نقش مداخلات تغذیهای در مدیریت درمانی درد راجعه شکمی در کودکان
چکیده
پیشینه
این مطالعه، به‌روزشده مرور اصلی کاکرین است، که آخرین بار در سال 2009 منتشر شد (Huertas‐Ceballos 2009). درد شکمی راجعه (recurrent abdominal pain; RAP)، شامل کودکان مبتلا به سندرم روده تحریک‌پذیر (irritable bowel syndrome)، مشکلی است شایع که در 4% تا 25% کودکان سنین مدرسه دیده می‌شود. در معاینه فیزیکی یا بررسی‌های بیشتر در اکثر این کودکان، هیچ علت عضوی برای درد پیدا نمی‌شود. به منظور بهبود نشانه‌های RAP، روش‌های تغذیهای بسیاری پیشنهاد شده، هم‌چون حذف مواد افزودنی از رژیم غذایی یا اضافه‌کردن مکمل‌هایی مثل فیبر یا پروبیوتیک‌ها.
اهداف
بررسی اثربخشی مداخلات غذایی در بهبود درد در کودکان سنین مدرسه مبتلا به RAP.
روش‌های جست‌وجو
در جون 2016، به جست‌وجو در CENTRAL؛ Ovid MEDLINE؛ Embase؛ هشت بانک اطلاعاتی دیگر، و دو پایگاه ثبت کارآزمایی پرداختیم، همراه با بررسی منابع، جست‌وجو در استنادات و تماس با نویسندگان مطالعه.
معیارهای انتخاب
کارآزمایی‌های تصادفی‌سازی و کنترل شده‌ای (randomised controlled trials; RCTs) را وارد کردیم که مداخلات تغذیهای را با دارونما (placebo) یا عدم درمان در کودکان سنین پنج تا 18 سال مبتلا به RAP یا یک اختلال گوارشی عملکردی مرتبط با درد شکم، مطابق با معیار Rome III، مقایسه کردند (Rasquin 2006).
گردآوری و تجزیه‌وتحلیل داده‌ها
از روش‌های استاندارد روش‌شناسی مورد نظر کاکرین استفاده کردیم. مداخلات غذایی را بر اساس نوع آن برای آنالیز در یک گروه قرار دادیم. در صورت نیاز، برای به دست آوردن اطلاعات ازدست‌رفته و شفاف‌سازی بیشتر، با نویسندگان مطالعه تماس گرفتیم. با استفاده از رویکرد درجهبندی توصیه، ارزیابی، توسعه و ارزشیابی (GRADE) کیفیت شواهد را برای هر پیامد بررسی کردیم.
نتایج اصلی
19 RCT را، که در 27 مقاله با مجموع 1453 شرکت‌کننده گزارش شدند، وارد کردیم. پانزده مورد از این نوزده مطالعه، در مرور قبلی حضور نداشتند. دوره پیگیری همه 19 RCT از یک تا پنج ماه متغیر بود. شرکتکنندگان در محدوده سنی چهار تا 18 سال و از هشت کشور مختلف بوده و عمدتا از درمانگاه‌های گوارش اطفال جذب مطالعات شدند. میانگین سن در زمان ورود به مطالعه، بین 6.3 و 13.1 سال بود. در اکثر مطالعات دختران بیش از پسران بودند. پانزده کارآزمایی، کودکانی را با تشخیص اختلالی که زیر چتر گسترده RAP قرار می‌گرفت یا اختلالات عملکردی گوارشی وارد کردند؛ پنج کارآزمایی به‌طور اختصاصی فقط کودکان مبتلا به سندرم روده تحریک‌پذیر را بررسی کردند. مطالعات در چهار دسته قرار گرفتند: مداخلات مبتنی بر تجویز پروبیوتیک (13 مطالعه)، مداخلات مبتنی بر مصرف فیبر (چهار مطالعه)، کارآزمایی‌های مربوط به رژیم‌هایی غذایی با محتوای پائین FODMAP (اولیگوساکاریدها، دی‌ساکاریدها، مونوساکاریدها و پلی‌اُل‌های تخمیرپذیر (fermentable oligosaccharides, disaccharides, monosaccharides and polyols) (یک کارآزمایی)، و کارآزمایی‌های مربوط به رژیم‌های غذایی دارای فروکتوز کم (یک کارآزمایی).
ما دریافتیم که کودکان درمان شده با پروبیوتیک‌ها نسبت به کودکانی که دارونما دریافت کردند، طی صفر تا سه ماه پس از دریافت مداخله کاهش بیشتری را در فراوانی درد نشان دادند (تفاوت میانگین استاندارد شده (SMD): 0.55‐؛ 95% فاصله اطمینان (CI): 0.98‐ تا 0.12‐؛ 6 کارآزمایی؛ 523 کودک). در گروه مداخله نیز کاهشی در شدت درد در همان نقطه زمانی دیده شد (SMD: ‐0.50؛ 95% CI؛ 0.85‐ تا 0.15‐؛ 7 مطالعه؛ 575 کودک). با این حال، به دلیل خطر سوگیری (bias) نامشخص حاصل از داده‌های ناکامل پیامد و وجود ناهمگونی قابل توجه، کیفیت شواهد را برای این پیامدها با استفاده از GRADE در سطح پائین در نظر گرفتیم.
ما دریافتیم کودکانی که با پروبیوتیک‌ها درمان شدند نسبت به کودکانی که دارونما دریافت کردند، طی ماه‌های صفر تا سه پس از اعمال مداخله با احتمال بیشتری بهبود یافتند (نسبت شانس (OR): 1.63؛ 95% CI؛ 1.07 تا 2.47؛ 7 مطالعه؛ 722 کودک). تعداد افراد مورد نیاز جهت درمان تا حصول یک پیامد مفید بیشتر (number needed to treat for an additional beneficial outcome; NNTB) تخمین زده شده برابر با هشت بود، به این معنی که هشت کودک باید پروبیوتیک دریافت کنند تا درد یک کودک در این مقیاس زمانی بهبود یابد. به دلیل ناهمگونی زیاد، کیفیت شواهد را برای این پیامد در سطح متوسط در نظر گرفتیم.
کودکان مبتلا به نشانه سندرم روده تحریک‌پذیر که با پروبیوتیک درمان شدند، نسبت به کودکان دریافت کننده دارونما، در ماه‌های صفر تا سه پس از مداخله با احتمال بیشتری بهبود یافتند (OR: 3.01؛ 95% CI؛ 1.77 تا 5.13؛ 4 مطالعه؛ 344 کودک). کودکانی درمان شده با پروبیوتیک نسبت به دارونما، با احتمال بیشتری در ماه‌های سه تا شش پس از مداخله به بهبودی دست یافتند (OR: 1.94؛ 95% CI؛ 1.10 تا 3.43؛ 2 مطالعه؛ 224 کودک). به دلیل تعداد اندک شرکتکنندگان مطالعه، کیفیت شواهد را برای این دو پیامد در سطح متوسط قرار دادیم.
ما دریافتیم کودکانی که با مداخلات مبتنی بر فیبر درمان شدند، نسبت به کودکانی که دارونما دریافت کردند، در ماه‌های صفر تا سه پس از مداخله احتمالا بهبودی نداشتند (OR: 1.83؛ 95% CI؛ 0.92 تا 3.65؛ 2 مطالعه؛ 136 کودک). همچنین هیچ کاهشی در شدت درد در مقایسه با دارونما در همان نقطه زمانی وجود نداشت (SMD: ‐1.24؛ 95% CI؛ 3.41‐ تا 0.94؛ 2 مطالعه؛ 135 کودک). کیفیت شواهد مربوط به این پیامدها را به دلیل خطر سوگیری نامشخص، عدم‐دقت، و ناهمگونی زیاد، در سطح پائین در نظر گرفتیم.
فقط یک مطالعه را از رژیم غذایی با محتوای پائین FODMAP و فقط یک کارآزمایی را از رژیم غذایی با فروکتوز محدود شده پیدا کردیم، به این معنی که نتوانستیم هیچ آنالیز جمع‌بندی شده‌ای را انجام دهیم.
به دلیل تعداد اندک مطالعاتی که به این پیامدها پرداختند یا معیارهای استفاده شده قابل مقایسه برای بررسی آنها، نتوانستیم متاآنالیزی را برای پیامدهای ثانویه عملکرد کودک در مدرسه، عملکرد اجتماعی یا روانی، یا کیفیت زندگی روزمره انجام دهیم.
به استثنای یک مطالعه، همه مطالعات، پایش کودکان را از لحاظ عوارض جانبی گزارش کردند؛ وقوع هیچ عارضه جانبی مهمی گزارش نشد.
نتیجه‌گیری‌های نویسندگان
به‌طور کلی، شواهدی را با کیفیت متوسط تا پائین پیدا کردیم که نشان می‌دهند پروبیوتیک‌ها ممکن است برای بهبود درد در کودکان مبتلا به RAP موثر باشند. بنابراین پزشکان می‌توانند مداخلات تجویز پروبیوتیک را به عنوان قسمتی از استراتژی مدیریت کلی RAP در نظر بگیرند. با این حال، برای ارزیابی پیامدهای طولانی‐مدت‌تر و افزایش اطمینان در تخمین اندازه تاثیر مداخله، و نیز تعیین گونه و دوز مطلوب پروبیوتیک، به انجام کارآزمایی‌های بیشتری نیاز است. از سوی دیگر، پژوهش‌های آتی باید اثربخشی پروبیوتیک‌ها را بر کودکان با نشانه‌های مختلف، مانند کودکان مبتلا به سندرم روده تحریک‌پذیر، نیز بررسی کنند.
فقط تعداد اندکی را از کارآزمایی‌ها از مداخلات مبتنی بر فیبر پیدا کردیم، که سطح کیفیت کلی شواهد موجود برای پیامدها در آن، پائین بود. بنابراین، هیچ شواهد متقاعد کننده‌ای وجود ندارد که نشان دهد مداخلات مبتنی بر فیبر درد را در کودکان مبتلا به RAP کاهش می‌دهد. برای بررسی مکمل‌های فیبری، به انجام RCTهایی با کیفیت بالا و با حضور تعداد بیشتری از شرکتکنندگان نیاز است. همچنین برای کمک به انتشار توصیه‌های مبتنی بر شواهد، لازم است کارآزمایی‌هایی در مورد رژیم‌های غذایی با محتوای پائین FODMAP و دیگر مداخلات تغذیهای انجام شوند.
PICO
خلاصه به زبان ساده
نقش مداخلات تغذیهای در مدیریت درمانی درد شکمی راجعه در کودکان
سوال مطالعه مروری
شواهد مرتبط با اثرات مداخلات تغذیهای را بر درد در کودکان سنین پنج تا 18 سال مبتلا به درد شکمی راجعه (recurrent abdominal pain; RAP) مرور کردیم.
پیشینه
درد راجعه شکمی، یا RAP، اصطلاحی است که برای اپیزودهای غیر‐قابل توجیه درد معده یا شکم در کودکان استفاده می‌شود. درد راجعه شکمی یک وضعیت شایع است، و احتمالا اکثر کودکان مبتلا به آن با اقدامات ساده‌ای درمان می‌شوند. با این حال، انجام طیفی از درمان‌ها، مثل تغییر دادن عادت غذایی کودک با اضافه کردن مکمل‌ها یا حذف یک ماده غذایی خاص، برای کاهش درد شکمی توصیه شده‌‌اند.
ویژگی‌های مطالعه
این شواهد تا جون 2016 به‌روز است.
نوزده مطالعه معیارهای ورود را داشتند، شامل 13 مطالعه از مداخلات پروبیوتیک‌ها و چهار مطالعه در مورد مداخلات فیبر. همچنین، یک مطالعه را از رژیم غذایی با محتوای پائین از موادی با نام FODMAPها (اولیگوساکاریدها، دی‌ساکاریدها، مونوساکاریدها و پلی‌اُل‌های تخمیرپذیر) و یک مطالعه را از رژیم بدون فروکتوز پیدا کردیم.
