Behavioral Stuttering Interventions for Children and Adolescents: A Systematic Review and Meta-Analysis

Review

Behavioral Stuttering Interventions for Children andAdolescents: A Systematic Review and

Meta-AnalysisChad Nye,a Martine Vanryckeghem,a Jamie B. Schwartz,a Carl Herder,b Herbert M. Turner III,c and

Courtney Howardd

Purpose: To evaluate the effectiveness of behavioralinterventions designed to treat stuttering in children.Method: Studies were included for review if (a) the treatmentwas a behavioral intervention, (b) participants were between 2and 18 years old, (c) the design was an experimental or quasi-experimental group design, and (d) the reported outcomemeasure assessed stuttering.An electronic search of 8 databases yielded a total of 9

studies, representing 327 treated participants across 7different intervention types. Data were extracted forparticipant, treatment, and outcome characteristics as well asfor methodological quality.

Results: An analysis of the treatment effects yieldedsignificant positive effects approaching 1 SD when comparedwith a nontreatment control group. No significant differencesemerged for studies comparing 2 different treatments.Conclusion: Conclusions drawn from the extant researchsuggest that data to support the efficacy of behavioralintervention in children exists for a limited number ofintervention strategies, based on a meager number ofmethodologically acceptable studies.

Key Words: stuttering, systematic review, children, efficacy

The treatment of stuttering in children and adultsusing both pharmacological and behaviorally basedtreatments has a long history of research interest.

Studies starting in the 1950s have focused on a variety oftreatments, including the effects of carbon dioxide therapy(Smith, 1953), stimulants (Fish & Bowling, 1965), sedatives(Derazne, 1966), neuroleptics (Rantala & Petri-Larmi, 1976),and antipsychotics (Maguire, Riley, Franklin, & Gottschalk,2000). In a recent systematic review, Bothe, Davidow,Bramlett, Franic, and Ingham (2006) concluded that the useof pharmacological treatment for stuttering resulted in, atbest, conflicting data in terms of the treatments’ effects onspeech, while producing potentially serious negative sideeffects and risks.

Although pharmacological intervention continues tobe of interest to both the researcher and clinical professional(Maguire et al., 2010), behavioral intervention for thetreatment of stuttering is a frequently used approach(Costello, 1983; Onslow, Packman, & Harrison, 2003; Ryan,2001; Starkweather, Gottwald, & Halfond, 1999). Itseffectiveness has been the topic of investigation for morethan eight decades. Behaviorally based treatment approachesfor stuttering have been generally defined as interventionsthat involve a change in speech behavior through (a) thedirect modification of a person’s stuttering, (b) operantprocedures, or (c) an integration of both approaches.

An early comprehensive and seminal review ofstuttering intervention approaches (R. J. Ingham &Andrews, 1973) summarized the major behavioral interven-tions for stuttering up to 1971. Results of this reviewindicated that rhythmic speech, prolonged speech, andconditioning showed the greatest clinical promise. Theauthors’ conclusions brought attention to the need to focuson, and systematically investigate, the efficacy of behavioraltreatments of stuttering.

R. J. Ingham and Lewis’s (1978) review focused on theabsence of a definitional consistency for behavioral inter-vention that could be used to generally describe thetreatment of stuttering. R. J. Ingham and Lewis identifiedthree factors that, according to them, could be understood ascommonalities across behavioral stuttering therapies,

aUniversity of Central Florida, OrlandobAmerican Institute for Stuttering, New York, NYcAnalytica, Phoenixville, PAdAdvantage Therapy, Springfield, MO

Correspondence to Chad Nye: [email protected]

Courtney Howard is now with Sunbelt Staffing, Tampa, FL.

Editor: Jody Kreiman

Associate Editor: Hans-Georg Bosshardt

Received January 31, 2012

Revision received May 10, 2012

Accepted October 9, 2012

DOI: 10.1044/1092-4388(2012/12-0036)

Journal of Speech, Language, and Hearing Research N Vol. 56 N 921–932 N June 2013 N � American Speech-Language-Hearing Association 921

including (1) ‘‘measures of relevant dimensions of speechbehavior, (2) therapy design, and (3) application of theclinical procedures designed to modify stuttering behavior’’(pp. 126–127). In both of these reviews, R. J. Ingham andcolleagues were critical of the state of knowledge that couldbe gleaned from the available research and made a point thatnone of the studies would be scientifically rigorous enough tosupport the use of many of the existing behavioral treatmentprograms in use at that time.

In the first meta-analytic application to study theeffects of stuttering treatment, Andrews, Guitar, and Howie(1980) summarized the typical treatment effects for indivi-duals who stutter. The results of the data analysis, of 42included studies, suggested that interventions using pro-longed speech, gentle onset, and rhythm resulted in thegreatest improvement in the treated participants. Further,Andrews et al. suggested that the strongest predictor oftreatment effect was the number of hours a client wastreated, with a minimum of 100 hours needed to produce asubstantial improvement in fluency.

Adams (1984) reviewed studies published from 1977 to1982 and identified the emergence of direct therapy forchildren as well as formal programs (e.g., prolonged speech)that were reported to be clinically effective approaches tothe treatment of stuttering. Adams further noted the absenceof studies with sufficient sample sizes and data to supportclaims for long-term treatment effects. In addition, Conture(1996) reported that the efficacy of stuttering treatment dataoften failed to reveal the ‘‘daily life’’ activities of individualswho stutter. In general, Conture interpreted the overallfindings as indicating that treatment for stuttering across allage groups revealed an improvement in approximately 70%of the treated participants.

Information relative to relapse after treatment forstuttering was critically examined by Craig (1998). In thisarticle, Craig concluded that the stuttering interventionapproaches reported in the literature to date providedevidence of substantial reductions in the immediate post-treatment measures. However, in the same literature,evidence to support the long-term maintenance of these gainswas noticeably absent. Craig drew support for these reviewconclusions using a retrospective ‘‘file-drawer’’ study ofmultiple treatment groups measured along a continuoustimeline. The data showed a significant decrease in stutteringin the immediate post-treatment measurement and a weakcorrelation between immediate post-treatment measure andlong-term maintenance of fluency outcomes at 12–18 monthspost-treatment.

