Dealing with Missing Outcomes: Lessons from a Randomized Trial of a Prenatal Intervention to Prevent Early Childhood Caries

INTRODUCTION

Severe early childhood caries (S-ECC) is an important public health problem. The US National Institutes of Health defined S-ECC as the presence of one or more missing, filled or decayed tooth surfaces, whether cavitated or not, in a child below 3 years of age [1]. If left untreated, it severely affects a child’s general health, learning ability and quality of life and can have a life-long impact on oral health [2, 3]. Children who experience caries as infants or toddlers have a much greater probability of further caries in their primary and secondary dentitions [3]. In the 1990s, the prevalence of S-ECC among 2-3 years olds in South Australia was 16.7% [4]. As such children are entirely dependent on the care provided by others, mothers and other childcarers need oral health programs to support them in preventing S-ECC, while communities need to know what does and does not work in S-ECC prevention [5]. To address this issue we conducted a randomised controlled trial (RCT) of anticipatory guidance [6] targeting first time mothers [7].

While RCTs are generally considered as the “gold standard” for obtaining solid evidence on the effect of health care interventions, some have questioned their applicability to complex interventions [8] and to health promotion strategies in particular [9-11]. The latter tend to be complex and require a long follow-up that may exceed the attention span of participants, who do not have a problem in the first place. Attrition bias (literally referring to ‘wearing out’) as people loose interest or are lost for one reason or another, may defeat the whole object of random allocation. This becomes especially problematic when retention rates and loss to follow-up differ substantially between the randomised groups [12-14].

Another, more general problem arises from people’s perception that what is new must be better, thereby limiting their willingness to be randomly assigned to what is perceived as the lesser of the strategies compared. Limited participation will inevitably affect the generalisability of the findings to people outside the actual participants. Zelen [15] described an approach to address this. In it, potential participants are randomised to the proposed study arms before consent is sought and consent is then sought only from those assigned to the experimental group. This design has been criticized by ethicists on several grounds, mostly relating to people’s right to know and to the fallacy of assuming that people in the control group would also have consented, if they had been aware of the alternative option [16-18].

These objections are largely overcome in a Zelen design with double consent [19]. In the double consent design, potential participants are still randomised before consent. Thereafter, they are informed about their group allocation, given full information on the alternative interventions and offered the choice of either accepting or rejecting the random allocation and of moving to the opposite group, if they choose to do so. As the most unbiased assessment is between the groups as allocated [19], irrespective of whether they received the intervention or not, based on the “intention-to-treat principle” (ITT) [20], there are two major drawbacks to this approach. The first is a loss of statistical power, if many participants refuse the allocation, and the second is a loss of difference between the groups as randomised, when participants move from one group to the other.

In this paper, we address the consequences of the double consent form, but especially the attrition bias inherent in studies with prolonged follow-up, using sensitivity analysis and multiple imputation. To do so, we have used the data of our RCT “Cavity free children” in which the intervention targeted pregnant women expecting their first child, while the outcome was the oral health of their child at 20 months of age [7]. We address two questions that are relevant to similar studies conducted elsewhere. First, to what extent did the change of subjects from their allocated group influence the results? Second, how would the results change, if all enrolled subjects had participated until the end of the study without loss to follow-up?

MATERIALS AND METHODS

In 2002, we started an RCT to assess an oral health promotion intervention “Cavity free children”, targeting pregnant women expecting their first child. Recruitment occurred with ethical approval at all five public maternity units in Adelaide during routine antenatal visits [7]. Zelen’s design with double consent [19] was used to allocate women to the intervention and control groups. The intervention consisted of providing expectant mothers with printed information on oral health and early childhood caries, which was reinforced with additional information, sent by mail when the child was 6 months and 12 months old, focusing on the child’s needs at that age [6]. Outcome assessment was the presence of any carious lesion on the upper incisors, assessed by dental examination at 20 months of age. The trial resulted in a significant difference in the occurrence of S-ECC between the intervention and control infants (1.7% versus 9.6%; p <0.01) [7].

