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. 2003 Oct 4;327(7418):785–789. doi: 10.1136/bmj.327.7418.785

Evidence for risk of bias in cluster randomised trials: review of recent trials published in three general medical journals

Suezann Puffer 1, David Torgerson 1, Judith Watson 1
PMCID: PMC214092  PMID: 14525877

Abstract

Objective To examine the prevalence of a risk of bias associated with the design and conduct of cluster randomised controlled trials among a sample of recently published studies.

Design Retrospective review of cluster randomised trials published in the BMJ, Lancet, and New England Journal of Medicine from January 1997 to October 2002.

Main outcome measures Prevalence of secure randomisation of clusters, identification of participants before randomisation (to avoid foreknowledge of allocation), differential recruitment between treatment arms, differential application of inclusion and exclusion criteria, and differential attrition.

Results Of the 36 trials identified, 24 were published in the BMJ,11 in the Lancet, and a single trial in the New England Journal of Medicine. At the cluster level, 15 (42%) trials provided evidence for secure allocation and 25 (69%) used stratified allocation. Few trials showed evidence of imbalance at the cluster level. However, some evidence of susceptibility to risk of bias at the individual level existed in 14 (39%) studies.

Conclusions Some recently published cluster randomised trials may not have taken adequate precautions to guard against threats to the internal validity of their design.

Introduction

In most clinical trials participants are randomised as individuals to different treatments. Sometimes individual allocation is not possible or desirable, and groups of individuals are randomised instead: this is known as cluster or group randomisation. Many reasons for using cluster allocation exist. For example, evaluation of clinical guidelines or medical education on patient outcomes almost always requires that healthcare professionals are the “unit” of allocation.

Although randomised trials are the most robust evaluative method, poorly conducted studies are susceptible to different forms of selection bias that can make their results unsound. Methodological reviews of individually randomised trials have shown that rigorously conducted trials produce different effect estimates from poorly conducted studies.1,2 Less attention has been paid, however, to cluster trials. Cluster trials are generally more difficult to design and execute than individually randomised studies, and some design features of a cluster trial may make it especially vulnerable to a range of threats that can introduce selection bias.

In cluster trials potential bias in the execution of the trial can occur at two levels, the first of which is the cluster level. Randomisation of clusters needs to be undertaken carefully and preferably independently. Otherwise, biased allocation may occur (certain clusters being allocated to a particular arm on the basis of reasons that might affect outcome). It is theoretically possible for allocation of clusters to be subverted, as has happened in individually randomised trials.3 Similarly, once clusters have been allocated it is important, as with individually randomised trials, to try to retain the cluster in its allocated group and avoid the cluster dropping out, to avoid the risk of attrition bias.

The second level at which bias can occur in cluster trials is after the clusters have been allocated and when individual participants are recruited into the study. Sometimes identification and recruitment of participants and assessment of outcome in a cluster trial are relatively straightforward with little scope for bias. For example, in an evaluation of the effect of offering routine influenza vaccination to healthcare workers on patient mortality, hospitals were randomised to offer routine vaccination to staff or not.w1 Any differences between the groups were then observed by using mortality data. Two important methodological aspects to this trial, and other similar cluster trials, limit the risk of bias. These are complete identification and inclusion of participants, partly owing to the fact that consent was not needed for either treatment or collection of data. Because all the participants were identified and included at the point of randomisation, except for chance imbalances the two groups should be similar at baseline (assuming that the allocation procedure was fair), which avoids the threat of selection bias.

In some cluster trials identification and inclusion of participants and assessment of outcome are less straightforward. Often participants have to be recruited prospectively after randomisation. For example, in a trial of the effectiveness of a training package for general practitioners, patients had to be identified prospectively after the general practitioner had been randomised.w2 The prospective inclusion of participants can potentially lead to selection bias through the recruitment of different types of participant by the researcher or clinician. If the person prospectively recruiting participants has “foreknowledge” of the allocation group then, as shown in individually randomised trials, bias can result.3 In addition to this source of selection bias, another can be introduced by the participant if consent is needed after randomisation.

Selection bias can be introduced if consent is withheld for either treatment or data collection. This is a well known disadvantage of acquiring consent after randomisation in individually randomised trials (known as Zelen's method4), because some refusal of treatment or data collection will usually occur.5 This is less of a problem in non-Zelen designs, as participants are told in advance about the treatment options and if they decline to be exposed to one of the options they are not randomised (although some may decline in the period between allocation and receipt of treatment).