همه این مطالعات، مداخلات تغذیهای را با دارونما یا کنترل مقایسه کردند. کارآزمایی‌ها در هشت کشور انجام شده، و شامل 1453 شرکت‌کننده در محدوده سنی پنج تا 18 سال بودند. اکثر کودکان از درمانگاه‌های سرپایی وارد مطالعه شدند. بیشتر مداخلات چهار تا شش هفته طول کشیدند.
نتایج کلیدی
پروبیوتیک‌ها
شواهدی را از 13 مطالعه پیدا کردیم که نشان داد پروبیوتیک‌ها ممکن است برای بهبود درد در کوتاه‐مدت موثر باشند. اکثر مطالعات، پیرامون زمینه‌های دیگر مانند کیفیت زندگی روزمره گزارشی را ارائه نکردند. همچنین اثرات مضری، به جز خشکی دهان در یک مطالعه، گزارش نشد. به دلیل اینکه برخی از مطالعات حجم نمونه کوچکی داشته، نتایج متفاوتی را نشان دادند، و در معرض خطر سوگیری (bias) قرار داشتند، سطح کیفیت شواهد را متوسط یا پائین در نظر گرفتیم.
مکمل‌های فیبری
شواهد روشنی را از بهبود درد در چهار مطالعه بررسی کننده مکمل فیبری پیدا نکردیم. اکثر مطالعات، پیرامون زمینه‌های دیگر مانند کیفیت زندگی روزمره گزارشی را ارائه نکردند. بروز عوارض جانبی گزارش نشد. تعداد مطالعات مکمل فیبری اندک بوده، و برخی از آنها خطر سوگیری بالایی داشتند. سطح کیفیت این شواهد را پائین در نظر گرفتیم.
رژیم‌های غذایی با محتوای پائین FODMAP
فقط یک مطالعه را یافتیم که اثربخشی رژیم‌های غذایی با محتوای پائین FODMAP را بر کودکان مبتلا به RAP ارزیابی کرد.
رژیم‌های بدون فروکتوز
فقط یک مطالعه به دست آمد که اثربخشی رژیم‌های بدون فروکتوز را بر کودکان مبتلا به RAP ارزیابی کرد.
نتیجه‌گیری
شواهدی را پیدا کردیم که نشان می‌داد پروبیوتیک‌ها ممکن است در کاهش درد در کودکان مبتلا به RAP در کوتاه‐مدت کمک‌کننده باشند. بنابراین، پزشکان می‌توانند مداخلات پروبیوتیک را به عنوان بخشی از استراتژی مدیریت درمانی RAP در نظر بگیرند. برای درک میزان اثربخشی پروبیوتیک‌ها در دوره‌های زمانی طولانی‌تر و پیدا کردن بهترین پروبیوتیک از نظر کارکرد، به انجام کارآزمایی‌های بیشتری نیاز است.
هیچ شواهد متقاعد کننده‌ای را پیدا نکردیم که نشان دهد مکمل‌های فیبری در بهبود درد در کودکان مبتلا به RAP موثر هستند. به انجام مطالعات بزرگ‌تر و با کیفیت بالایی برای بررسی اثربخشی رژیم‌های حاوی فیبر و با محتوای پائین FODMAP نیاز است.
Authors' conclusions
Summary of findings
| Probiotics compared to placebo for recurrent abdominal pain in childhood | ||||||
| Patient or population: Children with recurrent abdominal pain | ||||||
| Outcomes | Illustrative comparative risks* (95% CI) | Relative effect | Number of participants | Quality of the evidence | Comments | |
| Assumed risk | Corresponding risk | |||||
| Placebo | Probiotics | |||||
| Change in pain frequency: 0 to 3 months' postintervention Different measures were used to assess pain frequency, such as a visual analogue scale and the Wong‐Baker FACES Pain Rating Scale (McGrath 1996; Wong 1988). | — | The mean change in pain frequency: 0 to 3 months' postintervention scores in the intervention groups was 0.55 SDs lower (0.98 to 0.12 lower). | — | 523 | ⊕⊕⊝⊝ | As a rule of thumb, 0.2 SD represents a small difference, 0.5 SD a moderate difference, and 0.8 SD a large difference. |
| Change in pain intensity: 0 to 3 months' postintervention Different measures were used to assess pain intensity, as above. | — | The mean change in pain intensity: 0 to 3 months' postintervention scores in the intervention groups was 0.50 SDs lower (0.85 to 0.15 lower). | — | 575 | ⊕⊕⊝⊝ | As a rule of thumb, 0.2 SD represents a small difference, 0.5 SD a moderate difference, and 0.8 SD a large difference. |
| Improvement in pain: 0 to 3 months' postintervention Different measures and definitions were used for improvement in pain, such as Likert scale, visual analogue scale, and Subject’s Global Assessment of Relief Scale (McGrath 1996; Muller‐Lissner 2003). | 421 per 10003 | 542 per 1000 | OR 1.63 NNTB = 8 | 722 | ⊕⊕⊕⊝ | — |
| Improvement in pain: 0 to 3 months' postintervention Subgroup (irritable bowel syndrome) Different measures were used to assess improvement in pain, as above. | 359 per 1000 | 627 per 1000 | OR 3.01 NNTB = 4 | 344 | ⊕⊕⊕⊝ | — |
| Improvement in pain: 3 to 6 months' postintervention Different measures were used to assess improvement in pain, as above. | 589 per 1000 | 736 per 1000 | OR 1.94 NNTB = 7 | 224 | ⊕⊕⊕⊝ | — |
| *The basis for the assumed risk (e.g. the median control group risk across studies) is provided in footnotes. The corresponding risk (and its 95% confidence interval) is based on the assumed risk in the comparison group and the relative effect of the intervention (and its 95% CI). | ||||||
| GRADE Working Group grades of evidence | ||||||
| 1Downgraded one level due to incomplete outcome data in a number of included studies leading to an unclear or high risk of bias. | ||||||
| Fibre versus placebo for recurrent abdominal pain in childhood | ||||||
| Patient or population: Children with recurrent abdominal pain Comparison: Placebo | ||||||
| Outcomes | Illustrative comparative risks* (95% CI) | Relative effect | Number of participants | Quality of the evidence | Comments | |
| Assumed risk | Corresponding risk | |||||
| Placebo | Fibre | |||||
| Change in pain intensity: 0 to 3 months' postintervention Pain intensity was measured using different scales in the 2 included studies: the Wong Baker FACES Pain Rating Scale, Wong 1988, and the Numerical Rating Scale (von Baeyer 2009). | — | The mean change in pain intensity 0 to 3 months' postintervention score in the intervention groups was 1.24 SDs lower (3.41 lower to 0.94 higher) | — | 135 | ⊕⊕⊝⊝ | — |
| Improvement in pain: 0 to 3 months' postintervention Improvement in pain was defined and measured differently in the 2 included studies: using a "stomach ache diary" and the Faces Pain Scale (Bieri 1990). | 391 per 10001 | 541 per 1000 | OR 1.83 NNTB = 6.7 | 136 | ⊕⊕⊝⊝ | — |
| *The basis for the assumed risk (e.g. the median control group risk across studies) is provided in footnotes. The corresponding risk (and its 95% confidence interval) is based on the assumed risk in the comparison group and the relative effect of the intervention (and its 95% CI). | ||||||
| GRADE Working Group grades of evidence | ||||||
| 1Assumed risk in control group is based on the mean outcome of the control group in the two included studies. | ||||||
Background
Description of the condition
This review is an update of a previously published review in the Cochrane Library on 'Psychosocial interventions for recurrent abdominal pain and irritable bowel syndrome in childhood' (Huertas‐Ceballos 2009). Recurrent abdominal pain (RAP) is a common problem in paediatric practice. It has been suggested that 4% to 25% of school‐aged children will at some point suffer from recurrent or chronic abdominal pain that interferes with their activities of daily living (Konijnenberg 2005; Williams 1996; Youssef 2006), with a recent meta‐analysis estimating that 13.5% of children worldwide may be affected (Korterink 2015). Recurrent abdominal pain is often regarded as a relatively benign condition, but it is important to note the associated morbidity and the anxiety it causes for children and caregivers (Paul 2013). The condition is associated with school absences, hospital admissions, emotional disorders and, on occasion, unnecessary surgical intervention (Scharff 1997; Stickler 1979; Størdal 2005; Walker 1998; Youssef 2008). The abdominal pain is also commonly associated with other symptoms, including headaches, recurrent limb pains, pallor, and vomiting (Abu‐Arafeh 1995; Devanarayana 2011; Hyams 1995). Symptoms sometimes continue into adulthood; childhood RAP is associated with a higher risk of anxiety disorders in adults (Horst 2014; Shelby 2013).
Apley first sought to define the condition in the 1950s and suggested that the diagnostic label should be based on the presence of at least three episodes of severe abdominal pain (often, but not necessarily, with associated systemic symptoms) over three months (Apley 1958), with no established organic cause. Historically diverse terms have since been used to describe these conditions, some implying causation. These include: "abdominal migraine" (Bain 1974; Farquar 1956; Hockaday 1992; Symon 1986), "abdominal epilepsy" (Stowens 1970), "the irritable bowel syndrome in childhood" (Stone 1970), "allergic‐tension‐fatigue syndrome" (Sandberg 1973; Speer 1954), "neurovegetative dystonia" (Peltonen 1970; Rubin 1967), "functional gastrointestinal disorder" (Drossman 1995), and "the irritated colon syndrome" (Harvey 1973; Painter 1964).
It is now generally accepted that RAP in children represents a group of functional gastrointestinal disorders that have an unclear aetiology. The latest Rome Foundation criteria state that such disorders are defined by symptoms related to motility disturbance; visceral hypersensitivity; altered mucosal and immune function; altered gut microbiota; and altered central nervous system processing, and are "the product of ... interactions of psychosocial factors and altered gut physiology via the brain–gut axis" (Drossman 2016). The Rome Foundation has produced criteria for this group of conditions since 1994 by international consensus. Most studies included in this review use the Rome III criteria from 2006, which included a symptom‐based classification system with specific categories for paediatric presentations (Rasquin 2006). Throughout this review we have therefore used RAP as an umbrella term to refer to the five subcategories included within the Rome III category of childhood abdominal pain‐related functional gastrointestinal disorders, which are: functional dyspepsia, irritable bowel syndrome, abdominal migraine, functional abdominal pain, and functional abdominal pain syndrome. It should be noted that the pain classification for each of the Rome III diagnoses is defined by at least one episode per week for at least two months; this varies from Apley's original definition of RAP (Apley 1958). The Rome IV criteria were produced in spring 2016; in this new iteration the category of childhood functional abdominal pain disorders includes functional dyspepsia, irritable bowel syndrome, abdominal migraine, and functional abdominal pain not otherwise specified (Drossman 2016). However, the Rome classification is not based on known pathophysiological differences between the conditions, but rather on the constellation of clinical features. It is unclear the extent to which separating children into these categories defines groups that are distinct clinical entities that are likely to respond differently to treatment.
There is no consensus about which of the numerous proposed causal pathways result in the heterogeneous presentations of chronic abdominal pain, although it is suggested that physical, emotional, and environmental factors may contribute to the manifestation of unexplained abdominal pain. When considering the diverse proposed mechanisms, it is unsurprising that a variety of treatments have been suggested. The treatment approaches can be grouped as pharmacological, dietary, or psychosocial (psychological or behavioural, or both). This review focused on any intervention with dietary changes intended to improve the symptoms of RAP, and hence dietary approaches only are discussed below. Updated companion reviews of pharmacological interventions, Martin 2014a, and psychosocial interventions, Abbott 2017, for RAP have been published.
Description of the intervention
Dietary interventions may involve excluding or reducing a food group or specific ingredient from the diet or supplementing it and therefore increasing its intake. Such dietary interventions include eliminating or restricting food groups or food components, such as dairy products or fructose (Bain 1974; Bayless 1971; Wirth 2014), and taking fibre supplements (Horvath 2013). Probiotics, which are living micro‐organisms such as Lactobacillus, have also been used in managing children with RAP (Wilhelm 2008). More recently there has been interest in the use of low FODMAP (fermentable oligosaccharides, disaccharides, monosaccharides and polyols) diets in the management of irritable bowel syndrome, although the majority of studies have included adult populations (Rao 2015), with one recent randomised controlled trial in children (Chumpitazi 2015).
