Non‐pharmacological interventions for stuttering in children aged between birth and six years
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
Primary objective
To assess the immediate and long‐term effects of non‐pharmacological interventions for stuttering on speech outcomes in children aged between birth and six years.
Secondary objective
To describe the relationship between intervention effects and participant characteristics (i.e. child age, child’s communication attitudes and the impact stuttering has on the child’s QoL).
Background
Description of the condition
Stuttering, or stammering as it is referred to in some countries, is a communication disorder that affects the fluency of speech. It can be characterized by verbal and non‐verbal behaviors. Verbal stuttering behaviors can include repetitions of individual sounds, parts of words, whole words or phrases; or fixed postures, which may include prolongations whereby the production of an individual sound is extended, blocks whereby the individual is temporarily unable to produce any sound at all, or interjections whereby the individual may insert words that are redundant to what they wish to say (Teesson 2003; Wingate 1964; Yairi 2015). Non‐verbal stuttering behaviors may also occur during stuttering moments and may include visible facial or neck tension, blinking, audible inspiratory airflow, or changes in pitch and loudness (Teesson 2003).
Developmental stuttering is common; however, cumulative incidence rates reported in the literature vary. While Månsson 2000 found that 5.2% of children aged between three and five years stuttered, Dworzynski 2007 found that 8.4% of children aged between two and seven years stuttered. Later, Reilly 2013 reported that 11.2% of children aged between two and four years started stuttering. Among people with intellectual disabilities, the prevalence is often described to be higher, although reports vary from 0.8% to 20.3%, as summarized by Bloodstein 1995. Differences in inclusion criteria, definitions of stuttering, and age of participants might explain the differences in incidence rates reported across studies (Preus 1990; Yairi 2012). Stuttering typically begins suddenly between two and four years of age and coincides with the period of language development when children begin to combine words to form phrases (Reilly 2009). There are reports, however, of stuttering onset occurring as early as 12 months of age (Reilly 2009).
The exact cause of stuttering remains unknown (Büchel 2004). There is consensus, however, that stuttering is a polygenic disorder and is underpinned by a neural processing deficit (Buck 2002; Kraft 2012; Viswanath 2004). While evidence to describe the genetic component of the disorder is accumulating, to date the specific genes involved have not been identified (Yairi 2012). There is also a consensus that stuttering moments are triggered by linguistic and environmental variables (Van Lieshout 2004). Increased environmental demands (e.g. child recalling a story or being asked questions) and linguistic demands within the child (e.g. increased syntactic complexity or utterance length) may trigger stuttering moments (Buhr 2009; Johnson 2009; Yaruss 1997).
While the majority of children recover from stuttering by school age, spontaneously or after intervention, up to 35% of children develop persistent stuttering (Kefalianos 2017; Yairi 1999). Those who recover are unlikely to do so within the first 12 months after stuttering onset (Reilly 2013). While it is not currently possible to predict which children will recover from stuttering and which children will persist, there is a consensus in the literature that boys are more likely to persist with stuttering than girls (Yairi 2012).
Stuttering is a multifaceted disorder that can have an adverse effect on a person’s quality of life (QoL) (Shapiro 2011; Yaruss 2016). Studies have consistently found that young children who stutter report more negative attitudes towards their own speech compared to their peers who do not stutter (Clark 2012; Vanryckeghem 2005; Węsierska 2015; for a review, see Guttormsen 2015). Investigations of behavioral, emotional and social development have yielded less consistent findings. Based on parent reports, Reilly 2013 found no behavioral, emotional or social functioning differences between children who do and do not stutter at four years of age, while McAllister 2016 and Briley 2019 reported that children who stutter have poorer behavioral, emotional and social functioning compared to their non‐stuttering peers at three and five years of age respectively.
