ACE or ADE model fitting to twin data is limited in that C and D components cannot be simultaneously estimated

It's obvious. When rMZ is more than the half of rMZ, C is larger than 0. If rMZ is the half of rMZ, there no C and no D. When rMZ is lower than half of rMZ, there is D larger than 0. You can't have positive C and positive D at the same time. Thus, what's the limitation here ?

Moreover, assortative mating (AM) is not considered. What this means is that the estimates from these models cannot be correct.

ACE without taking account AM is worse doing than ADE without taking account AM. Unless you can prove there is no non-additive genetic effect, it is not justified to talk about A or h2 (narrow-sense). Remember that the interest of ADE is the decomposition of A and D components. Without this done, it's thus not justified to make claims about narrow h2 that has not been proven.

I haven't read Vinkhuyzen et al. study but don't understand your argument : "their H2 estimate comes to about 80 percent, which is similar to h2 estimates from studies that assume only additive heredity and no AM".

Specifically, what are you referring to by h2 ? Is it the h2 from Falconer's computation ? (in general I hate using h2/H2 because I'm always confused with the two, even if I have read the descriptions many times) And the H2 of Vinkhuyzen is the heritability when taking account AM ? So, why are they saying "much of IQ heritability is non-additive" ?

Yes it's a drawback of this paper that they didn't carry out model fitting so we have no way of knowing if a purely additive or epistatic model fits the data better.
However something I never liked about twin model fitting is a practice that is universally accepted: the most parsimonious model is always chosen also when it shows a worse fit to the data, as long as this is not significantly worse. So it's ok if it doesn't fit the data as well as the other, more parsimonious model unless the degeneration in fit is not significant. No appeals to theory or previous research is needed, the principle that fewer parameters are better is sufficient to reject a model with more of them (e.g. AE would be preferred over ACE even if the latter fits the data better but not significantly so).
To me this is an abuse of significance testing and Occam's razor principle.
I once pointed this out to a twin researcher and he admitted he didn't know why this practice is so universally used.

estimates from studies that assume only additive heredity and no AM.

Because almost all IQ studies use ACE or AE models and Falconer's formula does not give H2, either, I think we should talk about h2 or A rather than H2 in the paper. We can mention the methods used in each study.

Also, MH, 'precise' is not a verb in English. Use 'clarify' or 'specify' instead.

Dalliard and Chuck suggest the following changes:

Replace the beginning with:

"In behavioral genetic research, IQ variance is usually partitioned into three components: additive heredity (h2), shared environment (c2), and unshared environment (e2). These are also known as the ACE components. h2 (also referred to as a2) denotes genetic effects that act additively and independently of each other.[FOOTNOTE HERE] c2 refers to environmental effects that serve to make family members more similar...

[FOOTNOTE] Some of the genetic variance in IQ is probably non-additive in nature (Vinkhuyzen et al., 2012), but due to data and modeling limitations most studies assume additivity. We follow this convention in our analyses. In practice, the estimates for additive genetic components that we report may include some interactive genetic effects; this is probably particularly true for the estimates based on Falconer’s formula, which tend to be closer to the total genetic influence than to the additive genetic influence (Falconer and Mackay, 1996).

Add a column in table 2 which lists the variance decomposition method used for the particular study.

Is this acceptable?

ACE or ADE model fitting to twin data is limited in that C and D components cannot be simultaneously estimated

It's obvious. When rMZ is more than the half of rMZ, C is larger than 0. If rMZ is the half of rMZ, there no C and no D. When rMZ is lower than half of rMZ, there is D larger than 0. You can't have positive C and positive D at the same time. Thus, what's the limitation here ?

Let's say rMZ is 0.8 and rDZ is 0.3 (and there is no AM). This could be because there's D variance and no C variance. But it could as well be that there's both D and C variance but more D. In the classic twin design, C and D are confounded; they cannot be simultaneously estimated because of underidentification. You need additional types of relatives to estimate both C and D.

Moreover, assortative mating (AM) is not considered. What this means is that the estimates from these models cannot be correct.

ACE without taking account AM is worse doing than ADE without taking account AM. Unless you can prove there is no non-additive genetic effect, it is not justified to talk about A or h2 (narrow-sense). Remember that the interest of ADE is the decomposition of A and D components. Without this done, it's thus not justified to make claims about narrow h2 that has not been proven.