How the intervention might work
Probiotic‐based interventions containing living micro‐organisms are thought to improve symptoms through restoring the gut's microbial balance. It has also been suggested that they might alter the intestinal inflammatory response in the lining of the gut (Quigley 2008). Fibre‐based interventions might be effective in children with irritable bowel syndrome in particular, by modifying bowel habits and the transit time through the gut, as well as by decreasing intracolonic pressure (Romano 2013). It has been suggested that alterations in diet, such as low FODMAP interventions, may work in irritable bowel syndrome by reducing osmotic effects, fermentation, and gas production, hence decreasing distension and pain (Nanayakkara 2016).
Why it is important to do this review
Recurrent abdominal pain in children is very common, and in daily clinical practice there is no consensus on which treatments to offer patients. The approach to treating RAP is therefore inconsistent. This review, an update of one last carried out in 2009 (Huertas‐Ceballos 2009), is important to establish if there is new evidence for the effectiveness of dietary interventions in children with RAP. Together with updated reviews of pharmacological interventions, Martin 2014a, and psychosocial interventions, Abbott 2017, for RAP, this review can guide clinicians, patients, and their families in treatment decisions.
Objectives
To examine the effectiveness of dietary interventions in improving pain in children of school age with RAP.
Methods
Criteria for considering studies for this review
Types of studies
Randomised controlled trials (RCTs).
Types of participants
Children aged five to 18 years old with RAP or an abdominal pain‐related functional gastrointestinal disorder, as defined by the Rome III criteria (Rasquin 2006).
Recurrent abdominal pain is defined as at least three episodes of pain interfering with normal activities within a three‐month period. The Rome III criteria recognise five abdominal pain‐related categories: "abdominal migraine", "irritable bowel syndrome", "functional dyspepsia", "functional abdominal pain", and "functional abdominal pain syndrome" (Rasquin 2006).
Types of interventions
Any dietary intervention compared to placebo, waiting list, no treatment, or standard care.
Types of outcome measures
Primary outcomes
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Pain intensity, duration, or frequency.
There is no standard method for measuring pain in this condition. Studies may use any validated measurement of pain, and may report the proportion of participants with significant improvement in pain as defined by the trial author. We expected studies to vary in their duration of postintervention follow‐up. We therefore grouped studies according to duration of follow‐up: postintervention (immediately or the earliest data available following the end of treatment), medium‐term follow‐up (three to six months' postintervention), and long‐term follow‐up (six months or longer). See Differences between protocol and review.
Secondary outcomes
As measured by a validated tool:
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school performance (to include measures such as school functioning, behaviour, or school attendance);
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social or psychological functioning (to include measures such as anxiety or depression); and
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quality of daily life (to include measures such as quality of life or impairment to daily activities, functional disability, or activity limitations).
We also reported on adverse events, where these were monitored. See Differences between protocol and review.
We presented all outcomes in summary of findings Table for the main comparison and summary of findings Table 2.
Search methods for identification of studies
Electronic searches
We ran the first literature searches in April 2013 and updated them in April 2014, March 2015, and again in June 2016. We searched the electronic databases and trial registers listed below.
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Cochrane Central Register of Controlled Trials (CENTRAL; 2016, Issue 5) in the Cochrane Library, and which includes the Cochrane Developmental, Psychosocial and Learning Problems Specialised Register (searched 10 June 2016).
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Ovid MEDLINE In‐Process & Other Non‐Indexed Citations and Ovid MEDLINE (1946 to current; searched 9 June 2016).
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Embase Ovid (1974 to current; searched 9 June 2016).
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CINAHL Healthcare Databases Advanced Search (Cumulative Index to Nursing and Allied Health Literature; 1981 to current; searched 9 June 2016).
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PsycINFO Ovid (1806 to current; searched 9 June 2016).
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ERIC ProQuest (Educational Resources Information Center; 1966 to current; searched 9 June 2016).
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BEI ProQuest (British Education Index; 1975 to current; searched 9 June 2016).
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ASSIA ProQuest (Applied Social Sciences Index and Abstracts; 1987 to current; searched 9 June 2016).
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AMED Healthcare Databases Advanced Search (Allied and Complementary Medicine; 1985 to current; searched 9 June 2016).
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LILACS (Latin American and Caribbean Literature in Health Sciences; lilacs.bvsalud.org/en; searched 9 June 2016).
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OpenGrey (opengrey.eu; searched 9 June 2016).
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ClinicalTrials.gov (clinicaltrials.gov; searched 9 June 2016).
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World Health Organization International Clinical Trials Registry Platform (WHO ICTRP; apps.who.int/trialsearch; searched 9 June 2016).
The search terms were revised from the original Cochrane RAP reviews (Huertas‐Ceballos 2008a; Huertas‐Ceballos 2008b; Huertas‐Ceballos 2009); consequently, searches were run for all available years. We used RCT filters where appropriate and imposed no language limits. We translated any non‐English language studies identified so that they could be screened and considered for inclusion. The search strategies for each database are reported in Appendix 1.
Searching other resources
We used the Science Citation Index to locate relevant studies using the bibliographic details, and authors' names of relevant papers for forward and backward citations. We contacted researchers who have published studies in this field to ask for details of any relevant trials. We also checked the bibliographies of papers retrieved to establish if all pertinent references were found by our search.
Data collection and analysis
Selection of studies
Two review authors (TVN, AEM, RAA, AB, or RW) independently screened the titles and abstracts of studies for relevance. We obtained the full‐text reports of all potentially relevant papers and screened them for inclusion against the eligibility criteria (see Criteria for considering studies for this review). Any disagreements were resolved through discussion with a third review author (JTC). We recorded our decisions in a PRISMA diagram (Moher 2009).
Data extraction and management
Two review authors (TVN, AEM, RAA, AB, JTC, or RW) extracted the data and entered the data into Cochrane's statistical software, Review Manager 5 (Review Manager 2014). All review authors used the same data extraction form. We collected the following data.
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Study characteristics: number of participating children, inclusion and exclusion criteria, type of intervention and comparison, intervention characteristics (duration, frequency, setting), number of withdrawals.
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Participant characteristics: sex, age, diagnosis (e.g. RAP or other syndrome, as defined by the Rome III criteria) (Rasquin 2006).
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Outcome measures: measurement of pain and any secondary outcomes measured. See Types of outcome measures.
Assessment of risk of bias in included studies
We assessed the risk of bias of each included study using the Cochrane 'Risk of bias' tool (Higgins 2011a). We assessed the following categories of bias: selection bias (random sequence generation and allocation concealment), performance bias (blinding of participants and personnel), detection bias (blinding of outcome assessment), attrition bias (incomplete outcome data), reporting bias (selective reporting), and other potential sources of bias that could have altered the estimate of treatment effect; for example, any evidence of differential loss to follow‐up, whether the data collection tools were valid, whether there was sufficient power in terms of appropriate sample size, whether baseline parameters were similar, and whether data analyses were appropriate. Two review authors (TVN, AEM, RAA, AB, JTC, or RW) independently assessed and classified each study as being at 'low', 'high', or 'unclear' risk of bias across each of these domains, based on the methods detailed in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a); see Table 1 for more information. We considered a trial as having an overall low risk of bias if most of the above categories of bias were assessed as low risk of bias.
| Domain | 'Risk of bias' judgement | ||
| Low | High | Unclear | |
| Selection bias | |||
| Random sequence generation | If the study details any of the following methods: simple randomisation (such as coin‐tossing, throwing dice, or dealing previously shuffled cards, a list of random numbers, or computer‐generated random numbers) or restricted randomisation (blocked, ideally with varying block sizes or stratified groups, provided that within‐groups randomisation is not affected). | If the study details no randomisation or other inadequate method such as alternation, assignment based on date of birth, case record number, and date of presentation. These may be referred to as ‘quasi‐random’. | If there is insufficient detail to judge the risk of bias.
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| Allocation concealment | If the study details concealed allocation sequence in sufficient detail to determine that allocations could not have been foreseen in advance of or during enrolment. | If the study details a method where the allocation is known prior to assignment. | If there is insufficient detail to judge the risk of bias. |
| Performance bias | |||
| Blinding of participants and personnel | If the study details a method of blinding the participants and personnel. This requires sufficient detail to show they were unable to identify the therapeutic intervention from the control intervention. | Considering the nature of the interventions, it may not be possible to blind the participants and therapists. The effect of this will be addressed in the Discussion. | If there is insufficient detail to judge the risk of bias. |
| Detection bias | |||
| Blinding of outcome assessment | If the study details a blinded outcome assessment. This may only be possible for outcomes that are externally assessed. | If the outcome assessment is not blinded. We expect this may be unavoidable for self rated outcomes of unblinded interventions. | If there is insufficient detail to judge the risk of bias.
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| Attrition bias | |||
| Incomplete outcome data | If the study reports attrition and exclusions, including the numbers in each intervention group (compared with total randomised participants), reasons for attrition or exclusions, and any re‐inclusions. Also, the impact of missing data is not believed to alter the conclusions, and there are acceptable reasons for the missing data. | We may judge the risk of attrition bias to be high due to the amount, nature, or handling (such as per‐protocol analysis) of incomplete outcome data. | If there is insufficient detail to judge the risk of bias, e.g. if the number of people randomised to each treatment is not reported. |
| Reporting bias | |||
| Selective outcome reporting | If there is judged to be complete reporting, which will be found on comparison of the published study and protocol, if available. | If the reporting is selective, so that some outcome data are not reported. | If there is insufficient detail to judge the risk of bias, such as the protocol is not available. |
| Other sources of bias | |||
| Assessment of other sources of bias in other domains not covered by the tool, including validity of outcome measures utilised | If there is judged to be no other factors that would be likely to introduce major potential bias. | If other factors are identified that are judged to represent a high risk of bias. | If there is insufficient detail to judge the risk of other bias. |
Measures of treatment effect
We reported our study results as follows.
Continuous data
For continuous data (e.g. pain intensity or frequency), we analysed means and standard deviations (SDs), where available or could be calculated, and providing there was no clear evidence of skew in the distribution. When different scales were used to measure the same clinical outcome, we combined standardised mean differences (SMDs) across the studies. We presented the pooled estimates with 95% confidence intervals (CIs).
Dichotomous data
For dichotomous data (e.g. pain improved, yes or no), we analysed the data using odds ratios (ORs) and 95% CIs.
The definition of pain improvement varied across the studies. We used the author definition of improvement.
Unit of analysis issues
Cross‐over trials
We considered the results of this type of trial using the guidance in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b), in particular assessing whether an appropriate washout period was used. Given that RAP can be a stable and chronic condition, we considered a washout period of two to three weeks to be sufficient.
Please see Appendix 2 and our protocol, Martin 2014b, for additional methods for handling unit‐of‐analysis issues archived for use in future updates of this review.
Dealing with missing data
In the few cases where there were missing data, such as standard deviations, we contacted the original investigators to request if the missing data were available. When it was not possible to obtain the data from the original investigators, we did not impute values; this was a decision made a priori in our protocol (Martin 2014b). Studies for which authors provided additional data not originally published are detailed in the Characteristics of included studies.
Assessment of heterogeneity
We anticipated finding considerable heterogeneity among included studies. We assessed clinical heterogeneity by examining the distribution of relevant participant characteristics (e.g. age, definition of RAP) and study differences (e.g. concealment of randomisation, blinding of outcome assessors, interventions, or outcome measures). We described the statistical heterogeneity (observed variability in study results that is greater than that expected to occur by chance) by reporting the I² statistic (Higgins 2003). The I² statistic describes approximately the proportion of variation in point estimates due to heterogeneity rather than sampling error. A value of more than 50% may indicate significant heterogeneity. We used the Chi² test to further assess the strength of evidence of the heterogeneity. We regarded any result with a P value lower than 0.10 as indicating significant statistical heterogeneity. We interpreted this cautiously and used it to help quantify the impact of heterogeneity on the results of the meta‐analysis and ultimately on the GRADE quality rating (see Data synthesis). We also reported Tau² when using the random‐effects model (see Differences between protocol and review), which provides an estimate of the between‐study variance (Deeks 2011).