For the children who continue to stutter, more adverse effects of stuttering have been identified. Stuttering is associated with a heightened risk of anxiety disorders (Iverach 2016), bullying (Blood 2007) and reduced popularity amongst peers (Davis 2002). In the school‐aged population, Lankman 2015 revealed a moderate association between clinician‐rated stuttering severity and how the children perceived stuttering to affect their QoL. This result indicated that factors other than stuttering severity are associated with an impact on QoL. Yaruss 2016 found an association between negative reactions to stuttering and adverse effects of stuttering on QoL. Factors within the child’s environment may also be associated with the impact of stuttering on QoL, as several studies have found that children who stutter may experience teasing and social rejection (Ezrati‐Vinacour 2001; Langevin 2009; Langevin 2010). By adulthood, people who stutter and seek therapy have a 16‐fold increased odds of meeting the criteria for social anxiety disorder compared to non‐stuttering adults (Iverach 2009). They are also at increased risk for a number of other mental health disorders, including generalized anxiety disorder and depression (Iverach 2009). Stuttering can affect an individual’s educational and occupational attainment (Klein 2004; O'Brian 2011). Considering the potential negative impact that stuttering can have on many aspects of a person’s life, and the fact that it is currently not possible to predict who will recover from stuttering, it is important to determine the best management approaches during the early years for reducing the likelihood of children developing persistent stuttering.
Description of the intervention
Non‐pharmacological interventions for stuttering in children aged from birth to six years (hereafter referred to as young children) vary in terms of their aim, content, dosage and theoretical underpinnings. In this review, we refer to non‐pharmacological interventions that are conducted by, or under the guidance of, speech and language pathologists/therapists. These interventions are typically delivered in preschools or speech and language therapy clinics. In many intervention programs, the child’s parents/caregivers are instructed by a speech and language pathologist/therapist to implement the intervention at home, within structured treatment sessions or spontaneously throughout the day. Most interventions do not specify a prescribed amount of treatment for each child. Instead, intervention continues until the aims of that specific program have been achieved. Consequently, length of intervention is largely influenced by each child’s responsiveness to intervention.
While some intervention programs for young children aim to reduce or eliminate stuttering, others aim to establish an acceptable level of stuttering as agreed by the parent and speech and language pathologist/therapist (Sidavi 2010). Some intervention programs also include an additional aim to enhance the child’s QoL and develop positive communication attitudes (Baxter 2015).
Non‐pharmacological interventions for stuttering in young children have been categorized in different ways within the literature. A commonly used distinction is between direct and indirect interventions (de Sonneville‐Koedoot 2015; Nippold 2018; Sidavi 2010). Direct approaches involve teaching the child’s parents to alter the child’s speech. Programs that are typically described as direct are those that include strategies such as reducing the child’s linguistic output within structured conversations, reinforcing target speech behaviors or teaching the child speech restructuring strategies to control their fluency (Franken 2007; Onslow 2017; Waelkens 2018). Indirect approaches involve training the child’s parents to create a fluency‐inducing environment. Programs that are typically categorized within this approach include strategies like teaching the parents to reduce their own speech rate or asking the child fewer questions (Franken 2007; Kelman 2017). This dichotomous categorization, however, is arguably problematic as intervention programs often include a combination of direct and indirect approaches (Franken 2007; Kelman 2017; Waelkens 2018). Considering this, it may be more accurate to describe intervention programs for stuttering as lying on a continuum, according to the proportion of direct and indirect strategies used.
How the intervention might work
Many non‐pharmacological interventions for stuttering have been developed for young children. However, research to date has not thoroughly investigated which components in available intervention programs are responsible for instigating change in a child’s stuttering (Bernstein Ratner 2018; Nippold 2018). The theoretical frameworks that underpin the intervention programs may, however, provide some insight into mechanisms. Interventions typically described as indirect interventions focus more on changing the child’s environment to induce fluency and are based on the theory that reducing the demands placed on the child’s speech will increase their capacity to produce stutter‐free speech (Starkweather 1990). Interventions typically referred to as direct interventions are designed to allow the child to practice the target motor speech pattern, in consistent stutter‐free speech, during treatment time. As stuttering is caused by a neurological processing deficit, it is hypothesized that, over time, this practice alters the child’s motor speech patterns, so that the child naturally speaks stutter‐free in daily conversations.
