Single Subject Designs and Evidence Based Practice in Speech Therapy

I was really happy to see the tutorial on Single Subject Experimental designs in November’s issue of the American Journal of Speech-Language Pathology and Audiology, by Byiers, Reichle, and Symons. The paper does not really present anything new since it covers ground previously published by authors such as Kearns (1986). However, with the current focus on RCTs as the be-all and end-all for evidence based practice, it was a timely reminder that single-subject designs have a lot to offer for EPB in speech therapy. It really irritates me when I see profs tell their students that speech therapy practice does not have an evidentiary base: many of our standard practices are well grounded in good quality single subject research (not to mention some rather nice RCTs from the sixties as well but that is another story, maybe for another post).

Byiers et al. do a nice job of outlining the primary features of a valid single-subject experiment. The internal validity of the standard designs is completely dependent upon the stable baseline with no improving trend in the data prior to the introduction of the treatment. They indicate that “by convention, a minimum of three baseline data points are required to establish dependent measure stability.” Furthermore, it is essential to not see carry-over effects of treatment of one target to the second target prior to the introduction of treatment for the second target; in other words, performance on any given target must remain stable until treatment for that specific target is introduced. The internal validity of the experiment is voided when stable baselines for each target are not established and maintained throughout their respective baseline periods. This is true even for the multiple-probe design which is a variation on the multiple-baseline design in which the dependent measure is sampled at irregular intervals tied to the introduction of successive phases of the treatment program (as opposed to regular and repeated measurement  that occurs during each and every session of a multiple baseline design). Even with the multiple probe design, a series of closely spaced baseline probes are required at certain intervals to demonstrate stability of baselines just before you begin a new treatment phase. Furthermore, the design is an inappropriate choice unless a “strong a priori assumption of stability can be made” (see Horner and Baer, 1978).

I am interested in the multiple probe design because it is the preferred design of the research teams that claim that the “complexity approach” to target selection in phonology interventions is effective and efficient. However, it is clear that the design is not appropriate in this context (in fact, given the research question, I would argue that all single subject designs are inappropriate in this context).  The reasoning behind the complexity approach is that treating complex targets results in generalization of learning to less complex targets. This is supposed to be more efficient than treating the less complex targets first because these targets are expected to improve spontaneously without treatment (e.g., as a result of maturation) while not resulting in generalization to more complex targets. The problem of course is that improvements in less complex targets while you are treating a more complex one (especially when you get no improvement on the treatment target, see Cummings and Barlow, 2011) cannot be interpreted as a treatment effect. By the logic of a single-subject experiment, this outcome indicates that you do not have experimental control. To make matters worse, these improvements in generalization targets are often observed prior to the introduction of treatment –  and indeed the a priori assumption is that these improvements in less complex targets will occur without treatment – that is the whole rationale behind avoiding them as treatment targets! And therefore, by definition, both the multiple baseline and multiple probe designs are invalid approaches to the test of the complexity hypothesis. Without a randomized control trial one can only conclude that the changes observed in less complex targets in these studies are the result of maturation or history effects. (If you want to see what happens when you test the efficacy of the complexity approach using a randomized control trial, check out my publications: Rvachew & Nowak, 2001; Rvachew & Nowak, 2003; Rvachew, 2005; Rvachew & Bernhardt, 2010).

Some recent single subject studies have had some really nice outcomes for some children. Ballard, Robin and McCabe (2010) demonstrated an effective treatment for improving prosody in children with apraxia of speech, showing that work on pseudoword targets generalizes to real word dependent measures. Skelton (2004) showed that you can literally randomize your task sequence and get excellent results for the treatment of /s/ with carryover to the nonclinic environment (in other words you don’t have to follow the usual isolation-syllable- word-phrase-sentence sequence; rather, you can mix it up by practicing items with random difficulty level on every trial). Both of these studies showed uneven outcomes for different children however. Francoise and I suggested at ASHA2012 that the “challenge point framework” helps to explain variability in outcomes across children. The trick is to teach targets that are at the challenge point for the child – not uniformly complex but carefully selected to be neither too simple nor too complex for each individual child.