Assessment of reporting biases
We did not have more than 10 trials for each outcome, and so did not perform these analyses (see Appendix 2; Martin 2014b).
Data synthesis
We used Review Manager 5 for statistical analysis (Review Manager 2014). Two review authors (TVN, AEM, RAA, AB, JTC) independently entered data into Review Manager 5 (Review Manager 2014).
We anticipated significant statistical and clinical heterogeneity. We reported summary statistics for continuous data as mean differences (MDs) or SMDs using a random‐effects model, weighted using the inverse‐variance method. For dichotomous data, we also used a random‐effects model and calculated the ORs using Mantel‐Haenszel methods, as this has been shown to have better statistical properties where event rates are low or study size small (Deeks 2011).
We only conducted meta‐analyses if it was appropriate to do so, that is if the studies were sufficiently homogeneous. We thus only carried out a meta‐analysis using data from studies with equivalent dietary interventions. Where meta‐analysis was not appropriate, we provided a narrative description of the results.
For all outcomes where we conducted a meta‐analysis, we produced a 'Summary of findings' table detailing the number of trials and participants, the results of the analysis, and the GRADE rating of quality of evidence for the outcome; the procedure for this is described below.
Assessing the quality of evidence for each outcome
We used the GRADE approach to assess the overall quality of the body of evidence for a specific outcome (The Grade Working Group 2013). We used GRADEpro software to assess and present the findings in the 'Summary of findings' tables (GRADEpro GDT 2015). We completed a 'Summary of findings' table for each main treatment comparison (summary of findings Table for the main comparison; summary of findings Table 2).
For the dichotomous outcome of pain improvement, we calculated the probable outcome of events per 1000 for both the control group and those receiving the intervention, following the guidance in the Cochrane Handbook for Systematic Reviews of Interventions (Schünemann 2011a), similar to other reviews that include people with pain conditions (e.g. Eccleston 2014). We judged the studies included for each outcome using five criteria: risk of bias, indirectness, inconsistency, imprecision, and publication bias. We used limitations in the design and implementation to assess the overall risk of bias of included studies for each outcome, downgrading an outcome if the majority of studies had unclear or high risk of bias. We assessed indirectness if a population, intervention, or outcome was not of direct interest to the review. Inconsistency was determined by the heterogeneity of results. If there was evidence of significant statistical heterogeneity (see Assessment of heterogeneity), we downgraded the quality of the outcome. We assessed imprecision by the number of participants included in an outcome and by CIs; we downgraded outcomes when only a small number of participants could be included in the analysis or the analysis had wide CIs. Finally, we downgraded for publication bias if studies failed to report outcomes in the published manuscript or if there was a suspicion that null findings had not been published or reported (Schünemann 2011b).
We gave each outcome a quality rating ranging from 'very low' to 'high'. High‐quality ratings are given when "further research is unlikely to change our estimate of effect". Moderate‐quality ratings are given when "further research is likely to have an important impact on our confidence in the estimate of effect and may change the estimate". Low‐quality ratings are given when "further research is very likely to have an important impact on our confidence in the estimate of effect and is likely to change the estimate". Finally, very low‐quality ratings are given when "we are very uncertain about the estimate" (Balshem 2011).
Subgroup analysis and investigation of heterogeneity
Where data were available, we carried out subgroup analyses by subtype of RAP and by duration of follow‐up, as specified in our protocol (Martin 2014b).
Sensitivity analysis
In our protocol we planned to carry out sensitivity analyses to assess the robustness of our conclusions in relation to two aspects of study design (Martin 2014b). We intended to assess: 1) the effect of inadequate allocation concealment, and 2) the effect of inadequate blinding to treatment, by removal of studies judged to be at high or unclear risk of bias in these domains. We performed sensitivity analyses where pooled analyses included such studies.
Results
Description of studies
For a full description of the main characteristics of the studies, including details on participants and setting, intervention aspects, and outcome measures, see: Characteristics of included studies; Characteristics of excluded studies; Characteristics of studies awaiting classification.
Results of the search
For this updated review, we chose to redesign the search strategy in order to include the recognised terms for different types of RAP, as defined by the Rome criteria (Rasquin 2006). Consequently, we ran our searches across the databases with no date restriction. The results of the searching and screening are shown in the PRISMA flow chart (Figure 1). We screened a total of 9649 titles and abstracts, of which 231 were carried forward for further screening at full text. We excluded 203 reports at full text and included 27 reports (19 studies) in the review. One study is awaiting classification (Jarocka‐Cyrta 2002).
PRISMA study flow diagram
Included studies
We included 19 studies in this review, which were reported in 27 papers, four of which were included in the previous version of our review (Bausserman 2005; Feldman 1985; Gawronska 2007; Young 1997). Two of the included studies were only reported as abstracts, and we were unable to obtain further details of the methods or results; either we could not contact the authors of the studies or the authors were unable to provide the details requested (Sabbi 2011; Young 1997). However, based on the data in the abstracts, the studies met the inclusion criteria (Sabbi 2011; Young 1997).
Thirteen studies were trials of probiotic‐based interventions (Asgarshirazi 2015; Bausserman 2005; Eftekhari 2015; Francavilla 2010; Gawronska 2007; Giannetti 2017; Guandalini 2010; Kianifar 2015; Romano 2010; Sabbi 2011; Saneian 2015; Weizman 2016; Young 1997), and four studies were trials of fibre‐based interventions (Feldman 1985; Horvath 2013; Romano 2013; Shulman 2016). One study was a trial of a low FODMAP diet (Chumpitazi 2015), and one was a trial of a fructose‐restricted diet (Wirth 2014). All included studies were written in English. We contacted the authors of Romano 2010 and Shulman 2016, and they provided raw data for pain frequency and intensity outcomes, as these were not included in the published paper. The authors of Asgarshirazi 2015 also provided additional data. For more information, please see below and the Characteristics of included studies tables.
Participants
The 19 included studies involved a total of 1453 children. Thirteen studies, with a total of 1017 children, investigated the effects of probiotics versus placebo (Asgarshirazi 2015; Bausserman 2005; Eftekhari 2015; Francavilla 2010; Gawronska 2007; Giannetti 2017; Guandalini 2010; Kianifar 2015; Romano 2010; Sabbi 2011; Saneian 2015; Weizman 2016; Young 1997). Four studies, with a total of 299 children, investigated the effects of fibre‐based interventions versus placebo (Feldman 1985; Horvath 2013; Romano 2013; Shulman 2016). The single study of the FODMAP diet versus typical diet included 34 children (Chumpitazi 2015), and the trial of a fructose‐restricted diet included 103 children (Wirth 2014). Eleven included trials randomised between 50 and 90 children; the smallest study included only 11 children (Young 1997), and the six largest more than 100 each (Asgarshirazi 2015; Francavilla 2010; Gawronska 2007; Shulman 2016; Weizman 2016; Wirth 2014). Participants were aged between four and 18 years, with the mean age at recruitment ranging from 6.3 years to 13.1 years. Girls outnumbered boys in most included trials. Fourteen trials recruited children with a diagnosis under the broad umbrella of RAP or functional gastrointestinal disorders; five trials specifically recruited only children with irritable bowel syndrome (Bausserman 2005; Chumpitazi 2015; Guandalini 2010; Kianifar 2015; Shulman 2016). In Shulman 2016, children were only randomised if they first failed to respond to an eight‐day exclusion diet eliminating carbohydrates (defined as 75% or less improvement in abdominal pain frequency and severity).
Settings
The majority of studies took place in paediatric gastroenterology clinics. In Francavilla 2010, children were recruited from primary care paediatric practices, and in Feldman 1985 children came from private general practice practices and community paediatric clinics. Children in Shulman 2016 and Weizman 2016 came from care networks, including both primary and tertiary care. Chumpitazi 2015 advertised for participants from community settings as well as recruiting from paediatric gastroenterology clinics.
Location
Trials took place across eight countries. Six studies were conducted in Italy (Francavilla 2010; Giannetti 2017; Guandalini 2010; Romano 2010; Romano 2013; Sabbi 2011), four in Iran (Asgarshirazi 2015; Eftekhari 2015; Kianifar 2015; Saneian 2015), four in the USA (Bausserman 2005; Chumpitazi 2015; Shulman 2016; Young 1997), two in Poland (Gawronska 2007; Horvath 2013), and one each in Canada (Feldman 1985), Israel (Weizman 2016), Germany (Wirth 2014), and India (Guandalini 2010).
Interventions
We classified interventions into four groups: probiotic‐based interventions, fibre‐based interventions, low FODMAP‐based diet interventions, and fructose‐restricted diets. We did not include peppermint oil as a dietary intervention but categorised it as pharmacological; trials of this intervention are therefore considered in the companion pharmacological review (Martin 2014a).
Probiotic interventions
Thirteen trials used probiotic‐based interventions. Not all trials assessed the same probiotic‐based intervention. Five trials used Lactobacillus rhamnosus GG in slightly different preparations (Bausserman 2005; Francavilla 2010; Gawronska 2007; Kianifar 2015; Sabbi 2011). Three other trials used Lactobacillus reuteri (Eftekhari 2015; Romano 2010; Weizman 2016). The probiotic in Young 1997 was Lactobacillus plantarum (LP299V). Guandalini 2010 was a cross‐over trial where the intervention was VSL#3, a probiotic preparation of different strains. Giannetti 2017 was a cross‐over trial using a mixture of three Bifidobacterium species.Saneian 2015 and Asgarshirazi 2015 used Bacillus coagulans plus fructo‐oligosaccharides. The treatment period ranged from four weeks, in Asgarshirazi 2015, Bausserman 2005, Eftekhari 2015, Gawronska 2007, Kianifar 2015, Romano 2010, Saneian 2015, and Weizman 2016, to eight weeks, in Francavilla 2010. In most studies, outcomes were measured immediately postintervention; the longest period of follow‐up was 16 weeks, in Francavilla 2010. Only two studies measured outcomes at three to 12 months' postintervention (Francavilla 2010; Saneian 2015).
Fibre interventions
Four trials used fibre‐based interventions. These included a fibre biscuit containing 5 g of corn fibre (Feldman 1985), a preparation of partially hydrolysed guar gum (PHGG) (Romano 2013), a preparation of glucomannan (GNN) (Horvath 2013), and psyllium fibre (Shulman 2016). The treatment period ranged from four weeks, in Romano 2013 and Horvath 2013, to six weeks, in Feldman 1985 and Shulman 2016. Three of the studies measured outcomes immediately postintervention (Feldman 1985; Horvath 2013; Shulman 2016), and the fourth measured outcomes immediately postintervention and four weeks afterwards (Romano 2013).
Low FODMAP interventions
Only one included trial examined a low FODMAP diet intervention. Chumpitazi 2015 was a cross‐over trial comparing a two‐day low FODMAP diet intervention with a control of a typical American childhood diet (TACD). Outcomes were measured immediately after intervention at two days. We found no other RCTs of low FODMAP diets.
Fructose‐restricted diets
We found one trial of a fructose‐restricted diet (Wirth 2014), where participants with RAP for more than three months were randomised to a specified low‐fructose diet or a standard diet for two weeks, with outcomes measured immediately postintervention. We found no other eligible RCTs of this type of intervention.
Comparators
All included trials assessed the dietary intervention against a placebo comparison, with the exception of Chumpitazi 2015 and Wirth 2014, where the comparator was a standard diet. Asgarshirazi 2015 was a three‐arm trial where probiotics were compared against peppermint oil and placebo; however, only the probiotics versus placebo comparison was reported in this review.