Thomas and Howell (2001) summarized stutteringtreatment research reported from 1993 to 2001. Eighttreatment studies were analyzed on the basis of the 11specific criteria proposed by Mocicki (1993) as necessary forefficacy research studies, including defining the treatmentoutcome, reliability/validity of the outcome measure, nosource of bias in the analysis, appropriateness of dataanalysis, treatment described, adherence to treatment pro-tocol, sample size, control data, no source of bias in thedesign, follow-up, and baseline. Although Thomas and

Howell compared multiple treatment studies, there was noattempt to combine data across studies or to conduct ameta-analysis.

More recently, in a collaborative effort among severalresearchers to re-evaluate the stuttering treatment efficacyinformation, five articles were published in the Journal ofFluency Disorders (edited by Bothe, 2003) to collectivelyaddress the concept of evidence-based treatment. Theauthors of each article offered a critical evaluation of thebasic scientific needs that should be part of the research onstuttering intervention. J. C. Ingham (2003) concluded thatthe gold standard for experimental clinical trials, therandomized controlled trial (RCT), is rarely reported in theresearch literature. Finn (2003) articulated the notion that, inmost stuttering treatment studies, outcomes of stutteringinterventions are not clearly defined in order to reflectclinical significance, whereas Langevin and Kully (2003)expressed concern about the lack of carryover from evidence-based research into clinical practice. Onslow (2003) arguedfor the need to use evidence-based treatment in place of themore popular assertion-based treatments and for empower-ing clinicians in the use of empirical efficacy research forclinical decision-making.

After the 2003 compilation of articles addressingdifferent facets related to evidence-based treatment ofstuttering, Bothe, Davidow, Bramlett, and Ingham (2006)conducted a systematic review focusing on a trial qualityassessment of published research on behavioral, cognitive,and related approaches. The review of treatment approacheswith children and adults was qualitative in nature. Botheet al. used broad-based inclusion criteria that allowed fordifferent study designs (e.g., single-subject designs, RCTs,quasi-experimental designs [QEDs]) involving adult and childparticipants and a variety of outcome variables. The reviewused five methodological criteria and four treatment out-come criteria that were described as more ‘‘lenient’’ criteriarequirements (pp. 322, 323, 332). Bothe and colleagues’descriptive analysis revealed that, for preschoolers, response-contingent treatment (which forms the basis for theLidcombe program, for example) produced the most changesin stuttering behavior. Adolescents and adults seemed tobenefit most from prolonged speech procedures. These—incombination with self-management, performance-contingentmaintenance, and infrastructural variables—appeared to bethe keys to success.

At the time of this writing, there is a substantial bodyof accessible evidence available for assessing the efficacy ofbehavioral stuttering interventions. As described above,some of these studies have opted for a descriptive rather thana quantitative meta-analysis approach. Relative to theirstudy, Bothe, Davidow, Bramlett, and Ingham (2006) stated,‘‘Meta analyses that combined different types of stutteringtreatments were deemed of less interest to this project thandescriptive analyses of the effects of specified treatmentapproaches’’ (p. 325). Few attempts have been made toprovide a quantitative summary of treatment evidence todetermine the scientific basis for stuttering interventions;thus, a systematic review and meta-analysis of the best

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available evidence assessing stuttering intervention effects iswarranted. The ultimate goal in the area of stutteringintervention would be to provide a quantitative standard thatcan serve as a guide for the development of evidence-basedpractice and policy decisions, upon which successful stutter-ing intervention with children could be based. Morespecifically, this review provides a quantitative assessment ofthe effectiveness of behavioral interventions aimed atimproving the speech fluency of children and adolescentsbetween the ages of 2 and 18 years.

Method

The methodological approach taken for this systematicreview involved the establishment of the criteria to be used inall searches for the relevant studies to be included. Thosecriteria addressed procedures for study inclusion, studyretrieval, study selection, data extraction, and data analysis.

Study Inclusion

In order to minimize a study selection bias and to guidereviewers in the determination of those studies to be includedin this review, the following criteria were established at theoutset of the study. It was determined that only RCTs andQED studies of two or more groups would be included.Studies that utilized pre-experimental (i.e., single-group pre-test–post-test only) designs (Campbell & Stanley, 1963), single-subject designs, or qualitative approaches were not includeddue to the absence of adequate control group conditions,limitations to the interpretation and generalization of findings,and the lack of statistical procedures available to integrate theresults from studies with different research designs.

Participants of the included studies for this reviewwould be children and adolescents, preschool through highschool, ranging in age from 2 to 18 years. All participants inboth the intervention and control/comparison groups had tohave been identified as people who stutter. In addition to thedesign and participant characteristics, only studies thatmeasured a behavioral intervention for stuttering (i.e., anyintervention that seeks to change the physical speechproduction such as behavioral modification, desensitization,fluency shaping, parent training) were included.

Studies were excluded from this review if they involved(a) only pharmacological interventions for stuttering (in theevent that a study investigated both behavioral andpharmacological interventions, behavioral interventions wereincluded only if there was an accompanying behavioralcontrol group for comparison); (b) children below the age of2 and above the age of 18; and (c) only outcome measuresother than speech production, such as measures of attitude,emotional status, or observer ratings.

Study Retrieval

Prior to initiating the search for relevant studies,substantive terms for each of the following categorieswere identified and used as the key terms for all searches:(a) domain terms: Stutt*, Stam*, Fluency; (b) intervention

terms: Therap*, Treat*, Interven*; and (c) target populationterms: elementary, ‘‘young children’’, adolescen*, ‘‘highschool’’, ‘‘secondary students’’, ‘‘primary education’’,preschool*, schoolage.

Six electronic databases were searched for appropriatestudies from the earliest indexed date of each databasethrough July 2012. These databases included ERIC (1966–present), PsycINFO (1887–present), PubMed (1966–present),CINAHL (1982–present), Cochrane Central Register ofControlled Trials (1898–present), and Proquest Dissertations& Theses Full Text (1861–present). The thesaurus from eachdatabase was consulted where available to ensure that allappropriate synonyms had been included in the disorder andintervention categories. In addition, reference lists fromreviews and original studies meeting the inclusion criteriawere searched for additional citations.