However, of 649 women allocated to the intervention and control groups, only 441 (68%) brought their child for a dental examination to assess outcome at 20 months of age [7]. Twenty-four had been legitimately excluded for pre-specified reasons, unrelated to their allocation and all due to legitimate absence of a mother-infant pair because of miscarriage, stillbirth, infant death, congenital malformations, child in the custody of Child and Youth Services, or mother in custody. Fifteen were in the intervention group and nine in the control group. A further 184 participants were lost to follow-up: 32 had moved to a distant locality, 66 were not traceable, and 86 failed to attend for dental examination for reasons, such as a new pregnancy, conditions of employment, problems with the child’s health or with transport, or declining further participation.

The comparability of the groups was evaluated at baseline and again for those attending dental examinations to assess whether loss to follow-up had distorted the comparability of groups. Baseline characteristics assessed were various demographic factors (e.g. age, ethnicity, marital status, occupation, level of education) and women’s perception of their general and dental health and oral hygiene [7]. The same characteristics and the child’s age at tooth eruption were compared for those completing follow-up. There were no statistically significant differences between the intervention and control groups at baseline and at follow-up. While this suggests that the difference in S-ECC between the intervention and control groups is entirely attributable to the effect of the intervention, many would consider a loss to follow-up of 32% unacceptably high for an RCT [14]. We, therefore, conducted sensitivity analyses and multiple imputation as an approach to consolidate its findings.

Sensitivity analyses basically assess how robust the results are to changes in how the study was done. In other words, to what extent do different assumptions about the people, who were randomised but not included in the outcome assessment, affect the outcome. To do so, we tested the assumptions that those lost to follow-up would all have had S-ECC, no S-ECC, or the same incidence of S-ECC as those retained in the intervention group, the control group or overall.

We also conducted multivariable imputation, a simulation-based approach originally designed for complex surveys, in which several important data may be missing for variable proportions of participants [21, 22]. It addresses the fact that analyses including only participants with complete data may not yield valid inferences about the entire study population [22]. It is based on the statistical principle that every subject in a random sample can be replaced by another subject, randomly drawn from the same sample as the original subject, without compromising the conclusions. Missing values for each subject are filled in (imputed) with values predicted from the rest of the subject’s known characteristics. A random component is added to the imputed value to account for the uncertainty due to the imputed value not being observed, but estimated. This is done by creating not one but several (multiple) imputed data sets, which are analysed separately and later combined to provide estimates and covariance matrices [23]. Multivariable techniques, employing a sequence of regression models, are used for imputing missing values [23].

In our analysis, the estimates were calculated using IVEware [23]. Outcome data were imputed for each participant lost to follow-up, conditional on the known variables for that participant, considering imputation on a variable by variable basis [23]. The basic strategy was to create imputations through sequences of multiple regressions, each time overwriting previously drawn values, building interdependence among imputed values [23, 24]. In total, a series of five imputations were used to create the data set. The independent variables used in the regression model to predict the incidence of S-ECC were maternal age, gestational age at enrolment and at the time of birth, the mother’s body mass index and her self-reported decayed, missing or filled teeth (DMFT). Information on each of these was available for more than 97.5% of enrolled women (missing data: range: 0-14, mean: 5.2; 0.8%).

SPSS 15.0 for Windows, IVEware and Revman 4.2 were used for data analysis.

RESULTS

DISCUSSION

Over the years RCTs have attracted friends and foes. This is likely to continue as not everything can be evaluated in this way [11]. RCTs are formally planned, prospective studies to compare the effects of an intervention with those obtained by alternative approaches. Randomisation, analogous to a fair coin toss, is the key word in this type of study as it is the only known means of ensuring that every participant, irrespective of her or his prior characteristics, has an equal chance of being assigned to one intervention or another [13]. Proper conduct of an RCT is governed by several further requirements, including a clearly formulated protocol with stated conditions for inclusion and exclusion of subjects and prior calculation of the number needed to minimize the likelihood that the results will reflect the play of chance [13, 20]. While these elements are all essential to the interpretation and meaning of the findings, the real benefit of an RCT arises from whether its findings are likely to be applicable to others, both patients and clinicians, outside the trial.