Several ways of avoiding the biases outlined above exist. One is to try to identify trial participants before randomisation and obtain consent for treatment, data collection, or both before allocation. Use of prior identification and prior consent avoids potential biases occurring through foreknowledge of the allocation schedule, by the researcher and patient. If this is not possible, identification and recruitment of participants should ideally be undertaken by someone blinded to the group allocation.

Another problem that can lead to bias, in both individual and cluster randomised trials, is the differential application of inclusion and exclusion criteria. Differential exclusion between groups in an individually randomised trial of breast cancer screening, identified in a systematic review, has led to questions about its rigour.6 Again this problem can be reduced if the person applying the criteria is blinded to the group allocation.

In this paper we review some recently published cluster trials to determine the extent of their risk of bias. We also describe the steps that some authors took to reduce these risks.

Methods

Searching and data extraction

We hand searched the BMJ, Lancet, and New England Journal of Medicine for all cluster randomised trials published from January 1997 to October 2002. We based our choice of journals on anecdotal experience that the BMJ regularly publishes cluster trials, as does the Lancet, and a wish to include a non-British general medical journal. We limited our search to five years merely so that we had a sample of fairly recent trials. We did not have a predetermined sample size.

Definition of outcomes

Selection bias can be introduced into a trial in several different ways. In this paper we sought evidence for the risk of bias from several sources.

Secure cluster allocation—This is where evidence exists that cluster randomisation was securely undertaken.

Cluster attrition—This occurs when clusters are lost to follow up after randomisation.

Cluster imbalance—This is where evidence exists of imbalance in important variables at the cluster level.

Differential individual recruitment or consent—This is when different proportions of participants are recruited to the different arms of the trial. If recruitment rates differ between groups this may lead to the risk of bias.

Differential individual exclusion or inclusion—This can occur when eligibility criteria are applied differentially after randomisation, which can introduce bias.

Two of us (SP, JW) hand searched the journals and independently extracted data. The three authors met to discuss all the papers and any disagreements. If we observed differences in proportions between the randomised groups in recruitment, consent, and exclusion or inclusion rates we used χ2 to test for significance.

Results

We identified 42 potentially eligible trials. We excluded six studies: one was a 14 year follow up of an earlier trial,7 another measured the intervention and outcome on only one level,8 another had a switchback design,9 two guideline studies did not provide any data on individual participants,10,11 and the sixth trial had a mixture of cluster and individual allocation.12 Of the 36 trials included,w1-w36 24 were published in the BMJ, 11 in the Lancet, and one in the New England Journal of Medicine. In table 1 we describe the basic characteristics of the trials. In table 2 we examine whether the trials identified participants before random allocation and any evidence of bias occurring in the trials.

Table 1.