Assessing the impact of intervention
Stuttering pre‐ and post‐intervention is most commonly measured by assessing speech outcomes, such as the frequency of stuttering moments or stuttering severity. Speech and language pathologists/therapists or parents typically conduct these assessments (Guitar 2014). Stuttering frequency can be measured by calculating the percentage of stuttered syllables using a smartphone application or computer software program, etc. Stuttering severity can be rated on a Likert scale (Onslow 2017; Yairi 2015), based on observations of the child’s speech during clinic sessions or parents observations of their child throughout the day. Alternatively, or in addition, stuttering severity can be measured with a specific instrument that calculates an overall severity score based on the frequency of stuttering moments, and the duration and evaluation of types of stuttering behaviors produced, based on samples of the child’s speech (Riley 2009). Speech efficiency can also be measured to assess changes in speech, by calculating the number of words or syllables spoken per minute, mean length of utterance or rated naturalness of speech. To ensure that a representative measure of a child’s stuttering is obtained, measures of stuttering frequency and severity can be based on multiple 10‐ to 15‐minute speech samples, and preferably be video recorded (Guitar 2014; Riley 2009). Multiple speech samples across speaking situations and with different communication partners account for variability of stuttering. Video recordings, as opposed to audio‐only recordings, facilitate the identification of any non‐verbal stuttering behaviors. To conduct a holistic assessment of stuttering and the effect of intervention programs, the impact of stuttering can also be measured. Both parent‐report and child self‐report questionnaires can be used to assess the child’s reactions to their own stuttering or communication and the adverse effect that stuttering can have on QoL (Boey 2009; Langevin 2010; Vanryckeghem 2006).
Adverse effects
To our knowledge, few studies have examined potential adverse effects of non‐pharmacological stuttering interventions for young children. Of those that have, two studies reported no changes in child language skills after intervention (Bonelli 2000; Imeson 2018), and another indicated that there was no evidence of adverse effects on children who received intervention (Woods 2002). In contrast, a fourth study examined parents’ experiences in delivering the intervention, and found that some parents reported the use of particular behavioral reinforcements during the intervention that evoked a negative reaction, such as irritation or frustration, from their child (Packman 2007).
Why it is important to do this review
Over the last two decades, several systematic reviews and meta‐analyses have examined the evidence for non‐pharmacological interventions for stuttering; for a summary, see Appendix 1. None of these reviews, however, included a summary of studies focusing purely on interventions for young children, nor did they conduct moderator analyses to differentiate between treatment outcomes for different age groups or to assess the effect of interventions for stuttering in children under six years of age only. Therefore, we have no clear picture of how effective non‐pharmacological interventions for stuttering in young children are. As interventions for this age group typically differ in aim and content from those of older children and adults (Ambrose 2006; Onslow 2019), it is crucial to assess the effect of intervention for young children specifically. Once children grow older, stuttering becomes less tractable. This is thought to be attributable to declining neural plasticity of the brain with increasing age (Wohlert 2002). Consequently, interventions for older children and adults are believed to be less effective, and typically focus on methods to reduce stuttering in specific situations or to communicate more effectively with stuttering (Ambrose 2006).
In addition to the need to evaluate the evidence for the effectiveness of interventions for stuttering specifically in children of a young age, we note that previous systematic reviews in this area suffer from several other limitations. Nye 2013 used a restricted selection of databases in the literature search that may have limited the number of studies identified. While one of these databases included gray literature, no other procedures for identifying relevant gray literature were detailed and no gray literature was included in the review. Similarly, the gray literature was neither included in the search strategies nor the reviews by Baxter 2015, Bothe 2006 or McGill 2019. Given that null findings are less likely to be published (Borenstein 2009), the omission of gray literature from these reviews may have biased results in studies that aimed to assess the effects of interventions.
No prior meta‐analyses have calculated overall effect sizes for follow‐up data for stuttering interventions to assess the long‐term effects of the interventions. Nye 2013 did not summarize follow‐up effects due to no usable data for the calculation of an effect size in the included studies. Based on this, Nye 2013 saw a need for studies to be designed to assess the long‐term effects of each intervention, in order to address this issue. We will include an overall summary effect size for follow‐up, if available.
The latest published review that included a meta‐analysis of studies of children aged between birth and six years (and older children) was based on searches conducted in July 2012 (Nye 2013). As the field of non‐pharmacological interventions for stuttering is growing (Baxter 2015), a new systematic review and meta‐analysis is now called for.
Objectives
Primary objective
To assess the immediate and long‐term effects of non‐pharmacological interventions for stuttering on speech outcomes in children aged between birth and six years.
Secondary objective
To describe the relationship between intervention effects and participant characteristics (i.e. child age, child’s communication attitudes and the impact stuttering has on the child’s QoL).
Methods
Criteria for considering studies for this review
Types of studies
Randomized controlled trials (RCTs) in which groups have been established by random allocation, and quasi‐RCTs where the method of allocation is known but not considered strictly random (e.g. allocation based on birth date), compared with a) no intervention, b) a waiting‐list intervention or c) treatment as usual. Treatment as usual must not include the experimental treatment. We will exclude cross‐over trials.