Both of these studies (Ballard et al. and the Skelton study) used a multiple baseline design. This design tends to encourage the selection of complex targets because consistent 0% correct is as stable as you can get in a baseline. If you want to pick targets that are at the “challenge point” you may be working on targets for which the child is demonstrating less stable performance. Fortunately there is a single subject design that does not require a stable baseline for internal validity – it is called a single subject randomization design. We are using two different variations on this design in our current study of different treatments for childhood apraxia of speech. I will describe our application of the design in another post.


MMN and Speech Therapy

I haven’t had time to much time to blog these past four months because I have been starting a new treatment study, this time on Childhood Apraxia of Speech. Quite a few papers on this topic have caught my eye and now that our project is ready for lift-off I am going to comment on one paper that is particularly relevant to the interventions that we will be comparing. The paper by Froud, K., & Khamis-Dakwar, K. (2012) concludes that “there is some phonological involvement in CAS and that CAS cannot be characterized as a purely motoric disorder” and claims to be “the first investigation to utilize neurophysiological methodologies to examine the neural underpinnings of primary CAS” (p. 310). We will be comparing motor speech practice alone to approaches that combine motor speech practice with prepractice procedures designed to strengthen children’s underlying phonological representations at the acoustic-phonetic or articulatory-phonetic levels and thus the paper was of interest to me. I was surprised to find a mistake in the authors’ representation of prior work on the development of MMN responses to phonological categories in their introduction however. They begin by explaining that the mismatch negativity (MMN) response is an “automatic, preattentive [evoked potential] response to stimulus change that can be elicited in the absence of conscious attention”. This research technique is used in important infant perception research and therefore Francoise and I explain the technique carefully and present some seminal research findings in detail in our book Developmental Phonological Disorders: Foundations of Clinical Practice. Froud and Khamis-Dakwar mention one of these seminal studies, Nätäänen,Lrthokoski, Lennes et al. (1997), correctly reporting that adult Finnish-speaking participants in this study showed larger MMN responses to native language vowel contrasts than to stimulus changes that did not cross a phoneme boundary in their native language (one of the contrasts in question was phonemic in Estonian but not in Finnish). Then Froud and Khamis-Dakwar strangely report that Estonian research participants did not show MMN responses to the same stimuli which makes so little sense in relation to the actual study findings that there must be a typo involved. Whatever the source of the error, the whole flavour of the paper reinforces rather than dispels common misperceptions about early phonological development in general and MMN research in particular.

A common misreading of the literature is the notion that responses to non-native phoneme contrasts are lost in infancy – this is simply not true and the MMN research program led by Nätäänen and colleagues  illustrates this perfectly. Brain responses to non-native phoneme contrasts are retained throughout the lifespan although they reflect the purely acoustic properties of the input and are diffuse, bilateral and weaker than those observed in response to native language phoneme contrasts. During the first few years of life brain responses to language specific inputs reorganize to become more focal, left-dominant and efficient. The size of the MMN early in life reflects acoustic properties of the stimulus whereas the size of the MMN later in life reflects the linguistic (phonological) properties of the stimulus.  We cite other research in our book from labs using other techniques (fMRI, MEG etc) that reinforce this point.

Froud and Khamis-Dakwar report that a group of 5 children with CAS (aged 5 to 8 years) showed a larger MMN to a phonetic contrast (VOT 50 ms vs VOT 75 ms) and no MMN to a phonemic contrast (VOT 50 ms vs VOT 5 ms). The age matched comparison group with normal speech development showed the opposite pattern of results. The data are more-or-less uninterpretable given that they have no information about the children’s language or cognitive skills and the findings are not consistent with their hypothesis even though the  MMN responses for the CAS group differed from those of the comparison group. I expect that the means mask much heterogeneity in responding within their small group of participants. They claim that some aspects of the CAS group’s responses suggest persistence of immature acoustic processing (it is a little hard to see this because the stimuli are not properly controlled for acoustic distance as in the Näätänen et al studies).  They still go on to claim that the findings have implications for theoretical perspectives regarding the etiology of CAS and suggest that the results are compatible with the possibility that a primary phonological deficit is the causal mechanism. This brings me to the second common misperception about research on early speech perception development.

