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The World Health Organization (WHO) recommends treating all school children at regular intervals with deworming drugs in areas where helminth infection is common. As the intervention is often claimed to have important health, nutrition, and societal effects beyond the removal of worms, we critically evaluated the evidence on benefits.
To summarize the effects of giving deworming drugs to children to treat soil-transmitted helminths on weight, haemoglobin, and cognition; and the evidence of impact on physical well-being, school attendance, school performance, and mortality.
We searched the Cochrane Infectious Diseases Group Specialized Register (14 April 2015); Cochrane Central Register of Controlled Trials (CENTRAL), published in the Cochrane Library (2015, Issue 4); MEDLINE (2000 to 14 April 2015); EMBASE (2000 to 14 April 2015); LILACS (2000 to 14 April 2015); the metaRegister of Controlled Trials (mRCT); and reference lists, and registers of ongoing and completed trials up to 14 April 2015.
We included randomized controlled trials (RCTs) and quasi-RCTs comparing deworming drugs for soil-transmitted helminths with placebo or no treatment in children aged 16 years or less, reporting on weight, haemoglobin, and formal tests of intellectual development. We also sought data on school attendance, school performance, and mortality. We included trials that combined health education with deworming programmes.
At least two review authors independently assessed the trials, evaluated risk of bias, and extracted data. We analysed continuous data using the mean difference (MD) with 95% confidence intervals (CIs). Where data were missing, we contacted trial authors. We used outcomes at time of longest follow-up. The evidence quality was assessed using GRADE. This edition of the Cochrane Review adds the DEVTA trial from India, and draws on an independent analytical replication of a trial from Kenya.
We identified 45 trials, including nine cluster-RCTs, that met the inclusion criteria. One trial evaluating mortality included over one million children, and the remaining 44 trials included a total of 67,672 participants. Eight trials were in children known to be infected, and 37 trials were carried out in endemic areas, including areas of high (15 trials), moderate (12 trials), and low prevalence (10 trials).
Treating children known to be infected
Treating children known to be infected with a single dose of deworming drugs (selected by screening, or living in areas where all children are infected) may increase weight gain over the next one to six months (627 participants, five trials, low quality evidence). The effect size varied across trials from an additional 0.2 kg gain to 1.3 kg. There is currently insufficient evidence to know whether treatment has additional effects on haemoglobin (247 participants, two trials, very low quality evidence); school attendance (0 trials); cognitive functioning (103 participants, two trials, very low quality evidence), or physical well-being (280 participants, three trials, very low quality evidence).
Community deworming programmes
Treating all children living in endemic areas with a dose of deworming drugs probably has little or no effect on average weight gain (MD 0.04 kg less, 95% CI 0.11 kg less to 0.04 kg more; trials 2719 participants, seven trials, moderate quality evidence), even in settings with high prevalence of infection (290 participants, two trials). A single dose also probably has no effect on average haemoglobin (MD 0.06 g/dL, 95% CI -0.05 lower to 0.17 higher; 1005 participants, three trials, moderate quality evidence), or average cognition (1361 participants, two trials, low quality evidence).
Similiarly, regularly treating all children in endemic areas with deworming drugs, given every three to six months, may have little or no effect on average weight gain (MD 0.08 kg, 95% CI 0.11 kg less to 0.27 kg more; 38,392 participants, 10 trials, low quality evidence). The effects were variable across trials; one trial from a low prevalence setting carried out in 1995 found an increase in weight, but nine trials carried out since then found no effect, including five from moderate and high prevalence areas.
There is also reasonable evidence that regular treatment probably has no effect on average height (MD 0.02 cm higher, 95% CI 0.14 lower to 0.17 cm higher; 7057 participants, seven trials, moderate quality evidence); average haemoglobin (MD 0.02 g/dL lower; 95% CI 0.08 g/dL lower to 0.04 g/dL higher; 3595 participants, seven trials, low quality evidence); formal tests of cognition (32,486 participants, five trials, moderate quality evidence); exam performance (32,659 participants, two trials, moderate quality evidence); or mortality (1,005,135 participants, three trials, low quality evidence). There is very limited evidence assessing an effect on school attendance and the findings are inconsistent, and at risk of bias (mean attendance 2% higher, 95% CI 4% lower to 8% higher; 20,243 participants, two trials, very low quality evidence).
In a sensitivity analysis that only included trials with adequate allocation concealment, there was no evidence of any effect for the main outcomes.
Treating children known to have worm infection may have some nutritional benefits for the individual. However, in mass treatment of all children in endemic areas, there is now substantial evidence that this does not improve average nutritional status, haemoglobin, cognition, school performance, or survival.
In this Cochrane Review, Cochrane researchers examined the effects of deworming children in areas where intestinal worm infection is common. After searching for relevant trials up to April 2015, we included 44 trials with a total of 67,672 participants, and an additional trial of one million children.
What is deworming and why might it be important
Soil-transmitted worms, including roundworms, hookworms, and whipworms, are common in tropical and subtropical areas, and particularly affect children in low-income areas where there is inadequate sanitation. Heavy worm infection is associated with malnutrition, poor growth, and anaemia in children.
The World Health Organization currently recommends that school children in endemic areas are regularly treated with drugs which kill these worms. The recommended drugs are effective at eliminating or greatly reducing worm infections, but the question remains whether doing so will reduce anaemia and improve growth, and consequently improve school attendance, school performance, and economic development, as has been claimed.
What the research says
In trials that treat only children known to be infected, deworming drugs may increase weight gain (low quality evidence), but we do not know if there is an effect on cognitive functioning or physical well-being (very low quality evidence).
In trials treating all children living in an endemic area, deworming drugs have little or no effect on average weight gain (moderate quality evidence), haemoglobin (low quality evidence), or cognition (moderate quality evidence).
Regular deworming treatment every three to six months may also have little or no effect on average weight gain (low quality evidence). The effects were variable across trials: one trial from 1995 in a low prevalence setting found an increase in weight, but nine trials carried out since then from moderate or high prevalence settings showed no effect.
There is good evidence that regular treatment probably has no effect on average height (moderate quality evidence), haemoglobin (low quality evidence), formal tests of cognition (moderate quality evidence), or exam performance (moderate quality evidence). We do not know if there is an effect on school attendance (very low quality evidence).
Treating children known to have worm infection may improve weight gain but there is limited evidence of other benefits. For routine deworming of school children in endemic areas, there is quite substantial evidence that deworming programmes do not show benefit in terms of average nutritional status, haemoglobin, cognition, school performance, or death.
The three soil-transmitted helminth (STH) infections, ascariasis (roundworm), trichuriasis (whipworm), and hookworm, are the main intestinal helminth infections in humans (Bethony 2006; de Silva 2003b). Specialists estimate that each type of infection causes between 600 to 800 million cases worldwide each year (de Silva 2003b; Hotez 2009), with more than a quarter of the world's population infected with one or more of the soil-transmitted intestinal worms (Chan 1997). Estimates from 2003 suggest that global prevalence of STH infections is declining, with marked improvement in the Americas and Asia, but a static picture in sub-Saharan Africa (de Silva 2003b). STH infections particularly affect children living in poverty, where inadequate sanitation, overcrowding, low levels of education, and lack of access to health care make them particularly susceptible (Bethony 2006; de Silva 2003b). In 1993, the World Bank ranked STH infection as a greater cause of ill health in children aged five to 15 years than any other infection (World Bank 1993), but there has been considerable variation in the quoted estimates of global burden (de Silva 2003b), which are currently being updated.
Policy makers are concerned that the long-term effects of worm infestation impair childhood nutritional status, school performance, and long-term cognitive development (Bethony 2006). It is thought that iron status may mediate these effects, since hookworm and whipworm disease are associated with iron-deficiency anaemia (Crompton 2000; de Silva 2003a), and a fall in blood haemoglobin levels is associated with increasing intensity of infection (Crompton 2003). Furthermore, hookworm-induced iron-deficiency anaemia has been associated with decreased physical activity and worker productivity (Crompton 2003).
Worms are associated with malnutrition, impaired growth, and poor school performance. Roundworms obtain their nutrition from gastrointestinal contents. The association with malnutrition is possibly mediated through impaired fat digestion, reduced vitamin absorption (particularly vitamin A), and temporary lactose intolerance (WHO 2002). Whipworm infection has been associated with malnutrition, although the precise mechanism for this is unclear (Cappello 2004). Some suggest that the effects on nutrition are through appetite suppression, increased nutrient loss, and decreased nutrient absorption and utilization (de Silva 2003a; Stephenson 2000).
Roundworm, hookworm, and whipworm disease have all been associated with impaired growth in school children (de Silva 2003a). Observational trials have reported an association between worm infection and lower scores on tests of school performance (Kvalsvig 2003; Sakti 1999). In a multiple-regression model based on cross-sectional data, Sakti 1999 found that hookworm infection was associated with worse scores in six out of 14 cognitive tests in Indonesian school children. Severe whipworm (Trichuris dysentery syndrome) was associated with low intelligence quotient (IQ), school achievement, and cognitive function after a four-year follow-up of a specific group of Jamaican children with severe infection (Callender 1998).
While these associations would suggest potential benefits of deworming, the associations could equally be caused by the confounding factor of poverty. Even with adjustment for known confounding factors, residual confounding could be a problem. Furthermore, the causal link between chronic infection and impaired childhood development is extrapolated from the recorded improvement in these features after deworming (Bethony 2006). Hence, reliable randomized controlled trials (RCTs) are required to assess whether policies are effective. These can examine the effectiveness of treating worm infection in an individual, as evidence of efficacy, and treatment in schools or communities, as evidence of the effectiveness of programmes. The latter trials are ideally cluster-RCTs, and thus able to detect any externalities (benefits to other children) accruing as a result of reduced transmission.
Public health interventions to reduce worm infection include improved sanitation and hygiene and drug therapy for populations or targeted groups in the community, often coupled with health education. The work of the Rockefeller Sanitary Commission in the early 1900s in the USA with a grant of USD 11 million in the Southern States was combined with efforts to improve schooling. This led to the belief that sanitary reform was needed alongside chemotherapeutic approaches to eradicate hookworm to rid children of lethargy and improve their health (Brown 1979; Horton 2003). In Japan, worms virtually disappeared over a 20-year period after the Second World War; this has been credited to an integrated programme of sanitary reform combined with screening and treatment of positive cases (Horton 2003; Savioli 2002). A similar experience occurred in Korea (Savioli 2002). The current global decline in worm prevalence has been credited to economic development and deworming programmes (de Silva 2003b). The impact of the chemotherapeutic element is difficult to assess. In countries where an improvement in sanitation and hygiene has occurred as a component of economic growth, a parallel decline in the prevalence of soil-transmitted helminths has occurred: for example, in Italy between 1965 and 1980, the trichuriasis prevalence dropped from 65% to less than 5% without control activity (Savioli 2002).
The World Health Organization (WHO) recommends periodic treatment with anthelminthic (deworming) medicines, without previous individual diagnosis to almost all children living in endemic areas. The WHO does not recommend individual screening, since the cost of screening is four to 10 times that of the treatment itself. Treatment is recommended once a year when the prevalence of STH infections in the community is over 20%, and twice a year when the prevalence of STH infections in the community exceeds 50% (WHO 2015). The strategy is to target drug treatment to at-risk groups: pre-school-age children (between one and five years); school-age children (between six and 15 years); and women of childbearing age. The strategy requires a population survey for prevalence and intensity of infection to determine the population worm burden. This determines the recommended frequency of treatment, updated in a WHO field manual in 2006 (WHO 2006b).
The policy promotes the use of schools, maternal and child health clinics, and vaccination campaigns to reach at-risk groups. The WHO advocates school-based programmes in particular, as it is easy to deliver medicines through teaching staff, with estimated costs varying from USD 0.05 to 0.65 per child per year for annual dosing (Savioli 2002; WHO 2002). In areas with a high prevalence, the current policy recommends treatment three times per year (WHO 2006b), based on modelling and reinfection prevalence trials. Following drug treatment, worm populations tend to return rapidly to pretreatment levels; with roundworm and whipworm this happens in less than a year (Anderson 1991). Anderson 1991 suggests that, in order to control morbidity in areas of endemic infection, targeted treatment should be repeated every three to four months for roundworm and whipworm, with longer intervals acceptable for longer-lived species such as hookworm. The WHO recommends monitoring with a range of impact indicators, including prevalence and intensity, incidence, morbidity, and mortality (WHO 2010). The control programme is intended to reduce the worm burden in the 10% to 15% of children who are most heavily infected in a particular population and to keep it low through repeated treatments.
It has been argued that treating individuals in communities reduces transmission in the community as a whole (Anderson 1991), and that this can lead to health and schooling benefits for the whole population, including those who have not received deworming treatment (Bundy 2009). These 'spill over' effects, or externalities, are not captured in individually RCTs, since any benefit in the control group reduces the overall treatment effect. A cluster design is therefore required to identify these additional putative effects.
This Cochrane Review does not cover deworming and pregnancy (reviewed in Haider 2009).