Study Selection

The inclusion of studies was achieved by implementinga two-stage process: Stage 1, title and abstract screening, andStage 2, full-text manuscript screening. At Stage 1, thecitations and abstracts obtained during the individualdatabase searches were evaluated independently by twotrained students in speech-language pathology and werejudged to be potentially eligible to advance to Stage 2 of theinclusion process if they met any one of the followinginclusion criteria: (a) studies of behavioral treatment ofstuttering; (b) studies whose participants were between theages of 2 and 18 years; (c) studies that reported the use of anRCT or QED; or (d) studies that reported outcome measuresthat related to stuttering (e.g., percentage of syllables orwords stuttered, words spoken per minute).

Studies that met Stage 1 criteria were advanced toStage 2, in which a full text of the study was obtained andevaluated independently by the two trained students. Inorder to be included in the final review, a study had to meetall four of the criteria listed above. In the event of adisagreement, or if a question regarding the inclusion of aparticular study at either stage of the inclusion decisionprocess arose, the first author rendered a final inclusiondecision.

Data Extraction

The process of data extraction involved the coding foreach study across four primary dimensions: design char-acteristics, participant characteristics, intervention charac-teristics, and outcome characteristics. The coding of allincluded studies was conducted independently by two trainedstudents in speech-language pathology. The first authorverified all coding. Any discrepancy in coding was resolvedthrough consultation with the second author. The proce-dures used for data extraction are described below.

Research design characteristics. Each study was codedfor design features such as design type (RCT or QED)and method of assignment (random or nonrandom). Inaddition, for each design, it was indicated whether indivi-dual, group, or matching procedures were used. The number

Nye et al.: Stuttering Treatment in Children 923

of participants in experimental and control groups, how theywere recruited, and the number of participants who droppedout (attrition) between the pre- and post-test measurementwere indicated as well. Finally, information on presence ofblinding was coded in terms of whether or not it occurredand, if so, who was involved (e.g., researcher, participant, orassessor), and under what condition (e.g., participantselection, group assignment, pretreatment assessment, post-treatment assessment).

Participant characteristics. Each study was coded forparticipant characteristics such as age, gender, socioe-conomic status, school grade level, and any co-morbidconditions that might be present (e.g., language disorder,articulation disorder).

Intervention characteristics. Coding occurred based onthe type of behavioral intervention, length of the interventionprogram, length of time per session, and number of sessions.

Outcome characteristics. Each study was coded for thespecific behavioral outcome reported (e.g., number orpercentage of stuttered syllables or words per minute,syllables or words spoken per minute).

Assessment of Methodological Quality

The quality of the methodological rigor of a study canhave an important impact on the magnitude of the treatmenteffect. Individual study methodological quality was coded forfeatures of design (e.g., allocation, attrition, blinding,statistical analyses); participant characteristics (e.g., age,gender, socioeconomic status); intervention characteristics(e.g., parent training, behavior modification); and outcomecharacteristics (e.g., syllables or words stuttered; a completecoding form is available upon request).

In order to provide a quantitative assessment of themethodological quality of the included studies, each full-textstudy was analyzed using the Downs and Black (1998)checklist. Downs and Black presented an empiricallyvalidated instrument in which two reviewers (i.e., the firstauthor and a statistical consultant) independently evaluateeach study using a checklist to assess four categories ofmethodological quality: (a) reporting, (b) external validity,(c) internal validity bias, and (d) internal validity confound-ing. A fifth category, power, is provided in the checklist.However, due to inherent difficulties in coding criteria(N. Black, personal communication, March 15, 2010), thisitem was omitted from the analysis.

Calculating and Interpreting Effect Size

All data needed for calculating effect size wereanalyzed using the Comprehensive Meta-Analysis (CMA;Borenstein, Hedges, Higgins, & Rothstein, 2005) software.All individual outcome effect sizes were calculated using thestandardized mean difference statistic weighted by theinverse variance to allow larger n studies to contributeproportionately in any effect size average. In the event thatno summary statistics were provided (e.g., F value, t value)and individual outcome data were available, the mean and

SD were calculated by the authors and converted to an effectsize using CMA.

In order to maximize the interpretation of thecalculated treatment effect, all effect sizes were calculatedusing a 95% confidence interval (CI). Because of thepotential variability of sample sizes across studies, allreported effect sizes were calculated using Hedges’s g toproduce a standardized mean difference with a smallsample size bias correction factor. Effect sizes ranging fromg = 0.0 to g = 0.30 are defined as small, those ranging fromg = 0.30 to g = 0.80 are defined as moderate, and those inwhich g > 0.80 are defined as large (Cohen, 1988).

Synthesizing Effect Sizes

The average of effect sizes must (a) maintain theindependence of multiple effect sizes generated by a singlestudy, (b) account for effect size variations beyond samplingerror (heterogeneity), (c) allow for the assessment of theimpact of independent variables on treatment effects(moderators), and (d) account for potential bias in studyselection (publication bias). Because the average of multipledifferent effect sizes within a single study would not providea substantively interpretable result, all effect sizes wereaveraged across behaviorally similar outcome measures ofthe dependent variable. The resulting effect size representedthe magnitude of treatment effect for a specific outcomeacross all studies reporting that outcome. For example, ifStudy A reported number of stuttered syllables and Study Breported percentage stuttered syllables, an effect size (i.e.,Hedges’s g) was calculated for each study, and both studieswere included in an average of studies reporting stutteredsyllables. No across-study average was conducted for two ormore conceptually different outcome effect sizes. Forexample, if Study A reported stuttered words per minute,and Study B reported percentage stuttered syllables, thetwo outcomes would not have been combined into a singleeffect size.

Heterogeneity Analysis

The heterogeneity analysis allows for an assessment ofthe amount of variation in the calculated effect beyond whatis expected due to sampling error. Using the random effectsmodel provides the most defensible approach for theanalysis of treatment effects in light of several critical andreasonable assumptions about intervention research. Thereason for this is that (a) the random model assumes thepossible existence and potential impact of additional studiesthat are not included, thus allowing for a generalizableconclusion that takes into account the possibility of thosemissing studies, and (b) the random model assumes thatthere is substantial variation in one or more of the inde-pendent variables that might account for differences intreatment effects (e.g., not all studies use exactly the sameintervention protocol or intervention dosage), suggestingthat there would not be a functional equivalence among theincluded studies in terms of the quality or nature of theintervention programs.