Outcomes
The primary outcomes of this review related to abdominal pain, and pain outcomes were reported in every trial. Studies reported on pain in terms of pain improvement (usually defined as a percentage or number of points improved from baseline, or being pain‐free), pain severity/intensity, or pain frequency; or a combination of all three. Pain was most commonly assessed using versions of the Faces Pain Scale (Bieri 1990; McGrath 1996; Wong 1988), or by using a standard visual analogue scale, typically with a range of 0 to 10. Other studies used more general measures to assess improvement in symptoms, including pain, such as the Subject's Global Assessment of Relief Child version (SGARC) (Muller‐Lissner 2003). A number of studies specified that the outcome was child reported (Francavilla 2010; Gawronska 2007; Guandalini 2010; Shulman 2016). In other studies it was not specified whether the parent or child was completing the measure, or it was stated that pain was reported by "child or family/parent". As the age range in most studies was wide, this is likely to have influenced who was reporting on the measures. Authors usually reported that pain was assessed on a daily basis (Asgarshirazi 2015; Bausserman 2005; Chumpitazi 2015; Feldman 1985; Francavilla 2010; Giannetti 2017; Guandalini 2010; Romano 2010; Shulman 2016; Weizman 2016). Wirth 2014 reported that symptoms were recorded at the end of the intervention. In the remaining studies the frequency of measure completion was not clearly described.
Secondary outcomes included in this review were school performance, social or psychological functioning, and quality of daily life. Not all studies measured these outcomes. Gawronska 2007, Horvath 2013, and Weizman 2016 reported on school absenteeism, and Guandalini 2010 and Horvath 2013 reported on disruption of daily activities. Participants in Kianifar 2015 reported on both absence from school and disruption of social activities as part of functional changes on a three‐point Likert scale. In Giannetti 2017, participants completed the Functional Disability Inventory (Claar 2006), which assesses physical and psychosocial functions and quality of life. In Shulman 2016, participants completed Paediatric Quality of Life Generic Core Scales (Varni 2015).
Adverse events
All studies except Feldman 1985 and Wirth 2014 reported that they monitored children for adverse events. This information was not available in the two included abstracts, and the authors either did not respond to requests for further information (Sabbi 2011), or they were unable to provide details (Young 1997).
Funding
Ten studies did not report their source of funding (Asgarshirazi 2015; Feldman 1985; Francavilla 2010; Giannetti 2017; Horvath 2013; Romano 2010; Romano 2013; Weizman 2016; Wirth 2014; Young 1997). Four studies reported being funded by their university (Eftekhari 2015; Gawronska 2007; Kianifar 2015; Saneian 2015); one was funded by "locally available grants", although the intervention and placebo were provided by industry (Guandalini 2010), and one study was funded by a university seed grant (Bausserman 2005). Shulman 2016 was funded by various organisations, including the US National Institutes of Health and the US Department of Agriculture. Chumpitazi 2015 was funded by an academic society in conjunction with Nestlé and the National Institutes of Health.
Excluded studies
The PRISMA diagram (Figure 1) outlines the number of studies excluded at the full‐text screening stage (n = 231). The majority of these clearly involved an ineligible population (e.g. adults) or ineligible interventions (psychosocial or pharmacological), and therefore we have not listed or described these further. However, we excluded six studies for less obvious reasons, and have described these here and listed them in the Characteristics of excluded studies section.
We excluded three studies that were included in the 2009 review, Huertas‐Ceballos 2009, on the grounds of study design (Christensen 1982; Dearlove 1983; Lebenthal 1981). Christensen 1982 and Dearlove 1983 did not appear to be RCTs. It was also unclear whether participants in Lebenthal 1981 were randomised, and as we were unable to clarify this with the authors, we also excluded this study.
From our updated search in 2016, we excluded one study that was not a RCT (Agah 2015). We excluded two further studies because they used ineligible comparators (Chumpitazi 2014; Edwards 1991).
Risk of bias in included studies
We rated all included studies for risk of bias across the following categories: random sequence generation (selection bias), allocation concealment (selection bias), blinding of participants and personnel (performance bias), blinding of outcome assessment (detection bias), incomplete outcome data (attrition bias), selective reporting (reporting bias) and other potential sources of bias (other bias). Figure 2 displays the review authors' assessments of risk of bias for each study individually, and Figure 3 represents the authors' judgements about each risk of bias item presented as percentages across all included studies.
Risk of bias summary: review authors' judgements about each risk of bias item for each included study.
Risk of bias graph: review authors' judgements about each risk of bias item presented as percentages across all included studies.
Allocation
We rated no studies as being at high risk of bias in this domain.
Random sequence generation
We judged that the majority of studies had adequately randomised their participants as they used appropriate methods of randomisation as detailed in Table 1, such as computer‐generated random numbers. The exceptions were Asgarshirazi 2015, Eftekhari 2015, and Wirth 2014, all of which we rated as being at unclear risk in this domain due to insufficient detail provided about how randomisation was performed. We also rated the two studies for which only abstracts were available as at unclear risk of bias in this domain due to insufficient detail provided about randomisation (Sabbi 2011; Young 1997).
Allocation concealment
The most frequently encountered issue in assessing the risk of selection bias was poorly described allocation sequence concealment. The authors of seven studies provided insufficient detail on how this was done, leading to an assessment of unclear risk of bias (Asgarshirazi 2015; Eftekhari 2015; Feldman 1985; Romano 2013; Sabbi 2011; Wirth 2014; Young 1997).
Blinding
Blinding of participants and personnel
Most studies described the use of identical placebos and double‐blinding of participants and personnel, and so we judged them to be at low risk of performance bias. However, we rated Asgarshirazi 2015 as being at unclear risk of bias for this outcome, as although the study was blinded, the placebo regimen of folic acid tablets was different in timing and frequency to the intervention regimen, and the authors did not discuss the possible impact of this. In Chumpitazi 2015, the study was described as double‐blinded, but it was unclear whether the intervention and control diets were delivered in identical containers or what clues there might have been to the allocation, hence we also rated this study as being at unclear risk of bias. We rated one study as being at high risk of bias for this domain, as the children who rated their own symptoms were not blinded (Wirth 2014).
Blinding of outcome assessment
Outcomes were assessed by parents, children, and clinicians; the issues described above regarding blinding of participants and personnel also applied to the blinding of outcome assessment, consequently we rated all studies as being at low risk of bias for this domain with the exception of Asgarshirazi 2015, Chumpitazi 2015, Sabbi 2011, and Wirth 2014.
Incomplete outcome data
We rated 10 studies as being at unclear risk of attrition bias; many studies did not fully report outcome data, making it difficult to assess the risk of attrition bias (Asgarshirazi 2015; Eftekhari 2015; Horvath 2013; Kianifar 2015; Romano 2010; Sabbi 2011; Saneian 2015; Weizman 2016; Wirth 2014; Young 1997). For example, in Asgarshirazi 2015, 32 children were excluded during the trial after randomisation and not analysed because they did not complete the one‐month intervention; according to the authors this was "due to journey or lack of 2 weeks visit", but information was insufficient to determine if this could have resulted in attrition bias. Also, in Weizman 2016, the authors state that an intention‐to‐treat analysis was carried out, but the paper also states that eight participants were excluded due to "poor compliance and violation of the protocol" and not analysed, hence the exact methodology was unclear. Again, for the two studies for which only abstracts were available, insufficient detail was provided, so they too were rated as being unclear risk of bias for this domain (Sabbi 2011; Young 1997).
Selective reporting
We did not rate any studies as being at high risk of bias for this domain. Feldman 1985 presented insufficient information to assess reporting bias and so was judged to be at unclear risk of bias. We also judged Guandalini 2010 to be at unclear risk of reporting bias as comparisons were made pre/post and not between intervention and control at six weeks. Again, for the two studies for which only abstracts were available, insufficient detail was provided, so they too were rated as being unclear risk of bias for this domain (Sabbi 2011; Young 1997).
Other potential sources of bias
We rated the risk of other potential biases (such as validity of data collection tools, appropriate sample size, similarity of baseline details) as low for included studies for which we had the full text, as we did not find any other major sources of bias that would likely affect the results. The exceptions were Asgarshirazi 2015, which we rated at high risk of bias as there were imbalances in measures of pain at baseline; Wirth 2014, which we rated as being at unclear risk of bias as no details were given regarding the use of validated tools or of adherence; and Sabbi 2011 and Young 1997, which we also rated at unclear risk of bias due to insufficient information in the abstracts.
Effects of interventions
See: Summary of findings for the main comparison Probiotics compared to placebo for recurrent abdominal pain in childhood; Summary of findings 2 Fibre versus placebo for recurrent abdominal pain in childhood
We were able to perform a total of 10 analyses across the studies. We performed analyses within intervention type, as the mechanisms of action of each dietary intervention are different. We only performed analyses on those studies that provided equivalent outcome data in comparable formats, therefore not all studies within each intervention type were entered into the analyses.
For probiotic‐based interventions, we were able to perform three analyses for our primary outcomes (effects on pain frequency, pain intensity, and pain improvement), at zero to three months' postintervention. As four studies included only children with irritable bowel syndrome, or reported outcomes for this group separately, as per our protocol (Martin 2014b), we were also able to perform a subgroup analysis for this group for the outcome of improvement in pain at zero to three months' postintervention. We were able to perform one analysis for the outcome of improvement in pain at three to six months' postintervention. We also were able to perform sensitivity analyses for three outcomes, by removing studies judged to be at unclear or high risk of bias in the domains of allocation concealment, blinding of participants and personnel, and/or blinding of outcome assessment.
For fibre‐based interventions, we were able to perform two analyses: effect on pain improvement and change in pain intensity postintervention (zero to three months).
We were unable to perform any analyses for low FODMAP diet interventions or for fructose‐restricted diets, as we found only one study in each category eligible for inclusion.
We were unable to perform any pooled analyses of secondary outcomes for any dietary intervention, as these were either not reported or reported in formats that were not comparable. The results of individual studies are briefly presented below, followed by the results of the pooled analyses.
We assessed the quality of evidence using the GRADE criteria (The Grade Working Group 2013), and presented our ratings in 'Summary of findings' tables, which we constructed using GRADEpro software (GRADEpro GDT 2015). Within probiotic‐based interventions, we scored the evidence for the three improvement in pain outcomes as moderate quality, meaning that further research is likely to have an important impact on our confidence in the estimate of effect and may change the estimate. For the change in pain intensity and frequency outcomes, we rated the evidence as low quality, meaning that future research is likely to have an important impact on our confidence in the estimate of effect and is likely to change the estimate. See summary of findings Table for the main comparison. For fibre‐based interventions, we rated the evidence for the change in pain intensity and improvement in pain outcomes as low quality. See summary of findings Table 2.
Comparison 1: Probiotic interventions versus placebo
Thirteen included studies assessed the effects of probiotics (Asgarshirazi 2015; Bausserman 2005; Eftekhari 2015; Francavilla 2010; Gawronska 2007; Giannetti 2017; Guandalini 2010; Kianifar 2015; Romano 2010; Sabbi 2011; Saneian 2015; Weizman 2016; Young 1997).
Primary outcomes
Results of individual studies
Here, we briefly present the results of the individual studies (please note, we could only provide exact P values when these were available in the original report).
Change in pain frequency, change in pain intensity, and improvement in pain
Asgarshirazi 2015 reported on pain severity, duration, and frequency immediately following a four‐week intervention with Bacillus coagulans plus fructo‐oligosaccharides. Mean decrease in pain duration and pain frequency was greater in the probiotic group compared to the placebo group (P = 0.012 and P < 0.001, respectively).
Bausserman 2005 reported no difference between the probiotic arm and placebo arm in response to treatment, defined as improvement in abdominal pain of one or more levels, at six weeks (OR 1.18, 95% CI 0.38 to 3.63). There was also no difference between the two groups in terms of mean change in pain (P = 0.175) as measured by the Gastrointestinal Symptoms Rating Scale (Svedlund 1988).
Eftekhari 2015 reported no significant difference in pain intensity, pain frequency, or improvement in pain between probiotic and placebo arms at four and eight weeks' postintervention. At both time points, pain intensity and severity in both groups were significantly reduced from baseline (P < 0.001).