Types of participants
Young children aged up to six years at recruitment. We will include studies that also involve children over six years of age provided we are able to isolate the data for children aged up to six years.
We will include studies regardless of time since stuttering onset, language(s) spoken or language abilities of the participants. We will not exclude relevant studies that have included participants with physical or intellectual disabilities (e.g. Down syndrome) provided the stuttering is developmental in nature and not acquired.
Types of interventions
All forms of non‐pharmacological interventions for stuttering in young children aged between birth and six years, including the use of electronic devices or smart phone applications. We will exclude all pharmacological interventions from the review.
Types of outcome measures
We will include measurements from standardized tests or speech samples conducted by the speech and language pathologist/therapist, or child and parent reports completed at pre‐intervention (if available), short‐term follow‐up (up to 12 months post‐intervention) and long‐term follow‐up (12 months or longer post‐intervention).
We will include studies that meet the above inclusion criteria regardless of whether they report on the primary and secondary outcomes listed below. We will use the primary and secondary outcomes to populate the 'Summary of findings' table.
If studies report on measures other than those listed below, we will describe such measures in an additional table, but will not report on them when synthesizing the results.
Primary outcomes
-
Stuttering frequency, measured by calculating percentage of syllables stuttered, percentage of words stuttered or stuttering‐like disfluencies, etc.
-
Stuttering severity, measured using severity rating scales or stuttering severity instruments (e.g. Stuttering Severity Instrument ‒ Fourth Edition; Riley 2009), etc.
-
Speech efficiency, measured by calculating the number of words or syllables spoken per minute, mean length utterance, speech naturalness or using self‐evaluation questionnaires, etc.
Secondary outcomes
-
Communication attitudes, measured by parent report or self‐report (e.g. KiddyCAT (Communication Attitude Test for Preschool and Kindergarten Children Who Stutter); Vanryckeghem 2006)
-
Impact of interventions for stuttering on emotional, cognitive and psychosocial domains, or QoL, measured by parent/caregiver report (e.g. Child Behavior Checklist; Achenbach 2000)
-
Adverse effects, as reported by the study authors, including negative self‐evaluation or less participation in communication
Search methods for identification of studies
The database searches will be shared between the Cochrane Information Specialist for Cochrane Developmental, Psychosocial and Learning Problems (CDPLP) and the review team. The Information Specialist will search the databases listed under Electronic searches, apart from Open Grey, which will be searched by the review team. The review team will also undertake the searches outlined in Searching other resources.
We will not limit the search by language, year of publication or type of publication.
Electronic searches
We will search MEDLINE using the strategy in Appendix 2, which we developed in consultation with the Cochrane Information Specialist for Developmental, Psychosocial and Learning Problems (DPLP). We will adapt the MEDLINE strategy for the databases listed below, using appropriate syntax and indexing terms where they are available.
-
Cochrane Central Register of Controlled Trials (CENTRAL; current issue) in the Cochrane Library, which includes the Cochrane Developmental, Psychosocial and Learning Problems Specialised Register.
-
MEDLINE Ovid (1946 onwards).
-
MEDLINE In‐Process & Other Non‐Indexed Citations Ovid (current issue).
-
MEDLINE E‐Pub Ahead of Print Ovid (current issue).
-
Embase Ovid (1974 onwards).
-
CINAHL Plus EBSCOhost (1937 onwards).
-
PsycINFO Ovid (1806 onwards).
-
ERIC EBSCOhost (1966 onwards).
-
Epistemonikos (www.epistemonikos.org).
-
Cochrane Database of Systematic Reviews (CDSR; current issue); part of the Cochrane Library.
-
Scopus Elsevier (1823 onwards).
-
speechBITE (speechbite.com/).
-
Open Grey (www.opengrey.eu/).
-
ProQuest Dissertations & Theses A&I (1743 onwards).
-
ClinicalTrials.gov (clinicaltrials.gov).
-
WHO ICTRP (apps.who.int/trialsearch).
Searching other resources
The first review author (ÅS) will search for studies not identified by our electronic searches by reviewing the reference lists of included studies as well as other relevant studies, book chapters and other systematic reviews. Another review author (HH) will handsearch the Journal of Fluency Disorders (from 1974 to date), a stuttering‐specific journal, which so far is not included in Cochrane's Handsearched Journals List (Cochrane 2019).