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Results

Information Retrieval for Included and ExcludedStudies

Eight electronic databases were searched for potentialstudies to include in this review. The electronic search yielded3,271 citations across the following databases: AcademicPremier (n = 677), CINAHL (n = 0), Cochrane CentralRegister of Controlled Trials (n = 54), Database of Abstractsof Review Effects (n = 16), Dissertations & Theses (n = 91),ERIC (n=420),PubMed (n=1,141), andPsycINFO(n=872).

These 3,271 titles and abstracts were evaluated foradvancement to a full-text retrieval stage based on theinclusion criteria described earlier. A total of 2,959 citationswere excluded as not meeting the inclusion criteria, with mostof the citations being eliminated due to (a) nontreatment,(b) duplicate indexing across databases, (c) single-subject orpre-experimental design, or (d) pharmacological interven-tions. Full texts of the remaining 312 citations were obtainedand evaluated by two independent reviewers as to whetheror not the studies met all required inclusion criteria. Thereview of the full texts reduced the number to a total of ninestudies that met all four inclusion criteria: domain, age,design, and outcomes.

Summary of Included Studies

As can be seen in Table 1, a total of nine studies metthe inclusion criteria for analysis, with eight studies using anRCT design. Of the eight RCTs, four used the Lidcombeprogram as the experimental intervention, with three studies(Harris, Onslow, Packman, Harrison, & Menzies, 2002;Jones et al., 2005; Lattermann, Euler, & Neumann, 2008)providing an immediate post-intervention assessment com-parison of the treatment and control groups’ fluency. Thefourth study assessed treatment effects at 9 months post-intervention (Lewis, Packman, Onslow, Simpson, & Jones,2008). Of the remaining four RCT studies, two, once again,dealt with the Lidcombe program in some way. In the

Harrison, Onslow, and Menzies (2004) study, four Lidcombeprogram groups with and without parental verbal con-tingencies for stuttering and severity ratings were compared.The other study by Franken, Boves, Peters, and Webster(2005) compared Lidcombe to a different treatment program(demands and capacities model [DCM]). Finally, theremaining two RCT studies were designed to provide acomparison of two different treatment groups (Riley &Ingham, 2000; Ryan & Ryan, 1995).

The other included study (Craig et al., 1996) used aQED with a nonequivalent control group to assess thetreatment effect among children who stutter (CWS) throughthe use of three intervention approaches—intensive smoothspeech (ISS), intensive electromyography feedback (EMG),and home-based smooth speech (HSS)—in three interventionenvironments: clinic, home, and phone. Thus, Craig et al.provided treatment results in which the experimental groupswere compared both with a nontreatment control conditionand across different treatments.

The list that follows is a general description of thetreatment programs identified in the included studies.

1. Delayed auditory feedback (DAF). The client hears hisor her own speech with, typically, an initial delay of250 ms. This delay in auditory feedback produces aslowed, prolonged speech that results in a reduction ofstuttering. Gradually, the delay is decreased to zero in50-ms decrements.

2. Gradual increase in linguistic complexity of utterance(GILCU). This is a step-by-step structured fluency-shaping program based on operant conditioningtechniques. Fluency is established on a one-word levelby means of slowed speech. Words are graduallycombined to connected speech at the sentence level.

3. Speech motor training (SMT). This involves oralmotor coordination, sentence formulation, and audi-tory processing. The client moves from the productionof modeled nonsense syllables of increasing difficulty

Table 1. Summary of the design, participant, treatment, and outcome characteristics for each of the included studies.

Study Design MQR Treatment groups NAge range(yrs;mos) Program length

Outcomesmeasured

Ryan & Ryan (1995) RCT 14 DAF, GILCU 20 7;0–17;0 UTD SW/M,WS/M,%SSCraig et al. (1996) QED 17 EMG, ISS, HSS, control 97 9;0–14;0 1 wk, 1 wk, 4 wks %SS, SPMRiley & Ingham (2000) RCT 16 SMT, ELU 12 3;8–8;4 UTD %SSHarris et al. (2002) RCT 19 LP, control 23 2;0–4;11 12 wks %SSHarrison et al. (2004) RCT 21 LPa 38 2;0–5;11 4 wks %SSJones et al. (2005) RCT 21 LP, control 47 3;0–6;0 UTD %SSFranken et al. (2005) RCT 17 LP, DCM 23 < 6;0 ≤ 12 wks %SSLattermann et al. (2008) RCT 18 LP, control 45 3;0–5;11 16 wks %SSLewis et al. (2008) RCT 20 LP, control 22 3;0–4;6 9 mos %SS

Note. MQR = methodological quality rating; DAF = delayed auditory feedback; GILCU = gradual increase in linguistic complexity of utterance;EMG = electromyography feedback; ISS = intensive smooth speech; HSS = home-based smooth speech training; SMT = speech motor training;ELU = extended length of utterance; LP = Lidcombe program; DCM = demands and capacities model; UTD = unable to determine; SW/M =stuttered words per minute; WS/M = words spoken per minute; %SS = percentage syllables stuttered; SPM = syllables spoken per minute.aFour Lidcombe program groups with and without parental verbal contingencies for stuttering and severity ratings.

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to connected speech, controlling for number ofsyllables and rate of production.

4. Extended length of utterance (ELU). The client’sverbal output is gradually increased in length. Thisprocedure is combined with operant conditioningprinciples. Fluency is established from the sound levelto the mono- and multisyllabic word level, to wordcombinations, and, ultimately, to a monologue andconversational level.

5. EMG. This technique involves reducing excessivemuscular tension in the articulators. The techniqueinvolves some form of assistive device whereby surfaceelectrodes linked to a particular muscle at the site ofthe larynx, lip, chin, or jaw produce electricalpotentials in the underlying muscles. The clientmonitors the level of muscular tension by means of avisual or auditory signal. The goal of biofeedback is toproduce tension reduction in the muscles until aparticular threshold has been reached.