Characteristics of included cluster trials

Study No of clusters No of participants Description Clustering accounted for in sample size estimation?
Aveyard 1999w3 52 9 301 Expert system for smoking prevention and cessation in schools Yes
Bennewith 2002w4 98 2 141 Prevention of repeat episodes of deliberate self harm Yes
Carman 2000w1 20 1 437 Influenza vaccination of healthcare workers Yes
Chapman 2000w5 8 346 Educational intervention to prevent dog bites No
Field 2001w6 9 494 Two methods of data collection Yes
Flottorp 2002w7 142 12 369 To improve general practice management of sore throat and urinary tract infections Yes
Gavgani 2002w8 18 4 498 Insecticide impregnated dog collars on incidence of zoonotic visceral leishmaniasis No
Graham 2002w9 24 3 794 Teenagers' knowledge of emergency contraception Yes
Haider 2000w10 40 726 Community based peer counsellors on breast feeding Not clear
Jolly 1999w11 67 686 Programme to coordinate and support follow up care in general practice Not clear
Jordhoy 2000w12 6 707 Palliative care intervention Not clear
Kannus 2000w13 22 1 725 Hip protectors No
Kendrick 1999w14 36 2 152 Prevent unintentional injuries in children Yes
Kidane 2000w15 37 70 506 Maternal education for early treatment of paediatric malaria Yes
King 2002w2 116 410 Behavioural therapy to treat patients with depression Yes
Kinmonth 1998w16 43 360 Patient centred care for diabetes in general practice Yes
Kroeger 2002w17 14 2 913 Insecticide impregnated curtains to control transmission of cutaneous leishmaniasis No
MacArthur 2002w18 37 3 580 Community postnatal care Yes
McCartney 1997w19 28 182 200 General practitioner feedback to increase aspirin use No
Moher 2001w20 21 2 142 Secondary prevention of coronary heart disease Yes
Montgomery 2000w21 27 810 Interventions for management of hypertension Yes
Morrison 2001w22 221 689 Infertility guidelines for general practitioners Yes
Morrow 1999w23 39 130 Home based counselling to promote breast feeding Yes
O'Cathain 2002w24 13 10 327 Leaflets to promote informed choice in maternity care Yes
Olivarius 2001w25 311 1 470 Structured personal care of type 2 diabetes mellitus No
Premaratne 1999w26 40 48 800 Effectiveness of an asthma resource centre No
Sagliocca 1999w27 146 404 Hepatitis A vaccine No
Sahota 2001w28 10 636 School intervention to reduce risk factors for obesity Yes
Shah 2001w29 6 325 Peer led programme for asthma education in adolescents No
Smeeth 2001w30 106 42 278 Methods to administer a screening questionnaire No
Steptoe 1999w31 20 883 Behavioural counselling in general practice Yes
Thompson 2000w32 59 4 192 Detection and outcome of depression in primary care Yes
Van Eijk 2001w33 21 46 078 Academic detailing to reduce antidepressant use No
Wawer 1999w34 10 44 107 Prevention of sexually transmitted disease No
West 1999w35 270 44 646 Supplementation with vitamin A or β carotene on mortality related to pregnancy No
Wight 2000w36 25 8 430 Teacher delivered sex education Yes

Table 2.

Potential sources of bias

Study Did cluster allocation seem secure? Cluster allocation stratified? Evidence of Cluster imbalance? How many Clusters lost after randomisation? Patients identified before randomisation? Could selection have been biased? Evidence of risk of bias?
Aveyard 1999w3 Yes Yes No 1 Yes No No
Bennewith 2002w4 Yes Yes No 1 No No No
Carman 2000w1 Yes Yes Yes 0 Yes No No/Yes*
Chapman 2000w5 Unclear Unclear Yes 0 No No No
Field 2001w6 Yes Yes No 0 No Yes No
Flottorp 2002w7 Yes No No 22 Yes No No
Gavgani 2002w8 Unclear Yes No 0 Yes No Attrition
Graham 2002w9 Yes Yes Unclear 0 Yes Yes Consent
Haider 2000w10 Unclear No Unclear 0 No Yes No
Jolly 1999w11 Yes Yes Unclear 0 No Yes Recruitment
Jordhoy 2000w12 Unclear Yes Unclear 0 No Yes No
Kannus 2000w13 Unclear No Unclear 0 Yes Yes Consent
Kendrick 1999w14 Yes Yes Unclear 0 Unclear Unclear No
Kidane 2000w15 Unclear Yes Unclear 0 Yes No No
King 2002w2 Unclear No No 32 No No No
Kinmonth 1998w16 Yes Yes No 2 No Yes Recruitment
Kroeger 2002w17 Yes Yes No 1 Yes No No
MacArthur 2002w18 Yes Yes Unclear 1 No Yes Attrition
McCartney 1997w19 Unclear Unclear No 0 Yes No No
Moher 2001w20 Yes Yes No 0 Yes Yes Exclusion
Montgomery 2000w21 Yes Yes Unclear 0 No No No
Morrison 2001w22 Unclear Yes No 7 No Yes No
Morrow 1999w23 Yes Yes Unclear 8 No Yes No
O'Cathain 2002w24 No Yes Unclear 0 No Yes No
Olivarius 2001w25 Unclear Yes No 10 No Yes Exclusion
Premaratne 1999w26 Unclear Yes No 0 No No No
Sagliocca 1999w27 Unclear No Unclear 0 No No Attrition
Sahota 2001w28 No Yes Unclear 0 Yes No No
Shah 2001w29 Unclear No Yes 0 No No Inclusion
Smeeth 2001w30 Unclear Unclear Unclear 0 Yes No No
Steptoe 1999w31 Unclear Yes No 0 No Yes Recruitment
Thompson 2000w32 Yes Yes Unclear 4 No Yes No
Van Eijk 2001w33 Unclear Unclear No 0 Yes No No
Wawer 1999w34 Unclear Yes No 0 Yes No Consent
West 1999w35 Unclear Yes No 0 No Unclear No
Wight 2002w36 Unclear Unclear No 0 Unclear No Attrition
*

Not for main outcome, possibly for secondary outcome.