In IQ studies, rMZ is usually ≤2*rDZ, so models with D fit poorly and are not estimated. The model assumption that genetic variance is all A may be wrong, but that's what the data are usually consistent with.

I haven't read Vinkhuyzen et al. study but don't understand your argument : "their H2 estimate comes to about 80 percent, which is similar to h2 estimates from studies that assume only additive heredity and no AM".

Specifically, what are you referring to by h2 ? Is it the h2 from Falconer's computation ? (in general I hate using h2/H2 because I'm always confused with the two, even if I have read the descriptions many times) And the H2 of Vinkhuyzen is the heritability when taking account AM ? So, why are they saying "much of IQ heritability is non-additive" ?

H2=additive, dominance, and epistatic genetic effects

h2=A=additive genetic effects, usually estimated from MZ-DZ data with model fitting

Falconer's heritability is neither H2 nor h2 but it's closer to H2.

In Vinkhuyzen's preferred model, A=44%, D=27%, and AM=11%. AFAIK, the last should be interpreted as genetic variance. Summing them you get broad heritability H2=82%.

However something I never liked about twin model fitting is a practice that is universally accepted: the most parsimonious model is always chosen also when it shows a worse fit to the data, as long as this is not significantly worse. So it's ok if it doesn't fit the data as well as the other, more parsimonious model unless the degeneration in fit is not significant. No appeals to theory or previous research is needed, the principle that fewer parameters are better is sufficient to reject a model with more of them (e.g. AE would be preferred over ACE even if the latter fits the data better but not significantly so).

I completely agree with that. Especially since they use Chi-square, very sensitive to sample size. I have elsewhere noted this for the article of van Soelen (2011) where given their table 5 they say that PIQ h2 does not increase with age. The thing is that in childhood the selected model was AE due to C parameter non significant (and yet was non-trivial in magnitude = 0.17). I also said that when you drop one such parameter, the variance of the removed parameter will be given to either A or C (depending on which one is removed) because the total must be 100. Thus, they remove C and its variance is given to A, which becomes inflated. This is ridiculous. I even remembered the appendix of Behavioral Genetics (6th edition, by Plomin) where Shaun Purcell said explicitly that in principle we do not want the full model (ACE) because it's a null model (everything is estimated, no constraint imposed). Thus, the rationale is to test the full (or null) model against the reduced models. I was shocked when reading this.

Let's say rMZ is 0.8 and rDZ is 0.3 (and there is no AM). This could be because there's D variance and no C variance. But it could as well be that there's both D and C variance but more D. In the classic twin design, C and D are confounded; they cannot be simultaneously estimated because of underidentification. You need additional types of relatives to estimate both C and D.

I do not understand. What you seem to say is that we need twin + non twin data. But, in what is it a problem inherent to ADE model ?

In IQ studies, rMZ is usually ≤2*rDZ, so models with D fit poorly and are not estimated. The model assumption that genetic variance is all A may be wrong, but that's what the data are usually consistent with.

I did not remember very well the C parameters for non white samples, so I looked at the paper again. I see that the C is non-trivial, so yes it makes sense.

For those who are interested, here's a good article i read some time ago :

Hill, W. G., Goddard, M. E., & Visscher, P. M. (2008). Data and Theory Point to Mainly Additive Genetic Variance for Complex Traits. PLoS Genetics, 4, e1000008.

[quote='menghu1001' pid='1304' dateline='1408673982']

However something I never liked about twin model fitting is a practice that is universally

MH, can you review our changes?

I have attempted to replicate your results. I failed, and I will probably give up. NlsyLinks must hate me. You may want to look at your syntax again. Besides, if you want confidence intervals, given that your syntax ended up like this :

ace <-AceLavaanGroup(dsClean)
ace

In general, the thing to do is :

confint(ace, level=0.95)

That should do the trick.

For the rest, see below :

Three of the studies, Vanderberg (1970), Osborne and Meile (1969), and Osborne and Gregor (1968), were redundant with Osborne (1980) and so were excluded.

Vandenberg. Also, in your table 1, it's Miele, not Meile.

Sara Hart (personal communication, March, 16, 2014) provided twin correlations computed in relation to but not reported in Hart et al.

You probably missed some words, e.g. "in relation to race groups".

Unfortunately, our samples do not allow us to robustly determine whether or not this is the case as they differ in participant age and test type, differences which would cofound any such analysis and which cannot be controlled for given the dearth of samples available.