6. Smooth speech (including ISS and HSS). This programis based on prolonged speech principles. It includesgradual phonatory initiation, the production of stopconsonants in a nonobstructive way, and smoothtransition between words.

7. Lidcombe program. This program is an interventionprogram predominantly for preschool children inwhich parents are trained to identify and shape fluentand disfluent utterances through the use of verbalcontingencies.

Using CMA, all effect size statistics were calculatedincluding Hedges’s g, the 95% confidence interval (CI), andthe associated p value. Because not all salient features of theincluded studies are homogeneous (e.g., participant charac-teristics), a random effects model was used to assess themagnitude of the treatment effect. The total number of CWSwas 327. They ranged in age from 2 to 17 years. Seventy-sevenpercent of them were male, and 23% were female. Across thenine included studies, the following outcomes were measuredby either a raw score count, percentage, or units per minute:stuttered words per minute (SW/M), percentage syllablesstuttered (%SS), words spoken per minute (WS/M), andsyllables spoken per minute (SPM). A complete summary ofthe design, participant, treatment, and outcome character-istics is provided for each study in Table 1.

Data Analysis

The analysis of the data for this review was organizedaccording to types of study designs (i.e., RCT and QED) that(a) compared a treated CWS group with a nontreated CWSgroup (i.e., treatment vs. control) and (b) compared twogroups of CWS that received different treatments (i.e.,Treatment 1 vs. Treatment 2). When a sufficient number ofstudies are available for meta-analysis, a sensitivity, pub-lication bias, and moderator analysis may be applied toprovide potential further explanation of treatment effects.However, none of these analyses were appropriate due to

the small number of studies available. Thus, the resultsreported are limited to a single meta-analysis, with theremaining data presented in a descriptive format.

Methodological Quality

Assessment of the methodological quality of theincluded studies was accomplished using the Downs andBlack Checklist (1998) to rate 26 study features. A maximumof 27 points is possible because one item is scored 2, 1, or 0,whereas the remaining items are scored as either 1 or 0.Although no minimal standard is available to interpret therelative strength of the overall score, high scores areinterpreted as reflecting a higher level of methodologicalquality and scientific credibility (Downs & Black, 1998). Asseen in Table 1, results of this scoring of 26 items for each ofthe nine included studies ranged from 14 to 21, yielding amean overall score of 17.9, suggesting a moderate level ofquality. This score was consistent with the overall method-ological quality rating of 16.4 reported by Nye and Hahs-Vaughn (2011). This finding compares favorably with theaverage overall scores of 14 for RCT studies and 11.7 forQED studies reported by Downs and Black (1998).

Overall Treatment Effect: Treatment Versus ControlGroup Studies

Four studies—three RCTs (Harris et al., 2002; Joneset al., 2005; Lattermann et al., 2008) and one QED (Craiget al., 1996)—utilized a treatment-versus-control-group design.An analysis of these studies yielded an overall effect ofHedges’s g = 1.25 (95% CI [0.63, 1.87], p < .000). Table 2presents the effect size statistics associated with each study.

In order to assess the potential impact of any one ofthese studies on the overall treatment effect, a sensitivityanalysis was conducted using the one-study-removedprocedure (Borenstein et al., 2005), in which a total effectsize, confidence level, and significance level are determinedrelative to the average effect size of the remaining studies.Results of this analysis revealed that the removal of the Craiget al. study (1996) reduced Hedges’s g effect size by 0.18.

Treatment Versus Control Group: RCT DesignStudies

In order to answer the question of whether or not abehavioral intervention is effective, we first analyzed onlythose studies in which a treated group of CWS was comparedwith a nontreated CWS control group and a post-treatmentmeasurement was conducted immediately after completionof the intervention program. Three RCT studies (Harriset al., 2002; Jones et al., 2005; Lattermann et al., 2008)compared the effects of the Lidcombe program for treatingCWS 2–6 years of age in a therapy-versus-control condition.When these three studies were averaged, a large effect sizewas observed for the reduction in %SS (g = 0.97; 95% CI[0.58, 1.36], p < .000). These findings suggest that theaverage treated CWS exhibited an improvement approaching1 SD when compared with the average nontreated CWS.

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A fourth RCT study (Lewis et al., 2008) assessed theeffect of a telephone delivery approach of the Lidcombeprogram. Participants were first assessed at 9 months post-intervention for %SS. Results of the comparison of thetreated and control groups yielded a nonsignificant groupdifference (g = 0.76; 95% CI [–0.09, 1.61], p = .080).

Treatment Versus Control: QED Study

Craig et al. (1996) compared the effects of threetreatment approaches (EMG, HSS, ISS) on CWS acrossthree clinical contexts (clinic, home, and phone) to those ona nontreated control group. The calculated effect sizes foreach Treatment Grouping (experimental vs. control) ×Clinical Context (clinic, home, phone) interaction yieldedlarge effect sizes, ranging from g = 1.62 for EMG to g = 2.58for ISS. Table 3 presents a complete summary of these effectsizes associated with each intervention approach. However, in

order to maintain data independence, no statistical analyseswere possible due to the comparison of a single control groupwith three treatment approaches.

Treatment 1 Versus Treatment 2: RCT Design Study

Another group of studies included in this review werethose in which participants were assigned to differenttreatment groups. That is, the study did not use anontreatment control group as a methodological comparisonto assess the effects of a second intervention. These studieswould be understood as ‘‘head-to-head’’ studies of theadvantages of one treatment approach over a secondtreatment approach. A total of five studies were included inthis category of treatment design. Four of the studies(Franken et al., 2005; Harrison et al., 2004; Riley & Ingham,2000; Ryan & Ryan, 1995) used different treatment protocolsand reported participants ranging in age from 2 to 17 years.

Table 2. Effect size, 95% confidence interval, and p value of %SS for studies comparing treatment-versus-control-group designs with post-testmeasurement immediately after treatment.