The rationale for the effects of deworming programmes on population development depend on the assumption that they improve nutrition, haemoglobin, and cognition. As a result of these benefits, children are thought to have increased physical well-being, with improved intellect, and are better able to attend school. As a result, performance at school is enhanced, over the long-term this benefits society as a whole, and reduces poverty (WHO 2005, WHO 2011). This is expressed in our conceptual framework (see Figure Figure1).1). The figure provides the basis for this review: the primary outcomes sought are the main effects (increased haemoglobin, nutrition, and improved cognition); measurable aspects of the mediating pathways (school attendance and physical well-being); and measurable aspects of impact (mortality and school performance).
In this review we include community trials that measure effects after a single dose of deworming drugs ('efficacy' measures in the individual), as well as trials of multiple doses with longer follow-up periods. Multiple dose, cluster randomized trials with long follow-up periods are the best measure of policy effectiveness since they are likely to detect externalities within schools and potential long term benefits.
The intended impacts of deworming programmes are clearly worthwhile goals and are heavily promoted by advocates in the field such as the WHO (Montresor 2002; WHO 2002; WHO 2006b; WHO 2011; WHO 2015), the World Bank (World Bank 2011), and the Bill & Melinda Gates Foundation (Hawkes 2013). Furthermore, deworming with albendazole was recently endorsed in the 2012 Copenhagen consensus statement, as the fourth highest ranking solution to address “big issues facing the planet” in terms of cost and benefit (Copenhagen Consensus Center 2012). The widely-cited cost-effectiveness estimates from the Disease Control Priorities in Developing Countries (DCP2) report (Jamison 2006) state that deworming for STH infections was one of the most cost-effective interventions for global health. However, the reliability of these estimates has been questioned by the organization GiveWell, which suggests they have been overstated by a factor of about 100 (GiveWell 2011).
Advocates point to the favourable cost-effectiveness estimates for deworming programmes, with a focus on the putative effect on schooling outcomes and productivity (Deworm the World 2012). The evidentiary basis for this draws on a range of trial designs, including historical econometric trials such as Bleakely 2004, which analysed the Rockefeller Sanitary Commission's campaign to eradicate hookworm in the Southern states of the USA. This showed an association between areas with higher levels of hookworm infection prior to the campaign and greater increases in school attendance and literacy after the intervention, and an association with income gains in the longer term. Another influential trial is Miguel 2004 (Cluster), which is included in this Cochrane Review.
Current policies have become even more challenging to assess, as global specialists conflate the evidence on different helminths. The WHO, for example, describes the benefits of treating all helminths, including schistosomiasis, filariasis, and STH infections. The WHO states that deworming treatment against schistosomes and STH infections helps (1) eradicate extreme poverty and hunger; (2) achieve universal primary education; (3) promote gender equality and empower women; (4) reduce child mortality and improve maternal health; and (5) combat HIV/AIDS, malaria, and other diseases (WHO 2005; WHO 2011). The evidence for the benefit of treating populations with schistosomiasis is fairly clear (Danso-Appiah 2008), as the infection has a very substantive effect on health. However, this does not mean that a different drug treating a different helminth species is equally effective.
Despite the lack of rigour in considering the evidence for separate components of these policies, many countries are moving forward with large scale purchases of drugs. The current neglected tropical disease (NTD) policy focus has been on addressing 'polyparasitism' by treating the parasites that cause ascariasis, trichuriasis, hookworm, lymphatic filariasis, onchocerciasis, schistosomiasis, and trachoma with ivermectin, albendazole, azithromycin, and praziquantel (Hotez 2009). These four drugs are donated by pharmaceutical companies, and the 'overlapping specificity' would mean multiple pathogens would be targeted (Hotez 2006b). Thus, mass drug administration for NTDs is promoted as “one of the lowest cost and cost-efficient mechanisms for both improving maternal child health and lifting the bottom billion out of poverty” (Hotez 2011b). Significant resources are being invested in this agenda, with the UK Department for International Development committing GBP 50 million in 2008, and the US government committing USD 65 million in 2010 as part of the US Global Health Initiative (Hotez 2011a).
Given the amount of investment of public money in these programmes, it is important to be clear whether mass or targeted drug administration is able to contribute to health and development in such a substantive way. Indeed, international donors and developed country governments and tax payers are contributing to the efforts to tackle STH infections in the belief that they will improve the health of children in the way that the WHO claims (WHO 2005). For example, Deworm the World has worked with the Indian Government to treat 140 million children across India in 2015 on the basis of the Copenhagen Consensus Statement (Evidence Action 2015; Mudur 2015).
Thus, this systematic review of reliable evidence from RCTs will help clarify whether existing evidence supports the conclusion that there is an impact of these drugs in populations with STH infections (ascariasis, trichuriasis, and hookworm) and will evaluate the strength of the evidence.
Early on the debate was around medical outcomes, such as anaemia. More recently there has been a shift in focus from short-term impacts of deworming to potential longer-term developmental impacts (Figure (Figure1).1). Indeed, Givewell suggests that the most compelling case for deworming as a cost-effective intervention comes from “the possibility that deworming children has a subtle, lasting impact on their [children's] development, and thus on their ability to be productive and successful throughout life”, but further comments that “empirical evidence on this matter is very limited” (Givewell 2014). There have been some recent observational analyses with long-term follow-up of dewormed children which were considered during this update. None of these trials met the inclusion criteria of this review (Baird 2011; Croke 2014; Ozier 2011; described in the Characteristics of excluded studies section).
Important new trials have been published. The DEVTA trial of over one million children was completed in 2005 and published in 2013 (Awasthi 2013 (Cluster). A second important trial with a manuscript date of 2006 of over 2500 children remains unpublished, but we have included it in this review (Hall 2006 (Cluster).
The development organization 3ie recently commissioned the replication of the influential econometric trial from Kenya (Miguel 2004 (Cluster). We highlighted concerns about the quality of the evidence for school attendance on the basis of this trial in the previous version of this Cochrane Review (Taylor-Robinson 2012). The replication was published recently (Aiken 2014; Aiken 2015; Davey 2015). The authors checked the data and corrected any errors, and then carried out an analysis using exactly the methods in the original publication. The replication highlights important coding errors and this resulted in a number of changes to the results: the previously reported effect on anaemia disappeared; the effect on school attendance was similar to the original analysis, although the effect was seen in both children that received the drug and those that did not; and the indirect effects (externalities) of the intervention on adjacent schools disappeared (Aiken 2015). The statistical replication suggested some impact of the complex intervention (deworming and health promotion) on school attendance, but this varied depending on the analysis strategy, and there was a high risk of bias. The replication showed no effect on exam performance (Davey 2015).
In the light of the publication of the DEVTA trial of over one million children, the replication trials of the Kenya trial, the new longer term follow-up trials, and four new RCTs, we updated Taylor-Robinson 2012. We have added new trials and data, restructured the analysis, and updated the GRADE assessment of the quality of the evidence.
To summarize the effects of giving deworming drugs to children to treat soil-transmitted intestinal worms on weight, haemoglobin, and cognition; and the evidence of impact on physical well-being, school attendance, school performance, and mortality.
RCTs and quasi-RCTs. We included cluster-RCTs, provided more than two clusters were allocated to each treatment arm.
Infected children identified by screening in community trials.
All children must have lived in endemic areas.
We defined children as aged under 16 years. We excluded trials of sick children or children being treated for malnutrition.
Deworming drugs for soil-transmitted helminths, administered at any location (including health facilities, schools, and communities). We included trials examining effects after a single dose and after multiple doses.
The deworming drugs we included are those in the WHO Model List of Essential Medicines for deworming drugs of soil-transmitted helminths (WHO 2006a). This includes albendazole, levamisole, mebendazole, pyrantel, and ivermectin. Other drugs used are nitazoxanide, piperazine, tetrachlorethylene, and thiabendazole.
We did not exclude trials that also provided some health promotion activities supporting the deworming programmes. Studies that provided additional interventions (eg growth monitoring, micronutrient supplementation, malaria chemoprevention, or other drugs) were included when the additional intervention was given to both the control and intervention arm.
Placebo or no treatment.
The review authors and the Cochrane Infectious Diseases Group (CIDG) Information Specialist, Vittoria Lutje, attempted to identify all relevant trials regardless of language or publication status (published, unpublished, in press, and in progress). The date of the last search was 14 April 2015.
The Information Specialist searched the following databases using the search terms and strategy described in Table 1: CIDG Specialized Register (14 April 2015); Cochrane Central Register of Controlled Trials (CENTRAL), published in the Cochrane Library (2015, Issue 4); MEDLINE (2000 to 14 April 2015); EMBASE (2000 to 14 April 2015); and LILACS (2000 to 14 April 2015); and reference lists, and registers of ongoing and completed trials. We also searched the metaRegister of Controlled Trials (mRCT) using 'helminth* OR anthelminth*' (14 April 2015).
David Taylor-Robinson (DTR) checked the search results for potentially relevant trials and retrieved full articles as required. DTR and Paul Garner (PG) independently assessed the trial eligibility using an eligibility form based on the inclusion criteria; where there was uncertainty, all five review authors participated in the decision about inclusion. We checked that trials with multiple publications were managed as one trial. We recorded reasons for the exclusion of trials and we contacted authors of unpublished trials for information on when they intended to publish their results.
Nicola Maayan (NM), DTR, Sarah Donegan (SD), and Karla Soares-Weiser (KSW) independently extracted data using data extraction forms. PG extracted and cross-checked the data from a selection of papers. We resolved any differences in opinion by discussion. Where methods, data, or analyses were unclear or missing, we contacted trial authors for further details.
We extracted data on type of additional interventions (eg accompanying health promotion programme including programmes about hygiene and behaviour, water and sanitation; drug; or vitamin) and how this was delivered (mass media, community, or one-to-one); and whether these interventions were in both intervention and control groups, or only in the intervention group.
For each treatment group of each trial, we extracted the number of patients randomized. For each outcome of interest, we extracted the number of participants analysed in each treatment group of each trial.
For dichotomous outcomes, we planned to extract the number of patients with the event. For continuous outcomes, we aimed to extract means and standard deviations (SDs). Where these data were not reported, we extracted medians and ranges or any other summary statistics. Where change from baseline results were presented alongside results purely based on the end value, we only extracted the change from baseline results.
For each cluster-RCT, we extracted the cluster unit, the number of clusters in the trial, the average size of clusters, and the unit of randomization (such as household or institution). Where possible, we extracted the statistical methods used to analyse the trial along with details describing whether these methods adjusted for clustering or other covariates.
Where a cluster-RCT adjusted for clustering in their analysis, we extracted the cluster adjusted results. When the trial did not account for clustering in their analysis, we extracted the same data as for trials that randomize individuals.
For the analysis of Awasthi 1995 (Cluster) we took weight from the publication by Awasthi in 2008; height data from INCLEN 1995 monograph (references contained in the main reference). Means of cluster means were used in analysis; details of correspondence from previous review suggest that trial was ongoing; data for 3-year follow-up are provided from R. Dickson's correspondence with the author for the Dickson 2000a Cochrane Review, but the loss to follow up is very high: only 24% analysed.
One included trial, Miguel 2004 (Cluster), has been the subject of an independent re-analysis, with a full report published on the 3ie website (Aiken 2014), which also includes a response from the authors (3ie 2014); and two subsequent academic papers (Aiken 2015; Davey 2015). In this edition of the Cochrane Review we used new information on conduct of the trial, on the thorough evaluation for potential biases, and also corrected data from the replication, including the measure of variance for school attendance (Aiken 2014).
DTR, PG, NM, SD, and KSW independently assessed the risk of bias (Higgins 2011b). We resolved any differences through discussion. On occasion, we corresponded with trial investigators when methods were unclear.
For RCTs that randomized individuals we addressed six components: sequence generation; allocation concealment; blinding; incomplete outcome data; selective outcome reporting; and other biases. For cluster-RCTs, we addressed additional components: recruitment bias; baseline imbalance; loss of clusters; incorrect analysis; compatibility with RCTs randomized by individual. For each component, we placed judgments of low, high, or unclear/unknown risk of bias as described in Appendix 1. We displayed the results in 'Risk of bias' tables, a 'Risk of bias' summary, and a 'Risk of bias' graph.
We summarized continuous data (means and SDs) using the mean differences (MDs). We planned to use the risk ratio to compare the treatment and control groups for dichotomous outcomes. All treatment effects were presented with 95% confidence intervals (CIs).
For a particular cluster-RCT when the analyses had not been adjusted for clustering, we attempted to adjust the results for clustering by estimating the design effect calculated as 1+(m-1)*ICC where m is the average cluster size and ICC is the intra-cluster correlation coefficient. To make the adjustment, we estimated a treatment effect that did not adjust for clustering and then multiplied the standard errors of the estimate by the square root of the design effect. When the true ICC was unknown, we estimated it from other included cluster-RCTs.
We aimed to conduct a complete-case analysis in this Cochrane Review, such that all patients with a recorded outcome were included in the analysis.
We inspected the forest plots to detect overlapping CIs, applied the Chi² test with a P value of 0.10 used to indicate statistical significance, and also implemented the I² statistic with values of 30 to 60%, 59 to 90%, and 75 to 100% used to denote moderate, substantial, and considerable levels of heterogeneity, respectively.
We decided not to construct funnel plots to look for evidence of publication bias because there were a limited number of trials in each analysis.