Four review authors (ÅS, EK, LSG, MK) will handsearch conference proceedings and programs from the stuttering‐specific conferences listed below, for all available years, for conference abstracts.
-
The World Congress of Fluency Disorders.
-
The Croatian Clinical Symposium of Stuttering.
-
The Oxford Dysfluency Conference.
-
The International Conference on Stuttering
The first review author (ÅS) will email relevant researchers identified through this search, on behalf of the review team, to identify other published or unpublished data from completed or ongoing studies for possible inclusion.
Data collection and analysis
Selection of studies
We will import all records identified by our searches into EndNote (EndNote 2014), and subsequently DistillerSR (DistillerSR 2008), for screening. We will identify and eliminate duplicate records in EndNote (EndNote 2014) and DistillerSR (DistillerSR 2008).
The screening process will consist of two stages. The first stage will involve screening titles and abstracts against the selection criteria (see Criteria for considering studies for this review). Two review authors (ÅS, LSG) will complete this stage of screening independently, ensuring full double screening. The second stage will involve double screening full‐text reports of potentially relevant studies. The same review authors (ÅS, LSG) will conduct this second stage of screening, also independently. We will report Kappa scores for inter‐rater agreement. We have piloted and revised the questions that we will use for both stages of screening. These questions are set out in Appendix 3 and will be added to DistillerSR (DistillerSR 2008). The review team will discuss any ongoing disagreements between the reviewers regarding the eligibility of a study or difficulties in retrieving information from studies at both stages of the screening process. We will code those studies as 'Studies awaiting classification' (Lefebvre 2019), and include them in the PRISMA chart (Liberati 2009).
Where a study report does not contain the information required to determine its eligibility for the review, we will contact the corresponding author of the paper and request the additional information. Provided the study is indexed by the aforementioned databases, and the title, abstract or key words are written in English, we will include eligible studies for full‐text screening, irrespective of the language the full text is written in. The review team are fluent in English, Norwegian, Danish, Swedish and German and therefore will be able to review studies written in any of these languages. Studies that we consider relevant based on the title and abstract but that are written in any other language will be translated. We will develop a PRISMA flow chart to describe every step of the selection process (Liberati 2009).
To ensure we do not treat publications from the same study as independent studies, we will use the first publication as the primary reference. We will also report on the latest publication pertaining to follow‐up data (Borenstein 2009). In cases where it is unclear to the review authors whether two or more publications are based on the same sample, the first review author (ÅS) will contact the study authors for clarification.
Data extraction and management
After screening and selecting eligible studies, two review authors (ÅS, EK) will independently extract the required data from the included studies using DistillerSR (DistillerSR 2008). They will resolve any differences in opinion by discussion with a third review author (K‐ABN).
A data extraction form is under development. Based on the checklist provided in Table 5.3.a in the Cochrane Handbook for Systematic Reviews of Interventions (Li 2019), it will include (but not be limited to) the categories listed below.
-
Information about data extraction from reports (title, unique identifier and date of publication, etc.)
-
Eligibility criteria (reason for inclusion)
-
Study design and method (RCT or quasi‐RCT)
-
Participants characteristics (sample size, age, sex, country of origin, language spoken, presence of comorbidities, stuttering severity or frequency (or both) at recruitment, time since stuttering onset)
-
Intervention program details (name of intervention program; intervention provider; method of delivery; timing, frequency and duration of clinical visits; treatment provided at home, etc.)
-
Outcomes and outcome measures (any measures related to primary or secondary outcomes; see examples of measures under Types of outcome measures)
-
Results (number (n) allocated to each intervention group, missing participants, summary data for each intervention group (e.g. 2×2 table for dichotomous data, means and standard deviations for continuous data), estimate of effect with confidence intervals (CI), P value, subgroup analyses, etc.)
-
Miscellaneous details (key conclusion(s) from study authors, comments from study authors, required correspondence(s) with study authors to retrieve data, review authors' own comments on study, etc.)
See Appendix 4 for the draft data extraction form.
Once the review team agrees on the collected data, the first review author (ÅS) will enter the data into Review Manager 5 (RevMan 5) (Review Manager 2014), Cochrane’s recommended software program. Another review author (HH) will then cross‐check all entered data.