Francavilla 2010 reported results at eight and 16 weeks' postintervention. At eight weeks, treatment success was experienced by 72% of children in the probiotic group and 53% of children in the placebo group (OR 2.18, 95% CI 1.07 to 4.45), and the difference was maintained at 16 weeks (79% intervention, 62% control; P < 0.03). Pain intensity was lower in the intervention group at eight weeks (P < 0.01), and pain frequency was reduced at eight weeks (P < 0.01) and 12 weeks (P < 0.02).
Gawronska 2007 reported that at four weeks, 25% of the intervention group experienced treatment success in terms of no pain compared to 9.6% of the placebo group (OR 3.1, 95% CI 1.03 to 9.56). Overall, 25 children receiving probiotics experienced improvement in pain compared to 23 receiving placebo (OR 1.17, 95% CI 0.62 to 2.21). No other significant differences in outcome measure were reported, including change in pain frequency and intensity.
Guandalini 2010 reported only pre/post comparisons on change in pain frequency and intensity at week six, and we could obtain no additional information for these outcomes to enter in the meta‐analysis. At six weeks, 44 of 59 children experienced an improvement in pain in the intervention arm of the cross‐over, compared to 29 children in the placebo group (OR 3.03, 95% CI 1.4 to 6.6).
Giannetti 2017 was a cross‐over RCT with a six‐week treatment period and a two‐week washout period. The primary outcome was being pain‐free at six weeks. In children with irritable bowel syndrome, 42% experienced full resolution on probiotic versus 14% on placebo (P = 0.003); in those with functional dyspepsia there was no improvement (21% versus 32%; P = 0.5).
Kianifar 2015 measured pain severity at four weeks; the mean score in the probiotic group was significantly lower than the mean score in the placebo group at this time point (P < 0.001).
In Romano 2010, the intervention group experienced a significant decrease in pain intensity at eight weeks (P < 0.001), and both groups had a decrease in pain frequency at the same time point (P < 0.05).
Sabbi 2011 reported outcomes at six and 10 weeks. In the probiotic group, there was a significant reduction of both frequency (P < 0.01) and severity (P < 0.01) of abdominal pain at six weeks. These differences were still present at 10‐week follow‐up (P < 0.02 and P < 0.001, respectively).
In Saneian 2015, a higher proportion of children in the intervention group (60%) compared to the control group (39.5%) were defined as treatment responders at four weeks (P = 0.044), but this difference was not sustained at 12 weeks (64.4% intervention, 53.4% control; P = 0.204). The authors reported no statistically significant difference between intervention and control in terms of physician‐rated global pain severity or global improvement.
In Weizman 2016, pain intensity was significantly reduced in the intervention group compared to the placebo group at four weeks (P < 0.01) and eight weeks (P < 0.02); the difference in pain frequency was significant at four weeks (P < 0.02) but was not sustained at eight weeks (P = 0.09).
Young 1997 was a cross‐over RCT. In the abstract the authors report that children treated with probiotic had a significant reduction in symptoms at four weeks when compared to baseline, whereas placebo treatment did not produce significant improvement.
Results of pooled analyses
See summary of findings Table for the main comparison.
Change in pain frequency
We pooled data from six studies at zero to three months' postintervention in a meta‐analysis to examine change in pain frequency (Asgarshirazi 2015; Eftekhari 2015; Francavilla 2010; Gawronska 2007; Romano 2010; Weizman 2016). The SMD of effect across the studies was ‐0.55 (95% CI ‐0.98 to ‐0.12; Z = 2.52; P = 0.01; 523 children; Analysis 1.1). However, there was significant statistical heterogeneity (Tau² = 0.23; Chi² = 28.10; I² = 82%; P for heterogeneity < 0.001). Using GRADE, we rated the quality of evidence for this outcome as low, downgrading it two levels due to risk of bias in the included studies and the statistical heterogeneity. For our planned sensitivity analysis, we identified two included studies where there was an unclear risk of bias in relation to allocation concealment or blinding of participants and personnel and/or blinding of outcome assessment (Asgarshirazi 2015; Eftekhari 2015), and repeated the pooled analysis after excluding these two studies. The estimate of effect was a SMD of ‐0.54 (95% CI ‐0.94 to ‐0.14; Z = 2.62; P = 0.009; 4 studies; 389 children; Tau² = 0.12; Chi² = 11.24; I² = 73%; P for heterogeneity = 0.01; Analysis 1.2). Removing these studies therefore did not appreciably change the estimate of effect from the main analysis in Analysis 1.1.
Change in pain intensity
We entered data from seven studies into the meta‐analysis of change in pain intensity (Asgarshirazi 2015; Eftekhari 2015; Francavilla 2010; Gawronska 2007; Kianifar 2015; Romano 2010; Weizman 2016). The SMD of effect across the studies was ‐0.50, (95% CI ‐0.85 to ‐0.15; Z = 2.80; P = 0.005; 575 children; Analysis 1.3), and again there was considerable statistical heterogeneity (Tau² = 0.17; Chi² = 24.95; I² = 76%; P for heterogeneity < 0.001). Using GRADE, we rated the quality of evidence for this outcome as low, downgrading it two levels due to risk of bias in the included studies and the statistical heterogeneity. We were able to perform a sensitivity analysis (again excluding Asgarshirazi 2015 and Eftekhari 2015). The estimate of effect in the sensitivity analysis was a SMD of ‐0.68 (95% CI ‐1.05 to ‐0.30; P = 0.001; 5 studies; 441 children; Tau² = 0.13; Chi² = 14.00; I² = 71%; P for heterogeneity = 0.007; Analysis 1.4). Again, this did not result in appreciable change to the estimate of effect from the main analysis in Analysis 1.3.
Improvement in pain
Seven studies (722 children) were eligible for meta‐analysis for the outcome of improvement in pain (Bausserman 2005; Eftekhari 2015; Francavilla 2010; Gawronska 2007; Giannetti 2017; Guandalini 2010; Saneian 2015). The OR for pain improvement at zero to three months' postintervention was 1.63 (95% CI 1.07 to 2.47; Z = 2.27; P = 0.02; Tau² = 0.14; Chi² = 10.98; I² = 45%; P for heterogeneity = 0.09; Analysis 1.5), with eight as the number needed to treat for an additional beneficial outcome (NNTB) (see Figure 4). Using GRADE, we rated the quality of the evidence for this outcome as moderate, downgrading it one level due to evidence of statistical heterogeneity. In this analysis, the heterogeneity appeared to have been introduced by one of the new studies in the update search (Eftekhari 2015); prior to its inclusion in the pooled analysis there was no significant evidence of statistical heterogeneity (Tau² = 0.00; I² = 0%; P for heterogeneity = 0.41). On examination of the forest plot (see Figure 4), Eftekhari 2015 was also the only study where the point estimate of effect favours placebo rather than probiotic (OR 0.54, 95% CI 0.22 to 1.32). We carried out a planned sensitivity analysis by removing Eftekhari 2015 from the pooled analysis due to our judgement on the risk of bias present in this study. The resulting estimate of effect was an OR of 1.95 (95% CI 1.40 to 2.70; Z = 3.97; P < 0.001; 6 studies; 642 children; Tau² = 0.00; Chi² = 3.96; I² = 0%; P for heterogeneity = 0.56; Analysis 1.6).
Forest plot of comparison: 1 Probiotics versus placebo, outcome: Improvement in pain 0 to 3 months' postintervention.
We were able to perform one subgroup analysis of improvement in pain at zero to three months' postintervention for 344 children with irritable bowel syndrome only (Analysis 1.7). This included four studies (Bausserman 2005; Francavilla 2010; Giannetti 2017; Guandalini 2010). The OR for pain improvement at zero to three months' postintervention was 3.01 (95% CI 1.77 to 5.13; Z = 4.06; P < 0.001; Tau² = 0.06; Chi² = 3.77; I² = 21%; P for heterogeneity = 0.29), with a NNTB of four. Using GRADE, we rated the quality of the evidence for this outcome as moderate, downgrading it one level for imprecision, due to small numbers of participants in included studies.
Only two studies (224 children) were eligible for inclusion in an analysis of improvement in pain at three to six months' postintervention (Francavilla 2010; Saneian 2015), as most studies had short follow‐up periods. The OR for pain improvement at three to six months' postintervention was 1.94 (95% CI 1.10 to 3.43; Z = 2.28; P = 0.02; Tau² = 0.00; Chi² = 0.41; I² = 0%; P for heterogeneity = 0.52; Analysis 1.8), with a NNTB of seven. Using GRADE, we rated the quality of the evidence for this outcome as moderate, downgrading it one level due to imprecision.
Secondary outcomes
Results of individual studies
School performance
Gawronska 2007 assessed school absenteeism (included as a secondary outcome) as a dichotomous measure in 104 children (reported in diaries) and found no difference between control and intervention groups (P = 0.44). In Weizman 2016, the 101 included children kept a school absence diary; postintervention there was no significant difference in the number of days of absence between the two groups (2.7 versus 1.9 days per four weeks, in the placebo and the probiotic groups, respectively; P = 0.08). Kianifar 2015 assessed "functional changes", which included disruption of social activities, need to see a doctor, use of medications, and days of absence from school, on a three‐point Likert scale. The authors reported that this measure improved significantly in the probiotic group at four weeks' postintervention (2.4 (SD 0.5) in the probiotic group, 1.9 (SD 0.4) in the placebo group; P < 0.001).
Social or psychological functioning
Kianifar 2015 included "disruption of social activities" as part of their "functional changes" outcome, the results of which are reported above.
Quality of daily life
In Guandalini 2010, caregivers of 59 children were asked to assess family life disruption; the trial reported improvement in family life disruption after six weeks in the intervention group (P < 0.001), which was not present in the placebo group. Giannetti 2017 used the Functional Disability Assessment to measure quality of life (Claar 2006). An improved quality of life was reported by 46% of children with irritable bowel syndrome after probiotics, versus 16% after placebo (P = 0.002). There was no difference in the functional dyspepsia group.
Adverse events
Ten of the 13 studies included in this comparison reported that the probiotic was well tolerated and that there were no adverse events. In Saneian 2015, participants were specifically asked about a checklist of adverse effects; the only symptom where there was a significant difference was that of dry mouth, reported by 44% of the intervention group and 23% of the control group. The studies by Sabbi 2011 and Young 1997 were reported in abstracts and did not report on adverse events.
Results of pooled analyses
No pooled analyses were possible.
Comparison 2: Fibreinterventions versus placebo
Four studies assessed the effects of fibre in various forms (Feldman 1985; Horvath 2013; Romano 2013; Shulman 2016).
Primary outcomes
Results of individual studies
Change in pain frequency
Feldman 1985 only reported figures for improvement in frequency of pain at six weeks: 13 out of 26 children in the fibre cookie group and 7 out of 26 children in the placebo group experienced the outcome of improvement in pain following intervention (OR 2.71, 95% CI 0.85 to 8.64). No numerical data were given for the other outcome of improved intensity of pain, which was simply described as "not significant".
In Shulman 2016, the authors reported a significant reduction in pain frequency in the fibre group compared with the placebo group using the Numerical Rating Scale (NRS‐11) (McGrath 1996) after the six‐week intervention (P = 0.03).
Change in pain intensity
In Romano 2013, pain intensity was rated at baseline and at eight weeks' follow‐up using the Wong‐Baker FACES Pain Rating Scale (Wong 1988); whilst there was a greater decrease in intensity in the intervention group, this was not statistically significant at the P < 0.05 level.
Improvement in pain
Horvath 2013 measured improvement in pain using the Faces Pain Scale at four weeks (Bieri 1990): 23 out of 41 children in the intervention arm and 20 out of 43 in the placebo arm experienced the outcome of improvement in pain following intervention (OR 1.47, 95% CI 0.62 to 3.47).
Results of pooled analyses
See summary of findings Table 2.