DTR, NM, and SD analysed data with Review Manager 5.3. We structured the analysis into four sections
For trials involving children living in an endemic area, trials were also grouped by prevalence and intensity (high/moderate/low). High prevalence or high intensity areas are referred to as 'high prevalence'; moderate prevalence and low intensity are referred to as 'moderate prevalence'; and low prevalence with low intensity are referred to as 'low prevalence'. We used the WHO technical guidelines classification (WHO 2002; Table 2), rather than the simplified prevalence based field guide categories that are now used to determine treatment frequency (WHO 2006b; Table 2). In trials where information on intensity was not provided, we estimated the community category on the basis of quoted prevalence; it is possible that the community category has been underestimated in these trials.
When a trial reported data at multiple time points we included data collected at the longest follow-up time in the analysis of 'after multiple doses', because long term outcomes of multiple doses of deworming are of most relevance to policymakers, and short-term effects are captured in the single dose results. This decision was supported by findings from an exploratory meta-regression analysis that was applied to find out whether the intervention effect was modified by the length of follow-up (see below).
We combined cluster-RCTs that adjusted for clustering and RCTs that randomized individuals using meta-analysis. We used a fixed-effect meta-analysis when the assessments of heterogeneity did not reveal heterogeneity. In the presence of heterogeneity, we used random-effects meta-analysis.
For continuous data, we combined change from baseline results with end value results providing they were from distinct trials (Cochrane Collaboration 2011; Higgins 2011a). Labels on the meta-analyses indicate when end values were used.
We presented data that could not be meta-analysed in additional tables and reported on these in each section, under the heading 'other data'.
In the presence of statistically significant heterogeneity, we planned to explore the following potential sources using subgroup analyses: age group (< five years vs ≥ five years); manufacturer; treatment setting (community, school, health post, hospital). We did not carry out these analyses because there were too few trials in the analyses.
To find out whether the intervention effect was modified by the length of follow-up, SD and DTR performed a random-effects meta-regression for the outcome weight (in all children in an endemic area after multiple doses), with length of follow-up in months as a covariate using the 'metafor' package in R. The covariate was centred at its mean.
We also sorted the forest plot for weight (in all children in an endemic area after multiple doses) by year that the trial was carried out to visually inspect whether the intervention effect changed over time.
We carried out sensitivity analyses including only those trials with a low risk of bias regarding allocation concealment.
We interpreted results using 'Summary of findings' tables, which provide key information about the quality of evidence for the included trials in the comparison, the magnitude of effect of the interventions examined, and the sum of available data on the main outcomes. Using GRADE profiler (GRADEpro 2014), we imported data from Review Manager 5.3; the GRADE display was based on a recent trial of what users prefer (Carrasco-Labra 2015). We presented the primary outcomes for the review in the 'Summary of findings' tables, and added height, school attendance, and death for multiple dose trials.
We identified 45 trials reported in 64 articles that met the inclusion criteria (see Figure Figure2,2, Characteristics of included studies and Appendix 2). For a trial completed in 2006 but never published, the trial authors provided a manuscript with data we were able to use (Hall 2006 (Cluster)). For Alderman 2006 (Cluster), the trial authors did not adjust the CIs to take into account clustering for the primary outcome. For this Cochrane Review, we used the corrected values supplied by the trial author.
We excluded 40 trials (see Characteristics of excluded studies), and one trial is ongoing (see Characteristics of ongoing studies).
The included trials were undertaken in 23 different countries: Bangladesh (four trials); China (two trials); Ethiopia (two trials); Haiti (two trials); India (five trials); Indonesia (four trials); Jamaica (two trials); Kenya (five trials); Malaysia (two trials); Phillipines (two trials); South Africa (two trials); Uganda (two trials); Vietnam (three trials); Zanzibar (two trials); Benin, Botswana, Cameroon, Guatemala, Nigeria, Sierra Leone, Tanzania, Zaire (one trial in each); China, Philippines and Kenya; China and Myanmar (multi-centre trials).
Children were recruited from school populations in 26 trials, communities in 12 trials, and in health facilities or by health workers in seven trials. One of these trials recruited children on discharge from hospital (Donnen 1998) and another recruited children whose mothers had participated in the pregnancy phase of the trial (Ndibazza 2012). Olds 1999 and Wiria 2013 (Cluster) also included adolescents 17 to 19 years old, but most participants were under 16 years old.
Thirty-seven trials were based on mass targeted treatment of an unscreened population. Eight trials studied children who were screened and selected on the basis of their having high worm loads and the purpose of three of these trials was to measure cognitive outcomes. One trial of unscreened children, Stephenson 1993, also studied an infected subgroup of the larger unscreened trial population for cognitive and haemoglobin outcomes. Fifteen trials were conducted in populations where worms were of high prevalence or intensity (community category 1), 12 in populations with moderate prevalence and low intensity (category 2), and 10 in populations with low prevalence and low intensity (category 3).
Twenty-eight trials had albendazole only in one treatment arm; in addition, some of these trials had arms with combinations with albendazole and: praziquantel (Olds 1999); ivermectin (Beach 1999); and diethylcarbamazine (Fox 2005); the additional drugs were also given to children in the control arms.
One trial included Giardia treatment, secnidazole, in both intervention and control arms (Goto 2009).
One trial was a deworming programme that included deworming drugs for STHs, praziquantel to treat schistosomiasis in schools with = 30% prevalence, and health promotion interventions (Miguel 2004 (Cluster)).
Seven trials used mebendazole; and two trials used mebendazole in combination with pyrantel. Other deworming drugs used included pyrantel pamoate, piperazine, piperazine citrate, tetrachloroethylene, and levamisole.
Nine trials reported on a range of child health activities (Table 3). In eight trials, the accompanying activities appeared to be applied to both intervention and control arms.
One trial had a comprehensive health promotion programme accompanying the deworming, including regular public health lectures, teacher training, and health education targeted to avoid intestinal helminths and exposure to schistosomiasis (Miguel 2004 (Cluster).
Most trials used placebo or no treatment as a control. Others used vitamin A, vitamin C, or calcium powder.
There were 13 trials where both the treatment and control group received nutritional supplementation: multi-nutrient, vitamin B, iron, vitamin A, or child health packages, including growth monitoring and health education (Table 3).
Nine trials were cluster randomized, including one trial with quasi-random allocation of the 75 clusters (Miguel 2004 (Cluster)). The rest used the individual as the unit of randomization.
Six of the nine cluster-RCTs used an appropriate method to take clustering into account. Awasthi 2001 (Cluster) and Awasthi 1995 (Cluster) used urban slums as the unit of randomization (50 and 124 respectively), and Awasthi 2013 (Cluster) used 72 rural administrative blocks. These three trials were analysed at the cluster level (mean of cluster mean values and associated SDs). Stoltzfus 1997 (Cluster) randomized 12 schools and adjusted for within-school correlations using generalized estimating equations. Miguel 2004 (Cluster) adjusted for clustering in their regression estimates, and presented robust standard errors. Wiria 2013 (Cluster) randomized 954 households and used generalised linear mixed-effects models that captured the data correlations induced by clustering within households.
The three remaining cluster-RCTs did not adjust for clustering:
Four trials had a factorial design. Awasthi 2013 (Cluster) randomized clusters to usual care, six-monthly vitamin A, six-monthly 400 mg albendazole, and both vitamin A and albendazole. Kruger 1996 randomized individual participants to albendazole or placebo, and, also, three of the five schools in the trial received soup fortified with vitamins and iron, and two received unfortified soup. Le Huong 2007 randomized individual participants to iron-fortified noodles and mebendazole, noodles without iron fortification and mebendazole, iron-fortified noodles and placebo, noodles without iron fortification and placebo, and iron supplementation and mebendazole. Stoltzfus 2001 randomized households to iron, with random allocation of mebendazole by child, stratified by iron allocation and age grouped households; disaggregated data for each treatment allocation group was not provided for each outcome.
Follow-up periods for the trials that used a single dose ranged from one to 21 months, while the follow-up periods for trials that used multiple doses ranged from post-intervention to five years.
Miguel 2004 (Cluster) is an cluster quasi-randomized stepped-wedge trial of a combined education and drug-treatment intervention. The trial included 75 schools with a total of 30,000 pupils enrolled. In addition to helminth treatment, the phased complex intervention included public health lectures, teacher education, and child health education including handwashing, as noted above. In addition, a number of schools in the trial were also mass treated for schistosomiasis. In our previous update of the review we identified two potential quasi-randomized comparisons that provide unbiased estimates, one in 1998 and one in 1999, in the stepped-wedge design. Since our last review update this trial has been the subject of an independent reanalysis, with a full report published on the 3ie website (Aiken 2014), and two subsequent academic papers (Aiken 2015; Davey 2015). In this review update we used data from these sources to assess the methodological quality of the trial. The results are primarily draw from the replication report, Aiken 2014, which provides estimates corrected for coding errors in the original paper.
Forty-six trials measured nutritional indicators. Some trials reported absolute values, or changes in absolute values of weight and height (or other anthropometric measures). Many trials presented anthropometric data in terms of z-scores or percentiles of weight-for-age, weight-for-height, and height-for-age, and compared the trial results to an external reference. Sometimes these values were dichotomised and presented as the prevalence of underweight, stunting or wasting (defined as -2 SD z-scores). The external standard was usually quoted as the National Centre for Health Statistics (NCHS) standard, but a variety of references were quoted (including anthropometric computer packages or country standards). These data have not been used in the meta-analyses as the results were already incorporated in the values for weight and height. Furthermore, in some trials, outcome data were not reported or were incomplete and could not be used in meta-analysis. A number of reports did not provide summary outcome data for each trial arm, and the results were reported in terms of regression modelling outcomes or subgroup analyses. We have described the results of these trials in Table 4.
Nineteen trials measured haemoglobin. Of these, two trials did not report the measured haemoglobin results (Olds 1999; Solon 2003), two trials only measured this outcome in a subset of the participants (Awasthi 2013 (Cluster); Miguel 2004 (Cluster)) and one trial did not report results by randomized comparisons (Stephenson 1993).
Eleven trials measured intellectual development using formal tests (Table 5).
Four trials measured school attendance (Table 7).
In the 38 individually RCTs, the risk of bias was low in 13 trials (see Figure Figure33 and Figure Figure4),4), high in five, and unclear in the other trials. For the nine cluster-RCTs, the risk of bias was low in two trials (Alderman 2006 (Cluster); Wiria 2013 (Cluster)), high in two trials (Awasthi 1995 (Cluster); Miguel 2004 (Cluster)) and unclear in five trials (Awasthi 2001 (Cluster), Awasthi 2013 (Cluster), Hall 2006 (Cluster), Rousham 1994 (Cluster), Stoltzfus 1997 (Cluster).
For the 38 individually randomized trials, seven trials were at low risk of bias regarding allocation concealment (Fox 2005; Garg 2002; Le Huong 2007; Nga 2009; Olds 1999; Stoltzfus 2001; Sur 2005), high in two trials (Awasthi 2000; Kirwan 2010), and unclear in the other trials.
Fifteen trials were double blinded and judged to be at low risk of bias. Five trials were at high risk of bias as they did not use blinding. Details of blinding were unclear in the remaining 26 trials.
Twenty nine trials appeared to have low risk of bias in relation to outcome data. Overall, the percentage of randomized participants that were evaluable ranged from 4% to 100%, with 19 trials including 90% or more of the randomized participants (low risk cut-off). The percentage was particularly low in three of the trials measuring school performance and cognitive outcomes: 71% in Ndibazza 2012; 73% in Nokes 1992; and 52% in Stoltzfus 2001; and in one trial measuring haemoglobin: 26% in Kirwan 2010. In Miguel 2004 (Cluster) for haemoglobin a sample of around 4% (778/20,000) of the quasi-randomized comparison of group 1 vs group 2 in 1998 was analysed. Weight and height data were collected on all individuals in standards 3.8, 48% of the total comparison (9102/20000). For exam performance and cognitive tests, 34% of eligible children were included in the treatment school (group 1) and 32% in the control school (group 2 and 3). Wiria 2013 (Cluster) did not report the number of children that were randomized, so it was not possible to calculate the percentage evaluable in this trial.
Fourteen trials had evidence of selective reporting and were judged to be at high risk of bias (Goto 2009; Greenberg 1981; Kirwan 2010; Koroma 1996; Nga 2009; Nokes 1992; Olds 1999; Simeon 1995; Solon 2003; Stoltzfus 1997 (Cluster); Stoltzfus 2001; Sur 2005; Willett 1979). The remaining trials did not show evidence of selective reporting.
In general, quality of the design of the nine cluster-RCTs was good: they were judged as low risk for recruitment bias (six trials), baseline imbalance (nine trials), loss of clusters (nine trials), compatibility with RCTs that randomized individuals (one trial).These data are included in the “table of characteristics”).
There were problems with incorrect analysis noted above: Alderman 2006 (Cluster) did not adjust for clustering in the published trial, but gave us the adjusted data (see trial design above), and we used this to adjust the analysis in Hall 2006 (Cluster).
One trial was potentially confounded by co-interventions noted under “accompanying health promotion activities” under interventions (above).