Assessment of risk of bias in included studies
We will assess the risk of bias in included studies using Cochrane's revised 'Risk of bias' tool for randomized trials (RoB 2; Sterne 2019). This review is interested in the effect of assignment or the 'intention‐to‐treat' effect. We will assess risk of bias for each result from each study that contributes to the primary and secondary outcomes at post‐intervention. Two review authors (ÅS, LSG) will independently use the RoB 2 signalling questions (Appendix 5) to form outcome level judgments of material risk of bias for the following five domains: (1) bias arising from the randomization process; (2) bias due to deviations from intended interventions; (3) bias due to missing outcome data; (4) bias in measurement of outcome; and (5) bias in selection of the reported outcome (see Appendix 6 for more details on domains). RoB 2 also allows for a judgment of overall risk of bias for each included study: low risk of bias; some concern of bias; or high risk of bias. We will assign a rating of 'low risk of bias' to studies considered at low risk of bias for all five domains for the specific result. We will assign a rating of 'some concern of bias' to studies we judge to be at high risk of bias in at least one domain for the result in question. We will assign a rating of 'high risk of bias' to studies where there is a high risk of bias in at least one domain for a result or we judge the study to have some concerns for multiple domains in a way that substantially lowers confidence in the result (Sterne 2019). Both review authors will resolve conflicting ratings by discussion. If necessary, a third review author (K‐ABN) will arbitrate. We will present completed 'Risk of bias' tables and justifications for each judgment in the published review.
The specific outcomes of interest are the primary and secondary outcomes listed in the Types of outcome measures section.
Measures of treatment effect
Continuous data
We anticipate that data from the included studies will be mainly continuous. In instances where included studies use the same continuous outcome measure (e.g. percentage of syllables stuttered), we will estimate the intervention effect using the mean difference (MD) and present it with the 95% CI. When studies have used different outcome measures to assess the same construct (e.g. severity rating scales with different scale descriptors), we will calculate the standardized mean difference (SMD) and present it with 95% CI.
Dichotomous data
If studies report dichotomous data (e.g. the occurrence of non‐verbal stuttering behaviors), we will express these data as risk ratios (RR) and present them with 95% CI. Following guidance from Higgins 2019 (Section 6.4.1.1), we will convert any results reported as odds ratios (OR) to RR before interpreting them. When the data are actually continuous but have been measured in a dichotomous manner, we will transform the OR to an SMD effect size (e.g. measures under or over a specified stuttering severity or frequency score). We will calculate the SMD using Hedges' g, interpreting effect sizes ranging from 0.0 to 0.30 as small, more than 0.30 to 0.80 as moderate, and greater than 0.80 as large (Cohen 1988).
Unit of analysis issues
Cluster randomization
If we conduct a meta‐analysis, we will examine the level at which randomization occurred. In RCTs of children who stutter, participants are typically randomized at an individual level. However, where cluster randomization has been used to assign participants to groups (e.g. according to district, kindergarten), we will use an intra‐class correlation coefficient (ICC) to convert studies to their effective sample size before using the data in the meta‐analysis. If the information to calculate an ICC is not available from the included study's report, or the data were not analyzed appropriately by the study authors, the first review author (ÅS) will contact the study authors to retrieve the information needed. In cases where we are not able to obtain this information from the study authors, we will aim to gather external estimates from similar studies (Campbell 2000).
Studies with multiple treatment arms
If some of the included studies compare more than one intervention to a control group, we will combine the intervention groups to form a single intervention group before comparing it with the control group, in order to avoid double counting the participants in the control group.
Dealing with missing data
In cases of missing data, the first review author (ÅS) will contact the author(s) of the study, wherever possible, to request the unreported data. Where these are not provided, or it is not possible to provide them (e.g. attrition or when the child did not appear at a test point), we will use the nature of the data (i.e. whether they are missing at random or not missing at random) to decide on how to manage the non‐reported data. We will describe the missing data based on the information available in the study report.
We will note any missing data on the data extraction form (Appendix 4), and in the 'Risk of bias' table, and discuss the extent to which the reported missing data are likely to influence the results of the study in the Discussion section, as suggested by Deeks 2019.
Where we judge data to be missing at random, removing observations with missing values can produce a bias. We will therefore describe each study’s potential bias in the 'Risk of bias in included studies' section. We do not expect to have the data to be able to use replacements values. However, we will conduct a sensitivity analysis to determine the potential impact of the missing data on the findings of our review (see Sensitivity analysis), which we will also explore in the Discussion section of the review.