Change in pain frequency
We were not able to pool data for this outcome as it was either not reported in these studies or there was no equivalent outcome data.
Change in pain intensity
We were able to pool data from Romano 2013 and Shulman 2016 in a meta‐analysis for the outcome of change in pain intensity at zero to three months' postintervention. Both studies included only children with irritable bowel syndrome. The SMD of effect across the studies was ‐1.24 (95% CI ‐3.41 to 0.94; Z = 1.11; P = 0.27; 2 studies; 135 children; Tau² = 2.38; Chi² = 28.91; I² = 97%; P for heterogeneity < 0.001; Analysis 2.1). The 95% CIs for the point estimates of SMD in both studies did not overlap, and very high statistical heterogeneity was detected according to Chi² and I² tests. Romano 2013 used a tertiary clinic sample, and Shulman 2016 used a mixed population recruited from primary and specialist care. Using GRADE, we downgraded the quality of evidence for this outcome by two levels to low, based on the high levels of heterogeneity and the imprecision of the estimate.
Improvement in pain
We pooled data from Feldman 1985 and Horvath 2013 (136 children) in a meta‐analysis for the dichotomous outcome of improvement in pain at zero to three months' postintervention. The total number of events in the meta‐analysis was fewer than 70, with a consequently imprecise estimate. The pooled OR was 1.83 (95% CI 0.92 to 3.65; Z = 1.71; P = 0.09; 2 studies; 136 children; Tau² = 0.00; Chi² = 0.69; I² = 0%; P for heterogeneity = 0.40; Analysis 2.2; Figure 5). Using GRADE, we rated the quality of evidence for this outcome as low due to an unclear risk of bias in a number of domains in the included studies and the small numbers of events (fewer than 100).
Forest plot of comparison: 2 Fibre versus placebo, outcome: Improvement in pain 0 to 3 months' postintervention.
Secondary outcomes
Results of individual studies
School performance
Horvath 2013 reported on the frequency of school absenteeism in 84 children as described by parents (no specific measure reported), and found no significant difference between intervention and control groups (P = 0.56).
Social or psychological functioning
No studies reported data on this outcome.
Quality of daily life
Horvath 2013 reported no difference between intervention and control groups in changes in daily activities in 84 children (no measure reported) (P = 0.37). Shulman 2016 reported on health‐related quality of life using the Pediatric Quality of Life Generic Core Scales (Varni 2015); no difference was found between the intervention and control groups on child report (P = 0.73) or parent report (P = 0.99).
Adverse events
Horvath 2013 reported that no adverse events had occurred, although four children in the intervention group complained of symptom exacerbation compared to two in the placebo group; Romano 2013 and Shulman 2016 also reported that no adverse events had occurred. Feldman 1985 did not report adverse events.
Results of pooled analyses
No pooled analyses were possible.
Comparison 3: Low FODMAP diet versus normal diet
We found only one eligible study that examined the effect of a low FODMAP diet. Chumpitazi 2015 compared two days of a low FODMAP diet to two days of a typical American childhood diet (TACD) in 33 children using a cross‐over study design.
Primary outcomes
Results of individual studies
Change in pain frequency
Fewer episodes of abdominal pain per day occurred during the low FODMAP diet versus the control diet (P < 0.05), and compared to baseline, children had fewer daily abdominal pain episodes during the low FODMAP diet (P < 0.01), but more episodes during the control diet (P < 0.01). Exact P values were not reported in the paper.
Change in pain intensity
Median pain severity decreased on both diets in comparison to baseline (low FODMAP diet P < 0.001, TACD P < 0.01; exact P values not reported in the paper).
Improvement in pain
Eight children were categorised as responders (children who had significant improvement in pain on the low FODMAP diet only), 15 as non‐responders (children who did not have significant improvement on the low FODMAP diet or TACD), and 10 as placebo responders (children who improved on both diets or only on the TACD).
Results of pooled analyses
No pooled analyses were possible.
Secondary outcomes
Results of individual studies
No studies reported data on school performance, social or psychological functioning, or quality of daily life. No adverse effects were reported.
Results of pooled analyses
No pooled analyses were possible.
Comparison 4: Fructose‐restricted diet versus normal diet
We found only one eligible study that examined the effect of a fructose‐restricted diet. In Wirth 2014, children with RAP for more than three months were randomised to two weeks of a fructose‐restricted diet or two weeks of a normal diet. Pain intensity and frequency were measured at baseline and postintervention.
Primary outcomes
Results of individual studies
Change in pain frequency
In Wirth 2014, 37 out of 50 (74%) of children in the intervention group and 29 out of 51 (57%) in the control group reported a reduction in the number of pain episodes per week; both reductions were described as 'statistically significant'.
Change in pain intensity
Wirth 2014 reported a significant decrease in pain intensity in the intervention group after treatment (P < 0.001), and no difference in pain intensity in the control group.
Improvement in pain
No studies reported this outcome.
Results of pooled analyses
No pooled analyses were possible.
Secondary outcomes
No studies reported data on school performance, social or psychological functioning, or quality of daily life. Wirth 2014 did not report on adverse effects.
Results of pooled analyses
No pooled analyses were possible.
Discussion
Summary of main results
We included 19 studies with a total of 1453 participants in this review. With the exception of two studies, all studies assessed a treatment arm of probiotic or fibre‐based interventions against placebo, with an average treatment duration of six weeks. The remaining two studies assessed a dietary intervention (low FODMAP diet or fructose‐restricted diet) against a normal control diet. This update extends the evidence base in this area through the inclusion of 15 new studies, along with four from the original review (Huertas‐Ceballos 2009); 10 pooled analyses were possible.
Evidence for probiotic interventions
Overall, the data in this review provided some evidence suggesting that probiotics may be effective in the management of children with RAP, based on the results of 13 studies. Trials used a range of probiotic preparations: five used Lactobacillus rhamnosus GG in slightly different preparations; three used Lactobacillus reuteri; two used Bacillus coagulans with fructo‐oligosaccharides; one used a patented mixture; one used Lactobacillus plantarum; and one used a mixture of Bifidobacterium species.
The majority of studies measured short‐term outcomes at zero to three months' postintervention only. We found that probiotics improved pain in the meta‐analysis of seven probiotic trials at this time point (OR 1.63, 95% CI 1.07 to 2.47; P = 0.02), with an estimated NNTB of eight, meaning that eight children would need to receive probiotics for one to experience improvement in pain in this timescale. The planned sensitivity analysis removing studies where the risk of bias for allocation concealment or blinding of participants and personnel and/or blinding of outcome assessment was high or unclear also found that children treated with probiotics were more likely to experience an improvement in pain (OR 1.95, 95% CI 1.40 to 2.70; P < 0.001). The planned subgroup analysis of children identified as having irritable bowel syndrome only at the same time point resulted in a pooled OR of 3.01 (95% CI 1.77 to 5.13; P < 0.001), and an estimated NNTB of four.
For all children, we also found a reduction in pain frequency (SMD ‐0.55, 95% CI ‐0.98 to ‐0.12; P = 0.012) and pain intensity (SMD ‐0.50, 95% CI ‐0.85 to ‐0.15; P = 0.005), in those treated with probiotics compared to placebo at zero to three months' postintervention.
We were able to perform only one pooled analysis of two studies for outcomes at three to six months' postintervention, for the outcome of improvement in pain. The pooled OR was 1.94 (95% CI 1.10 to 3.43; P = 0.023), with a NNTB of seven.
Using the GRADE approach, we rated the quality of the evidence for all the improvement in pain outcomes as moderate, and the quality of evidence for change in pain frequency and intensity as low.
Evidence for fibre interventions
As in the previous version of this review (Huertas‐Ceballos 2009), the data in this analysis did not provide convincing evidence suggesting that fibre supplements are effective in RAP, on the grounds of a paucity of studies and a lack of moderate‐ or high‐quality evidence. We performed two meta‐analyses, neither of which found that fibre interventions were effective in improving pain.
Only two studies were eligible for inclusion in the meta‐analysis for the outcome of improvement of pain, with a pooled OR of 1.83 (95% CI 0.92 to 3.65; P = 0.09). Two different studies were eligible for pooled analysis for the outcome of change in pain intensity: the SMD of effect across the studies was ‐1.24 (95% CI ‐3.41 to 0.94; P = 0.27); both studies included only children with irritable bowel syndrome. Using GRADE, we assessed the quality of the evidence for both outcomes as low.
Evidence for low FODMAP diet and fructose‐restricted diet
We found only one study each that examined the effects of a low FODMAP diet and a fructose‐restricted diet on pain in children with RAP. We were therefore unable to perform any pooled analyses for these two interventions.
Overall completeness and applicability of evidence
There are some important considerations relating to the overall completeness and applicability of the evidence from this study. First, 11 out of 13 included probiotic studies measured outcomes at zero to three months' postintervention only, and most interventions lasted only between four and six weeks. Only two included studies measured outcomes at 12 weeks or more, although the pooled analysis did find that improvement in pain was sustained at this time point. Consequently, the evidence base for the longer‐term effectiveness of probiotics in the included studies needs to be strengthened. Second, we were only able to perform one subgroup analysis by category of RAP, which was for probiotics for children with irritable bowel syndrome. However, the pooled analysis suggested that a significant improvement in pain was experienced by this group at short‐term follow‐up. Third, we were only able to identify one study of low FODMAP diets and one of fructose‐restricted diets eligible for inclusion. A number of RCTs of low FODMAP diets have been conducted in adults with irritable bowel syndrome (Nanayakkara 2016), but it appears that the area of exclusion diets in children requires further research before evidence‐based recommendations regarding the use of these interventions can be made.
We would also like to highlight that few studies reported on our secondary outcomes relating to school absence, social or psychological functioning, and quality of life, which represents a gap in the completeness of the evidence base. These 'secondary' outcomes are important, as they are likely to indicate disability and to be highly significant for the child and family.
Finally, we also note that the majority of studies took place in paediatric gastroenterology clinics, with three taking place in mixed settings and one in "primary care paediatrics". We were therefore unable to comment on any potential difference in outcome by setting.
Quality of the evidence
The overall quality of evidence within this review as assessed by the GRADE approach ranged from 'low' to 'moderate'. We rated the quality of the evidence for the three improvement in pain outcomes in the probiotic and placebo comparison as moderate, downgrading for imprecision or heterogeneity. This means we judged that further research is likely to have an important impact on our confidence in the estimate of effect and may change the estimate. We rated the quality of the evidence for the change in pain frequency and intensity outcomes for the same comparison as being low due to significant levels of heterogeneity and risk of bias introduced by incomplete outcome data. This means that future research is very likely to have an important impact on our confidence in the estimate of effect and is likely to change the estimate.
In the case of the two pooled analyses comparing fibre interventions to placebo, we rated the quality of the evidence as low due to significant heterogeneity, imprecision, and an unclear risk of bias in a number of domains in the included studies. Future research in this area is therefore very likely to have an important impact on our confidence in the estimate of effect and is likely to change the estimate.
Potential biases in the review process
We conducted a comprehensive search of electronic databases, but did not find sufficient studies to perform a formal assessment of the likelihood of publication bias; consequently it is possible that smaller studies may have been missed. Two review authors independently carried out screening and 'Risk of bias' assessments, discussing any areas of disagreement with another review author. Two review authors also checked data extraction. The methods used were therefore unlikely to introduce bias.
Agreements and disagreements with other studies or reviews
The findings of this review are in keeping with other systematic reviews of dietary interventions in RAP. Horvath 2011, and more recently Rutten 2015, reported that Lactobacillus rhamnosus GG was associated with significantly more treatment responders than placebo in their meta‐analyses; the same authors found only inconclusive data regarding the effects of fibre supplements (Horvath 2012; Rutten 2015).
Issues for consideration
We rated the quality of the evidence provided by the included studies as moderate or low (for probiotics) or low (for fibre). There were additionally further issues for consideration. As discussed above, the majority of studies were short term. We also noted variety in the definition and scales used to assess improvement in pain, meaning that this outcome does not reflect a universally agreed clinically significant benchmark. It is therefore harder to draw conclusions as to whether the reported improvements in pain were clinically meaningful, although this is to some extent a matter of judgement. The outcome of improvement in pain in most included studies represented either a change to no pain or a decrease by 50%, which could be argued to be clinically important. This observation also applied to the assessment of other outcomes, such as pain intensity and frequency.