See: Summary of findings for the main comparison Multiple doses of deworming drugs given to all children, longest follow-up; Summary of findings 2 Single dose of deworming drugs given to infected children; Summary of findings 3 Single dose of deworming drugs given to all children
The effects were grouped into trials in children known to be infected, and trials of all children in endemic areas. In the trials treating whole populations, we stratified the results by community worm prevalence. We have detailed the prevalence strata in Table 2 (high prevalence or high intensity areas (referred to as 'high prevalence'); moderate prevalence and low intensity referred to as ('moderate prevalence'); and low prevalence with low intensity referred to as 'low prevalence'). Within each section, we present the results of the meta-analysis, and then report any other data from trials that we could not include in the meta-analysis.
These trials screened for infection, and then included only children with proven infection; or were conducted in settings where all the children were known to be infected. None of these trials provided data for the outcomes school attendance (number of children dropping out), school performance, mortality, or adverse events. No trials appeared to have potentially confounding health promotion activities (Table 3). For single dose, see Summary of findings 2.
Trials measured weight (n = 5), height (n = 5), MUAC (n = 4), triceps (n = 3), subscapular skinfold (n = 2) and BMI (n = 1). Large effects were seen in two trials for weight, MUAC, and skinfold, with an average weight gain of over one kg in both trials (Stephenson 1989; Stephenson 1993). These trials were in a high prevalence area of Kenya. The gain in weight in the deworming group ranged from 0.2 kg to 1.3 kg more (627 participants, five trials, Analysis 1.1), height gain (0.25 cm, 95% CI 0.01 to 0.49; 647 participants, five trials, Analysis 1.2), and gains in MUAC, triceps and subscapular skinfold values (Analysis 1.3; Analysis 1.4; Analysis 1.5). No difference in body mass index was detected after a single dose (Analysis 1.6).
There was no difference in overall mean haemoglobin at the end of two trials with deworming (Analysis 1.7).
Two trials reported on formal tests (Table 5). Kvalsvig 1991a did not clearly report change in cognitive scores; Nokes 1992 did not report unadjusted data, but results of multiple regression suggested an improvement in treated children in three of the 10 tests carried out (fluency, digit span forwards, digit span backwards).
Two trials in the same high prevalence area of Kenya measured performance on the Harvard Step Test in non-randomly selected subgroups (Stephenson 1989; Stephenson 1993), and both indicated benefit. Yap 2014 found no effect on any of the measures of physical well-being (Table 6).
Three trials did not provide data in a form that we could use in meta-analysis. We have collated these data in Table 4, and this information is summarized below:
Stephenson 1993 demonstrated weight, MUAC, triceps, subscapular and skinfold gains, but no improvements in height (Analysis 2.1; Analysis 2.2; Analysis 2.5; Analysis 2.6; Analysis 2.7). For body mass index, Simeon 1995 did not demonstrate a difference (Analysis 2.3). They also reported height for age z-score and did not detect a difference (Table 4).
Simeon 1995 measured intellectual development using a wide range achievement test in the main trial, and digit spans and verbal fluency tests in subgroups. The trial authors reported that deworming had no effect on intellectual development scores, but did not report the data (Table 5).
Simeon 1995 found no demonstrable effect on school attendance rates of children actively attending school (MD -2.00, 95% CI -5.49 to 1.49; 407 participants, one trial, Analysis 2.4).
One trial had substantive health promotion activities accompanying the deworming group (Table 3).
See Summary of findings 3.
No trials provided data for the outcomes school attendance, physical well-being, and mortality.
Trials measured weight in high (n = 2), moderate (n = 2), and low (n = 3) prevalence areas. The trials demonstrated no effect on weight (-0.04 kg, 95% CI -0.11 to 0.04; 2719 participants, seven trials; Analysis 3.1), height (-0.12 cm, 95% CI -0.33 to 0.10; 1974 participants, five trials; Analysis 3.2) or MUAC (0.04 cm, 95% CI -0.19 to 0.26; 911 participants, three trials; Analysis 3.3).
Two trials were in moderate prevalence areas, and one in low prevalence areas. No effect was demonstrable in individual trials or on meta analysis (MD 0.06 g/dL, 95% CI -0.05 to 0.17; 1005 participants, three trials; Analysis 3.4).
Solon 2003 measured cognitive ability using a standardized written mental-abilities test, and reported that deworming had either no effect or a negative effect on mental ability scores, but did not report the data. Nga 2009 reported no effects on any cognitive tests measured (Table 5).
Some trials did not provide data in a form that we could use in meta-analysis. We have collated these data in Table 4, and we have summarized this information below:
In the sensitivity analysis including only trials where the risk of bias for allocation concealment was low, no difference between treatment and control groups in weight, height, MUAC, or haemoglobin was evident (Analysis 5.1; Analysis 5.2; Analysis 5.3; Analysis 5.4).
See Summary of findings for the main comparison.
No trials provided data for adverse events.
Trials were in high (n = 2), moderate (n = 3), and low (n = 5) prevalence areas. For weight, overall there was no evidence of an effect (Analysis 4.1), although one trial (Awasthi 1995 (Cluster) (low prevalence) showed a large weight gain of almost 1 kg in the treatment groups. Notably two subsequent trials in the same area as Awasthi 1995 (Cluster) did not demonstrate an effect (Awasthi 2000; Awasthi 2001 (Cluster)). Overall, the meta-analysis did not demonstrate a difference in weight gain between intervention and control (MD 0.08 kg, 95% CI -0.11 to 0.27; 36,038 participants from cluster trials and 2354 individually randomized participants, 10 trials), but the heterogeneity was high (I² statistic = 83%). When the trials were stratified by community category, heterogeneity was explained for the high and moderate prevalence trials, but not for the low prevalence trials. No significant effect was apparent in any subgroup. For MUAC (two trials) and triceps skinfold (one trial), no overall effects were evident (Analysis 4.3; Analysis 4.4). No effect on height was demonstrated in any of the trials measuring this (5384 participants from cluster trials and 1673 participants from individually randomized, seven trials; Analysis 4.2).
Seven trials reported this, with no difference between intervention and control apparent (Analysis 4.5). In addition, the re-analysis of Miguel and Kremer (Aiken 2015) reported no difference in the prevalence of anaemia between the groups.
Five trials (30,000 participants from cluster trials and 2486 individually randomized participants) measured this outcome (Table 5). Ndibazza 2012 measured a range of cognitive tests, Watkins 1996 measured reading and vocabulary, and Stoltzfus 2001 measured motor and language development. All reported that no effect was demonstrated. Miguel 2004 (Cluster) also measured a range of cognitive tests. The results were not reported, but the trial authors stated that no deworming effect was demonstrated. Awasthi 2000 measured developmental status using the Denver Questionnaire, and did not demonstrate an effect of deworming.
Three trials reported on this outcome (Kruger 1996; Miguel 2004 (Cluster); Watkins 1996; Table 7). Watkins reported attendance rates of children actively attending school on the basis of school registers, at baseline and after treatment, and no effect was demonstrated. Miguel 2004 (Cluster) reported on end value differences in attendance for girls under 13 years of age and all boys based on direct observation.
For outcomes measures at the longest follow-up point we found no difference in school attendance (MD 2%, 95% CI -4 to 8%; Analysis 4.6; 20,000 participants in cluster trials and 243 participants from an individually RCT, two trials) ). This uses the longest point of follow-up from Miguel 2004 (Cluster) at two years (group 1 vs group 3), in line with our analytical plan.
Two trials measured this (Hall 2006 (Cluster); Miguel 2004 (Cluster); Table 8). Miguel 2004 (Cluster) measured exam score performance (English, Mathematics, and Science-Agriculture exams in pupils in grades 3 to 8). Results showed no difference in performance. This included the results in the original trial analysis, Miguel 2004 (Cluster), in the analysis after coding errors had been corrected, Aiken 2015), and in the statistical replication, Davey 2015. Hall 2006 (Cluster) found no difference in test scores at the end of the trial.
Deworming showed no effect in the DEVTA cluster trial of over one million children (Awasthi 2013 (Cluster)) (MD in deaths per child-care centre at ages 1.0 to 6.0 was 0.16 (SE 0.11); mortality ratio 0.95, 95% CI 0.89 to 1.02). Ndibazza 2012 reported that during the trial there were 16 deaths, eight in the placebo arm and eight in the treatment arm. Awasthi 1995 (Cluster) reported 23 deaths during the trial, 13 of which were in the usual care arm, and 10 were in the treatment arm.
Including only trials with low risk of bias for allocation of concealment, no significant difference between treatment and control groups was detected in weight, height, or haemoglobin (Analysis 5.1; Analysis 5.2, Analysis 5.3, Analysis 5.4; Analysis 6.1, Analysis 6.2; Analysis 6.3).
The MD in weight (between deworming drugs vs control in children in an endemic area after multiple doses) did not differ by length of follow-up (results not presented) or by publication year (Analysis 7.1).
We identified 45 trials, including nine cluster-RCTs, that met the inclusion criteria. One trial that assessed mortality in addition to other endpoints included over one million children, and the remaining 44 trials included a total of 67,672 participants.
For infected children, deworming drugs may increase average weight gain over one to six months, but we do not know if there is an effect on haemoglobin or cognitive functioning.
In trials treating all children living in endemic areas of varying endemicity (15 in high prevalence areas, 12 in moderate prevalence, and 10 in low prevalence areas), a single dose of deworming drugs probably has little or no effect on average weight gain or average haemoglobin, and may have little or no effect on cognition or physical well-being. For multiple doses of deworming drugs over six months to three years after the intervention started, there was little or no effect on average weight gain, height, or haemoglobin, and probably little or no effect on formal tests of cognition. We do not know if there was an effect on school attendance, but there is probably no effect on exam performance or death.
Since the previous version of this review, the DEVTA trial has been published and is now included in this Cochrane Review. One further trial (of 2660 children in Vietnam from 1999) remains unpublished (Hall 2006 (Cluster)). In May 2015 we offered the trial investigators an opportunity to present the trial as an annex to this review, and await a response from them. Meanwhile, the data from the unpublished manuscript are included in this review.
In children infected with worms, a single dose of deworming medicine appears to result in some weight gain. This evidence comes from trials conducted in a single school in Kenya more than 20 years ago, where all of the children were infected—the majority with heavy worm loads of both hookworm and Trichuris (Stephenson 1989; Stephenson 1993). However, when the intervention is used in the way the WHO currently recommends — giving treatment to whole school populations — an overall average effect is not evident. An effect on average weight was seen in one cluster-RCT assessing long-term multiple dosing in a low-burden community undertaken in 1995 in India (Awasthi 1995 (Cluster)). Trials conducted subsequently, some in the same area, including large cluster-RCTs, have not demonstrated effects.
Some policy arguments point out that deworming programmes will not provide a detectable average effect on nutritional status, but actually will provide a substantial effect in a proportion of children with heavy worm load infections. Even if this were the case, there should be an effect on average values, and in this review treating children known to be infected may have some effect on weight gain (driven mainly by data from Kenya from a highly endemic area conducted over twenty years ago) but not other variables. If policy makers feel this is credible even in the absence of differences in average effect, then further trials are needed to evaluate this.
Ten trials measured intellectual development using formal tests. Only one of these trials demonstrated an effect on cognitive outcomes in 3/10 of the outcomes measured (Nokes 1992; Table 5). The trials used a range of cognitive tests, which seems to reflect the difficulty inherent in choosing appropriate cognitive performance tests since there is no accepted test battery that can be applied across cultures and settings, and, as Miguel 2004 (Cluster) pointed out, the mechanisms for any putative effects are unknown.
For school attendance, one quasi-RCT reported an effect, which was apparent in only one of the two comparisons in up to a year of follow-up, and not apparent in the one comparison after one year (Miguel 2004 (Cluster)). Miguel 2004 (Cluster) measured attendance outcomes directly, unlike the other two trials (Simeon 1995; Watkins 1996) which measured attendance using school registers, which may be inaccurate in some settings. Two large cluster-RCTs measured school performance and neither demonstrated an effect of deworming (Hall 2006 (Cluster); Miguel 2004 (Cluster)).
For children living in endemic areas, in terms of the logic framework (Figure (Figure1)1) evidence on the desired impacts (child mortality and school performance) is absent. The evidence for school attendance is limited, and there is no evidence of effects on physical well-being. In terms of the main effects there may be no effect on weight, and there is fairly good evidence of no impact on haemoglobin, cognition, and school performance.
There have been some recent trials on long-term follow-up, none of which met the quality criteria needed in order to be included in this review (Baird 2011; Croke 2014; Ozier 2011; described in Characteristics of excluded studies). Baird 2011 and Ozier 2011 are follow-up trials of the Miguel 2004 (Cluster) trial. Ozier 2011 studied children in the vicinity of the Miguel 2004 (Cluster) to assess long-term impacts of the externalities (impacts on untreated children). However, in the replication trials (Aiken 2014; Aiken 2015; Davey 2015), these spill-over effects were no longer present, raising questions about the validity of a long-term follow-up. Baird 2011 compared children who received two years more deworming to those who received less in the Miguel 2004 (Cluster) analysis.
Croke 2014 is a follow-up of the Alderman 2006 (Cluster), but assessed only 3% (1097/37,165) of the original randomized participants, and furthermore all children were offered treatment after the original follow-up period in the Alderman 2006 (Cluster) trial.
Overall, given the growing evidence of a lack of short-term effects, arguments for long-term population impacts appear implausible in our view.