Study nameStatistics for each study

Treatment n Control n Hedges’s g LL UL p

Craig et al. (1996) 77 20 1.75 1.05 2.45 .000Harris et al. (2002) 10 13 0.67 –0.23 1.56 .144Jones et al. (2005) 27 20 0.94 0.34 1.54 .002Lattermann et al. (2008) 23 22 1.51 0.53 1.77 .000Overall effect 1.25 0.63 1.87 .000

Note. LL = lower limit; UL = upper limit.

Table 3. Craig et al. (1996) study effect sizes, 95% confidence interval, and p values associated with the comparison of treatment approach(treatment vs. control, and Treatment 1 vs. Treatment 2) across clinical contexts for %SS and SPM.

Treatment comparison Clinical condition Outcome Hedges’s g LL UL p

EMG vs. Ctl Clinic %SS 2.41 1.65 3.18 .000HSS vs. Ctl Clinic %SS 2.29 1.54 3.03 .000ISS vs. Ctl Clinic %SS 2.53 1.77 3.30 .000EMG vs. Ctl Home %SS 2.10 1.38 2.82 .000HSS vs. Ctl Home %SS 1.82 1.27 2.50 .000EMG vs. Ctl Phone %SS 1.62 0.95 2.28 .000HSS vs. Ctl Phone %SS 2.09 1.37 2.81 .000ISS vs. Ctl Phone %SS 2.58 1.80 3.35 .000EMG vs.HSS Clinic %SS 0.34 –0.21 0.89 .223EMG vs. ISS Clinic %SS –0.26 –0.79 0.28 .351ISS vs. HSS Clinic %SS 0.55 0.01 1.10 .048EMG vs.HSS Home %SS 0.22 0.33 0.77 .435EMG vs. HSS Phone %SS 0.00 –0.55 0.55 1.000EMG vs. ISS Phone %SS –0.38 0.92 0.16 .166ISS vs. HSS Phone %SS 0.67 0.12 1.22 .017EMG vs. HSS Clinic SPM 0.34 –0.21 0.89 .230EMG vs. ISS Clinic SPM 0.95 0.40 1.52 .001ISS vs. HSS Clinic SPM –0.74 –1.30 –0.19 .009EMG vs. HSS Home SPM 0.50 –0.06 1.05 .078EMG vs. HSS Phone SPM 0.20 –0.35 0.75 .475EMG vs. ISS Phone SPM 0.87 0.31 1.43 .002ISS vs. HSS Phone SPM –0.88 –1.44 –0.32 .002

Note. Ctl = control.

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An analysis of the four studies comparing twotreatment approaches yielded no statistically significant(p > .05) differences for stuttered syllables or stuttered words.That is, there appeared to be no advantage of one treatmentover another in any of the comparisons reported for anysingle study, whether at the point of immediate post-intervention or at a subsequent follow-up time. No twostudies presented data regarding comparable group ages forindividual ages (e.g., 7-year-olds, 12-year-olds, etc.). Thus, nostatement of the treatment impact across age groups orranges was possible.

Because all of the studies used different interventionsfor comparison, no average of an overall effect could beconducted. Table 4 presents a summary of the includedstudies, a comparison of the intervention approaches, andthe magnitude of the intervention effect. The combined effectsize for Harrison et al. (2004) reflects an aggregation of thefour participant groups with sample sizes of either nine or 10children.

Treatment 1 Versus Treatment 2: QED Study

Craig et al. (1996) compared the treatment effect ofthree different intervention approaches assessing both %SSand SPM. As shown in Table 3, the ISS treatmentsignificantly reduced the %SS when compared with HSS forboth the clinic and phone contexts. However, when the twotreatment comparisons were assessed for the effect of anincrease in SPM, EMGwas superior to ISS in both clinic andphone contexts, but ISS resulted in a statistically significantincrease in SPM when compared with the HSS approach.Although these data are taken from a single study and arenot amenable to a meta-analytic average, they are presentedas a descriptive statement of the magnitude of effectassociated with each outcome separately.

Follow-Up Treatment Effects

Two RCT studies reported follow-up treatment effects.Ryan and Ryan (1995) assessed participants’ %SS at 14months post-intervention, whereas Harrison et al. (2004)assessed %SS at 4 weeks post-intervention. A calculation ofthe effect sizes associated with all comparisons for bothstudies yielded statistically nonsignificant (p > .05) differ-ences for %SS.

In the QED study, Craig et al. (1996) also assessed%SS and SPM at 12 and 52 weeks post-intervention. Ananalysis of the associated effect sizes for each intervention–comparison group across the three clinical contexts yielded

no statistically significant (p > .05) advantage for anyindividual treatment condition or clinical context at either 12or 52 weeks.

Discussion

Overall Effects

A total of nine studies were identified for inclusion inthis review. The overall effect of intervention for stutteringsuggests that, on average, a child who stutters can expect toreduce the percentage of stuttered syllables or words byapproximately 1 SD upon completion of a treatmentprogram. However, when this omnibus result is analyzedfurther, we see that several factors must be considered tomore accurately define the intervention effects.

Intervention Effects: Experimental Versus ControlComparison

A total of four studies were included that measured thetreatment effect by comparing treatment (experimental) withnontreatment (control) groups when the dependent measurewas assessed immediately after the intervention. Theaggregated effect size of 1.15 suggests a significant interven-tion effect as measured by the reduction of the frequency ofsyllables stuttered. However, the Craig et al. (1996) studyused a QED, and when this study was removed from theaveraging of effect sizes, the intervention effect was reducedto a significant g = 0.97 (95% CI [0.58, 1.30], p < .000). WithCraig et al. removed, the three remaining studies (Harriset al., 2002; Jones et al., 2005; Lattermann et al., 2008)provide consistent evidence for the impact of one particularintervention: the Lidcombe program.

Considering the results of all of the RCT-versus-control-group–designed studies (see Table 2), it would not beunreasonable to view the control group participants’performance as a measure of spontaneous recovery. In thisregard, it is noteworthy that only Harris et al. (2002) found anonsignificant difference in the performance of the partici-pants in their treated and nontreated groups. However, in theremaining reported RCT studies (Jones et al., 2005;Lattermann et al., 2008; Lewis et al., 2008), the observedeffect size revealed a statistically significant advantage of thetreated group relative to the control group. Given therandomization process used in rigorous RCTs, which reducesthe potential bias that might be associated with naturalrecovery (Onslow, Jones, O’Brien, Menzies, & Packman,

Table 4. Study, effect size, 95% confidence interval, and number of participants associated with the RCTs comparing two treatmentapproaches.