That should be confound, instead.

Generally, the average H/W mean score difference (d-value) in these samples was of a similar size to that found nationally (0.7 versus 0.7), while the average B/W d-value was somewhat smaller (0.8 versus 1.0). The reduced magnitude of the B/W d-value from these samples was likely due to a participant age and test type effect.

If you imply that BW gap is expected to be lower at early ages, I will not necessarily disagree, but by saying test type, it's not clear what you're referring to. But I see many tests are PPVT, or reading/vocabulary types. Did you mean the BW gap is lower in vocabulary test compared to non-vocabulary tests ?

The tests used are digit span forward (DSF), digit span backward (DSB); the Peabody achievement tests of math (PIAT-M), reading recognition (PIAT-RR), and reading comprehension (PIAT-RC); and the Peabody receptive vocabulary test (PPVT).

It should be Picture.

In the paragraph that follows, I don't see why you're talking about Flynn effect confoundings because you're looking to see whether age can make a difference, not if cohort makes a difference or not.

Sample sizes for each test/age combination correlate at >0.98 between races, giving approximately the same relative weights to the same tests across races.

Don't understand the sentence. What is being correlated with what ?

We used structural equation modeling to fit ACE models to family data.

Did you look at DeFries-Fulker regressions ?

Another assumption is that no assortative mating took place in the parental generation with respect to cognitive abilities. Violations of the first assumption may inflate heritability estimates, while violations of the second assumption may deflate them.

I have problems with the sentence. I thought that AM reduces heritability in twins because MZ twins are genetically identical (100%) and not DZ (50%). I don't see how it applies to siblings.

Depending on which estimates you choose, heritability is either similar or lower or higher in whites compared to non-whites

I prefer we choose.

Finally, somewhere, you cited Winship (2003). I didn't see the article appearing in your reference list.

I have attempted to replicate your results. I failed, and I will probably give up. NlsyLinks must hate me. You may want to look at your syntax again. Besides, if you want confidence intervals, given that your syntax ended up like this :ace <-AceLavaanGroup(dsClean) ace

D would have to help you with this. The syntax seems to be under continual revision, so you have to check the latest coding.

Fixed Vandenberg.

Sara Hart (personal communication, March, 16, 2014) provided twin correlations computed in relation to but not reported in Hart et al....You probably missed some words, e.g. "in relation to race groups".

I basically meant what I said. Try:

"Sara Hart (personal communication, March, 16, 2014) provided twin correlations computed in relation to (but not reported in) Hart et al. (2013)."

I mean that the results were computed in relation to -- though not presented in -- the paper Hart et al. (2013).

Fixed confound.

If you imply that BW gap is expected to be lower at early ages, I will not necessarily disagree, but by saying test type, it's not clear what you're referring to. But I see many tests are PPVT, or reading/vocabulary types. Did you mean the BW gap is lower in vocabulary test compared to non-vocabulary tests ?

I deleted the sentence as I didn't find a correlation between age and d; I imagine that g-load (or test type) was an issue, but I have no way of determining. Basically, many of these samples didn't use FSIQ scores, which probably had an effect on the magnitude of the B/W differences.

Fixed Picture.

In the paragraph that follows, I don't see why you're talking about Flynn effect confoundings because you're looking to see whether age can make a difference, not if cohort makes a difference or not.

A differential Flynn effect across cohorts (and so ages groups) could mess up our ACE estimates. But there didn't seem to be one.

Sample sizes for each test/age combination correlate at >0.98 between races, giving approximately the same relative weights to the same tests across races.....Don't understand the sentence. What is being correlated with what ?

We N weight averaged across subtests. If there was a N x subtest x race interaction that could have impacted our results as then our averages would not be isometric. However, there seemed to be no interaction.

We used SEM because it's more standard. We did check DF; the results were comparable. See at the very bottom of the page here, for example.

I have problems with the sentence. I thought that AM reduces heritability in twins because MZ twins are genetically identical (100%) and not DZ (50%). I don't see how it applies to siblings.

Maybe D can comment. I thought AM raised the correlations between first degree (but non MZ) relative. How does it affect Cousins and HS?

I prefer we choose.

Fixed.

Finally, somewhere, you cited Winship (2003). I didn't see the article appearing in your reference list.

Fixed.

As I said, the A, C and E letters have problems.