There have been previous claims that deworming benefits not only the individuals, but also those around them. Whilst not ignoring this, we tried to establish first that there was a benefit to individuals; as this seems debatable, examining for externalities seems less important. Miguel 2004 (Cluster), in their original analysis, stated their analysis demonstrated externalities. After correction of coding errors, the pure replication failed to find any evidence of externalities (Aiken 2015).
Critics of a previous version of this review, Dickson 2000a, stated that the impact must be considered stratified by the intensity of the infection (Cooper 2000; Savioli 2000). We have done this comprehensively in this edition and no clear pattern of effect has emerged. Other criticisms were that trials of short-term treatment cannot assess the long-term benefits of regular treatment (Bundy 2000). However, this analysis clearly examines long-term outcomes from trials conducted over the last 10 years.
Advocates of deworming argue that the evidence of benefit seen in selective deworming provides an evidential base for targeted deworming, because the latter reduces costs due to diagnostic screening. The argument is that population treatment benefits those infected, but this benefit is simply not detectable. Even among those children known to be infected, this Cochrane Review does not clearly demonstrate a consistent benefit on weight: there are two trials from 20 years ago in which all the children were heavily infected and had large weight gain, but this was not consistent across all trials (Table 2).
The WHO has raised concerns about the prevalence of choking in young children (aged between one to three years), with several pages of recommendations in a newsletter about how to administer albendazole in tablet form without children choking. Although common sense might suggest this is a rare occurrence, nevertheless some might argue there is a lack of evidence on the safety of administering deworming drugs to young children in tablet form in a community setting.
Individuals and communities are often infected with more than one helminth infection (Molyneux 2005) and the WHO is currently promoting the large-scale use of 'preventive chemotherapy'. This involves use of multiple anthelminthic drugs to treat a range of diseases, including STHs, schistosomiasis, and filariasis. Engels 2009 comments on the need for a comprehensive assessment of the impact of deworming. In the absence of such evidence, there is a need to demonstrate that a drug is effective against a particular parasite and to quantify its effects on people before combining all the drugs into a basket treatment for all helminth infections, and assuming that all components are effective.
Evidence of the benefit of deworming on nutrition appears to depend on three trials, all conducted more than 15 years ago, with two from the same area of Kenya where nearly all children were infected with worms and worm burdens were high. Later and much larger trials have failed to demonstrate the same effects. It may be that over time the intensity of infection has declined, and that the results from these few trials are simply not applicable to contemporary populations with lighter worm burdens.
Conducting field trials to test this intervention is complex and challenging, and researchers have worked hard to generate this body of research evidence. There is now a reasonable amount of evidence from trials in a range of settings, including high, moderate, and low burden areas. There have also been ten trials (Analysis 4.1) that have assessed the effects of multiple doses of deworming, four of which were cluster-RCTs. These are particularly important because they can detect the 'real life' community level effects of treatment that include possible effects from a reduction in worm transmission (Bundy 2009).
Of the eight cluster-RCTs, three did not take adequate account of cluster randomization (Alderman 2006 (Cluster); Hall 2006 (Cluster); Rousham 1994 (Cluster)). This has the potential substantive impact on the interpretation of the trials. For example, the significant difference between intervention and control quoted on the cover of the BMJ for Alderman 2006 (Cluster) assumed 27,995 children had been individually randomized. When we clarified this with the trial authors, they provided the BMJ with a correction, which showed that no significant difference was detected in weight gain between intervention and control groups; this corrected result has been used in the meta-analysis in this trial.
Advocates of deworming have emphasised the potential impacts on school attendance, on the basis of the influential econometric trial Miguel 2004 (Cluster). The recent replication trials of Miguel 2004 (Cluster) substantiate our concerns in the previous version of this Cochrane Review about the high risk of bias in this trial (Aiken 2015; Davey 2015). In particular the replication trials raise concerns about the validity of combining the school attendance data across years, since this involves a non-randomized before and after comparison. We have thus presented the corrected separate year estimates in this review, and present the longest follow-up time point in line with our a priori analysis strategy.
Miguel 2004 (Cluster) also reported data on school attendance at one year of follow-up, in two groups: group 1 versus group 2+3; and group 2 versus group 3. As outlined in the previous edition of the review, it is methodologically incorrect to combine these in meta-analysis as they are not independent (Taylor-Robinson 2012). The analysis in the previous edition presents each comparison separately (Analysis 4.7 in Taylor-Robinson 2012), both with modest effects, and both non-significant in the meta-analysis (including Watkins 1996) and this is not repeated in this edition.
The included trials reported a range of nutritional status outcomes. For meta-analysis, we did not use nutritional data expressed as z-scores or percentile scores calculated on the basis of reference standards, or dichotomised z- or percentile scores (eg proportion stunted with height-for-age z-score < -2). As these data were derived from the absolute values, we used these values for evidence of benefit. We knew the nutritional data would be captured in the absolute values and wanted to reduce selective reporting through collection of multiple variables from papers that are all derived from the same basic outcomes measured in the trial. We noted that in some trials there was a discrepancy between what was measured and what was reported; eg Nokes 1992 recorded but did not report anthropometric data. This is a concern as it may indicate selective reporting. However, we have systematically reported all relevant outcomes not included in meta-analysis in Table 4.
Some trials presented data from subgroups, selected on the basis of factors such as infection status (Beach 1999; Fox 2005; Greenberg 1981), location (Koroma 1996), age (Stoltzfus 2001), frequency of treatment (Stoltzfus 1997 (Cluster)), and sex (Lai 1995). These comparisons were not randomized and have not been included in meta-analysis. Two trials, one of which one was a cluster-RCT, demonstrated improvements in nutritional outcomes in subgroup analyses (Stoltzfus 1997 (Cluster); Stoltzfus 2001). We have reported these data in Table 4.
A review and meta-analysis by Hall 2008, funded by the World Bank, presented evidence in favour of an effect of deworming on weight gain (MD 0.21 kg, 95% CI 0.17 to 0.26, 11 trials). This analysis differs from our analyses of weight gain in a number of respects: it was not a protocol-driven systematic review; the review excluded trials in lower prevalence areas (< 50%); pooled results were presented without exploration of significant heterogeneity; it combined trials that included both screened and unscreened children; it included trials excluded from our review on the basis of methodological quality; it included data from subgroup analyses; and included data unadjusted for cluster randomization.
The narrative review, Albonico 2008, explored the evidence for the impact of deworming on pre-school age children, and concluded that deworming has been shown to improve growth. Their analysis differed from our analyses in a number of ways: a different population was considered, although our review considers data from this subgroup; it was not a protocol-driven systematic review; it included trials excluded from our review; it was a narrative summary rather than meta-analysis of data; it reported results from subgroup analyses; it reported point estimates without taking into account statistical significance; and it included data unadjusted for cluster randomization. The authors state: “A few trials have failed to show any impact of deworming on growth”. This is at odds with our interpretation of the reliable randomized comparisons of nutritional outcomes in this review, which suggests that most trials have failed to show an effect on nutrition.
Gulani 2007 undertook a systematic review of the effects of deworming on haemoglobin, and reported a marginal increase in mean values that could translate into small reduction (5% to 10%) in anaemia in a population with a high prevalence of intestinal helminths. This systematic review differs from our analysis of haemoglobin in a number of respects: it included trials in adults and pregnant women and it included trials excluded from our review on the basis of methodological quality.
Other advocates of deworming, such as Bundy 2009, have argued that many of the underlying trials of deworming suffer from three critical methodological problems: treatment externalities in dynamic infection systems, inadequate measurement of cognitive outcomes and school attendance, and sample attrition. We agree with these points. However, externalities will be detected by large cluster-RCTs and there are now nine trials such as this included in this review, and the externalities previously reported in Miguel 2004 (Cluster) were not found in the replication analysis after various coding and classification errors had been corrected (Aiken 2015).
It is good medical practice that children known to be infected with worms should receive treatment. This is obvious and not the subject of this Cochrane Review.
There is now good evidence to show that routine, repeated deworming public health programmes at a large scale have little or no benefit on average biomedical parameters or school performance. Current evidence does not support large public health programmes of deworming in developing countries.
The replication of the Miguel and Kremer trial highlighted a number of errors in the original analysis which have been corrected. This demonstrates the value of replication in trials that are controversial and where there is a lack of clarity over methods and the analysis.
The quality of evidence is graded as moderate on most of the outcomes, in relation to demonstrating little or no effect of community deworming. This means that research could possibly have important impact on the confidence of the results and alter the effect. Therefore, further research may be useful, but this needs to be balanced against the declining worm burdens worldwide and the absence of any good evidence of an effect given the current research.
Authors of trials, whether they are small or large, should publish the results of the trials promptly irrespective of the findings, in line with the basic principles of research integrity (Garner 2013). We encourage the authors of the Vietnam trial to publish their results.
We thank all people who gave of their time and expertise to comment on this Cochrane Review and also the authors of the first version of this Cochrane Review (Dickson 2000a). We are grateful to Dr. David Sinclair for his advice and assistance in preparing 'Summary of findings' tables.
This document is an output from a project funded by the UK Department for International Development (DFID) for the benefit of developing countries. The views expressed are not necessarily those of DFID.
This 2015 review update was partly supported by a grant from the Evidence and Programme Guidance Unit, Department of Nutrition for Health and Development, WHO.
The academic editors for this Cochrane Review are Hellen Gelband and David Sinclair.