Authors Comparison Outcome Hedges’s g LL UL Treatment 1 n Treatment 2 n

Ryan & Ryan (1995) DAF vs. GILCU SWM 0.30 –0.80 1.39 11 9Riley & Ingram (2000) SMT vs. ELU %SS –1.08 –2.21 0.05 6 6Harrison et al. (2004) Combined %SS –0.14 –1.01 0.73 9–10 9–10Franken et al. (2005) LP vs. DCM %SS –0.28 –1.07 0.52 11 12

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2008), the effect size difference is more likely to be attributedto treatment.

Craig et al. (1996) assessed the effect of intervention onthe reduction of stuttered syllables and a correspondingincrease in total number of words spoken per minute. Thesummary presented in Table 3 suggests that the interventionwas generalized across settings, with about the same level ofintervention effect for each of the three different interventionapproaches. That is, those participants receiving the ISStherapy demonstrated a similar level of effect during thephone conversation as in clinical settings. This was also thecase for the EMG and HSS intervention approaches. As aresult of Craig and colleagues’ use of a single control groupfor all comparisons, no aggregation of effect sizes waspossible. Thus, any conclusion about the effect of interven-tion from this study can be understood only as a descriptivepresentation with limited support.

Intervention Effects: Treatment 1 Versus Treatment 2Comparison

A total of five studies were included for analysis.Although no two studies reported the same comparison oftreatments, the overall mean effect ranged from –1.08 to0.30. However, the 95% CI for all five studies included 0.00,suggesting that no single treatment approach exhibited asignificant difference in the magnitude of effect whencompared with a second defined intervention approach.These data suggest that the mere provision of interventionmay be as much a factor in the improvement of speech inCWS as the specific treatment approach, or componentsthereof. It is worth noting that Franken et al. (2005)produced a nonsignificant treatment impact when theLidcombe program was compared with a DCM approach. Itneeds to be mentioned that there are no control group studiessupporting the efficacy of any of the treatments in theTreatment 1 versus Treatment 2 studies. These data must beinterpreted cautiously due to the underpowered samples in atleast four of the five studies and the absence of anontreatment control condition for any of the treatmentapproaches.

Intervention Follow-Up Effects

The assessment of the longer term follow-up effects oftreatment were reported in only three studies that measuredstuttering beyond the immediate post-intervention phase(Craig et al., 1996; Harrison et al., 2004; Ryan & Ryan,1995). The finding of no significant difference across anycomparison—whether dealing with two comparison treat-ment groups or a treatment-versus-control condition—suggests that there is limited knowledge as to the sustainedeffectiveness of any of the reported intervention procedures.

One study that did not meet inclusion criteria (Jones etal., 2008) did assess the long-term effects of the Lidcombeprogram reported in an earlier study (Jones et al., 2005) thatwas included in this review. In the 2008 report, childrenfrom the earlier study were contacted and their speech wasassessed via a recorded telephone conversation. Although the

results of this follow-up pointed to a positive long-termeffect, no assessment of the causal nature of the Lidcombeprogram could be drawn because no usable data for thecalculation of an effect size were provided for the controlgroup at the follow-up measurement. Certainly, well-controlled studies designed to assess the long-term effects ofeach intervention are needed in order to address this issue.

Limitations of Evidence

Several study limitations that potentially affect theinterpretation—and, thus, the utility—of these data areworth considering. We were particularly struck by (a) thelimited number of studies, (b) the limited reporting ofintervention details, (c) variations in treatment protocol, (d)participant attrition, and (e) the lack of follow-up assessmentof treatment effects.

Limited number of included studies. One of the moststriking factors of this review is the limited number of studiesthat were identified and included. For a communicationdisorder with more than 75 years of research history and asymptomatology readily recognizable to the general public, areview sample of eight RCT studies and one QED study thatprovided analyzable data for interventions focusing onchildren was surprising. Furthermore, only four of the ninestudies were of the highest quality—an RCT design—using ano-treatment control for comparison purposes. It was thislack of viable studies investigating treatment efficacy amongschool-age children that led Nippold (2011) to write aneditorial urging new and upcoming investigators to considerdevoting time and effort to treatment outcome studies forchildren ‘‘before the disorder becomes an entrenched andlifelong pattern’’ (p. 101).

Inadequate reporting. A second observation is theinadequate reporting of intervention and participant char-acteristics that would seem to be crucial to the adoption ofan intervention program that demonstrates positive effects.For example, four of the nine included studies reportedinsufficient information to adequately quantify the length ofthe treatment program. That is, the coders could not identifythe total length of time that a participant would spend inthe intervention program (e.g., 2 weeks, 3 months, etc.), thenumber of sessions, or the length of each session. Certainly,the absence of such basic information reduces the value ofthe interpretation of the results based on a treatmentimplementation fidelity description.

In terms of participant characteristics, the age rangesincluded in six of the studies spanned 5 or more yearsbetween the youngest and oldest participant (i.e., 7–17 years,9–14 years, 3–8 years), with a mean age of the participantsavailable for five studies. With such a wide chronological agespan, the reader may question whether the investigatorsoperated on the assumption that the participants’ speechdevelopment was complete by the youngest age represented.However, such an assumption is not a plausible base for theresearch design used by these experienced researchers. Oursummary of the treatment effects did not allow for theidentification of the specific treatment effect by well-definedage groups because the data for independent age subgroups

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(e.g., ages 6;0, 6;6, 7;0 [years; months]) were not reported inthe primary studies.

Treatment protocol variations. A third observationinvolves the issue of variations in treatment protocol. Forexample, Jones et al. (2005) reported deviations from theprotocol for four participants in the control group whoreceived some intervention. The resulting treatment groupperformance, as such, no longer produces a ‘‘pure’’ treatmenteffect because of the confounding control group condition.The authors do provide a description of the nature of thevariation in the protocol for both treatment and controlgroups, but they did not account for this in the data analysis.