As previously mentioned, many studies did not collect data on the prespecified secondary outcomes of interest, such as school performance or quality of daily life, meaning that the effect of dietary interventions on these important outcomes was not measured and that it was therefore not possible to conduct pooled analyses. Data on these outcomes would also assist in determining the clinical relevance of improvements in pain.
We performed no subgroup analyses by type or concentration of probiotic, as we did not specify this in our protocol (Martin 2014b); each pooled analysis included studies using different strains of probiotic, the most common being L rhamnosus GG and L reuteri.
Finally, the majority of studies included children under the broad umbrella of RAP and did not present results by RAP subtype. Consequently, we were only able to perform one pooled analysis for the subtype of irritable bowel syndrome for probiotic interventions, although the eligible studies for the pooled analysis for pain intensity in fibre interventions also included only children with irritable bowel syndrome.
PRISMA study flow diagram
Risk of bias summary: review authors' judgements about each risk of bias item for each included study.
Risk of bias graph: review authors' judgements about each risk of bias item presented as percentages across all included studies.
Forest plot of comparison: 1 Probiotics versus placebo, outcome: Improvement in pain 0 to 3 months' postintervention.
Forest plot of comparison: 2 Fibre versus placebo, outcome: Improvement in pain 0 to 3 months' postintervention.
Comparison 1 Probiotics versus placebo, Outcome 1 Change in pain frequency: 0 to 3 months' postintervention.
Comparison 1 Probiotics versus placebo, Outcome 2 Change in pain frequency: 0 to 3 months' postintervention. Sensitivity analysis.
Comparison 1 Probiotics versus placebo, Outcome 3 Change in pain intensity: 0 to 3 months' postintervention.
Comparison 1 Probiotics versus placebo, Outcome 4 Change in pain intensity: 0 to 3 months' postintervention. Sensitivity analysis.
Comparison 1 Probiotics versus placebo, Outcome 5 Improvement in pain: 0 to 3 months' postintervention.
Comparison 1 Probiotics versus placebo, Outcome 6 Improvement in pain: 0 to 3 months' postintervention. Sensitivity analysis.
Comparison 1 Probiotics versus placebo, Outcome 7 Improvement in pain: 0 to 3 months' postintervention. Subgroup analysis (irritable bowel syndrome).
Comparison 1 Probiotics versus placebo, Outcome 8 Improvement in pain: 3 to 6 months' postintervention.
Comparison 2 Fibre versus placebo, Outcome 1 Change in pain intensity: 0 to 3 months' postintervention.
Comparison 2 Fibre versus placebo, Outcome 2 Improvement in pain: 0 to 3 months' postintervention.
| Probiotics compared to placebo for recurrent abdominal pain in childhood | ||||||
| Patient or population: Children with recurrent abdominal pain | ||||||
| Outcomes | Illustrative comparative risks* (95% CI) | Relative effect | Number of participants | Quality of the evidence | Comments | |
| Assumed risk | Corresponding risk | |||||
| Placebo | Probiotics | |||||
| Change in pain frequency: 0 to 3 months' postintervention Different measures were used to assess pain frequency, such as a visual analogue scale and the Wong‐Baker FACES Pain Rating Scale (McGrath 1996; Wong 1988). | — | The mean change in pain frequency: 0 to 3 months' postintervention scores in the intervention groups was 0.55 SDs lower (0.98 to 0.12 lower). | — | 523 | ⊕⊕⊝⊝ | As a rule of thumb, 0.2 SD represents a small difference, 0.5 SD a moderate difference, and 0.8 SD a large difference. |
| Change in pain intensity: 0 to 3 months' postintervention Different measures were used to assess pain intensity, as above. | — | The mean change in pain intensity: 0 to 3 months' postintervention scores in the intervention groups was 0.50 SDs lower (0.85 to 0.15 lower). | — | 575 | ⊕⊕⊝⊝ | As a rule of thumb, 0.2 SD represents a small difference, 0.5 SD a moderate difference, and 0.8 SD a large difference. |
| Improvement in pain: 0 to 3 months' postintervention Different measures and definitions were used for improvement in pain, such as Likert scale, visual analogue scale, and Subject’s Global Assessment of Relief Scale (McGrath 1996; Muller‐Lissner 2003). | 421 per 10003 | 542 per 1000 | OR 1.63 NNTB = 8 | 722 | ⊕⊕⊕⊝ | — |
| Improvement in pain: 0 to 3 months' postintervention Subgroup (irritable bowel syndrome) Different measures were used to assess improvement in pain, as above. | 359 per 1000 | 627 per 1000 | OR 3.01 NNTB = 4 | 344 | ⊕⊕⊕⊝ | — |
| Improvement in pain: 3 to 6 months' postintervention Different measures were used to assess improvement in pain, as above. | 589 per 1000 | 736 per 1000 | OR 1.94 NNTB = 7 | 224 | ⊕⊕⊕⊝ | — |
| *The basis for the assumed risk (e.g. the median control group risk across studies) is provided in footnotes. The corresponding risk (and its 95% confidence interval) is based on the assumed risk in the comparison group and the relative effect of the intervention (and its 95% CI). | ||||||
| GRADE Working Group grades of evidence | ||||||
| 1Downgraded one level due to incomplete outcome data in a number of included studies leading to an unclear or high risk of bias. | ||||||
| Fibre versus placebo for recurrent abdominal pain in childhood | ||||||
| Patient or population: Children with recurrent abdominal pain Comparison: Placebo | ||||||
| Outcomes | Illustrative comparative risks* (95% CI) | Relative effect | Number of participants | Quality of the evidence | Comments | |
| Assumed risk | Corresponding risk | |||||
| Placebo | Fibre | |||||
| Change in pain intensity: 0 to 3 months' postintervention Pain intensity was measured using different scales in the 2 included studies: the Wong Baker FACES Pain Rating Scale, Wong 1988, and the Numerical Rating Scale (von Baeyer 2009). | — | The mean change in pain intensity 0 to 3 months' postintervention score in the intervention groups was 1.24 SDs lower (3.41 lower to 0.94 higher) | — | 135 | ⊕⊕⊝⊝ | — |
| Improvement in pain: 0 to 3 months' postintervention Improvement in pain was defined and measured differently in the 2 included studies: using a "stomach ache diary" and the Faces Pain Scale (Bieri 1990). | 391 per 10001 | 541 per 1000 | OR 1.83 NNTB = 6.7 | 136 | ⊕⊕⊝⊝ | — |
| *The basis for the assumed risk (e.g. the median control group risk across studies) is provided in footnotes. The corresponding risk (and its 95% confidence interval) is based on the assumed risk in the comparison group and the relative effect of the intervention (and its 95% CI). | ||||||
| GRADE Working Group grades of evidence | ||||||
| 1Assumed risk in control group is based on the mean outcome of the control group in the two included studies. | ||||||
| Domain | 'Risk of bias' judgement | ||
| Low | High | Unclear | |
| Selection bias | |||
| Random sequence generation | If the study details any of the following methods: simple randomisation (such as coin‐tossing, throwing dice, or dealing previously shuffled cards, a list of random numbers, or computer‐generated random numbers) or restricted randomisation (blocked, ideally with varying block sizes or stratified groups, provided that within‐groups randomisation is not affected). | If the study details no randomisation or other inadequate method such as alternation, assignment based on date of birth, case record number, and date of presentation. These may be referred to as ‘quasi‐random’. | If there is insufficient detail to judge the risk of bias.
|
| Allocation concealment | If the study details concealed allocation sequence in sufficient detail to determine that allocations could not have been foreseen in advance of or during enrolment. | If the study details a method where the allocation is known prior to assignment. | If there is insufficient detail to judge the risk of bias. |
| Performance bias | |||
| Blinding of participants and personnel | If the study details a method of blinding the participants and personnel. This requires sufficient detail to show they were unable to identify the therapeutic intervention from the control intervention. | Considering the nature of the interventions, it may not be possible to blind the participants and therapists. The effect of this will be addressed in the Discussion. | If there is insufficient detail to judge the risk of bias. |
| Detection bias | |||
| Blinding of outcome assessment | If the study details a blinded outcome assessment. This may only be possible for outcomes that are externally assessed. | If the outcome assessment is not blinded. We expect this may be unavoidable for self rated outcomes of unblinded interventions. | If there is insufficient detail to judge the risk of bias.
|
| Attrition bias | |||
| Incomplete outcome data | If the study reports attrition and exclusions, including the numbers in each intervention group (compared with total randomised participants), reasons for attrition or exclusions, and any re‐inclusions. Also, the impact of missing data is not believed to alter the conclusions, and there are acceptable reasons for the missing data. | We may judge the risk of attrition bias to be high due to the amount, nature, or handling (such as per‐protocol analysis) of incomplete outcome data. | If there is insufficient detail to judge the risk of bias, e.g. if the number of people randomised to each treatment is not reported. |
| Reporting bias | |||
| Selective outcome reporting | If there is judged to be complete reporting, which will be found on comparison of the published study and protocol, if available. | If the reporting is selective, so that some outcome data are not reported. | If there is insufficient detail to judge the risk of bias, such as the protocol is not available. |
| Other sources of bias | |||
| Assessment of other sources of bias in other domains not covered by the tool, including validity of outcome measures utilised | If there is judged to be no other factors that would be likely to introduce major potential bias. | If other factors are identified that are judged to represent a high risk of bias. | If there is insufficient detail to judge the risk of other bias. |
| Outcome or subgroup title | No. of studies | No. of participants | Statistical method | Effect size |
| 1 Change in pain frequency: 0 to 3 months' postintervention Show forest plot | 6 | 523 | Std. Mean Difference (IV, Random, 95% CI) | ‐0.55 [‐0.98, ‐0.12] |
| 2 Change in pain frequency: 0 to 3 months' postintervention. Sensitivity analysis Show forest plot | 4 | 389 | Std. Mean Difference (IV, Random, 95% CI) | ‐0.54 [‐0.94, ‐0.14] |
| 3 Change in pain intensity: 0 to 3 months' postintervention Show forest plot | 7 | 575 | Std. Mean Difference (IV, Random, 95% CI) | ‐0.50 [‐0.85, ‐0.15] |
| 4 Change in pain intensity: 0 to 3 months' postintervention. Sensitivity analysis Show forest plot | 5 | 441 | Std. Mean Difference (IV, Random, 95% CI) | ‐0.68 [‐1.05, ‐0.30] |
| 5 Improvement in pain: 0 to 3 months' postintervention Show forest plot | 7 | 722 | Odds Ratio (M‐H, Random, 95% CI) | 1.63 [1.07, 2.47] |
| 6 Improvement in pain: 0 to 3 months' postintervention. Sensitivity analysis Show forest plot | 6 | 642 | Odds Ratio (M‐H, Random, 95% CI) | 1.95 [1.40, 2.70] |
| 7 Improvement in pain: 0 to 3 months' postintervention. Subgroup analysis (irritable bowel syndrome) Show forest plot | 4 | 344 | Odds Ratio (M‐H, Random, 95% CI) | 3.01 [1.77, 5.13] |
| 8 Improvement in pain: 3 to 6 months' postintervention Show forest plot | 2 | 224 | Odds Ratio (M‐H, Random, 95% CI) | 1.94 [1.10, 3.43] |
| Outcome or subgroup title | No. of studies | No. of participants | Statistical method | Effect size |
| 1 Change in pain intensity: 0 to 3 months' postintervention Show forest plot | 2 | 135 | Std. Mean Difference (IV, Random, 95% CI) | ‐1.24 [‐3.41, 0.94] |
| 2 Improvement in pain: 0 to 3 months' postintervention Show forest plot | 2 | 136 | Odds Ratio (M‐H, Random, 95% CI) | 1.83 [0.92, 3.65] |