|Potential bias||Authors' judgement|
|Random sequence generation (selection bias)||High – not randomized or quasi-randomized Unclear – states “randomized”, but does not report method Low – describes method of randomization|
|Allocation concealment (selection bias)||High – not concealed, open label trial for individually randomized, method of concealment not adequate Unclear – details of method not reported or insufficient details Low – central allocation, sequentially numbered opaque sealed envelopes|
|Blinding (performance bias and detection bias)||High – personnel, participants or outcome assessors not blinded Unclear – no details reported, insufficient details reported Low – personnel, participants and outcome assessors blinded|
|Incomplete outcome data (attrition bias)||High – losses to follow-up not evenly distributed across intervention and control group, high attrition rate (20% or more for the main outcome) Unclear - no details reported, insufficient details reported Low – no losses to follow-up, losses below 20% and evenly distributed across groups, ITT analysis used. Note: for cluster-RCTs, the loss relates to the clusters|
|Selective reporting (reporting bias)||High – did not fully report measured or relevant outcomes Unclear – not enough information reported to judge Low – all stated outcomes reported|
|Other bias||Low – no obvious other source of bias of concern to reviewers High – major source of bias such as unexplained differences in baseline characteristics|
|TrialID Country||Who was treated? (Age)||How long was the follow-up?||Trialdesign? (No. of participantsa)||Was it a cluster-RCT? (No. of clusters)||What intervention? (Dose)||Co-interventions?b||What control?||How long was the treatment?||Endemic area? (Community category number)|
|Alderman 2006 (Cluster) Uganda||Children (1 to 7 years)||3 years||RCT (27,995)||Yes (48)||Albendazole (400 mg)||Child health package – both groups||No treatment||Every 6 months||Yes (2)|
|Awasthi 1995 (Cluster) India||Children (1 to 4 years)||2 years||Quasi-RCT (3712)||Yes (50)||Albendazole (400 mg)||None||Placebo||Every 6 months||Yes (3)|
|Awasthi 2000 India||Children (1.5 to 3.5 years)||2 years||Quasi-RCT (1045)||No||Albendazole (600 mg)||None||Placebo||Every 6 months||Yes (3)|
|Awasthi 2001 (Cluster) India||Children (1 to 4 years)||1.5 years||RCT (1672)||Yes (124)||Albendazole ± vitamin A (100,000 units)||Child health package – both groups||Placebo + vitamin A||Every 6 months||Yes (3)|
|Awasthi 2013 (Cluster) India||Children (≤ 5 years)||5 years||RCT factorial (8338)||Yes (72)||Albendazole (400 mg) ± vitamin A||Child health package – both groups||Usual care||Every 6 months||Yes (3)|
|Beach 1999 Haiti||Children (grades 1 to 4)||4 months||RCT (853)||No||Albendazole (400 mg) Ivermectin (200 to 400 μg/kg)||None||Placebo + vitamin C (250 mg)||Single dose||Yes (3)|
|Donnen 1998 Zaire||Children (0 to 72 months)||1 year||RCT (222)||No||Mebendazole (500 mg)||None||Placebo + vitamin A (60 mg) No treatment||Every 3 months||Yes (3)|
|Dossa 2001 Benin||Children (3 to 5 years)||10 months||RCT (65)||No||Albendazole (200 mg) ± iron||None||Placebo||Repeated 1 month later||Yes (2)|
|Fox 2005 Haiti||Children (5 to 11 years)||6 months||RCT (626)||No||Albendazole (400 mg) ± vitamin C (250 mg) Diethylcarbamazine (DEC, 6 mg/kg)||None||Placebo||Single dose||Yes (2)|
|Freij 1979a Ethiopia||Children (1.5 to 5 years)||28 days||Quasi-RCT (13)||No||Piperazine (3 g)||Child health package – both groups||Placebo||Single dose||Infected children (unclear)|
|Freij 1979b Ethiopia||Children (1 to 5 years)||34 days||Quasi-RCT (44)||No||Piperazine (3 g x 2)||None||Placebo||Single dose||Infected children (3)|
|Garg 2002 Kenya||Children (2 to 4 years)||6 months||RCT (347)||No||Mebendazole (500 mg)||Child health package – both groups||Placebo||Single dose||Yes (2)|
|Goto 2009 Bangladesh||Children (≤ 11 months)||36 weeks||RCT (410)||No||Albendazole (200 mg) ± secnidazole (0.5 mL/kg, anti-Giardia)||None||Placebo||Every 12 weeks||Yes (2)|
|Greenberg 1981 Bangladesh||Children (1.5 to 8 years)||11 months||RCT (152)||No||Piperazine citrate (80 mg/kg)||None||Placebo||Two doses in 2 weeks||Yes (1)|
|Hadju 1996 Indonesia||Children (6 to 10 years)||7 weeks||RCT (64)||No||Pyrantel pamoate (10 mg/kg)||None||Placebo||Single dose||Yes (1)|
|Hadju 1997 Indonesia||Children (± 8.3 years)||1 year||RCT (330)||No||Albendazole (400 mg) Pyrantel pamoate (10 mg/kg)||None||Placebo||Single dose or every 6 months||Yes (1)|
|Hall 2006 (Cluster) Vietnam||Children (± 104.5 months)||2 years||RCT (2,659)||Yes (80)||Albendazole (400 mg) ± retinol (200,000 IU)||None||Placebo||Every 6 months||Yes (1)|
|Kirwan 2010 Nigeria||Children (1 to 5 years)||14 months||RCT (320)||No||Albendazole (200 to 400 mg)||Child health package – both groups||Placebo||Every 4 months||Yes (3)|
|Kloetzel 1982 Cameroon||Children (1 to 8 years)||10 months||RCT (337)||No||Mebendazole (100 mg x3)||None||Placebo||3 doses in 3 days||Yes (1)|
|Koroma 1996 Sierra Leone||Children (6 to 10 years)||6 months||RCT (187)||No||Albendazole (400 mg)||None||Placebo||Single dose||Yes (2)|
|Kruger 1996 South Africa||Children (6 to 8 years)||11 months||RCT (74)||No||Albendazole (400 mg) ± soup fortified with iron and vitamin C||Child health package – both groups||Placebo||Repeated at 4 months||Yes (3)|
|Kvalsvig 1991a South Africa||Children (primary school)||1 month||RCT (unclear)||No||Mebendazole (500 mg)||None||Placebo||Single dose||Infected children (1)|
|Lai 1995 Malaysia||Children (8 years)||2 years||RCT (314)||No||Mebendazole (100 mg) + pyrantel (200 mg)||None||Placebo||Every 3 months||Yes (1)|
|Le Huong 2007 Vietnam||Children||6 months||RCT factorial (510)||No||Mebendazole (500 mg)||Iron-fortified noodles||Placebo||Twice 3 months apart||Yes (2)|
|Michaelsen 1985 Botswana||Children (5 to 14 years)||5 months||RCT (121)||No||Tetrachloroethylene (0.1 mL/kg)||None||Placebo||Single dose||Yes (1)|
|Miguel 2004 (Cluster) Kenya||Children (8 years)||2 years||RCT (9102)||Yes (65)||Albendazole (400 to 600 mg)||Child health package – only intervention group||No treatment||Every 6 months||Yes (1)|
|Ndibazza 2012 Uganda||Children (± 15 months)||Post-treatment||RCT factorial (1423)||No||Albendazole (200 to 400 mg)||Child health package – both groups||Placebo||??||Yes (3)|
|Nga 2009 Vietnam||Children (6 to 8 years)||4 months||RCT (510)||No||Albendazole (400 mg) ± multi-micronutrient fortified biscuit||None||Placebo||Single dose||Yes (2)|
|Nokes 1992 Jamaica||Children (9 to 12 years)||9 weeks||RCT (103)||No||Albendazole (400 mg x3)||None||Placebo||Single dose||Infected children (1)|
|Olds 1999 China, Philippines and Kenya||Children (school children)||6 months||RCT (103)||No||Albendazole (400 mg) ± praziquantel (40 mg/kg)||None||Placebo||Single dose||Yes (1)|
|Palupi 1997 Indonesia||Children (2 to 5 years)||9 weeks||RCT (191)||No||Albendazole (400 mg)||Iron||Iron (30 mg weekly)||Single dose||Yes (2)|
|Rousham 1994 (Cluster) Bangladesh||Children (2 to 6 years)||18 months||RCT (1,402)||Yes (13)||Mebendazole (500 mg) Pyrantel pamoate (10 mg/kg)||None||Placebo||Every 2 months||Yes (1)|
|Sarkar 2002 Bangladesh||Children (2 to 12 years)||16 weeks||RCT (81)||No||Pyrantel pamoate (11 mg/kg)||None||Placebo||Single dose||Infected children (1)|
|Simeon 1995 Jamaica||Children (6 to 12 years)||26 weeks||RCT (392)||No||Albendazole (800 mg)||None||Placebo||Repeated 3 to 6 months after||Infected children (1)|
|Solon 2003 Philippines||Children (grades 1 to 6)||16 weeks||RCT (851)||No||Albendazole (400 mg) ± multivitamin and iron||None||Placebo||Repeated 3 to 6 months after||Yes (2)|
|Stephenson 1989 Kenya||Children (grades 1 to 2)||6 months||RCT (150)||No||Albendazole (400 mg)||None||Placebo||Single dose||Yes (1)|
|Stephenson 1993 Kenya||Children (grades 1 to 5)||8 months||RCT (284)||No||Albendazole (600 mg)||None||Placebo||Repeated 3 to 6 months after||Yes (1)|
|Stoltzfus 1997 (Cluster) Tanzania, Zanzibar||Children (± 10.5 years)||12 months||RCT (3063)||Yes (12)||Mebendazole (500 mg, 2x or 3x)||None||Placebo||Every 4 or 6 months||Yes (1)|
|Stoltzfus 2001 Tanzania, Zanzibar||Children (6 to 59 months)||12 months||RCT factorial (359)||No||Mebendazole (500 mg) ± iron||None||Placebo||Every 3 months||Yes (2)|
|Sur 2005 India||Children (2 to 5 years)||12 months||RCT (683)||No||Albendazole (400 mg) ± vitamin B||None||Placebo||Every 6 months||Yes (2)|
|Tee 2013 Malaysia||Children||12 months||RCT (33)||No||Albendazole (400 mg x 2)||None||Placebo||Single dose||Yes (NA)|
|Watkins 1996 Guatemala||Children (7 to 12 years)||6 months||RCT (226)||No||Albendazole (400 mg)||None||Placebo||Repeated at 12 weeks||Yes (1)|
|Willett 1979 Tanzania||Children (6 to 91 months)||12 months||RCT (268)||No||Levamisole (2.5 mg/kg)||None||Placebo||Every 3 months||Yes (3)|
|Wiria 2013 (Cluster) Indonesia||Children and adults ≥ 2 years||21 months||RCT (855)||Yes (954)||Albendazole (400 mg x 3)||None||Placebo||Single dose||Yes (1)|
|Yap 2014 Myanmar, China||Children (9 to 12 years)||6 months||RCT (194)||No||Albendazole (400 mg x 3)||None||Placebo||Single dose||Infected children (NA)|
aNumber of participants analysed for primary outcome.
bFor details on “child health package” please see Table 3: Accompanying health promotion activities.
Dear Dr. Taylor-Robinson, Dr. Maayan, Dr. Soares-Weiser, Dr. Donegan, and Dr. Garner:
We are writing to clarify several points that you raise in your recent 2012 Cochrane review of deworming regarding our 2004 paper “Worms: Identifying impacts on education and health in the presence of treatment externalities” in Econometrica.
In particular, we have four main concerns about the discussion of our piece in the recent review, and believe that they could change the assessment of the quality of the evidence presented in our paper. We list these points here in the letter below, with a brief discussion of each point. We then discuss several additional points in the attached document below, following this letter. We hope that these detailed responses to your review will start a productive discussion about the interpretation of the evidence in the Miguel and Kremer (2004) paper.
(All page numbers listed below refer to the July 2012 version of your review, with “assessed as up-to-date” as May 31, 2012.)
We recognize that writing a Cochrane review is a major undertaking, and we appreciate the time you have taken to read our paper, and the dozens of other papers covered in the review. We hope that this note can serve as the starting point for discussion, both in writing and via phone, if appropriate.
Our four points all relate to the claim made on page 6 of your review, and repeated throughout the review, about the Miguel and Kremer (2004) paper:
“Miguel 2004 (Cluster) has a high risk of bias for sequence generation, allocation concealment, blinding, incomplete outcome data and baseline imbalance.”
We have serious concerns about the claims you make about the risk of bias for baseline imbalance, incomplete outcome data, and sequence generation. We discuss these in turn below.
Point (1): A leading issue is your current assessment of the quality of evidence on school attendance and participation, which is the main outcome measure in the Miguel and Kremer (2004) trial. Several concerns are raised, including: a lack of baseline values for these measures (leading to a risk of baseline imbalance), and statistically significant impacts for only one of the comparisons considered. The quotes from your review are as follows:
[p. 21] “For school attendance (days present at school): (Miguel 2004 (Cluster) Table 6; Analysis 5.4) reported on end values for attendance rates of children (1999, Group 1 versus Group 3), and found no significant effect (mean difference 5%, 95% CI -0.5 to 10.5). No baseline values were given so there is potential for any random differences between the groups to confound the end values.”
[p. 24] “Similarly, for school attendance, the GRADE quality of the evidence was very low. One quasi-randomized trial (Miguel 2004 (Cluster) reported an effect, which was apparent in only one of the two comparisons in up to a year of follow up, and not apparent in the one comparison after one year. Miguel 2004 (Cluster) measured attendance outcomes directly, unlike the other two trials (Simeon 1995; Watkins 1996) which measured attendance using school registers, which may be inaccurate in some settings. However, in Miguel 2004 (Cluster), the values for school attendance were end values and not corrected for baseline. Thus random differences in baseline attendance between the two groups could have confounded any result.”
We feel that these concerns are misplaced, and explain why here. We first discuss concerns about “baseline imbalance".
First, we in fact do have baseline data on school participation (our preferred measure) for one of the comparisons that you focus on. The authors of the Cochrane appear to have missed this data in our paper. In Table VIII, Panel A, there is a comparison of 1998 school participation for both Group 2 and Group 3, when both were control schools. There is no statistically significant difference in school participation across Group 2 and Group 3 in 1998, and if anything school participation is slightly lower in Group 2 (-0.037, s.e. 0.036). This makes the difference between Group 2 and Group 3 in 1999 (0.055, s.e. 0.028), when Group 2 had become a treatment school, even more impressive, since at baseline Group 2 had slightly lower school participation. We respectfully request that the authors of the Cochrane review include this data as evidence of baseline balance in our key outcome measure, school participation, and that they edit their claim that we do not have any such evidence.
It is interesting to note that, if we take the difference between Group 2 and Group 3 at baseline seriously, then the overall effect for this “year 1” comparison is 3.7 + 5.5 = 9.2 percentage points. This is almost exactly the same as the 9.3 percentage point effect in the other “year 1” comparison that the Cochrane authors focus on (Group 1 versus Groups 2 and 3 in 1998). Taken together, this is quite striking evidence that the first year of deworming treatment significantly improves school participation. The Cochrane authors' repeated concerns in their review about baseline balance being critical in randomized experiments suggests (to us) that they might find it methodologically preferable to use a “difference-in-difference” design that explicitly controls for any baseline differences across treatment groups, rather than the standard unbiased “endline” comparison across treatment groups. If this is in fact the case, then the relevant year 1 deworming treatment effect for the Group 2 versus Group 3 comparison (for which we have baseline data, as noted above) is the 9.2 percentage point estimate, which we note is significant at 99% confidence.
Second, regarding baseline data on school attendance, we discuss that there is indeed evidence from school registers that recorded attendance is indistinguishable in the three groups of schools in early 1998 (in Table I). While the register data has its weaknesses – precisely the reason we developed the much more rigorous approach of unannounced school participation checks, combined with tracking of school transfers and drop-outs – it is used in other trials, and in fact the Cochrane review considers school register data sufficiently reliable to include a trial (Watkins 1996) that uses it in their meta-analysis of school attendance.
We are puzzled as to why the evidence in the Watkins (1996) trial is included at all in the Cochrane review if similar register data is considered unreliable when Miguel and Kremer (2004) use it. If school register data is considered (largely) unreliable, then the Watkins (1996) article should be excluded from the review, in which case the “meta-analysis” of school attendance and participation impacts will yield estimated effects that are much larger and statistically significant (since the Watkins impact estimates are close to zero). If the register data is considered (largely) reliable, then the Watkins (1996) trial should be included in the review, but the baseline register data in Miguel and Kremer (2004) should be considered as evidence that we do in fact have baseline balance on school participation. But there is an inconsistency in how register data is considered across the two trials. This seemingly inconsistent approach taken by the authors raises questions about the evenhandedness of the Cochrane review.