Participant attrition. A fourth issue, participant attri-tion, was noted for the majority of the included studies. Ofthe nine included studies, three reported no participantattrition (Craig et al., 1996; Lattermann et al., 2008; Riley &Ingham, 2000). The remaining six studies (all RCT designs)reported participant differential group attrition ranging from13% to 23% from pre-treatment to immediate post-treatment.The issue of concern here is that, in a randomized trial,the unequal loss of participants may produce a significantdifference in the participant characteristics represented inboth the experimental and control groups. For example, adifferential attrition of participants may produce significantgroup age differences when compared with the originalsample of participant groups. Even though some studiesexclude the pre-treatment scores for participants who did notcomplete the intervention from the final analysis, a potentialbias may be reflected in the measured outcomes’ (e.g., age)impact on the overall magnitude of the observed treatmenteffect. Further, participant attrition may lead to a spuriousinterpretation of the results due to changes in the sample-to-population representation. These kinds of critical designquality issues can detract from the usefulness and accuracy ofstudy findings and thus affect the potential clinical imple-mentation based on those findings. Although small degrees ofattrition are generally tolerable, with so few studies usingrelatively small sample sizes, consideration should have beengiven to provide, where appropriate, a methodologicalaccounting for the attrition (e.g., intent-to-treat analysis).Certainly, attention to attrition rates across treatment andcontrol groups is important for both replication of findingsand application to the clinical setting.

Limited follow-up. With only three studies (Craig et al.,1996; Harrison et al., 2004; Ryan & Ryan, 1995) reportingfollow-up measurements of the impact of the treatmentprograms beyond the end of treatment assessment, few usefuldata can be evaluated. None of these studies used the sametreatment approach or same post-treatment time point fordependent variable measurement. With such basic treatmentand design characteristic shortcomings, conclusions regard-ing the potential long-term impact of treatment are leftrelatively unanswered.

Implications for Research

As pointed out in the tutorial on clinical trials byOnslow et al. (2008), and echoed by Nippold (2011), there isa need for high-quality trials that provide a fair comparison

of treatment and nontreatment participants or of twodifferent treatment programs. Specifically, the promiseexhibited by the Lidcombe program, as was also evident inthe Bothe, Davidow, Bramlett, and Ingham (2006) study,should be subjected to a large-scale trial by other indepen-dent researchers. Comparison with both nontreatment andalternative treatment conditions to assess the magnitude oftreatment effect of the Lidcombe program is needed beforeits adoption as an effective intervention for preschoolchildren can be considered. However, at the time of thisreport, no other treatment approach has been found to showthe reported effects under the same well-controlled scientificconditions. Nevertheless, Onslow and colleagues (2008)argued that the results of nonrandomized trials, includingthose of the Lidcombe program, need to be interpreted withcaution, or more succinctly put, ‘‘… considering theirunreliability, the extent of stuttering reductions in nonran-domized clinical trials of stuttering treatment should bedisregarded’’ (p. 406). In addition, studies that assess theimpact of non-Lidcombe treatments should be conducted toassess the effect of a particular approach under controlledconditions before the clinical application of a particulartreatment program can be recommended.

As indicated above, the assessment of the long-termeffects of all intervention approaches remains relativelyunanswered and unexplored (Jones et al., 2008; Lewis et al.,2008). In the descriptive review by Bothe, Davidow,Bramlett, and Ingham (2006), only about half of the studiesmeasured frequency of stuttering 6 months post-therapy. Theprofessional community cannot, with confidence, supportthe notion of retention of the benefits of any interventionapproach for CWS. Positive long-term treatment effects arecritical to the justification of the value of all interventionapproaches identified in this review.

Implications for Practitioners

The review concluded that there is clear support foronly one intervention approach: the Lidcombe program.Alternatively, the findings for those studies comparing twotreatment groups suggest that, while the intervention mayresult in a positive effect, the magnitude of the effect may beno greater for one type of intervention than for another.Further, the absence of the demonstrated efficacy of non-Lidcombe interventions provides little help to the practi-tioner in reaching a clinical decision. With so few includedstudies available that provide a clear causal treatmentimpact, no conclusion can be drawn regarding the potentialmoderating or subgroup variables that might affect themagnitude of the treatment outcome.

Indeed, as many colleagues in the field have pointedout, there is a need to recognize the different subtypes ofindividuals who stutter and deal with them in a differentialway. In addition, as Franken et al. (2005) alluded to, acertain treatment program might be more suitable for anindividual and his or her family than another program. Thereis, however, limited evidence to account for the impact acrossindividual differences. In addition, as Herder, Howard, Nye,and Vanryckeghem (2006), and Bothe, Davidow, Bramlett,

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and Ingham (2006) alluded to, variables such as clinicianimpact, infrastructural parameters, and attention factors canbe as crucial or equally important to the success of theintervention as the principal treatment itself. However, withthe limited data available that measure these variables asdependent variables in a causal manner, their real impact instuttering treatment is a matter of speculation.

Clinicians have limited high-quality research to drawon in order to assess the evidentiary basis for interventionsfor CWS. Whereas Bothe, Davidow, Bramlett, and Ingham(2006) do provide a substantive descriptive summary of thestuttering treatment evidence, our findings support theircontention that, although the criteria for inclusion in theirqualitative study represented a ‘‘truly minimal’’ (p. 332)paradigm, the fact that ‘‘few articles met these standards mayreasonably be viewed as problematic’’ (p. 332).

At the time of this report, the Lidcombe programoffers the best evidence for an effective intervention forCWS, but this applies only to children under 6 years of age.Given the young age of the children for whom this programis designed, and the incipient nature of the disorder, it is to beexpected that treatment will be more effective compared withtreatment geared toward older children and adolescents. Forthose studies using the Lidcombe approach and reportingthe basic participant characteristics, a general assessment ofthe fidelity of intervention can be made because of theprescriptive nature of the intervention program that has beenwidely publicized and reported. This is not to say that otherapproaches may not be effective, but the available data onlyallow us to conclude that there is insufficient informationusing the highest research standards in the discipline.

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