The two crucial issues of ‘are the results an unbiased assessment of the intervention studied’ and ‘are the results applicable to other people than those in the trial’ are commonly referred to in the literature respectively as internal and external validity [25]. The latter is often referred too as ‘generalisability’ [25]. In the field of health promotion, these two issues are more intertwined than in any other field. If the results are seriously biased, there is no need to know about them. If they are unbiased, but cannot be generalised to a substantial part of the population, their usefulness for enhancing population health is likely to be minimal.

In our RCT, we dealt with these issues using a strict protocol with inclusion and exclusion criteria, validated outcome measures and prior power analysis [7]. We recruited women at all public maternity units in Adelaide. By comparing the characteristics of our participants with those of all women giving birth in Adelaide [26], we could ascertain that these women were a ‘random sample’ of first time mothers attending for public antenatal care. The results may not be generalisable to the 35% of women seeking private maternity care, as these tend to be older, of higher socio-economic status and more likely to be Caucasian than women attending public hospitals [26]. Our concern, however, was to ensure that the results would be applicable to the majority of first time mothers and their infants in the public health system. Our exclusion criteria, based on the fact that not every pregnant woman will have a child nearly two years down the track, were also explicit and stringent. We could not control, however, for women opting out, choosing the alternative approach, lost to follow-up, or declining further participation for one reason or another. While our choice for a Zelen design was based on the need to enhance participation and to obtain a representative sample of the population, the current in-depth analysis was prompted by the substantial and unavoidable loss to follow-up.

Zelen’s original design [15], intended to address issues of validity, is rightly rejected by most ethicists [16, 17], as it results from an era in which people’s need for full information about alternative options and responsibility for their own health were not given the same attention as they are today. In its double consent form, Zelen’s design [19] largely overcomes such objections and substantially enhances the generalisability of the conclusions that can be derived from a single trial. The findings are more likely to be applicable to the population concerned than those of a trial in which few eligible persons have sufficient equipoise to accept chance allocation. This would seem to be particularly important with preventative strategies. Firstly, there is often some refusal to participate in preventative actions, which the Zelen design can account for. Secondly, contamination of the control group, whose members wittingly or unwittingly acquire some of the exposure that should have been restricted only to those in the intervention group, can be a major problem in such trials. This problem, also referred to as ‘contamination bias’ or ‘dilution bias’ [27], is largely avoided by offering participants a genuine choice of moving from one group to the other, if they desire to do so.

Cross-over from one group to another is a major concern, however, as groups that were comparable at the time of randomisation may no longer be comparable at the time of outcome assessment based on the actual treatment received. Analyses based on the ‘intention to treat’ (ITT) principle, the accepted standard for all RCTs [12, 20], cannot resolve this either when treatments have become effectively ‘homogenised’ [17, 19]. Adamson et al. [27], who identified 58 trials that had used a Zelen design between 1990 and 2005, found a mean cross-over rate of 13.8%. Even with the single consent design, a cross-over rate of only 10% requires a 20% increase in sample size to maintain power [19]. With a 10% cross-over in the double consent design, sample size needs to increase with 60% in order to achieve the power of a conventional RCT [19, 27]. Fortunately, cross-over was a minor issue in our trial, occurring in less than 1% and being uni-directional, only from the control group to the intervention group. As no cases of S-ECC were observed in the few participants who changed group allocation, adjustment of the outcome statistics affected only the denominators and not the numerators. This may not be so in other trials, however, and emphasises the need for sensitivity analyses when interpreting the results of such trials.