Secure cluster allocation—Fifteen trials seemed to use a secure method of allocating clusters; the remainder did not clearly describe who undertook the allocation (table 2) or how this was done. Most trials used some form of stratified random allocation to reduce the possibility of “chance bias.”

Cluster attrition—In 10 trials a loss of clusters occurred between randomisation and follow up. Most of the trials lost only a small proportion of their clusters, but one study lost more than half (56%) of all the randomised clusters.w2

Differential consent or recruitment—We found some evidence for differential consent or recruitment in seven of the 23 trials that had not undertaken prior identification of participants (table 2). Three trials recruited more participants from one group than the other,w11 w16 w31 and the other four studies differentially obtained consent from more participants in one arm than the other.w9 w13 w29 w34 One trial, although it seemed to identify all the participants before allocation for the main mortality outcome, seemed to have introduced the risk of selection bias into the measurement of its secondary outcome.w1

Differential application of inclusion or exclusion criteria—We found two trials that seemed to have applied inclusion or exclusion criteria differentially between groups after randomisation.w20 w25 Moher et al, in a study promoting methods of secondary prevention of coronary disease, excluded significantly more participants owing to misdiagnosis in the intervention groups than in the control group.w20 Similarly, Olivarius et al excluded twice as many participants because of illness in the intervention group than in the control arm.w25

Differential attrition—Evidence of differential attrition between the randomised groups existed in four trials.w8 w18 w27 w36

Table 3 summarises the potential sources of bias risk in 14 trials in which we observed differences between the groups that indicate a risk of selection bias. Authors of six studies alerted the reader to the potential risk of bias in their study.

Table 3.

Evidence of risk of bias

Study Potential source of bias Acknowledgment of risk by authors and steps taken
Carmen 2000w1 48% v 33% of patients having influenza vaccination, P<0.01; 69% (258/375) v 78% (269/344) accepted virological screening for secondary outcome assessment, P=0.004 Yes, for cluster imbalance, used adjusted odds ratios
Gavgani 2002w8 7.6% (143/1870) v 11.4% (229/2006) attrition in control and intervention groups, P<0.001 No
Graham 2002w9 12.2% (216/1768) of control group refused consent v 17% (344/2026) of intervention group, P<0.001 No
Jolly 1999w11 Control group recruited 15.5% more than intervention group; practice population not given, so impossible to see if significantly different Noted recruitment “imbalance” in discussion
Kannus 2000w13 31.4% (204/650) of intervention group refused consent v 8.7% (94/1075) of control group, P<0.001 Acknowledged potential for selection bias in discussion
Kinmonth 1998w16 0.06% (142/225 015) v 0.047% (108/230 560) of practice populations were recruited for intervention and control groups, P=0.02 No
MacArthur 2002w18 4.2% (46/1087) v 2.6% (25/977) of intervention and control groups withdrew or moved away, P=0.04 Commented on loss to follow up in discussion
Moher 2001w20 0.32% (2/623) v 2.6% (20/772) and 1.3% (10/747) misdiagnoses for control and two intervention groups, P=0.002 No
Olivarius 2001w25 8.7% (67/774) v 4.0% (28/696) excluded owing to illness in intervention group and control group, P<0.01 Noted in results more post-randomisation exclusions
Sagliocca 1999w27 3.9% (7/178) v 0% (0/173) lost to follow up in control and intervention groups, P=0.02 No
Shah 2001w29 22.3% (148/662) v 17.3% (124/717) included in control and intervention groups, P=0.02 No
Steptoe 1999w31 Control practices recruited 567 v 316 participants given similar sized populations (P value not calculable) Differential recruitment rate mentioned in discussion, but not as a potential source of bias
Wawer 1999w34 17.5% (4002/22 915) v 14.7% (3125/21 192) refused consent or treatment in intervention and control groups, P<0.001 No
Wight 2002w36 30.6% (1070/3493) v 27.5% (1069/3892) attrition in numbers reporting intercourse in intervention and control groups, P=0.003 No

Discussion

Cluster trials can be difficult to do; nevertheless, they are needed to evaluate some interventions. Although a large literature exists about sources of potential bias that can occur in individually randomised trials, less evidence is available about the special problems encountered in cluster trials.

