rather than using the p value that is often reported in studies, it is important to examine these differences by comparing means or proportions visually. The extent to which you might be concerned about a baseline difference between the groups depends on how large a difference it is and whether it is a key prognostic variable, both of which require some clinical judgement. The stronger the relationship between the characteristic and the outcome of interest, the more the differences between groups will weaken the strength of any inference about efficacy.⁵ For example, consider a study that is investigating the effectiveness of group therapy in improving communication for people who have chronic aphasia following stroke compared with usual care. Typically, such a study would measure and report a wide range of variables at baseline (that is, prior to the intervention) such as participants’ age, gender, education level, place of residence, time since stroke, severity of aphasia, side of stroke and so on. Some of these variables are more likely to influence communication outcomes than others. The key question to consider is: are any differences in key prognostic variables between the groups large enough that they may have influenced the outcome(s)? Hopefully if differences are evident, the researchers will have corrected for this in the data analysis process.

As a reader (and critical appraiser) of research articles, it is important that you are able to see data for key characteristics that may be of prognostic value in both groups. Many articles will present this data in a table, with the data for the intervention group presented in one column and the data for the control group in another. This enables you to easily compare how similar the groups are for these variables. As well as presenting baseline data about key sociodemographic characteristics (for example, age and gender), articles should also report data about important measures of the severity of the condition (if that is relevant to the study—most times it is) so that you can see if the groups were also similar in this respect. For example, in a study that involves participants who have had a stroke, the article may present data about the initial stroke severity of participants, as this variable has the potential to influence how participants respond to an intervention. In most cases, sociodemographic variables alone are not sufficient to determine baseline similarity.

One other area of baseline data that articles should report is the key outcome(s) of the study (that is, the pre-test measurement(s)). Let us consider the example presented earlier of people receiving group communication treatment for aphasia to illustrate why this is important. Although such an article would typically provide information about sociodemographic variables and clinical variables (such as severity of aphasia, type of stroke and side of stroke), having information about participants’ initial (that is, pre-test) scores on the communication outcome measure that the study used would be helpful for considering baseline similarity. This is because, logically, participants’ pre-test scores on a communication measure are likely to be a key prognostic factor for the main outcome of the study, which is communication ability.

When appraising an article, if you do conclude that there are baseline differences between the groups that are likely to be big enough to be of concern, hopefully the researchers will have statistically adjusted for these in the analysis. If they have not, you will need to try and take this into account when interpreting the study.