In fact, the appropriate use of school register data is more subtle than the Cochrane authors currently consider, since its use as baseline data may in fact be appropriate even if it is inappropriate for use as outcome data. There are at least two reasons why. First, one of the major weaknesses of the school register data used in Watkins (1996) is that it excludes any students who have dropped out, potentially giving a misleading picture about school participation over time. However, this concern about drop-outs is irrelevant when we use school register data at baseline, since the universe of students considered in the Miguel and Kremer (2004) article was restricted to those currently enrolled in school in January 1998 (at the start of the school year), and thus the exclusion of drop-outs is not a concern. Note that our use of the school register data at the start of the school year is a likely explanation for why the baseline average attendance rates we obtain using this data are much higher than the average school participation rate that we estimate over the course of the entire school year.
A second related issue is the quality of measured school attendance data conditional on student enrollment in school. Note that to the extent that differences in attendance record-keeping prior to the introduction of the program are random across schools, they will not bias estimates of treatment impact and any “noise” in these measures will be correctly captured by reported standard errors. However, there are plausible concerns about the quality of school register data collected in treatment versus control schools in the context of an experimental evaluation, with a leading concern being that school officials could erroneously inflate figures in the treatment group. Yet once again these concerns are irrelevant in the Miguel and Kremer (2004) trial context since the baseline 1998 school register data that we present (in Table I, Panel B) was collected before any interventions had even been carried out in the sample schools, once again making the baseline school register data potentially more reliable than school register data used as an outcome.
While the data and measurement issues here are somewhat subtle, if anything they argue in favor of including the baseline school register data in assessing the baseline balance in the Miguel and Kremer (2004) paper, while excluding the school register outcome data in Watkins (1996) as potentially unreliable. Instead, the Cochrane authors completely dismiss the baseline register data in Miguel and Kremer (2004) as unreliable evidence for baseline balance, while including the Watkins (1996) data in their meta-analysis of school participation impacts, giving it equal weight with the Miguel and Kremer (2004) school participation impact evidence (which uses more rigorous outcome data). Once again, the seemingly selective approach taken by the authors raises questions about the evenhandedness of the Cochrane review.
An important final point has to do with the claim that there might have been “random differences” across groups. Given the randomized design of Miguel and Kremer (2004), there is no systematic difference to expect there to have been such random differences. The endline comparison of outcomes across treatment groups yields unbiased treatment effect estimates. The remarkable balance across the three groups in terms of dozens academic, nutritional, and socioeconomic outcomes at baseline (Table I) makes it even more unlikely that there were large differences in school participation solely by chance. If the Cochrane authors would like to consider other characteristics (other than school participation) to gauge the likelihood that Groups 1, 2 and 3 in our trial are in fact balanced at baseline they should look at the whole range of outcomes presented in Table I of Miguel and Kremer (2004). The lack of significant baseline academic test scores across Groups 1, 2 and 3 in our sample (Table 1, Panel C) is particularly good evidence that schooling outcomes were in fact balanced at baseline, for instance. It is not clear to us why the Cochrane authors remain so concerned about baseline imbalance issues given the experimental design (which leads to unbiased estimates) and the remarkable balance we observe along so many characteristics in Table I of Miguel and Kremer (2004), and their review does not provide compelling justification for their concerns.
Moreover, in the standard statistical methods that we use, only those differences across groups that are too large to have been generated “by chance” are considered statistically significant impacts. In other words, the standard errors generated in the analysis itself are precisely those that address the risk of imbalance “by chance” given our research design and sample size. Of course, random variation that is orthogonal to treatment assignment does not alone generate bias.
Speculating about the possibility that there were simply positive impacts “by chance” in order to cast doubt on one set of results, but not doing the same when there are zero estimated impacts, again raises questions about the evenhandedness of the Cochrane review. (For instance, perhaps the “zero” impacts on Hb outcome measures in our sample were zero simply “by chance", when the real point estimates are in fact strongly positive, like the large school participation impacts we estimate. Yet this possibility is not mentioned in the Cochrane review.) In our view, the Cochrane authors do not provide sufficient justification for their fears about imbalance “by chance” in our sample, and we feel further concrete details about these concerns are needed to substantiate their assertions.
Taken together, the Cochrane review's claim that there is a “high risk of bias for … baseline imbalance” (the claim made on p. 6 and p. 136, and throughout the review) appears highly misleading to us, given the: balance in school participation we observe between Group 2 and Group 3 in 1998; the balanced school attendance based on register data across Groups 1, 2 and 3 at baseline; the balance in other measures of academic performance (including academic test scores) as well as multiple socioeconomic and nutritional characteristics at baseline; and most importantly given the randomized experimental design, which implies that there is no systematic reason why the three treatment groups would differ significantly along unobservable dimensions.
We respectfully request that the authors of the review consider these factors and reconsider their assessment regarding the claimed “high risk of bias for … baseline imbalance” in Miguel and Kremer (2004).
Point (2): There is also an important methodological point to make regarding how the authors of the Cochrane review assess the school participation evidence. At several points they note that only some of the school participation comparisons are statistically significant at 95% confidence. To be specific, the comparisons they focus on have the following estimated impacts and standard errors (from p. 130-131 of their review):
School participation outcomes measured £ 1 year:
9.3 percentage point gain (s.e. 3.1 percentage points)
5.5 percentage point gain (s.e. 2.8 percentage points) School participation outcomes measured = 1 year:
5.0 percentage point gain (s.e. 2.8 percentage points)
It is unclear to us why the reviewers separate out the three comparisons, rather than combining the groups in a single analysis using standard analytical methods, as their principal assessment of the impact of deworming on school participation. They give no clear methodological justification for this separation. Pooling data from three valid and unbiased “comparisons” still yields an unbiased treatment effect estimate, but with much greater statistical precision, and is thus a methodologically preferable approach. At a minimum, the Cochrane authors should discuss the pooled estimates (which are the focus of Miguel and Kremer 2004) in addition to the three separate comparisons.
One simple approach to doing so that maintains the “comparisons” above, and at least goes part of the way towards using the full sample, would be to pool 1998 and 1999 data for the Group 1 versus Group 3 comparison, since Group 1 is treatment during this entire period and Group 3 is control for the entire period. The distinction between < 1 year and = 1 year outcomes seems rather artificial to us, as discussed further below. It is unclear to us why the Cochrane authors never present this comparison of Group 1 versus Group 3 for 1998 and 1999 pooled together.
The preferred analysis in the Miguel and Kremer (2004) paper pools multiple years of data, and all groups, to arrive at the most statistically precise estimated impact of deworming on schooling outcomes. This includes both school participation outcomes, as well as academic test score outcomes (which the Cochrane authors currently exclude since in the paper we only present these “pooled” test score results, rather than the simple differences across treatment groups). If the Cochrane authors would like to see the simple differences across treatment groups for the academic test scores, we would be delighted to share the data with them. (To be clear, the test score impact estimates in Miguel and Kremer (2004) come from a regression analysis that relies on the experimental comparison between the treatment and control groups, and is not a retrospective analysis based on non-experimental data.)
In our view, the Cochrane authors do not provide adequate statistical justification for splitting results into the different “comparisons", or into “year 1” versus “year 2” impacts. “Pooling” these different comparisons, as we do in the Miguel and Kremer (2004) paper, is standard with longitudinal (panel) data analysis with multi-year panels, and is appropriate for those that care about deworming impacts at multiple time frames, ie at less than one year and at more than one year of treatment. Use of our full sample would immediately lead to the conclusion that there are in fact positive impacts of deworming on school participation in our sample, with very large impact magnitudes and high levels of statistical significance. This is the conclusion of the Miguel and Kremer (2004) paper, and a quick look at the comparisons presented above also indicate that there are strong impacts: all three of the comparisons have large impact estimates and all three are statistically significant at over 90% confidence, with one significant at over 99% confidence and another nearly significant at 95% confidence (despite the data being split up into the three different comparisons). By treating each comparison independently and in isolation, the authors are reaching inappropriate conclusions, in our view.
To illustrate why the approach taken by the current version of the Cochrane review is inappropriate, imagine the simple thought experiment of splitting up the data from Miguel and Kremer (2004) into “quarters” (three month intervals) rather than years of treatment. There is no obvious a priori reason why this should not be as valid an alternative approach as the =1 year and <1 year approach in the Cochrane review, as some other reviewers might instead have been interested in the impact of deworming treatment over intervals shorter than one year. Then we would have 2 comparisons in quarter 1 of treatment (Group 1 versus Groups 2 and 3 in early 1998, and Group 2 versus Group 3 in early 1999), 2 comparisons in quarter 2 of treatment, 2 comparisons in quarter 3, 2 comparisons in quarter 4, and 1 comparison in each quarter from 5 through 8 (Group 1 versus Group 3 in 1999). This approach would generate 12 valid “comparisons” of treatment and control schools over multiple time periods, but by slicing up the data ever more finely and reducing the sample size considered in each comparison, it is almost certain that none of these comparisons would yield statistically significant impacts of deworming on school participation at 95% confidence, even though the average estimated effect sizes would remain just as large. This would clearly not be an attractive methodological approach. You could even imagine considering a month by month treatment effect estimate, which would yield 36 different “comparisons”, all of which would be severely underpowered statistically.
However, we view the Cochrane review's slicing of our full dataset into three comparisons (two for year 1 treatment, and one for year 2), rather than conducting the analysis in the full dataset in much the same way. As we show in Miguel and Kremer (2004), when the data from all valid comparisons is considered jointly, in order to maximize statistical precision using standard longitudinal (panel) data regression methods, the estimated impacts are large and highly statistically significant. Just to be clear, we do not use any controversial statistical methods, and our results do not rely on any non-experimental comparisons. The regression analyses in our paper rely entirely on the variation in treatment status induced by the experimental design of the trial, and thus are just as appropriate analytically as the simple “treatment minus control” differences that the Cochrane authors focus on. In our view, the most robust analytical approach should use our full dataset, rather than the (in our view) more fragmented way of presenting the results in Table 6 of your review, which leads to less statistical precision and no greater insight.
If the Cochrane authors feel that there is a strong a prior reason to focus on year 1 treatment results separately from year 2 treatment results, then at a minimum they should consider both of the year 1 “comparisons” that they focus on jointly (ie Group 1 versus Groups 2 and 3 in 1998, and Group 2 versus Group 3 in 1999), in order to improve statistical precision and thus generate impact estimates with tighter confidence intervals. If they wish to strictly employ the same exact “comparison” groups over time, then they should at a minimum pool the 1998 and 1999 data and focus on the Group 1 versus Group 3 comparison. Doing either would yield an unambiguous positive and statistically significant impact of deworming on school participation in our sample.
We respectfully request that the authors of the review consider these suggestions and reconsider their assessment regarding the claimed lack of statistically significant school participation impacts in Miguel and Kremer (2004).
Point (3): The Cochrane review concludes that our trial has a “high risk of bias for … incomplete outcome data” (p. 90). We believe this point is simply incorrect when applied to our school participation data, as we explain here. The review authors focus on the lack of detail in Miguel and Kremer (2004) regarding the collection of Hb data, but then unfairly use this lack of clarity to downgrade the reliability of all data in the trial, including the school participation data. The exact quote from the review is as follows:
[p. 15] However, results for health outcomes were presented for the 1998 comparison of Group 1 (25 schools) versus Group 2 (25 schools). Details of the outcomes we extracted and present are:
• Haemoglobin. This was measured in 4% of the randomized population (778/20,000). It was unclear how the sample were selected.
The Hb sample was a random (representative) sub-sample of the full sample, chosen by a computer random number generator. Appendix Table AI of the Miguel and Kremer (2004) paper does discuss how the parasitological and Hb surveys were collected jointly in early 1999. Table V mentions that the parasitological data in 1999 was collected for a random sub-sample. A random subset of those individuals sampled for parasitological tests also had Hb data collected; this was not explicitly stated but should have been. The reason for the relatively small sample for Hb testing was simply that a random (representative) sub-sample was selected for this testing. For both Hb and parasitological tests, the time and expense of testing the entire sample of over 30,000 school children was prohibitive, hence the decision to draw a representative sub-sample. Collection of this data for a representative sample should reduce concerns about bias due to incomplete outcome data and selective attrition.
[p. 15] • Weight and height. This was measured in an unknown sample of the 20,000 children. No sampling method was given.
Section 3.1 of Miguel and Kremer (2004) does state explicitly that the anthropometric data was collected during pupil questionnaires at school during 1998 and 1999. These were collected in standards (grades) 3-8, rather than in all grades, and for that reason there is only data on a subset of the full sample. Height and weight data was collected on all individuals in standards 3-8.
We acknowledge that the discussion of sampling for hemoglobin outcomes was unclear in Miguel and Kremer (2004). However, the fact that we only have Hb data for a random subset in no way affects the attrition rate for school participation data, which was collected for the entire sample. There is no problem with attrition in the main outcome measure in the Miguel and Kremer (2004) trial, namely, school participation. In fact the school participation data is unusually rigorous. We tracked individuals as they transferred across schools, or dropped out of schools, and collected school attendance on unannounced visit days to get a more representative picture of actual school participation. This is in sharp contrast to most other trials.
For instance, Watkins (1996), which shows smaller school attendance impacts than Miguel and Kremer (2004), only considers school attendance based on register data, among those attending school regularly, missing out on school drop-outs and transfers entirely. Yet that trial surprisingly received equal weight with Miguel and Kremer (2004) in the meta-analysis of school attendance carried out in this Cochrane review.