This idea that MMN data can tell us something about the ‘neurophysiological’ underpinnings of CAS is pervasive but perverse. The notion seems to be that these responses are somehow more ‘biological’ than behavioral tests that indicate difficulties with phonological processing and language among children with this disorder. For the life of me I cannot imagine why. MMN research with normally developing children is fascinating because it illustrates beautifully the impact of environmental inputs on the reorganization of brain responses to linguistic stimuli that are co-incident with changes in behavioral responses to those same linguistic inputs. If (and this is a really big if given the state of this literature) rather old children with CAS have immature MMN responses that suggest acoustic rather than phonological processing of speech input, what do these responses tell us about the etiology of the  speech deficit in CAS? Well, not much really. A large part of any individual’s responses to speech input is formed by that individual’s experience with speech input. Children with CAS are probably not experiencing linguistic input in the same way as other children and thus it is not surprising to find differences in their MMN responses relative to normally developing children. What are the possible interpretations of this finding?

First, as Barbara Lewis has suggested, at least some children with CAS may have a more severe version of a developmental phonological disorder. Although this population is heterogeneous there is genetic overlap with dyslexia and ERP studies of new-born infants with dyslexic parents do in fact confirm a primary problem with speech processing in this population. In addition to speech therapy targeting the articulatory component, the child will need therapy to improve  phonological representations and efforts must be made to ensure a rich language environment for the child.

Second, children with CAS tend to not babble and to talk late. The shift from language-general to language-specific processing of speech in infancy is dependent upon the social context in which speech input is provided. It is very likely that children who do not vocalize in the normal way are not receiving the usual linguistic and social inputs during this sensitive period. I remember working with a mum who was depressed because her baby “only growled at her” (it was true – the infant’s only non-cry vocalization was a very low pitched growl, in this case secondary to chronic otitis media in the first six months of life). It took a bit of coaching to teach the mum to perceive and respond to the growls positively but what a difference that made – full babbling emerged shortly after the mum began engaging in reciprocal vocal interactions with her baby. Vihman has hypothesized that the infant’s own vocalizations play a role in the perceptual salience of the input as well. An important aspect of speech perception development is the linking of acoustic to articulatory representations via the dorsal stream, a developmental event that appears to begin with the onset of babbling. Therefore, immature MMN responses to phonemic stimuli may still reflect a primary problem in the motoric rather than perceptual or phonological domains. That is not to say that the intervention must be solely focused on the child’s motor skills. Clearly the intervention must be concerned with the quality of linguistic inputs to the child and the social context in which those inputs are provided to the child even when the core deficit appears to be motoric in nature.

Thirdly, the biological events that produced the core motor deficit may produce additional “core deficits” in other domains as is probably the case in FOXP2, a syndrome that associates multiple cognitive and linguistic deficits with severe oro-motor and speech dyspraxia. Once again the child will require a broad based intervention program, targeting multiple levels of representation, although the focus of therapy will shift with the child’s developmental needs over time.

Overall I am happy that this paper focuses attention on the requirement to attend to these children’s perceptual and phonological representations in therapy. I am not sure that I agree that it is actually necessary to understand the underlying etiology to design an effective intervention for the child; rather it is important to fully understand normal speech development and to be able to determine the child’s specific developmental needs as they unfold over time. I definitely don’t agree that MMN studies illuminate the neurophysiological underpinnings of CAS.



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Froud, K., & Khamis-Dakwar, K. (2012). Mismatch negativity responses in children with a diagnosis of childhood apraxia of speech (CAS). American Journal of Speech-Language Pathology, 21, 302-312.

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Vargha-Khadem, F., Gadian, D. G., Copp, A., & Mishkin, M. (2005). FOXP2 and the neuroanatomy of speech and language. Neuroscience, 6, 131-138.

Vihman, M. M. (2002). The role of mirror neurons in the ontogeny of speech. In M. Stamenov & V. Gallese (Eds.), Mirror Neurons and the Evolution of Brain and Language (pp. 305-314). Amsterdam, Netherlands: John Benjamins Publishing Company.