Loss to follow-up is a major issue in any RCT addressing outcomes that are not immediate. After all, its major strength is in the ITT principle, analysing results irrespective of what happens after randomisation [13, 20] or, as others have put it, ‘once randomised, always analysed’ [14]. In health promotion interventions, which target healthy people and distant outcomes, this is a genuine nightmare. Efforts to track all participants for as long as is needed, however intensive, are bound to fail as people pursue other objectives in life. Sensitivity analyses in general and multiple imputation techniques in particular, imperfect as they are, provide an answer to this. They have not been given much attention, however [12, 28]. For example, the extensive glossary of the Cochrane Collaboration on terms and definitions related to RCTs (http://www.cochrane.org/resources/glossary.htm) does not even refer to multiple imputation.

Frequent as loss to follow-up is, there is no consensus on how to deal with it in an RCT, other than that every effort should be made to reduce losses to the absolute minimum [12-14, 28]. This is more readily achieved when the interval between intervention and outcome is short, when targeting people dependent on ongoing care, and when there is ongoing contact between investigators and participants. None of this applied to our trial, as the protocol stipulated absence of any contact with the control group between informed consent and outcome assessment, about two years later, in order to mimic the real life situation.

Some consider that the results of RCTs with substantial loss to follow-up should be disregarded, but it is arbitrary what percentage should be considered as substantial [14]. When only a minority of people experience the outcome of interest, any loss to follow-up that exceeds the frequency of that outcome has the potential of creating a two-fold difference between what was observed and what could have been observed, if there had been no loss to follow-up. To avoid this issue, some have chosen intermediate outcomes, that are more readily available, as surrogates for what really matters [29, 30]. Not infrequently, intermediate outcomes have led to conclusions that could not be upheld by more substantive assessments later on [30, 31]. It has also led to different interpretations of what is meant by the ITT principle [12, 32]. Generally, little attention has been given to other means of testing the robustness of the findings.

Our most simple sensitivity analyses, assuming all possible outcomes for the missing mothers and infants randomised, as shown in Table 2, confirmed and added strength to the conclusion that anticipatory guidance can reduce the prevalence of S-ECC [7]. In its least favourable or “worst case” scenario, providing anticipatory guidance would still benefit 5% of the population, as one case of S-ECC would be prevented for every 20 pregnant women provided with such guidance. More often than not, however, the “worst case” scenario will provide results that are of little relevance to practice. Even if there are only a moderate number of missing outcomes, assuming all missing values to be good or bad is too strong an assumption to give a reasonable estimate of the effect of an intervention [33]. Moreover, such analyses can easily provide inconsistent or even contradictory results [12], leaving little option but to disregard the data.

While, for our trial, these simple analyses demonstrate the robustness of the findings to any assumptions made about missing outcomes, this is still of little value when people want to know not only whether something works, but also how much it works. Where resources are limited, numbers needed to treat that differ 2.5-fold are not particularly helpful. Multiple imputation, whilst not replacing the need for complete data, provides a far more reasonable approach to the problem. Apart from a more balanced appraisal of the validity of a trial, when there are differences between people randomised and those with outcome assessment, it also provides a more realistic estimate of what can be expected when the intervention is applied to a similar population elsewhere. Obviously, it will be helpful mainly if it incorporates variables that are shown to be predictive of attrition bias and loss to follow-up [33].

In conclusion, although evaluating preventative strategies and oral health promotion programmes in particular by means of RCTs is fraught with difficulties [9, 10], this is not a reason to abandon RCTs when seeking solutions to important health issues. Despite their difficulties, RCTs remain at the top of all known methods for evaluating whether something works or not. Neither do we advocate that sensitivity analyses and multiple imputation techniques provide an adequate alternative to complete follow-up of all subjects randomised. However, RCTs and multiple imputation are not goals by themselves. They are merely tools in the quest of what is and what is not effective in health care. Every tool has its limitations and, as every dentist knows, few complicated tasks are ever accomplished with only a single tool.

REFERENCES