Taken together, the claim that there is a “high risk of bias for … incomplete outcome data” (the claim made on p. 6 and p. 136, and throughout the review) appears incorrect to us, given the remarkably high quality of follow up data for school participation, which serves as the main outcome of the trial, and the collection of a representative sub sample for both Hb and nutritional measures.
We respectfully request that the authors of the review consider these factors and reconsider their assessment regarding the claimed “high risk of bias for … incomplete outcome data” in Miguel and Kremer (2004), especially in regards to the school participation data.
(One small point: In the summary of findings table on page 5, it is stated that we only have school participation data for 50 clusters, rather than 75 clusters. This is incorrect, since even using the Cochrane authors' three “comparisons", there are 75 distinct clusters that contribute to the year 1 evidence for Group 1 versus Groups 2 and 3 in 1998, for instance.)
Point (4): The Cochrane review also considers the Miguel and Kremer (2004) trial to have “a high risk of bias for sequence generation” [p. 6].
In particular, it discusses the quasi-random allocation of the 75 clusters:
[p. 14] “Eight trials were cluster randomized (Alderman 2006 (Cluster); Awasthi 2008 (Cluster); Awasthi 2001 (Cluster); DEVTA (unpublished); Hall 2006 (Cluster); Rousham 1994 (Cluster); Stoltzfus 1997 (Cluster)), one was a trial with quasi-random allocation of the 75 clusters (Miguel 2004 (Cluster))".
It is never clearly specified why the randomization approach makes the trial “quasi-randomized". It may be due to the use of an alphabetical “list randomization” approach, rather than a computer random number generator, but if so, this is never laid out explicitly by the Cochrane authors. The remarkable baseline balance on a wide range of characteristics (educational, nutritional, socioeconomic, etc. shown in Table I of Miguel and Kremer 2004) across 75 clusters and over 30,000 individuals surely helps alleviate these concerns. We would like to obtain more detailed information from the Cochrane authors on why the research design in Miguel and Kremer (2004) is considered to have a “high risk of bias". This is never explicitly discussed in the review.
We respectfully request that the authors of the review consider these factors and reconsider their assessment regarding the claimed “high risk of bias for … sequence generation” in Miguel and Kremer (2004).
We carefully read through the entire document and noted additional instances where we had questions and concerns below (following this letter), and note the relevant page numbers in your review.
Finally, we also would like to briefly mention two working papers that we believe could usefully be incorporated into future versions of the Cochrane review on deworming. One working paper (Baird et al.) trials long-term impacts of deworming treatment on labor market outcomes. We are both co-authors on this paper. We are currently finishing the write up of this paper and hope to submit it to a working paper series and a journal in 2013, and at that point we will share that paper with your group. That trial shows very large long-run impacts of deworming treatment on labor market outcomes, up to ten years after the start of the primary school deworming project that we trial. The second is a working paper by Dr. Owen Ozier of the World Bank, which examines long-run educational impacts on individuals who were very young children at the start of the Kenya deworming project, and finds large positive test score effects. One advantage of Ozier’s trial is his ability to compare outcomes across schools and across birth cohorts within those school communities, allowing him to include “school fixed effects” that control for any baseline differences across schools. This methodological approach addresses any lingering concerns about baseline “imbalance” across treatment groups.
We look forward to starting a discussion of these issues with your team, and we thank you for the time you have taken to consider them. We realize that this is an extremely time-consuming process for your entire team, given the detailed reading you need to carry out for literally dozens of trials, and we appreciate your willingness to consider these points.
Additional comments on the Cochrane review: (Cochrane text noted in italics, page numbers noted)
The Cochrane authors have the following discussion of the exam score data and school sample:
[p. 67] “Participants Number analysed for primary outcome: … Unclear for exam performance and cognitive tests Inclusion criteria: none explicitly stated. “Nearly all rural primary schools” in Busia district, Kenya, involved in a NGO deworming programme were studied, with a total enrolment of 30,000 pupils aged six to eighteen. Exclusion criteria: girls = 13 years old".
The claim that there was no explicit inclusion criteria stated in the paper for the exam data appears inaccurate. Section 7.2 of Miguel and Kremer (2004) discusses our attempts to test all students, including efforts to administer exams even to those students who had since dropped out of school (see footnote 52).
In terms of the inclusion of schools in the sample, there were a total of 92 primary schools in the trial area of Budalangi and Funyula divisions in January 1998. Seventy-five of these 92 schools were selected to participate in the deworming program, and they form the analysis sample here. The 17 schools excluded schools from the program (and thus the analysis) include: town schools that were quite different from other local schools in terms of student socioeconomic background; single-sex schools; a few schools located on islands in Lake Victoria (posing severe transportation difficulties); and those few schools that had in the past already received deworming and other health treatments under an earlier small-scale ICS (NGO) program.
The Cochrane authors make the following point about worm infection rates, which relates to potential baseline imbalance across treatment groups:
[p. 68] “Group 1 schools have an overall prevalence of 38% heavy/moderate worm infection in 1998, compared to the initial survey in control schools in 1999, where it was 52%.”
This is a misleading comparison. The comparison of Group 1 worm infection in 1998 versus Group 2 worm infection in 1999 is simply inappropriate, given the well-known variability across seasons and years in worm infection rates (as a function of local weather, precipitation, temperature, etc.). There is abundant health and nutritional data from pupil surveys for Groups 2 and 3 at baseline in 1998, and they indicate that these groups appear very similar to Group 1 at baseline (see Table I of Miguel and Kremer 2004) but no parasitological data was collected for Groups 2 and 3 in 1998, nor for Group 3 in 1999, since it was considered unethical to collected detailed worm infection data in a group that was not scheduled to receive deworming treatment in that year. Once again, standard errors for the comparison of outcomes among different treatment groups take into account the possibility of random differences at baseline, and thus statistical significance levels already reflect the possibility that there is some random baseline variation across schools, but this variation alone of course does not cause bias.
The Cochrane authors have the following discussion of our health data:
[p. 68] “However, in a personal correspondence the authors state that there is no health data for Group 3 schools for 1999.”
This claim is not entirely accurate, and must be the result of a misunderstanding. There is abundant health and nutritional data from pupil surveys for Group 3 in 1999, but no parasitological data was collected for Group 3 in 1999, since it was considered unethical to collected detailed worm infection data in a group that was not scheduled to receive deworming treatment in that year.
[p. 68] 27/75 schools were involved in other NGO projects which consisted of financial assistance for textbook purchase and classroom construction, and teacher performance incentives. The distribution of these other interventions is not clear, but the authors state that these schools were stratified according to involvement in these other programmes.
[p. 70] The intervention was a package including deworming drugs for soil transmitted helminths, praziquantel to treat schistosomiasis in schools with = 30% prevalence, and health promotion interventions. In addition 27/75 schools were involved in other NGO projects which consisted of financial assistance for textbook purchase and classroom construction, and teacher performance incentives. The distribution of the latter interventions is not clear. These co-interventions confound the potential effects of deworming drugs to treat STHs. However, the authors kindly provided a re-analysis of their data, with the praziquantel treated schools removed from the analysis. This represents as subgroup analysis of the original quasi-randomized comparison".
Given that these other interventions had no measurable impacts on educational outcomes (as reported in several other articles), and that they are balanced across our treatment groups, these prior interventions are not a major concern for the analysis.
Ted Miguel and Michael Kremer
I agree with the conflict of interest statement below:
I certify that we have no affiliations with or involvement in any organization or entity with a financial interest in the subject matter of our feedback.
We appreciate these helpful and detailed comments. We have checked through these carefully, and responded to the key points below.
Miguel and Kremer were concerned that we had been unduly harsh on assessing the risk of bias of their trial in several points in their comments. We have reassessed this in the light of their comments and the recent replication, which is helpful as it clarifies more details on the methods.
Baseline imbalance: We agree and now move the risk of bias in relation to imbalance at baseline to “low". The remaining criteria of the risk of bias remain unaltered.
Incomplete data: Thank you for your additional information about the methods. This is also contained in the replication analysis, and this has been adjusted to low.
Miguel and Kremer were concerned that the quality of the evidence on school attendance was ranked as “very low". We thank them for their concern and have revaluated the reasons for downgrading, taking into account the pure and the statistical replication. It remains ranked as very low with full justification given in the 'Summary of findings' table footnotes.
Miguel and Kremer also advocate combining results for school participations from the three school participation results from quasi-randomized comparisons. Just to recap, for year 1 follow-up, there are results from:
Group 1 vs Groups 2+3;
Group 2 vs Group 3.
And at two years of follow-up, results from Group 1 vs Group 3.
We have not combined the estimates from the quasi-randomized comparisons in meta-analysis because they are not independent. However the separate estimates are all documented in the review.
Due to the trial design the pooled estimate that Miguel and Kremer prefer contains a non-randomized before and after comparison, as clarified in the replication trials.
The second point the authors raise in the paragraph “However, we view the Cochrane's slicing…". We have addressed this by combining the multiple dose trials in one analysis, using the longest follow-up time point. Justification for this is provided in the review text. This is a helpful comment and has helped with shortening the review.
Thanks for these clarifications about the sampling for height, weight, and Hb. These are noted in the review.
For school attendance, there is downgrading as stated in the table so that the GRADE assessment of the quality is very low, for risk of bias, imprecision, and indirectness. The missing data and many of the methodological issues debated here are now made much clearer in the replication trials. The other information that is highly relevant is the health promotion co-intervention.
The GRADE table is agreed by all authors after considerable discussion. It is also checked by two other editors. This is based on information in the original trial reports and now, with your trial, the two papers concerning the replication.
Thank you for this information.
This is a quasi-randomized method of allocation, as described in the Cochrane Handbook for Systematic Reviews of Interventions, and as clarified in the replication trials.
Thanks for these additional papers you mention. They were considered by the authorship team and do not meet the inclusion criteria for the review.
David Taylor-Robinson, Paul Garner, Karla Soares-Weiser, Sarah Donegan.
Shortly after my paper on deworming in Uganda was published in the BMJ, I had an exchange of correspondence with Dr. Garner regarding the standard errors reported in one table. After that exchange I shared the following letter with the BMJ and with him in April 2007:
Prof. Paul Garner has kindly pointed out that, in an article published in the BMJ, my coauthors and I inadvertently failed to adjust standard errors in one of the tables for cluster based sampling. While table 2 of that paper reports means for growth in grams of 2413 [CI=2373 - 2454] and 2259 [CI=2216 - 2301] for the treatment and control groups respectively, once the design effect is taken into consideration the confidence intervals should, in fact, be [CI=2295 - 2533] and [CI=2121 - 2396].
The conclusions of the trial, however, are unaffected as they are based on the multivariate regressions reported in table 3 for which the standard errors had been corrected for cluster based sampling. For example, the confidence interval for the finding that the children who attended child health days every six months where deworming medicine was provide had a significantly greater weight gain than similar children who attended child health days at which albendazole was not provided is unaffected; the CI for the difference in weight gain remains [59g - 262 g].”
Recently the BMJ has invited me to submit a letter addressing the earlier comments as well as more recent variations of that theme. I believe that it is sufficient to indicate that the results presented in the multivariate analysis remain the basis for the conclusion of the trial. Given the heterogeneity of ages in the trial population and the fact that the velocity of weight gain is dependent on age, table 2 was presented for background only while the primary analysis was presented in table 3. The results in this table control for these covariates as well as the duration of time between visits or the total time a child participated in the child health days organized for his or her community. These results provide more precise estimates.
International food Policy Research Institute
I agree with the conflict of interest statement below:
I certify that I have no affiliations with or involvement in any organization or entity with a financial interest in the subject matter of my feedback.
Thank you for this information which is duly noted.
David Taylor-Robinson, Paul Garner, Sarah Donegan.
DTR wrote the protocol, applied inclusion criteria, assessed quality, extracted data, conducted data analysis, and wrote the first draft of the review. KSW and NM applied inclusion criteria, assessed quality, extracted data, conducted data analysis, and drafted the results of the update. SD assessed risk of bias and extracted data for a subset of the trials, and contributed to the analysis and the writing of the review. PG provided advice at all stages of the review production, applied inclusion criteria, assessed quality, quality assured data extraction, helped construct the comparisons, and helped write the review.
This Cochrane Review is supported by a DFID grant aimed at ensuring the best possible systematic reviews, particularly Cochrane Reviews, are completed on topics relevant to the poor, particularly women, in low- and middle-income countries. DFID does not participate in the selection of topics, in the conduct of the review, or in the interpretation of findings. The grant provides partial salary support for PG, SD, and the funds for the contract with Enhance Reviews Ltd. PG receives additional salary support from the COUNTDOWN Research Consortium, which is funded by the DFID. COUNTDOWN is committed to trials and development of mass treatment programmes related to NTDs.
Anthelmintics [*pharmacology; therapeutic use]; Child Development [drug effects]; Cognition [*drug effects]; Growth [drug effects]; Helminthiasis [complications; .drug therapy]; Intestinal Diseases, Parasitic [complications; .drug therapy]; Nutritional Status [*drug effects]; Randomized Controlled Trials as Topic; Soil [*parasitology]; Weight Gain [drug effects]
Adolescent; Child; Child, Preschool; Humans
References to studies included in this review