We added the following footnote:

"[FOOTNOTE] Some of the genetic variance in IQ is probably non-additive in nature (Vinkhuyzen et al., 2012), but due to data and modeling limitations most studies assume additivity. We follow this convention in our analyses. In practice, the estimates for additive genetic components that we report may include some interactive genetic effects; this is probably particularly true for the estimates based on Falconer’s formula, which tend to be closer to the total genetic influence than to the additive genetic influence (Falconer and Mackay, 1996). "

Thus we acknowledged that our A could include non-additive effects, but that we assume that it doesn't.

As for tables, I don't want to waste a lot of time on these. OBG isn't too picky about format.

New Version.

The reason why I asked for the syntax is because i prefer not to write a reply if I found something was wrong. Concerning AM, it's not really big thing either (even though it annoys me somewhat). The most important thing is that you get your analysis right, and I don't disagree with what you did or how you interpret the results.

I can give my approval for this piece. However, I would like the tables to be better made next time.

In your final version, don't forget to change "Meile" by "Miele" :

Three of the studies, Vandenberg (1970), Osborne and Meile (1969), and Osborne and Gregor (1968), were redundant with Osborne (1980) and so were excluded.

I can give my approval for this piece. However, I would like the tables to be better made next time.

In your final version, don't forget to change "Meile" by "Miele" :

Three of the studies, Vandenberg (1970), Osborne and Meile (1969), and Osborne and Gregor (1968), were redundant with Osborne (1980) and so were excluded.

So I have one tentative approval.

Emil and Davide can you review my corrections?

Note that I am just being useful and reviewing, I am not a reviewer for this journal so my vote has no power.

That's a problem, since this leaves, apart from MH:

Duxide
Peter Frost
nooffensebut

HBFFernandes
LYNNR540@aol.com
Gmeisenberg

And the latter three aren't particularly involved; can I submit this to ODP, instead?

Chuck, what do you mean by "tentative approval" ? Maybe my post wasn't very clear, but in fact I already gave you my approval. You have it. Concerning switching from OBG to ODP, my question is... is that really appropriate ? I know this journal don't have lot of OBG reviewers, or enough to get involved, but still, I'm wondering if it's alright with ODP. Ideally, we should probably try to email some people around, and see if they accept to review it (that is, if nooffensebut, Piffer, Frost and others here are uninvolved). One problem is that non-hereditarians will surely not approve it, for ideological and political reasons. So, you have only a very limited pool of reviewers.

I can give my approval for this piece. However, I would like the tables to be better made next time.

In your final version, don't forget to change "Meile" by "Miele" :

Three of the studies, Vandenberg (1970), Osborne and Meile (1969), and Osborne and Gregor (1968), were redundant with Osborne (1980) and so were excluded.

So I have one tentative approval.

Emil and Davide can you review my corrections?

I reviewed it and I eventually will give you my approval. I still have a quibble: I've never met the word "Environmentality" in the context of behavior genetics before. It sounds odd. Where did you get it from?

I reviewed it and I eventually will give you my approval. I still have a quibble: I've never met the word "Environmentality" in the context of behavior genetics before. It sounds odd. Where did you get it from?

I first saw it in Rushton and Jensen (2005; 2010), then elsewhere.

It's: 1-heritability

"cultural theory predicts a positive correlation between environmentality and group differences." (Rushton, J. P., & Jensen, A. R. (2010)

I have seen it multiple times. Plomin et al 2012 use it as a headline even. Jensen 1998 uses it on p. 449. About 500 results on Google for: environmentality hereditability.

I've done half a PhD in behavior genetics and attended conferences and workshops on BG but I never heard that expression. It's totally underused.
Wikipedia has only this definition, which is entirely different: http://en.wikipedia.org/wiki/Ecogovernmentality

However, I acknowledge that some people use that word. It just sounded odd to me.

I give my approval for publication because I think this is an important area of research.

Now you've got 2 approvals (MH and myself). OpenPsych allows authors to pick an external reviewer with qualifications (it's not for the editor to vet that as this would introduce subjectivity and potential abuse of power so I cannot forbid you from naming anyone. I'll just trust your good sense and of course I can raise my objections if I am not satisfied and other reviewers can do the same, but as editor I cannot veto it. However, if 3 reviewers are against your external reviewer, you'll have to find another one, but hopefully this won't be necessary).