But at this point we frequently run into a problem: we have no clue what questions to ask with the model. The issue is not that we lack questions; it's that we have a hard time picking out important ones. Using math, we can make more detailed predictions about how the system should behave under certain conditions, but often testing those model-generated predictions don't a) tell us anything fundamentally new about the system and b) differ qualitatively from less precise predictions we could have made without the model.
The bottom line is that biologists are often stuck when it comes to asking system-level questions. So in step the engineers to the rescue. Engineers spend a lot of time thinking about control systems, feedback loops, robustness, etc. And they've been trained with the right mathematical framework for asking such questions; biologists who dip into this area are a little like an astronomer trying to solve a two-body problem without any calculus. Without the proper mathematical tools, you're going to have a hard time solving complex problems, no matter how good your intuition is.
Engineers who jump into systems biology bring a lot to the table, but I find that they often don't ask the kinds of questions that interest biologists. As an example, check out this older paper (PDF) by John Doyle and Marie Cseste. (If you're interested in the application of control theory to biology, Doyle's papers are the place to start.)
The goal of the paper is to "describe insights from engineering theory and practice that can shed some light on biological complexity." But the one major quantitative example in the paper is about robustness and fragility of feedback loops:
In most technologies as well as in biochemistry, it is relatively easy to build either uncertain, high-gain components or precise, low-gain ones; but the precise, high-gain systems essential to both biology and technology are impossible or prohibitively expensive to make unless a feedback strategy like that in Fig. 2 is used...
Even these simple toy examples show the robust yet fragile features of complex regulatory networks. Their outward signatures are extremely constant regulated variables (yet occasional cryptic fluctuations) as well as extraordinary robustness to component variations (yet rare but catastrophic cascading failures). These apparently paradoxical combinations can easily be a source of confusion to experimentalists, clinicians, and theoreticians alike (53), but are intrinsic features of highly optimized feedback regulation. Because net robustness and fragility are constrained quantities, they must be manipulated and controlled with and within complex networks, even more so than energy and materials. Figure 3B shows how extreme open-loop versus closed-loop behavior can be, and thus how dangerous loss of control is to a system relying on it. The tradeoff in Eq. 4 shows that even when working perfectly, net fragility is constrained, and thus some transient amplification is unavoidable.
This is a nice example of a systems-level question, the kind of question you can ask when you're not looking at individual components (like genes), but rather the functioning of the system as a whole. Certainly how you achieve robustness is one interesting question, but before the explosion of genomics and computational biology, you wouldn't find many biologists assigning that question a high priority. You can find hundreds of robustness studies now, because, frankly, we know how to study it. In other words, the kinds of questions we're asking in systems biology are determined not by what is most intellectually pressing, but by what we know how to do. (The same thing is true in a related area, noise in biological systems.)
The questions that most molecular biologists have long been interested in relate to function. Instead of understanding how a feedback loop achieves robustness to fluctuations in parameters, I want to understand how a cellular system reads information from various sources, makes a decision (like, say, a cell fate decision), and then executes a genetic program to carry out the decision. That is the kind of thing I want to study quantitatively. Certainly robustness and noise play a role here, but they aren't really the main issues. Information processing and decision making are much more interesting.
I'm afraid that systems biology, in spite of the hype surrounding it, is going to be limited in the intellectual contributions it makes to biology as a whole, until systems biologists figure out how to address questions whose answers will change the way all biologists think.