Assessment of heterogeneity
We will assess clinical heterogeneity between studies by examining the distribution of participant characteristics (e.g. age, stuttering severity), characteristics of interventions used (e.g. intervention program), and variability in outcomes reported (e.g. results from different speech outcome measures). Similarly, we will assess methodological heterogeneity between studies by examining variability in study design and risk of bias. We will also discuss any unexpected variability.
To assess statistical heterogeneity, we will use the Chi² test, which provides evidence that variation in effect is caused by heterogeneity and not by chance. The Chi² test might, however, have low power in the meta‐analysis if a small number of studies are included or the included studies use small samples. Therefore, as suggested by Deeks 2019, we will use a P value of 0.10 to determine statistical significance. We will also report Tau² as a measure of between‐study variability when reporting the results of the random‐effects model. We will further assess the degree of heterogeneity across studies using the I² statistic. We will interpret the I² statistic in line with Section 10.10.2 of the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2019) as follows.
-
0% to 40%: might not be important.
-
30% to 60%: may represent moderate heterogeneity.
-
50% to 90%: may represent substantial heterogeneity.
-
75% to 100%: considerable heterogeneity.
If we identify statistically significant, unexplained heterogeneity, we will interpret the results with caution.
Assessment of reporting biases
If we are able to pool data from 10 or more studies in a meta‐analysis, we will create funnel plots using RevMan 5 (Review Manager 2014), to assess reporting bias. When interpreting these results, we will consider possible explanations for funnel plot asymmetry, including true heterogeneity of effect with respect to sample size, bias of small trials, and publication bias (Deeks 2019).
Data synthesis
If data are available from at least two studies considered to be clinically homogenous, we will undertake a meta‐analysis using RevMan 5 (Review Manager 2014). We will synthesize the data using a random‐effects model, as we expect the effect size to vary between studies, and we will make inferences that are as broadly generalizable as possible. A random‐effects model will account for variations between studies by increasing the standard errors and CI (Cook 2002). However, as a limited number of studies will create uncertainty in estimates of between‐studies variance (Tau²), we will also perform an analysis based on a fixed‐effect model, to detect differences between the two calculations (Deeks 2019). We will interpret the results giving due consideration to any differences between them as well as the number of studies.
We will conduct the analyses to assess the effect of non‐pharmacological interventions for stuttering in children aged between birth and six years old at immediately post‐intervention. In addition, we will use follow‐up data to assess maintenance of treatment effect. If meaningful, we will pool data separately for short‐term follow‐up (up to 12 months post‐intervention) and long‐term follow‐up (12 months or longer post‐intervention).
In the case that we are unable to perform a meta‐analysis, or we identify only one study reporting on an outcome, we will provide a narrative summary of the available data.
Summary of findings
Having imported data from RevMan 5 (Review Manager 2014), we will create a ‘Summary of findings’ table for each comparison, using the GRADEprofiler Guideline Development Tool (GRADEpro GDT). We will report the outcomes listed in the Types of outcome measures section in these tables at post‐intervention.
Two review authors (ÅS, EK) will independently assess the quality of the evidence for each outcome, and assign ratings of high, moderate, low or very low quality, according to the presence of the five criteria listed below and depicted in MECIR Box 14.2.a in the Cochrane Handbook for Systematic Reviews of Interventions (Schünemann 2019).
-
Within‐study risk of bias (methodological quality)
-
Directness of evidence
-
Heterogeneity
-
Precision of results
-
Risk of publication bias
Subgroup analysis and investigation of heterogeneity
Where possible, we will analyze subgroups by conducting a moderator analysis, to test for intervention effects by subgroup interactions. If we include sufficient data in the meta‐analysis, we will explore the possible sources of clinical heterogeneity, by conducting the following subgroup analyses.
-
Age of participants (up to four years of age, up to six years of age)
-
Intellectual disabilities (children with and without intellectual disabilities)
-
Stuttering severity (categories will depend on the data included in the studies)
-
Sex of participants (girls only and boys only)
-
Time since stuttering onset (up to two years post‐stuttering onset, more than two years post‐stuttering onset)
Sensitivity analysis
We will perform the following sensitivity analyses to explore the influence of publication status and overall risk of bias on effect size.
-
Repeating the analysis excluding unpublished studies
-
Repeating the analysis excluding studies where the overall risk of bias is high