Evidence of bias risk at cluster level

Some authors did not clearly describe the allocation process of the clusters, which is important as this can be subverted; other trialists were clear in stating that an independent person undertook the allocation. In most trials some form of stratification was used to reduce the element of chance bias, although this was not always successful. Some trials lost complete clusters after randomisation. However, with the exception of one trial,w2 the proportion of clusters lost was relatively low and therefore would be unlikely to introduce bias.

Evidence of bias risk at individual level

One of the major risks for introduction of bias is when prospective recruitment is needed. This difficulty can be overcome and the risk of bias reduced, as two examples serve to illustrate. Bennewith et al reduced the possibility of recruitment bias by blinding the clinician identifying participants until after the patient was assessed as being eligible or not.w4 Similarly, King et al reduced the same threat by asking a trained receptionist to recruit patients.w2 Because that trial evaluated a training package to help general practitioners to manage depressed patients, the training would probably have reduced the diagnostic threshold of the general practitioners. Thus, had the doctors recruited participants themselves, this would have increased the risk that they could have recruited either more or less seriously depressed participants than the control doctors. Use of receptionists reduced this risk.

As well as differences between groups in recruitment and consent, we found that differential post-randomisation exclusion or inclusion was a problem in some studies. Inclusion of the “wrong” participant is likely to be a problem in some cluster trials. Two ways exist to deal with wrong inclusions and avoid bias. Firstly, all participants could be retained within the trial after allocation whether or not they fitted the inclusion criteria and even if they could not or did not receive the allocated treatment (that is, intention to treat analysis).13 This could lead, however, to some dilution of treatment effect. As an alternative, decisions on exclusion could be made by a person blind to the group allocation.

A new CONSORT statement?

Elbourne and Campbell have recently argued for amending the CONSORT statement to allow for the special methodological circumstances of cluster trials.14 We would echo this call. We found it very difficult in several of the trials to ascertain whether a risk of bias was likely or not. We would wish the following additions to be made. Firstly, a clear statement as to whether the population was identified before or after the allocation decision had been made. Secondly, was the person who recruited the participants blind to group allocation? Thirdly, what was the size of the population within the clusters? For example, Steptoe et alw31 did not state the size of the general practice populations in their trial arms and Kinmonth et alw15 gave only means. For the first of these studies we could only assume that the recruitment was significantly different, and for the second study we had to make an estimate. This missing information also meant that for some studies we could not be completely sure if recruitment bias had taken place. For example, in Kendrick et al no suggestion of any recruitment bias was apparent; however, we could not be absolutely sure as the authors did not present the practice population sizes.w14

Conclusion

Cluster trials are vulnerable to the risk of bias. Careful planning and execution of such trials can avoid these biases.

What is already known on this topic

Reviews of individually randomised trials show that results can differ according to quality of methods

Foreknowledge of allocation and failure to use intention to treat analysis can lead to bias

What this study adds

Cluster randomised trials are susceptible to forms of selection bias

Careful planning and execution of such trials can avoid these biases

Supplementary Material

Additional references
bmj_327_7418_785__.html (8.1KB, html)

Inline graphicAdditional references appear on bmj.com

We thank Doug Altman, Diana Elbourne, Craig Ramsay, and Trevor Sheldon for their helpful comments on an earlier version of this manuscript.

Contributors: DJT suggested the idea of the review and wrote the first draft. SP and JW did the searches and extracted data from the included papers; they also helped to write and comment on the draft manuscript. DJT is the guarantor.

Funding: JW is trial coordinator of the SAPPHIRE trial funded by the Medical Research Council; SP and DJT are funded by the University of York.

Competing interests: None declared.

Ethical approval: Not needed.

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Supplementary Materials

Additional references
bmj_327_7418_785__.html (8.1KB, html)

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