Review for "Temporal variability predicts the magnitude of between-group attentional blink differences in developmental dyslexia: a meta-analysis"

Completed on 18 Apr 2014 by Franck Ramus. Sourced from Publons:


Login to endorse this review.

Comments to author

Basic reporting

  • The acronym RSVP is often used in ways that seem to mean something other than « rapid serial visual presentation ». Sometimes to refer to the fixation symbol at the beginning of a trial, sometimes to refer to a trial or to items within a trial. The language should be clarified in this respect. My impression is that removing RSVP in many instances will help.

  • Line 153 the fixation duration parameter should be better explained. It is actually the fixation symbol duration. It remains unclear to me what a duration of 0 ms means. If it means “no fixation symbol”, is it legitimate to treat this situation on the same scale as those with a fixation symbol?

  • Line 161: “if T2 is a FIXED letter of the alphabet” would be clearer.

  • Line 163: there -> they

  • Line 187: remove “in”

  • Lines 231-232: r values differ slightly from those reported in the table.

Experimental design

Although I am not an expert of meta-analyses (I hope that another reviewer is), I have a few important concerns with the way the meta-analysis is conducted in the present paper :

  • Three studies are excluded from the meta-analysis, two of which for reasons that seem hardly justified (lines 128-135). One is excluded on the grounds that the effect is in the opposite direction from the others. In my view this is no reason for exclusion. Imagine if a meta-analysis of clinical trials excluded trials where the treatment had a negative (rather than positive) effect on patients! The virtue of meta-analyses is to provide an objective synthesis of contradictory research findings. It defies the entire purpose of a meta-analysis to a priori exclude a study because it seems in contradiction with the others. The same reasoning applies for the second study that is excluded on the grounds that the authors judge the effect size to be anomalous. If they suspect that the odd effect size results from a typo in a table or a miscalculation, then they should contact the authors to clarify this. But if it turns out that the numbers do reflect the actual data, then the study should be included in the meta-analysis. With respect to the third study (whose effect size could not be computed from the reported results), it should be easy enough to contact the authors and obtain the desired numbers. Given that the number of studies in this meta-analysis is quite low for the purpose of the mediation analyses proposed, all reasonable efforts should be made to include as many as possible.

  • I wonder if the approach consisting of just testing simple correlations between effect size and all possible parameters represents the state of the art for this kind of research. First, shouldn’t a test of heterogeneity (of effect sizes) be done to justify the search for mediators? Second, shouldn’t slightly more sophisticated meta-regression models be used? Again, I am not an expert on meta-analysis so I might be wrong on this. The view of a real expert would be welcome.

  • The number of parameters investigated (18) is disproportionately large compared to the number of studies meta-analysed (6 to 9). Given that many parameters are confounded with each other, maybe a more parsimonious approach would be to start with a factor analysis, use it (if its results are clear enough) to compute a more limited number of composite measures (average z-scores of some variables) to be tested as mediators in the meta-regression, and when some of them turn out to be significant, discuss which of the underlying variables is likely to produce the effect. It may well be that in some cases this is undecidable because some parameters are equally plausible and turn out to be confounded in published studies. This approach may be preferable to adjudicating between parameters on the basis of small, non-significant differences between correlations (as has been done between distractor ID and T2 time max and difference, for instance). An alternative approach would be to carry out multiple rather than simple regressions, in order to try and disentangle between confounded variables. But this will still be limited by the small number of studies.

More minor comments:

The justification for rescuing the non-significant effect of SOA with R=-0.66 but not the non-significant effect of distractor ID with R=-0.78 is a bit awkward. Either Pearson’s test applies or it doesn’t. Perhaps reporting and reasoning only on Pearson when distribution is normal, and on Spearman when not, would make it clearer. This problem would disappear with the factor analysis approach mentioned above.

Validity of the findings

Apart from the problem of confounded variables that are impossible to disentangle, I am not entirely convinced by some of the interpretations offered in the discussion.
With respect to fixation duration, wouldn’t the authors’ interpretation predict a negative correlation instead? If the task is more difficult with shorter fixation duration, and if dyslexics need more preparation time, they should be at a greater disadvantage (large effect size) when fixation duration is short (thus negative correlation). The idea that dyslexics would not benefit at all from greater preparation does not seem very plausible.
Similarly for T2 temporal position and variability, it is suggested that in the more variable and difficult conditions, the task is so challenging that floor effects are reached for both groups (hence small effect size), and it is in the less variable (easier) conditions that group differences emerge. In many tasks with dyslexic participants, this is just the contrary: performance is at ceiling in easy conditions and group differences emerge in more difficult conditions (see for instance discussion of task difficulty in Ramus and Ahissar 2012). Furthermore the Badcock et al (2011) study that is cited does not seem to support the authors’ interpretation: if there is a group difference in the first half of the experiment (without practice, difficult) but not in the second half (with practice, easier), then this is a ceiling, not a floor effect. At any rate, any conjecture on a floor or on a ceiling effect could be tested by looking at absolute performance in the initial studies.
I can’t see clearly the link between SOA and the discussion in lines 349-365.

  • In their discussion (section 7.1) of the “anomalous” results of Lacroix et al. and Buchholz et al., the authors speculate about experimental parameters that might explain such results: children rather than adult participants, number stimuli, target-distractor relationship, and task-set. But the proper way to test these hypotheses would be to include these studies and these additional parameters in the analysis.

  • Line 390: I don’t understand how the effect might reverse (as opposed to just disappearing) in adults as retrieval becomes more automatic.